Author Response

Reviewer #1 (Public Review):

The manuscript is very-well written. Although the study is well-conducted the authors should be more convincing on how bacteria residing in tissues do not induce death. The association with IL-10 cytokine production appears weak and more experiments are needed to make it more robust.

Thank you very much for your thoughtful and constructive feedback on our manuscript. We appreciate your positive assessment of the writing quality and the acknowledgment of the wellconducted nature of the study.

In regard to the reviewer's comment that "The association with IL-10 cytokine production appears weak," we would like to provide a comprehensive response based on the findings and insights presented in our study (Fig 5). We would like to emphasize several key points to further elucidate this association:

The established knowledge underscores IL-10's capacity to hinder the activation and proliferation of macrophages, thereby safeguarding against an overly aggressive immune-inflammatory reaction (as referenced). In our earlier investigations, we demonstrated that NAD+ orchestrates a systemic generation of IL-10, which assumes a pivotal function in curtailing proinflammatory responses across various conditions, such as autoimmune diseases (as referenced), alloimmunity (as referenced), and bacterial infections (as referenced). In our latest research, we divulge that the introduction of NAD+ leads to an elevated occurrence of IL-10-producing CD4+ T cells, CD8+ T cells, and macrophages, although not dendritic cells (depicted in Figure 5B and C). Furthermore, our comprehensive analyses have substantiated that NAD+ administration thwarts pyroptosis by specifically targeting the non-canonical inflammasome pathway. Intriguingly, our in vitro outcomes suggest that the neutralization of the autocrine IL-10 signaling pathway through a neutralizing antibody and an IL-10 receptor antagonist partially reverses the NAD+-mediated blockage of pyroptosis. These in vitro results imply that NAD+ induces the production of IL-10 cytokines by macrophages, contributing to the suppression of pyroptosis. To corroborate our in vitro conclusions, we employed IL-10 knockout mice and wild-type mice, both treated with either NAD+ or a placebo solution. The wild-type mice treated with NAD+ displayed a survival rate exceeding 80%, whereas the IL-10 knockout mice exhibited a survival rate of "only" 40%. These in vivo findings align with our in vitro discoveries, underscoring the crucial role of NAD+mediated IL-10 cytokine production in impeding pyroptosis through NAD+ and shielding against septic shock. Drawing from our prior and current investigations, we respectfully disagree with the reviewer's characterization of our work as "weak."

Reviewer #2 (Public Review):<br /> Iske et al. provide experimental data that NAD+ lessens disease severity in bacterial sepsis without impacting on the host pathogen load. They show that in macrophages, NAD+ prevents Il1b secretion potentially mediated by Caspase11.

Thank you for taking the time to review our manuscript. We appreciate your insightful comments and valuable feedback regarding our study on the role protective role and underlying mechanisms of NAD+ in septic shock.

While the in vivo and in vitro data is interesting and hints towards a crucial role of NAD+ to promote metabolic adaptation in sepsis, the manuscript has shortcomings and would profit from several changes and additional experiments that support the claims.

We would like to point out that our current study does not underscore a metabolic adaptation in sepsis but more an immune regulation and a specific blockade of the non-canonical inflammasome signaling machinery.

Conceptually, the definition of sepsis is outdated. Sepsis is not SIRS, as in sepsis-2. Sepsis-3 defines sepsis as infection-associated organ dysfunction. This concept needs to be taken into account for the introduction and when describing the potential effects of NAD+ in sepsis. Also, LPS application cannot be considered a sepsis model, since it only recapitulates the consequence of TLR-4 activation. It is a model of endotoxemia. Also, the LPS data does not allow to draw conclusions about bacterial clearance (L135).

Our study uses highly lethal doses of E. Coli or LPS. These doses have been shown to result in multiple organ failure (1, 2). For many decades until now an un-numerable number of studies have used LPS as a model of sepsis (3, 4, 5). We have used LPS animal model based on a study published in 2013 by Kayagaki et al. (1), where the authors reported a novel TLR4-independent mechanism but mediated via activate caspase-11. We used the same animal model to demonstrate the specific role of NAD+ in targeting this TLR4-independent mechanism but mediated via activate caspase-11 and underscore NAD+’s mode of protection.

Moreover, we have not only used LPS but bacterial infection as well using E. Coli. We have also previously published an additional research article demonstrating the protective effect against Listeria Monocytogenes (6). The only model we currently did not use in our current study, is a cecal ligation puncture (CLP) model which is also another common animal model for sepsis.

Our conclusions regarding bacterial clearance are based not only on LPS results but also based on the bacterial load measurement and survival (Figure 1B&C) following E. Coli administration in different tissues (kidney and liver) and not LPS.

The authors state that protective effects by NAD were independent of the host pathogen load. This clearly indicates that NAD confers protection via enhancing a disease tolerance mechanism, potentially via reducing immunopathology. This aspect is not considered by the authors. The authors should incorporate the concept of disease tolerance in their work, cite the relevant literature on the topic and discuss it their findings in light of the published evidence for metabolic alteration sand adaptations in sepsis.

We respectfully disagree with the reviewer’s comment and do not believe that NAD+ enhances disease tolerance. We have supporting data indicating that NAD+ mediates protection via a specific blockade of the non-canonical inflammasome pathway, which prevents an over-zealous immune response that results in organ damage and multiple organ failure (MOF). Moreover, we demonstrate that not only NAD+ mediates protection via a specific blockade of the non-canonical inflammasome pathway but prevents septic shock induced death by an additional immunosuppression mediated by the systemic production of IL-10.

Both Caspase-11 and IL-10 pathways are crucial in NAD+ mediated protection against lethal doses of E. Coli and LPS administration. Figure 5A indicates that caspase-11-/- mice treated with PBS have a modest survival rate (~40% survival) when compared to the group of mice treated with NAD+ (>80% survival). These data indicate that NAD+ promotes survival via a caspase-11independent mechanism. Similarly, wild type mice subjected to NAD+ administration exhibited >80% survival, while NAD+ administration to IL-10-/- mice resulted only in a 40% survival rate. Based on these findings, we believe that NAD+ mediated protection against septic shock via a blockade of caspase-11 blockade and by IL-10 cytokine production that dampened the overzealous immune response rather than a disease tolerance.

For the in vitro data, the manuscript would benefit from additional experiments using in vitro infection models.

In the current study we have used two in vivo models using LPS and E. Coli a gram-negative bacterium. We have also previously reported the protective role of NAD+ in the context of Listeria Monocytogenes (6) a gram-positive bacterium. In the current study, our aim was to demonstrate the inhibitory role of NAD+ on the non-canonical pathway specifically. We believe that additional in vitro experiments for this study are out of scope.

In the merge manuscript, the authors provide two different versions of the figures. In one, bar plots are shown without individual data and in the other with scatter blots. All bar plots need to be provided as scatter plots showing individual values.

As requested by reviewer #2 all bar plots are now provided as scatter plots showing individual values.

The authors should show further serology data for kidney and liver failure etc. as well as further cytokine data such as IL-6 and TNF to better characterize their models.

We did not perform further serology analysis, but we did measure IL-6 and TNFα in mice treated with NAD+ or PBS. Mice treated with NAD+ had a reduced systemic level of both cytokines IL-6 and TNFα. We have now added the figures (Figure 1F). In addition, we performed a long-term survival, and all mice treated with NAD+ recovered fully after 10 days and survived over a year after infection. In addition, the mice that survived following NAD+ treatment died of old age.

Careful revision of the entire manuscript, the figure legends and figures is required. The figure legend should not repeat the methods and materials section. The nomenclature for mouse protein and genes needs to be thoroughly revised.

A Careful revision of the entire manuscript has been performed.

L350. The authors write that they dissect the capacity of NAD+ to dampen auto- and alloimmunity. In this work, no data that supports this statement is shown and experiments with autoantigens or alloantigens are not performed.

We thank the reviewer for this comment. We have now re-phrased our last sentence in the discussion and included references for our previous work. We have now stated:” We have previously reported that NAD+ administration can block auto- (7) and allo-immunity (8) via IL10 cytokine production. Here, we unveiled the capacity of NAD+ to protect against sepsisinduced death via a specific blockade of the non-canonical inflammasome pathway and a robust immunosuppression mediated by IL-10 cytokine production.

L163 The authors describe pyroptosis but in the figure legend call it apoptosis. Specific markers for each cell death should be measured and determined which cell death mechanisms is involved.

We thank the reviewer for this comment. We have focuses on pyoptosis-mediated cell death and not apoptosis. We have now replaced the term “apoptosis” by “pyroptosis-mediated to cell death”.

Animal data comes from an infection model and LPS application. The RNAseq data is obtained from cells primed with Pam3CSK4 and subsequently subjected to LPS. It is unclear how the cell culture model reflects the animal model. As such the link between IFN signaling and the bacterial infection/LPS model are not convincing and need to be further elaborated.

Our findings, depicted in Figure 3, pertain exclusively to in vitro investigations rather than in vivo examinations. Our research has demonstrated the selective inhibition of the non-canonical inflammasome pathway by NAD+, with a primary focus on unraveling the specific signaling pathway influenced by NAD+. Our in vitro outcomes indicate that the introduction of recombinant IFN-β counteracted the inhibitory effect of NAD+ on the non-canonical pathway. However, it's important to note that we have not evaluated the IFN-β pathway within our E. Coli and LPS in vivo models. Our primary intention was to exclusively decipher the roles of IFN-β and NAD+ in the context of inhibiting the non-canonical inflammasome, without extending our investigation to the broader in vivo scenarios.

Figure 5: It is unclear how many independent survival experiments were done, how many mice per group were used and whether the difference between groups was statistical significant. This information should be added.

We have now included the number of experiments, p values and number of animals used in Figure 5.

Further experiments with primary cells from Il10 k.o. and Caspase11 k.o. animals should be provided that support the findings in macrophages.”

We concur with the reviewer's suggestion regarding the need for further experiments involving primary cells from IL-10-/- and Caspase-11-/- mice. However, we are uncertain about the potential contribution of these experiments in generating novel or supplementary findings to the existing study.

Author Response

Reviewer #1 (Public Review):

The goal of this study is to understand the allosteric mechanism of overall activity regulation in an anaerobic ribonucleotide reductase (RNR) that contains an ATP-cone domain. Through cryo-EM structural analysis of various nucleotide-bound states of the RNR, the mechanism of dATP inhibition is found to involve order-disorder transitions in the active site. These effects appear to prevent substrate binding and a radical transfer needed to initiate the reaction.

Strengths of the manuscript include the comprehensive nature of the work - including numerous structures of different forms of the RNR and detailed characterization of enzyme activity to establish the parameters of dATP inhibition. The manuscript could be improved, however, by performing additional experiments to establish that the mechanism of inhibition can be observed in other contexts and it is not an artifact of the structural approach. Additionally, some of the presentations of biochemical data could be improved to comply with standard best practices.

The work is impactful because it reports initial observations about a potentially new mode of allosteric inhibition in this enzyme class. It also sets the stage for future work to understand the molecular basis for this phenomenon in more detail.

We thank the editor and reviewers for their positive evaluation of the potential impact of our work. We completely agree that hypotheses based on structural data require orthogonal experimental verification. However, the number and consistency of the cryo-EM structures speak in favour of the data being representative of conditions in solution. We feel that in particular cryo-EM data should be relatively free of artefacts, e.g. biased or incorrect relative domain orientations or artificially reduced mobility, compared to crystallography, where crystal packing effects can affect these parameters. As we write in response to Reviewer #2, it has been difficult to propose a direct structural mechanism for transmission of the allosteric signal from the a-site in the ATP-cone to the active site and GRD given that the ATP-cones and linker are disordered in the dATP-bound dimers and only partly ordered in the dATP-bound tetramers. Further verification experiments will be performed in future but are outside the scope of the present article.

We will improve the presentation of the biochemical data in a revised version.

General comments:

1) It would be ideal to perform an additional experiment of some type to confirm the order-disorder phenomena observed in the cryo-EM structures to rule out the possibility that it is an artifact of the structure determination approach. Circular dichroism might be a possibility?

Circular dichroism reports only on the approximate relative proportions of helix, sheet and loop structure in a protein; thus we believe that it would not be a sensitive enough tool to distinguish between ordered and disordered states of the GRD. We are considering what alternative methods might be appropriate.

2) Does the disordering phenomenon of one subunit in the ATP-bound structures have any significance - could it be related to half-of-sites activity? Does this RNR exhibit half-of-sites activity?

Half-of-sites activity has not been biochemically proven in any ribonucleotide reductase although it was first suggested in 1987 (PMID: 3298261). However, a strong structural indication was recently published in the form of the holo-complex of the class Ia ribonucleotide reductase from Escherichia coli, which is highly asymmetrical and in which productive contacts forming an intact proton-coupled electron transfer pathway are only formed between one of two pairs of monomers (PMID: 32217749). We have not been able to prove half-of-sites activity for PcNrdD due to low overall radical content, but the structural results are indeed consistent with such an activity.

3) Does the disordering of the GRD with dATP bound have any long-term impact on the stability of the Gly radical? I realize that the authors tested the ability to form the Gly radical in the presence of dATP in Fig. 4 of the manuscript. But it looks like they only analyzed the samples after 20 min of incubation. Were longer time points analyzed?

Radical content was measured after 5 min and 20 min incubation; 5 min incubations (not included in the manuscript) consistently gave higher radical content compared to 20 min incubation. Longer time points were not analysed, as we assumed that the radical content would be even lower after 20 min.

4) Did the authors establish whether the effect of dATP inhibition on substrate binding is reversible? If dATP is removed, can substrates rebind?

This is an interesting question. We measured KDs for dATP in the micromolar range and are hence confident that dATP binding is reversible. Our measurements do not, however, directly prove that inhibition of the enzyme is reversible. Nevertheless, it is worth noting that the protein as purified contained significant amounts of dATP and purification conditions had to be optimised to remove dATP. This is evidence that PcNrdD that has “seen” dATP can subsequently bind substrate in the presence of ATP. We will describe the purification more clearly in a revision.

5) In some figures (Fig. 6e, for example), the cryo-EM density map for the nucleotide component of the model is not continuous over the entire molecule. Can the authors comment on the significance of this phenomenon? Were the ligands validated in any way to ensure that the assignments were made correctly?

Indeed, we sometimes saw discontinuous density for the nucleotides, both in the active site and in the specificity site. However, the break was almost always near the C5’ carbon atom, which is common to all nucleotides. While we cannot readily explain this phenomenon, the nucleotides refined well with full occupancy, giving B-factors similar to those of the surrounding protein atoms. The identity of the nucleotide could always be inferred from a) the size of the base (purine or pyrimidine); b) the known nucleotide combinations added to the protein before grid preparation; c) prior knowledge on the combinations of effector and substrate that have been found valid for all RNRs since the first studies of allosteric specificity regulation.

Reviewer #2 (Public Review):

This manuscript describes the functional and structural characterization of an anaerobic (Class III) ribonucleotide reductase (RNR) with an ATP cone domain from Prevotella copri (PcNrdD). Most significantly, the cryo-EM structural characterization revealed the presence of a flap domain that connects the ATP cone domain and the active site and provides structural insights about how nucleotides and deoxynucleotides bind to this enzyme. The authors also demonstrated the catalytic functions and the oligomeric states. However, many of the biochemical characterizations are incomplete, and it is difficult to make mechanistic conclusions from the reported structures. The reported nucleotide-binding constants may not be accurate because of the design of the assays, which complicates the interpretation of the effects of ATP and dATP on PcNrdD oligomeric states. Importantly, statistical information was missing in most of the biochemical data. Also, while the authors concluded that the dATP binding makes the GRD flexible based on the absence of cryo-EM density for GRD in the dATP-bound PcNrdD, no other supports were provided. There was also a concern about the relevance of the proposed GRD flexibility and the stability of Gly radical. Overall, the manuscript provides structural insights about Class III RNR with ATP cone domain and how it binds ATP and dATP allosteric effectors. However, ambiguity remains about the molecular mechanism by which the dATP binding to the ATP cone domain inhibits the Class III RNR activity.

Strengths:

1) The manuscript reports the first near-atomic resolution of the structures of Class III RNR with ATP domain in complex with ATP and dATP. These structures revealed the NxN flap domain proposed to form an interaction network between the substrate, the linker to the ATP cone domain, the GRD, and loop 2 important for substrate specificity. The structures also provided insights into how ATP and dATP bind to the ATP cone domain of Class III RNR. Also, the structures suggested that the ATP cone domain is directly involved in the tetramer formation by forming an interaction with the core domain in the presence of dATP. These observations serve as an important basis for future study on the mechanism of Allosteric regulation of Class III RNR.

2) The authors used a wide range of methodologies including activity assays, nucleotide binding assays, oligomeric state determination, and cryo-EM structural characterization, which were impressive and necessary to understand the complex allosteric regulation of RNR.

3) The activity assays demonstrated the catalytic function of PcNrdD and its ability to be activated by ATP and low-concentration dATP and inhibited by high-concentration dATP.

4) ITC and MST were used to show the ability of PcNrdD to bind NTP and dATP.

5) GEMMA was used successfully to determine the oligomeric state of PcNrdD, which suggested that PcNrdD exists in dimeric and tetrameric forms, whose ratio is affected by ATP and/or dATP.

Weaknesses:

1) Activity assays.

The activity assays were performed under conditions that may not represent the nucleotide reduction activity. The authors initiated the Gly radical formation and nucleotide reduction simultaneously. The authors also showed that the amount of Gly radical formation was different in the presence of ATP vs dATP. Therefore, it is possible that the observed Vmax is affected by the amount of Gly radical. In fact, some of the data fit poorly into the kinetic model. Also, the number of biological and technical replicates was not described, and no statistical information was provided for the curve fitting.

The highest turnover activity of PcNrdD measured in presence of ATP was 1.3 s-1 (470 nmol/min/mg), a kcat comparable to recently reported values for anaerobic and aerobic RNRs from Neisseria bacilliformis, Leeuwenhoekiella blandensis, Facklamia ignava, Thermus virus P74-23, and Aquifex aeolicus (PMID: 25157154, PMID: 29388911, PMID: 30166338, PMID: 34314684, PMID: 34941255). The general trend illustrated in Figure 1 is that ATP has an activating effect, whereas high concentrations of dATP have an inactivating effect, which cannot be explained by suboptimal assay conditions since our EPR results consistently show that more radical is formed in incubations with dATP compared to incubations with ATP. Curve fitting methods used are listed in Materials and Methods (as specified in the Figure 1 legend), and standard errors for all specified curve fitting results (from triplicate experiments) are shown in Figure 1.

2) Binding assays.

The interpretation of the binding assays is complicated by the fact that dATP binds both a- and s-sites and ATP binds a- and active sites. dATP may also bind the active site as the product. It is unknown if ATP binds s-site in PcNrdD. Despite this complexity, the binding assays were performed under the condition that all the binding sites were available. Therefore, it is not clear which event these assays are reporting.

Both ITC and MST experiments involving ATP and dATP binding to the a-site were performed in the presence of at least 1 mM GTP substrate (5 mM in MST) to fill the active site, and 1 mM dTTP effector to fill the s-site (specified in the legend to Figure 2). These conditions enable binding of ATP or dATP only to the a-site in the ATP-cone.

3) Oligomeric states.

Due to the ambiguity in the kinetic parameters and the binding constants determined above, the effects of ATP and dATP on the oligomeric states are difficult to interpret. The concentrations of ATP used in these experiments (50 and 100 uM) were significantly lower than KL determined by the activity assays (780 uM), while it is close to the Kd values determined by ITC or MST (~25 uM). Since it is unclear what binding events ITC and MST are reporting, the data in Figure 3 does not provide support for the claimed effects of ATP binding. For the effects of dATP, the authors did not observe a significant difference in oligomeric states between 50 or 100 uM dATP alone vs 50 uM dATP and 100 uM CTP. The former condition has dATP ~ 2x higher than the Kd and KL (Figure 1b) and therefore could be considered as "inhibited". On the other hand, NrdD should be fully active under the latter condition. Therefore, these observations show no correlation between the oligomeric state and the catalytic activity.

The results in Figure 3 show that at in presence of 100 µM ATP plus 100 µM CTP the oligomeric equilibrium is 64% dimers plus 36% tetramers, and in presence of 50-100 µM dATP the oligomeric equilibrium is 32% dimers and 68% tetramers. We agree that there is no clear and strong correlation between oligomeric state and inhibition. We will also try to make it clearer in a revised version. Meanwhile, to add some further clarity, SEC experiments at higher nucleotide concentrations will be included in the revision.

4) Effects of dATP binding on GRD structure

One of the key conclusions of this manuscript is that dATP binding induces the dissociation of GRD from the active site. However, the structures did not provide an explanation for how the dATP binding affects the conformation of GRD or whether the dissociation of GRD is a direct consequence of dATP binding or it is due to the absence of nucleotide substrate. Also, Gly radical is unlikely to be stable when it is not protected from the bulk solvent. Therefore, it is unlikely that the GRD dissociates from the active site unless the inhibition by dATP is irreversible. Further evidence is needed to support the proposed mechanism of inhibition by dATP.

We admit that it has been difficult to propose a direct structural mechanism for transmission of the allosteric signal from the a-site in the ATP-cone to the active site and GRD given that the ATP-cones and linker are disordered in the dATP-bound dimers and that the linker can only be partly modelled in the dATP-bound tetramers. Most likely dATP binding causes a change in the dynamics of the linker region and NxN flap that directly affects substrate binding and simultaneously causes disorder of the GRD, given that all are part of a connected system (described as “nexus” in the manuscript). The structures determined in the presence of dATP and CTP show that CTP cannot bind in the absence of an ordered NxN flap.

In any case a major conclusion of the work is that dATP does not inhibit the anaerobic RNR by prevention of glycyl radical formation but by prevention of its subsequent transfer. We agree that further evidence is required to support the proposed mechanism but, given the extent of the data already presented in the manuscript, we feel that such studies should be the subject of a future publication.

5) Functional support for the observed structures.

Evidence for connecting structural observations and mechanistic conclusions is largely missing. For example, the authors proposed that the interactions between the ATP cone domain and the core domain are responsible for tetramer formation. However, no biochemical evidence was provided to support this proposal. Similarly, the functional significance of the interaction through the NxN flap domain was not proved by mutagenesis experiments.

We did actually make mutants to verify the observed interactions in the tetramer, but several of them did not behave well in our hands, e.g. with regard to protein stability. Since we have no evidence that oligomerisation is coupled to inhibition, and since we did not observe any conservation between protein sequences in the interaction area, we chose not to pursue this point further. The main merit of the tetramer structures is that they allowed a high-resolution view of dATP binding to the ATP-cone and a comparison to previously observed ATP-cones. Nevertheless, mutation experiments, also including the NxN flap, could be the subject of future work.

Reviewer #3 (Public Review):

The manuscript by Bimai et al describes a structural and functional characterization of an anaerobic ribonucleotide reductase (RNR) enzyme from the human microbe, P. copri. More specifically, the authors aimed to characterize the mechanism by how (d)ATP modulates nucleotide reduction in this anaerobic RNR, using a combination of enzyme kinetics, binding thermodynamics, and cryo-EM structural determination. One of the principal findings of this paper is the ordering of a NxN 'flap' in the presence of ATP that promotes RNR catalysis and the disordering of both this flap and the glycyl radical domain (GRD) when the inhibitory effector, dATP, binds. The latter is correlated with a loss of substrate binding, which is the likely mechanism for dATP inhibition. It is important to note that the GRD is remote (>30 Ang) from the binding site of the dATP molecule, suggesting long-range communication of the structural (dis)ordering. The authors also present evidence for a shift in oligomerization in the presence of dATP. The work does provide evidence for new insights/views into the subtle differences of nucleotide modulation (allostery) of RNR through long-range interactions.

The strengths of the work are the impressive, in-depth structural analysis of the various regulated forms of PcRNR by (d)ATP using cryo-EM. The authors present seven different models in total, with striking differences in oligomerization and (dis)ordering of select structural features, including the GRD that is integral to catalysis. The authors present several, complementary biochemical experiments (ITC, MST, EPR, kinetics) aimed at resolving the binding and regulatory mechanism of the enzyme by various nucleotides. The authors present a good breadth of the literature in which the focus of allosteric regulation of RNRs has been on the aerobic orthologues.

Given the resolution of some of the structures in the remote regions that appear to be of importance, the rigor of the work could have been improved by complementing this experimental studies with molecular dynamics (MD) simulations to reveal the dynamics of the GRD and loops/flaps at the active site.

We will discuss this option with expert colleagues.

The biochemical data supporting the loss of substrate binding with dATP association is compelling, but the binding studies of the (d)ATP regulatory molecules are not; the authors noted less-than-unity binding stoichiometries for the effectors.

Most of the methods used measure only binding strength, not the number of binding sites (N), whereas ITC also measures number of sites. N is dependent on the integrity of the protein, i.e. the number of protein molecules in a preparation that are involved in binding, and quite often gives lower values than the theoretical number of binding sites.

Also, the work would benefit from additional support for oligomerization changes using an additional biochemical/biophysical approach.

SEC (chromatography), GEMMA (mass spectrometry) and cryo-EM were used to study oligomerization. Since each method has restrictions on nucleotide concentrations as well as protein concentrations that can be used, the results are not directly comparable, but all three methods indicate nucleotide dependent oligomerization changes. The SEC results will be included in a revised version.

Overall, the authors have mostly achieved their overall aims of the manuscript. With focused modifications, including additional control experiments, the manuscript should be a welcomed addition to the RNR field.

Author Response

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

Review 1

Public Review

The authors set out to develop an organoid model of the junction between early telencephalic and ocular tissues to model RGC development and pathfinding in a human model. The authors have succeeded in developing a robust model of optic stalk(OS) and optic disc(OD) tissue with innervating retinal ganglion cells. The OS and OD have a robust pattern with distinct developmental and functional borders that allow for a distinct pathway for pathfinding RGC neurites.

This study falls short on a thorough analysis of their single cell transcriptomics (scRNAseq). From the scRNAseq it is unclear the quality and quantity of the targeted cell types that exist in the model. A comparative analysis of the scRNAseq profiles of their cell-types with existing organoid protocols, to determine a technical improvement, or with fetal tissue, to determine fidelity to target cells, would greatly improve the description of this model and determine its utility. This is especially necessary for the RGCs developed in this protocol as they recommend this as an improved model to study RGCs.

Future work targeting RGC neurite outgrowth mechanisms will be exciting.

We are grateful to Reviewer 1 for these constructive comments. We added plots for quality control in supp. Fig. S5 and quantification of cell clusters in Tab. 1. We compared the transcriptomes between CONCEPT organoids, Gabriel et al.’s brain/optic organoids (Gabriel et al., 2021; PMID: 34407456), and human fetal retinas HGW9 (Lu et al., 2020; PMID: 32386599), which strongly support our findings (Figs. 5, 6; see responses below for details). Besides FGFs/FGFR signaling, scRNA-seq identified additional candidate molecules that may provide axon guidance functions, and these candidate molecules are the focus of our future study.

Recommendations For The Authors

This study falls short on a thorough analysis of their single cell transcriptomics (scRNAseq).

The scRNAseq figure needs to be better presented to allow for an adequate assessment of the model. As written the classification of the different clusters is hard to follow. A representative labeling of the suspected identity of the clusters in an infographic would aid the figure. Since it is hard to follow it is difficult to determine how well clusters correlate with designated cell types. PAX2 expression designating optic stalk seems to correlate well with the group 2 and the designation of the Optic disk, however PAX2 expression for the optic stalk is half in group 4 and half in group 9. what are group 4 and 9? It is also not clear how the thresholding for the given clusters was reached.

To present the scRNA-seq dataset in a clearer way, we added dotted red lines in Fig. 4C to delineate eye (mostly retinal), telencephalic, and mixed cell populations. In Tab. 1, we showed assigned cell types, counts, and percentage for each cluster.

PAX2+ VSX2- optic stalk cells were at edges of clusters 4, 8, 9 that had dorsal telencephalic identities. Clusters 4, 8, 9 were largely segregated along cell cycle phases (Fig. 4A, B, F), and these clusters differentially expressed gene markers SOX3, FGFR2, PRRX1, EDNRB, and FOXG1 (supp. Fig. S7A-S7D; Fig. 4C). In E14.5 mouse embryos, mouse orthologs of SOX3, FGFR2, PRRX1, and EDNRB were specifically expressed in dorsal telencephalon (Fig. S8AS8E); Foxg1 was specifically expressed in both dorsal and ventral telencephalon. Therefore, clusters 4, 8, and 9 have dorsal telencephalic identities, and PAX2+ VSX2- optic stalk cells are at edges of these telencephalic clusters. Lines 259-261; 297-298.

Thresholding of cell clusters were determined by cell clustering parameters, which is described in Materials and Methods: FindVariableFeatures (selection.method = "vst", nfeatures = 2000), ScaleData, RunPCA, ElbowPlot, FindNeighbors (dims = 1:17), FindClusters (resolution = 0.5), and RunUMAP(dims = 1:17). Lines 717-721.

The authors should make an attempt to calculate which different cell types are present and in what proportions. They should also discuss groups that are confounding. Since this is the first description of this technique it is critical to know how much of the model represents mature welldefined cells of interest.

We assigned cell types to clusters and calculated cell counts and proportions of each cluster (Tab.1). The only undetermined cell cluster was cluster 13, which was the smallest one. We described top DEGs of cluster 13 and discussed the cluster. Lines 266-268.

Concerning the focus on RGC isolation. It is interesting that CNTN2 can be used for an effective isolation however, there are many protocols for generating RGCs. Is CNTN2 expression unique to this protocol? If the authors claim that this protocol could be used for studying glaucoma, how does this protocol improve on the quality of RGCs compared to other protocols?

RGC-specific CNTN2 expression was not unique to CONCEPT organoids. We isolated RGCs via CNTN2 from both CONCEPT organoids and 3-D retinal organoids in suspension. Indeed, isolated RGCs shown in the manuscript were from 3-D retinal organoids (see Materials and Methods for details). Importantly, our single cell RNA sequencing analysis demonstrated that CNTN2 was also differentially expressed in early RGCs from human fetal retinas (Fig. 5L, 5M). Therefore, isolation of human early RGCs via CNTN2 should be applicable widely.

In CONCEPT organoids, RGC differentiation and directional axon growth were very efficient. Our study supports a model that FGFs from optic disc cells efficiently induce RGC differentiation and directional axon growth in adjacent retinal progenitor cells, as FGFR inhibitions drastically decreased the number of RGC somas and directional axon growth (Fig. 9). Therefore, CONCEPT organoids are useful in studying axon guidance cues in humans, which knowledge is much needed for axon regrowth from RGCs that are damaged in glaucoma. Notably, juvenile glaucoma gene CYP1B1 was found in assigned optic disc cells in both CONCEPT organoids and human fetal retinas (Fig. 4I, 5D), making CONCEPT organoids a testable model in studying the functions of CYP1B1 in human cells.

A comparative analysis of the scRNAseq profiles of their model with existing organoid protocols, to determine a technical improvement, or with fetal tissue, to determine fidelity to target cells, would greatly improve the description of this model and determine its utility.

In the revised manuscript, we compared the transcriptomes between CONCEPT organoids, Gabriel et al.’s brain/optic organoids (Gabriel et al., 2021; PMID: 34407456), and human fetal retinas HGW9 (Lu et al., 2020; PMID: 32386599). Gabriel et al. (2021) report “axon-like” projections in their “optic vesicle-containing brain organoids”. We found that PAX2+ optic disc, PAX2+ optic stalk, FOXG1+ telencephalic, and VSX2+ neuroretinal cell clusters that were found in CONCEPT organoids did not exist in Gabriel et al.’s organoids (supp. Fig. S12), indicating striking differences between Gabriel et al.’s organoids and our CONCEPT telencephalon-eye organoids.

On the other hand, CONCEPT organoids and human fetal retinas HGW9 had similar expression signatures (Fig. 5). First, we identified a PAX2+ cell cluster in the human retinas HGW9. 64/113 DEGs in the PAX2+ cluster from human fetal retinas HGW9 were also DEGs of cluster 2 (assigned PAX2+ optic disc cells) from CONCEPT organoids. Second, CNTN2 was also differentially expressed in early RGCs of human fetal retinas. Third, when cells in cluster 18 and retinal progenitor clusters from the HGW9 dataset were combined with cells in clusters 2, 4, 5, 7 from the CONCEPT dataset for Seurat anchor-based clustering, cells in cluster 18 from HGW9 (H18) were grouped with cluster 2 from CONCEPT organoids (C2, assigned optic disc; N), and these cells expressed both PAX2 and VSX2 (arrowheads in Fig. 5N-5R). A small portion of H18 cells were grouped with cluster 4 from CONCEPT organoids (C4, assigned optic stalk; N), and these cells expressed PAX2 but not VSX2 (arrows in Fig. 5N-5R). Fourth, CONCEPT organoids and human fetal retinas shared many enriched GO terms in DEGs of assigned optic disc cells (Fig. 6).

Collectively, transcriptomic comparisons support that our CONCEPT organoids are innovative and similar to human fetal retinas. Lines 325-392.

Not clear what reporting on Lens cells in Figure 3 adds to the focus of the manuscript. The figure seems out of place with the flow of the manuscript.

Lens cells were obvious in CONCEPT organoids. The presence of lens cells indicates that cysts have the developmental potential for both neural and non-neural anterior ectodermal cells. For a better flow, we added a transitional sentence at the beginning of the lens section. Lines 207208.

Reviewer #2

Public Review

The study by Liu et al. reports on the establishment and characterization of telencephalon eye structures that spontaneously form from human pluripotent stem cells. The reported structures are generated from embryonic cysts that self-form concentric zones (centroids) of telencephaliclike cells surrounded by ocular cell types. Interestingly, the cells in the outer zone of these concentric structures give rise to retinal ganglion cells (RGCs) based on the expression of several markers, and their neuronal morphology and electrophysiological activity. Single-cell analysis of these brain-eye centroids provides detailed transcriptomic information on the different cell types within them. The single-cell analysis led to the identification of a unique cellsurface marker (CNTN2) for the human ganglion cells. Use of this marker allowed the team to isolate the stem cell-derived RGCs.

Overall, the manuscript describes a method for generating self-forming structures of brain-eye lineages that mimic some of the early patterning events, possibly including the guidance cues that direct axonal growth of the RGCs. There are previous reports on brain-eye organoids with optic nerve-like connectivity; thus, the novel aspect of this study is the self-formation capacity of the centroids, including neurons with some RGC features. Notably, the manuscript further reports on cell-surface markers and an approach to generating and isolating human RGCs.

Recommendations For The Authors

The following significant issues, however, need to be addressed:

The authors show RGC-like cells that grow axons toward the Pax2+ cells, suggesting that this is a model for RGC axon pathfinding. Is there support from transcriptomic data on the expression of guidance molecules? In addition, the authors need to characterize Pax2+ cells further. Do some give rise to astrocyte-like cells?

We assessed the expression of known axon guidance genes in CONCEPT organoids. FGF8 and FGF9 trigger axon outgrowth in motor neuron column explants (Shirasaki et al., 2006). In CONCEPT organoids, FGF8 and FGF9 were differentially expressed in assigned optic disc cells; FGFR inhibition drastically decreased the number of RGC soma and directional axon growth (Fig. 9). In addition, SEMA5a and EFNB1 were expressed in both assigned optic disc and stalk cells, EFNB2 was highly expressed in assigned optic disc cells, and NTN1 was mostly expressed in assigned optic cells (supp. Fig. S12). Lines 307-310.

We compared the transcriptomes between CONCEPT organoids, Gabriel et al.’s brain/optic organoids (Gabriel et al., 2021; PMID: 34407456), and human fetal retinas HGW9 (Lu et al., 2020; PMID: 32386599). Gabriel et al. (2021) report “axon-like” projections in their “optic vesicle-containing brain organoids”. We found that PAX2+ optic disc, PAX2+ optic stalk, FOXG1+ telencephalic, and VSX2+ neuroretinal cell clusters that were found in CONCEPT organoids did not exist in Gabriel et al.’s organoids (supp. Fig. S12), indicating striking differences between Gabriel et al.’s organoids and our CONCEPT telencephalon-eye organoids. Lines 327-345.

To authenticate PAX2+ cells in CONCEPT organoids, we analyzed a single-cell RNA-seq dataset of human fetal retinas HGW9 and identified a similar PAX2+ cell population, cluster 18 (Fig. 5). Expression signatures of PAX2+ cells between CONCEPT organoids and human fetal retinas HGW9 were similar. Notably, cluster 18 differentially expressed PAX2, COL9A3, CYP1B1, SEMA5A, and FGF9 (Fig. 5B-5F), which were top DEGs of cluster 2 in CONCEPT organoids (Fig. 4F, 4G, 4I, 4K; SEMA5A was shown in supp. Fig. S12A). Overall, 64/113 DEGs of cluster 18 in human fetal retinas HGW9 were also DEGs of cluster 2 in CONCEPT organoids. In both HGW9 and CONCEPT organoids, expression of OLIG2, CD44, and GFAP was undetectable (supp. Fig. S14), indicating that astrocytes had not been generated yet at these stages.

When cells in cluster 18 and retinal progenitor clusters from the HGW9 dataset were combined with cells in clusters 2, 4, 5, 7 from the CONCEPT dataset for Seurat anchor-based clustering, cells in cluster 18 from HGW9 (H18) were grouped with cluster 2 from CONCEPT organoids (C2, assigned optic disc; N), and these cells expressed both PAX2 and VSX2 (arrowheads in Fig. 5N-5R). A small portion of H18 cells were grouped with cluster 4 from CONCEPT organoids (C4, assigned optic stalk; N), and these cells expressed PAX2 but not VSX2 (arrows in Fig. 5N5R).

We then compared functional annotations of DEGs (top 200 genes) of cluster 2 in CONCEPT organoids and DEGs (113 genes) of cluster 18 in human fetal retinas HGW9. Top GO terms in GO:MF, GO:CC, and GO:BP are shown (Fig. 6). For DEGs of cluster 2 in CONCEPT organoids, top enriched GO terms in GO:MF, GO:CC, and GO:BP were extracellular matrix structural constituent, collagen-containing extracellular matrix, and system development, respectively. Additional interesting GO:BP terms included axon development, astrocyte development, eye development, response to growth factor, cell adhesion, cell motility, neuron projection development, glial cell differentiation, and signal transduction. For DEGs of cluster 18 in human fetal retinas HGW9, top enriched GO terms in GO:MF, GO:CC, and GO:BP were cell adhesion molecule binding, extracellular space, and developmental process, respectively. Many GO terms were enriched in both samples, further indicating transcriptomic similarities in PAX2+ optic disc cells between CONCEPT organoids and human fetal retinas. Notably, GO terms astrocyte differentiation, neuron projection development, and glial cell differentiation were enriched in the DEGs of assigned optic disc cells for both CONCEPT organoids and human fetal retinas, consistent with expectations.

Transcriptomic comparisons between CONCEPT organoids and human fetal retinas are found in lines 346-392.

The Vsx2+Pax2+ population is not typically detected in vivo in the developing mouse eye. The authors claim that they detected them in vivo, but the data supporting this statement are lacking.

We demonstrate that assigned optic disc cells expressed both VSX2 and PAX2, and this statement is trued for CONCEPT organoids and human fetal retinas HGW9 (Fig. 5N-5R). Please see the underlined sentence in the response to the comment above.

Do the RGCs express subtype-specific markers? Do they detect markers of other retinal neurons typically born early in development-cones, amacrine cells, horizontal cells? The authors need to compare the transcriptome of different clusters to the published datasets from human and mouse retinae.

The stage of CONCEPT organoids for scRNA-seq was at an early stage. In this dataset, subtypes of RGCs were undetectable. Isolated RGCs via CNTN2 were at more advanced stages. Distinct expression of POU4F2, ISL1, RBPMS, and SNCG indicate multiple subtypes of RGCs (Fig. 7L-7P).

We did find other early retinal neurons in the scRNA-seq dataset: photoreceptor cells, amacrine/horizontal cells in CONCEPT organoids (Fig. 4U-4X), and these cells were also in cluster 11 in which RGCs were found.

We performed transcriptomic comparisons between CONCEPT organoids, brain/optic organoids, and human fetal retinas. We found that PAX2+ optic disc, PAX2+ optic stalk, FOXG1+ telencephalic, and VSX2+ neuroretinal cell clusters that were found in CONCEPT organoids did not exist in Gabriel et al.’s organoids, indicating striking differences between Gabriel et al.’s organoids and our CONCEPT telencephalon-eye organoids (supp. Fig. S13). On the other hand, we found that expression signatures of CONCEPT organoids and human fetal retinas are similar (Figs. 5, 6).

Transcriptomic comparisons are found in lines 325-392.

Fig. 3: where are the "lens like" cells located? The structures in panels B and D look very different. Are these lens-cells toward the periphery or scattered throughout?

Lens cells were dispersed in the zone in which neural retinal cells are located, which is shown in a low-magnification image (Fig. 3K). Panel B and D in Figure 3 were at different stages. At early stages, lens clusters were small (Fig. 3B). At later stages, lens clusters became bigger (Fig. 3D).

Fig. 3K and L, TEM images: how do the authors know that these are lens cells?

Western blot of these transparent cell clusters demonstrated that they were lens cells (Fig. 3L).

Fig. 5: The authors claim that a reduced number of Pax2+ cells is associated with entry of the axons. It is not clear if this is just due to physical barriers or to active axon guidance.

We believe that Reviewer 2 referred to the gap region of PAX2 expression in Fig. 7A, 7F. RGC axons grew toward and along adjacent PAX2+ VSX2+ cells. Since PAX2+ VSX2+ cells grossly formed a circular shape, RGC axons followed this circular shape. In a gap region of PAX2 expression, RGC axons exited the circle. The association of RGC axon growth with PAX2+ VSX2+ cells was very robust. Besides PAX2+ cell populations, we did not find any other cell populations that directed RGC axon growth.

Fig. 5K: The authors refer to ALDH1A3 expression in the optic disk, but the presented section does not include the optic disk. In addition, ALDH1A3 is expressed in other regions of the developing retina (Fig. 5K, ref 71).

We are sorry we did not make it clear. We referred to Li et al.’s (2000) paper (Mech Dev 95, 283-289) for Aldh1a3 expression in the optic stalk. Figure 7K was used to shown Aldh1a3 expression in peripheral retinas on sections.

Line 263, Reference 68: The authors claim that col13A1 is specific to the human optic disk. However, col13A1 is expressed in many additional eye lineages (PMID: 10865988).

We are sorry we did not make it clear. We meant that Col13A1 is prominently expressed in the optic disc, which is clearly shown in the referred paper (Figure 3D in the paper PMID: 10865988).

The authors show that inhibiting FgfR results in fewer RGCs and loss of directed axonal growth. The number of cells is drastically reduced; thus, the relevance of the finding directly to axon guidance is not resolved.

FGFR inhibitions drastically the number of RGC somas (Fig. 9F-9K). Additionally, remaining RGCs nearly did not grow directional axons (arrowheads in Fig. 9K), and a few remaining axons wandered around (arrow in Fig. 9K), indicating the role of FGF/FGFR signaling in RGC differentiation and directional axon growth.

Fig. 1H and J: Vsx2 is outside the centroid in panels H and I, but inside the centroid in panels J and K. It is not clear what part of the centroid is shown. This needs to be clarified by adding a scheme.

We are sorry we did not make it clear. We added separate-channel images showing VSX2 and PAX6 expression (supp. Figs. S1, S2) and a new diagram (left panel in Fig. 1B). Overall, FOXG1, VSX2, and PAX6 expression at days 15-17 formed three concentric zones spanning from the center to the periphery. At days 22-26, VSX2 expression expanded peripherally, largely overlapping PAX6 expression (supp. Figs. S1, S2).

Pax6 should be in all cells, also on day 17. Show the separate channels, including DAPI.

We added separate-channel images (supp. Figs. S1, S2). In cysts, PAX6 was expressed in all cells. After cysts attached to the culture surface and grew as colonies, distinct levels of PAX6 expression emerged in concentric zones. At days 17 and 26, PAX6 expression at the central zone (which cells expressed FOXG1) became lower, which is obvious in separate-channel images (supp. Figs. S1, S2). Consistently, PAX6 expression was low in FOXG1+ telencephalic cells in the scRNA-seq (Fig. 4C, 4D).

Lines 27-30: this is a long and complex sentence which needs to be clarified.

We broke it into a few sentences to make it clearer.

Line 43: fix "Retina" to "Retinal"

We fixed it.

Lines 376-377: repeated "mechanisms of".

We fixed it.

Author Response

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

We are grateful for the comments from the reviewers, which helped us to strengthen our analyses and communicate more effectively the details of our findings and their significance. To address their criticisms, we have performed new analyses and revised the text and figures. We believe the manuscript was significantly improved. We provide the line number of important parts of the text that were changed, here in this letter. Below, we address the specific comments from the reviewers in detail.

Reviewer #1 (Public Review):

Gehr and colleagues used an elegant method, using neuropixels probes, to study retinal input integration by mouse superior collicular cells in vivo. Compared to a previous report of the same group, they opto-tagged inhibitory neurons and defined the differential integration onto each group. Through these experiments, the author concluded that overall, there is no clear difference between the retina connectivity to excitatory and inhibitory superior colliculus neurons. The exception to that rule is that excitatory neurons might be driven slightly stronger than inhibitory ones. Technically, this work is performed at a high level, and the plots are beautifully conceived, but I have doubts if the interpretation given by the authors is solid. I will elaborate below.

Some thoughts about the interpretation of the results.

My main concern is the "survivor bias" of this work, which can lead to skewed conclusions. From the data set acquired, 305 connections were measured, 1/3 inhibitory and 2/3 excitatory. These connections arise from 83 RGC onto 124 RGC (I'm interpreting the axis of Fig.2 C). Here it is worth mentioning that different RGC types have different axonal diameters (Perge et al., 2009). Here the diameter is also related to the way cells relay information (max frequencies, for example). It is possible that thicker axons are easier to measure, given the larger potential changes would likely occur, and thus, selectively being picked up by the neuropixels probe. If this is the case, we would have a clear case of "survival bias", which should be tested and discussed. One way to determine if the response properties of axonal termini are from an unbiased sample is to make a rough functional characterization as generally performed (see Baden et al. 2006). This is fundamental since all other conclusions are based on unbiased sampling.

First of all, we want to thank the reviewer for the detailed and constructive comments based on which we refined the analysis and updated the figures. We hope that our changes adequately address the concerns of reviewer #1.

We would like to clarify that Fig. 2C represents an example from a single experiment. In total, we recorded 326 RGCs and 680 SC neurons in total, with 161 individual RGCs making connections onto 183 individual SC neurons. Moreover, we thank the reviewer for bringing up that important point about the potential “survivor bias”. To address this concern, we would like to provide some clarifications (see below). In addition, we now added the point that different RGCs can have different axonal diameter as requested by the reviewers (line 605).

It is important to note that our approach does not capture the total pool of retinal inputs. Moreover, we did not want to convey the impression that our approach equally captures all retinal inputs to a given SC neuron, as this is not the case. Likewise, it is important to note that our current method does not allow for the measurement of axonal diameters. To obtain an estimate of axonal thickness, complementary techniques such as imaging/staining or electron microscopy would be needed. Our study aimed at characterizing connected RGC-SC pairs and how excitatory and inhibitory neurons in the SC integrate retinal inputs, providing valuable insight on their wiring principles.

We greatly appreciate the reviewer for highlighting this limitation and we now address these points in the discussion of the revised version of our manuscript (line 603).

Regarding the suggested “rough functional characterization” of the RGCs. We have thought about this analysis and unfortunately, we did not present the necessary stimuli, e.g. chirp, in all experiments to be able to perform this analysis. Moreover, the dataset represented in this work contains only 326 RGC neurons, with 161 identified RGCs making connections to SC neurons. Thus, it is unlikely that our dataset uniformly covers all ~30 RGC types in the mouse. However, given that our dataset is the first measurement of RGC inputs to SC INs and SC EXNs in vivo, we believe it provides a first step and a foundation for future studies focusing on specific RGC types to refine our understanding of the RGC-SC circuitry. We discuss this point now in the revised manuscript (line 586).

One aspect that is not clear to me is to measure of connectivity strength in Figure 2. Here it seems that connectivity strength is directly correlated with the baseline firing rate of the SC neuron (see example plots). If this is a general case, the synaptic strength can be assumed but would only differ in strength due to the excitability of the postsynaptic cell. This should be tested by plotting the correlation coefficient analysis against the baseline firing rate.

We appreciate the reviewer for bringing up this important point. From the analysis perspective, we would like to clarify that the efficacy measure is independent of the baseline firing rate. It quantifies the probability of adding spikes on top of the baseline rate by subtracting the baseline firing rate before measuring the area of the peak (Usrey et al., 1999).

Furthermore, we acknowledge the reviewer’s interesting and valuable observation about the relationship of the firing rate and the excitability of the SC neuron in the example plots. To test whether the efficacy is directly related to the mean firing rate, we conducted additional analyses to show the efficacy measure as a function of the mean firing rate (Author response image 1 and Figure 2G). To that end, we utilized two different measures of firing rate: the mean firing rate during spontaneous activity (gray screen) over a duration of 10 sec (across 30 trials), which was interleaved with the natural movie presentations, and the overall firing rate throughout the entire recording session. Our findings indeed reveal a positive correlation, as predicted by the reviewer (Author response image 1, gray screen: EXC r = 0.22721; p < 0.00081; INH: r = 0.34677, p= 0.00076; entire recording: EXC r = 0.42685; p < 0.0005; INH: r = 0.43543, p = 0.00002).

Author response image 1.

Efficacy measure of connected RGC-SC pairs as a function of the mean firing rate during different stimulus conditions: during spontaneous activity (gray screen, left) and throughout the entire recording session (right).

However, it is important to note that although we observe a correlation on the population level, the relationship between postsynaptic firing and efficacy is diverse. We identify pairs with strong connections despite the firing rate of the postsynaptic SC cell being low. Likewise, we also find pairs with weak connections despite the firing rate of the SC neuron being high (Author response image 2). These observations suggest that factors beyond the postsynaptic firing contribute to the efficacy of the connection. This is exemplified by the fact that SC neurons can receive both strong and weak connections from their convergent presynaptic RGC pool.

Author response image 2.

RGC-SC connectivity. Cross-correlograms showing 4 connected RGC-SC pairs (top) with two RGCs connecting onto the same SC neuron. Raster plots of SC neuron spiking activity in response to firing of the presynaptically connected RGC. The same SC neuron can receive both strong and weak RGC inputs.

In summary, we thank the reviewer for bringing up this important question, and we believe that our additional analyses shed light on the relationship between firing rate and efficacy. This result is very interesting, and we include these findings in the updated Figure 2 in the revised manuscript (panel 2G) in exchange with the panel of the peak latency. Moreover, we also address this point now in the results and discussion section of the revised manuscript (line 280 and line 525).

My third concern is the assessment of functional similarity in Fig. 3. It is not clear to me why the similarity value was taken by the arithmetic mean. For example, even if the responses are identical for one connected pair that exclusively responds either to the ON or OFF sparse noise, the maximal value can only be 0.67. Perhaps I misunderstood something.

We thank the reviewer for raising this point about the clarification regarding the calculation of the similarity index. We apologize for any confusion caused by our description on the similarity index calculation. To clarify, the similarity index was calculated specifically between the responses of the RGC and the responses of the postsynaptic SC neuron, rather than between the neurons and the visual stimulus. As a result, the similarity index reflects the degree of similarity in the responses of the connected pairs. Therefore, if the responses of the RGC and the connected postsynaptic neuron are identical, regardless of whether they respond exclusively to ON, only to OFF, or a mixture of ON-OFF, the similarity index will be one. We have updated the relevant part in the methods section to make this point clearer to the reader (line 917).

Secondly, correlations in natural(istic) movies can differ dramatically depending on the frame rate that the movie was acquired and the way it is displayed to the animal. What looks natural to us will elicit several artifacts at a retinal level, e.g., due to big jumps between frames (no direction-selective response) or overall little modulation (large spatial correlations). I would rather opt for uniform stimuli, as suggested previously. Of course, these are also approximations but can be easily reproduced by different labs and are not subjected to the intricacies of the detailed naturalistic stimulus used.

We agree with the reviewer that spatiotemporal correlations of naturalistic stimuli are complex. To address this point, we added two stimuli with little spatiotemporal correlations to the similarity analysis. The first stimulus we added is a phase scrambled version of the natural movie (PSM, also taken from Froudarakis et al. (2014)). The second is a binary white noise checkerboard stimulus. These stimuli were presented randomly interleaved with the natural movie, for 30 trials each. The similarity index analysis revealed that even with uniform stimuli included, the average similarity index is correlated to the efficacy. We show this data now in Figure 3.

Fourth. It is important to control the proportion of inhibitory cells activated optogenetically across the recording probe. Currently, it is not possible to assess if there are false negatives. One way of controlling for this would be to show that the number of inhibitory interneurons doesn't vary across the probe.

We thank the reviewer for highlighting this important aspect of the experiment and analysis. We are aware of this point and therefore took extra care to minimize the biases that could be introduced by our recording and stimulation method. Our approach to include recorded excitatory and inhibitory neurons was conservative, briefly:

1. We included only excitatory and inhibitory neurons that were within the SC, defined by visually driven activity and continuous retinotopy (see method).

2. We further restricted the included neurons to neurons that were located within the boundaries of the LED evoked responses, i.e. the recording channels with optogenetic evoked MUA responses within the SC (Figure 1 – figure supplement 1).

3. Both excitatory and inhibitory SC neurons were selected in this way.

These inclusion criteria were specifically designed to avoid sampling excitatory neurons from regions on the Neuropixels probe that lacked optogenetically evoked responses and thus to minimize the number of falsely labeled excitatory neurons.

To illustrate these inclusion criteria and the resulting spatial distribution of the selected excitatory and inhibitory SC neurons along the 384 channels of the Neuropixels probe, we now added a supplementary figure (Figure 1 – figure supplement 1). This figure shows the multi- unit activity in response to optogenetic stimulation and the distribution of inhibitory and excitatory single units within the range of channels that are activated via LED stimulation for 3/11 selected experiments. This highlights that we employed stringent criteria for determining the boundaries and selecting which neurons to include in our study. The distribution of excitatory and inhibitory SC neurons is not significantly different for 9/11 experiments (Wilcoxon rank-sum test, p values = 0.307, 0.0115, 0.755, 0.834, 5.0110-6, 0.79, 0.80, 0.26, 0.33, 0.08, 0.13). Moreover, in the two significantly different experiments only 2 RGC-SC EXC pairs were located in the region without identified SC INs, and thus will not affect the results. We now address this point in the methods section (line 859).

Fifth. In Fig. 4, the ISI had a minimal bound of 5 ms. Why? This would cap the firing rate at 200Hz, but we know that RGC in explants can fire at higher frequencies for evoked responses. I would set a lower bound since it should come naturally from the after-depolarization block.

The chosen 5 ms minimal bound was in the range used in previous literature, e.g. 4-30 ms in Usrey et al. 1998 (Usrey et al., 1998). To address the question of the reviewer, we re-analyzed the data with a lower bound of 2 ms (2 – 30 ms) to include RGCs that fire at higher frequencies than 200Hz. However, we did not observe a clear difference between the 2-30 and 5-30 ms groups for inhibitory connections (SC IN: p = 0.604). Only the excitatory connections show a statistically significant difference (p = 0.011), however, the effect size is small (Cohen’s d = EXC = 0.063, INH = 0.030). Nonetheless we updated a panel in figure 4 to represent the 2-30 ms group (Figure 4F).

Another aspect that remains unclear is to what extent the paired-spike ratio depends on the baseline firing rate. This would change the interpretation from the particular synaptic connection to the intrinsic properties of the cell and is plausible since the bassline firing rate varies tremendously.

To address how the paired-spike ratio depends on the baseline firing rate we plotted the change of PSR depending on ISI as suggested by the reviewer.

One related analysis would be to plot the change of PSR depending on the ISI. It would be intuitive to make a scatter plot for all paired spikes of all recorded neurons (separated into inhibitory and excitatory) of ISI vs. PSR.

We appreciate the valuable suggestion from the reviewer. We have now separated the ISIs into distinct groups spanning 5 ms intervals represented in Author response image 3, right. These intervals range from 5-10 ms up to 25-30 ms. Notably, we observe a difference between the excitatory and inhibitory populations. The excitatory population exhibits a monotonic decrease in mean PSR across the intervals, while the inhibitory population shows a peak around 10/15 ms.

Author response image 3.

Change of mean paired-spike ratio (PSR) depending on ISI. Left) Comparison of PSR between two groups of different ISIs. The 2-30 ms group ensures to include high-firing RGCs (excitatory pairs 2-30 vs 5-30 ms p = 0.011; inhibitory pairs 2-30 vs 5-30 ms p = 0.604, Wilcoxon signed-rank). Right) PSR for groups of different ISI intervals. Mean PSR ± SEM for excitatory groups: 2.0±0.09, 1.75±0.09, 1.51±0.05, 1.31±0.05, 1.2±0.05; inhibitory groups: 1.35±0.06, 1.51±0.09, 1.5±0.1,1.22±0.06, 1.21±0.07. p E vs I (within group): 1.5510-5, 9.55±10-2, 4.21±10-1, 3.74±10-1, 6.22 ±10-1, Wilcoxon rank-sum test.

Panel 4E is confusing to me. Here what is plotted is efficacy 1st against PSR (which is efficacy 2nd/efficacy 1st). Given that you have a linear relation between efficacy 1st and efficacy 2nd (panel 4C), you are essentially re-plotting the same information, which should necessarily have a hyperbolic relationship: [ f(x) = y/x ]. Thus, fitting this with a linear function makes no sense and it has to be decaying if efficacy 2nd > efficacy1st as shown in 4C.

We thank the reviewer for raising this question which helped us to improve the representation and disruption of the results shown in figure 4. Panel 4E is intended to investigate whether there is a correlation between the efficacy strength (eff 1st) and the amount of facilitation (PSR). From panel 4C it is already evident that the data points for high efficacies lie closer to the unity line, as compared to the data points for low efficacies. This suggests that the PSR is stronger for connections with smaller efficacies 1st. To quantify this relationship, we have plotted the efficacy 1st vs the PSR in panel 4E, which thus adds new information to the figure. Importantly, this panel is shown in log-log scales, and therefore the decaying relationship is not evident. If we had shown the data on linear-linear scale, the decaying function would have been evident (Author response image 4). And indeed, as the reviewer pointed out, we cannot fit a hyperbolic relationship with a linear function. This is exactly the reason why we show the data in log-log scale and also estimate the Pearson correlation also from the logs of the efficacies and PSRs.

In Author response image 4 we show the relationship plotted on linear scale using an approach to fit the hyperbolic relationship employing a hyperbolic cosecant function 𝑎/𝑠𝑖𝑛ℎ(𝑏 ∗ 𝑥) + 𝑐.

Author response image 4.

Relationship between efficacy to 1st RGC and PSR visualized on linear scale using a hyperbolic fitting approach 𝑎/𝑠𝑖𝑛ℎ(𝑏 ∗ 𝑥) + 𝑐.

Finally, in Figure 5, the perspective is inverted, and the spike correlations are seen from the perspective of SC neurons. Here it would also be good to plot the cumulative histograms and not look at the averages.

We added the cumulative histogram in Figure 5 (panel B), in addition to represent the raw data points and the mean.

Regarding the similarity index and use of natural stats, please see my previous comments. Also, would it be possible to plot the contribution v/s the firing rate with the baseline firing rate with no stimulation or full-field stimulation? This is important since naturalistic movies have too many correlations and dependencies that make this plot difficult to interpret.

We now show the contribution vs firing rates for different stimulus conditions in a new figure supplement (Figure 5- figure supplement 1). We added the correlations to the different stimuli for baseline firing rate with no stimulation (gray background), full-field stimulation (checkerboard) and phase scrambled natural movie.

Overall, the paper only speaks from excitatory and inhibitory differences in the introduction and results. However, it is known that there are three clear morphologically distinct classes of excitatory neurons (wide-field, narrow-field, and stellate). This topic is touched in the discussion but not directly in the context of these results. Smaller cells might likely be driven much stronger. Wide-field cells would likely not be driven by one RGC input only and will probably integrate from many more cells than 6.

We thank the reviewer for this comment. We agree with the reviewer that addressing how the different excitatory and inhibitory cell-types integrate RGC input is important to understand the visual processing mechanisms in the SC. The presented study aimed at comparing the excitatory and inhibitory population in general using the VGAT-ChR2 mouse line. Understanding how specific genetically defined cell-types integrate RGC inputs is clearly very interesting and should be done. Unfortunately, the mouse lines that would allow targeting genetically identified inhibitory cell-types are still limited and therefore we can only use functional measurements to assess different types of neurons in the SC. We now address this point about distinct SC cell-types in the discussion (line 643).

One possible functional measurement is the size of the receptive field, which, to some degree, could be used as a proxy for different morphologies, i.e. small receptive fields could hint towards compact morphology while large receptive fields could indicate a wider morphology. It is known for example that narrow-field and stellate cells have small RF sizes, while wide-field cells have large RFs. We studied the relationship between the RF size and spike waveform duration but did not find a significant correlation (Figure R6). Moreover, the spike waveform duration, as discussed in the manuscript, is not a valid criterion to separate EXNs and INs in the SC, as it is common practice in the cortex. We now also looked into whether the connectivity strength is related to the RF size. Interestingly, while in the current dataset we do not find a significant correlation between the efficacy and the receptive field size for both EXN and IN (Author response image 5, left), we do find a significant negative correlation between contribution and receptive field size for the excitatory neurons (Author response image5, right). This result indicates that SC excitatory neurons with small receptive fields are more strongly coupled to the RGC input as compared to neurons with larger receptive fields.

Author response image 5.

Relationship between RF size and connectivity measures (efficacy and contribution) for RGC-SC EXN and RGC-SC IN pairs (two-sided Wilcoxon rank-sum test).

Reviewer #2 (Public Review):

This study follows up on a previous study by the group (Sibille et al Nature Communications 2022) in which high density Neuropixel probes were inserted tangentially through the superficial layers of the superior colliculus (SC) to record the activity of retinocollicular axons and postsynaptic collicular neurons in anesthetized mice. By correlating spike patterns, connected pairs could be identified which allowed the authors to demonstrate that functionally similar retinal axon-SC neuron pairs were strongly connected.

In the current study, the authors use similar techniques in vGAT-ChR2 mice and add a fiber optic to identify light-activated GABAergic and non-light-activated nonGABAergic neurons. Using their previously verified techniques to identify connected pairs, within regions of optogenetic activation they identified 214 connected pairs of retinal axons and nonGABAergic neurons and 91 pairs of connected retinal axons and GABAergic neurons. The main conclusion is that retinal activity contributed more to the activity of postsynaptic nonGABAergic SC neurons than to the activity of postsynaptic GABAergic SC neurons.

The study is very well done. The figures are well laid out and clearly establish the conclusions. My main comments are related to the comparison to other circuits and further questions that might be addressed in the SC.

It is stated several times that the superior colliculus and the visual cortex are the two major brain areas for visual processing and these areas are compared throughout the manuscript. However, since both the dorsal lateral geniculate nucleus (dLGN) and SC include similar synaptic motifs, including triadic arrangements of retinal boutons with GABAergic and nonGABAergic neurons, it might be more relevant to compare and contrast retinal convergence and other features in these structures.

Thank you for pointing out that crucial point. Indeed, the comparison to the thalamus is a valid argument, as both the SC and LGN are primary targets of RGC axon terminals. During the preparation of the manuscript, we extensively discussed whether to compare our new SC dataset with existing literature on the LGN or the primary visual cortex (V1) is the more appropriate. Ultimately, we decided on using the visual cortex as the main comparison because of the following reasons:

1. The SC is widely recognized as an evolutionary conserved circuit for visual computation and visually guided behaviors, while the dLGN is generally regarded as a relay station for RGC information to the visual cortex (Steriade, McCormick, 1997). Thus, we believe it is more relevant to compare the evolutionary older visual circuit (SC) to the evolutionary newer visual circuit (visual cortex).

2. In the mouse, the dLGN contains only a limited number of inhibitory interneurons and represent only approximately 6% of the total dLGN neuronal population (Butler, 2008; Evangelio et al., 2018). It has been suggested that the rodent somatosensory thalamus even lacks interneurons (Arcelli et al., 1997). Consequently, directly comparing inhibitory interneurons in the SC to those in the dLGN would pose challenges.

3. Along the same line, the density and also the diversity of inhibitory neurons in the SC is high and likely more comparable to the density and diversity of inhibitory neurons in the visual cortex, than to the dLGN circuit. In the dLGN, TC projection neurons far outnumber inhibitory neurons (Arcelli et al., 1997; Evangelio et al., 2018) and the dLGN is inhabited by just 1-2 classes of GABAergic retinorecipient interneurons (Arcelli et al., 1997; Jaubert-Miazza et al., 2005; Krahe et al., 2011; Ling et al., 2012). Classification approaches (e.g. 3D reconstruction) so far have not revealed any subclasses except for distinctions in intrinsic membrane properties (Leist et al., 2016), suggesting low interneuron diversity in the dLGN. This is in contrast to the vLGN, where a recent study found a diversity of GABAergic neurons (Sabbagh et al., 2021).

4. In the thalamo-cortical circuit, there exists a notable difference in how cortical excitatory and cortical inhibitory neurons are driven by their thalamic input (Alonso and Swadlow, 2005; Cruikshank et al., 2007). This discrepancy forms the basis for several models of visual processing in the visual cortex (Kremkow et al., 2016; Taylor et al., 2021). Which is why we wanted to assess whether the SC follows similar or different rules.

That said, the reviewer is correct that the dLGN and the SC share certain wiring motifs, such as the triadic arrangements of retinal boutons. Unfortunately, the VGAT-ChR2 mouse line used in our study does not specifically label SC inhibitory neurons that are involved in the formation of triadic arrangements. Therefore, we are unable to draw specific conclusion regarding this point. To further investigate this aspect, the usage of GAD67 mice, which have been shown to selectively label intrinsic interneurons which receive RGC input and contact non-GABAergic dendrites (Whyland et al., 2020), would be necessary. Nonetheless, we acknowledge the question raised by the reviewer and in response, we have now provided a more in-depth comparison to the dLGN in the discussion section of the revised manuscript (line 565).

The GABAergic and nonGABAergic neurons showed a wide range of firing rates. It might be interesting to sort the cells by firing rates to see if they exhibit different properties. For example, since the SC contains both GABAergic interneurons and projection neurons it would be interesting to examine whether GABAergic neurons with higher firing rates exhibit narrower spikes, similar to cortical fast spiking interneurons. Similarly, it might be of interest to sort the neurons by their receptive field sizes since this is associated with different SC neuron types.

We thank the reviewer for the interesting suggestions of SC neurons classification into different categories. The relationship between connectivity measures and RF size has been addressed in Author response image 5. We have now studied the relationship of spike waveforms and several measures such as firing rate and RF size in more detail (Author response image 6).

As the baseline firing is generally low in SC and our experiments are performed under anesthetized conditions, we used the evoked firing rates to sort the cells by firing rates or RF sizes. We have added an analysis showing the mean firing rate (calculated over the full recording duration) as a function of the spike width (peak-to-trough duration). We observe no significant relationship between the different groups of cell types. The same accounts if we sort the SC neurons by their RF size. RF sizes were calculated from PSTHs and summed RF for SL and SD. We do not see a relationship between neuron type and firing or RF size.

Author response image 6.

Mean firing rate (left) and RF size (right) as a function of peak-to-trough (PT) duration for excitatory and inhibitory SC neurons. Both measures are not correlated to the PT duration (Pearson correlation coefficient, two-sided Wilcoxon rank-sum test).

The recording techniques allowed for the identification of the distance between connected retinocollicular fibers and postsynaptic neurons. It might also be interesting to compare the properties of connected pairs recorded at dorsal versus ventral locations since neurons with different genetic identities and response properties are located in different dorsal/ventral locations (e.g. Liu et al. Neuron 2023). Also, regarding the strength of connections, previous electron microscopy studies have shown that the retinocollicular terminals differ in density and size in the dorsal/ventral dimension (e.g Carter et al JCN 1991).

We thank the reviewer for raising this interesting and relevant point to compare the properties of the connected pairs across the dorsal and ventral location. Unfortunately, our tangential recording approach is not ideally suited for comparing the properties of neurons across the different SC depths. For comparing dorsal versus ventral located neurons in the SC, as done in Liu et al., Neuron 2023, vertical recordings would be more appropriate. We now provide a discussion on this aspect (line 589).

Was optogenetic activation of GABAergic neurons ever paired with visual activation? It would be interesting to examine the receptive fields of the nonGABAergic neurons before and after activation of the GABAergic neurons (as in Gale and Murphy J Neurosci 2016).

This is an important point and indeed we have paired activation of GABAergic neurons with visual stimulation (checkerboard stimulus) to assess the impact of the GABAergic neurons on the firing of the excitatory neurons. We observed a diversity of effects, with some EXNs being strongly suppressed and others being only weakly suppressed. Thus, we predict that the receptive field of those EXN that are suppressed by optogenetically evoked IN firing, should be affected in some way. However, the checkerboard stimulus was only presented for a short duration (1 s) and for only a few trials (n = 30). Therefore, estimating the receptive fields of EXN before and after optogenetic activation of GABAergic neurons is unfortunately not possible with the existing dataset. We now mention this point in the discussion (line 668).

Reviewer #3 (Public Review):

This study performs in vivo recordings of neurons in the mouse superior colliculus and their afferents from the retina, retinal ganglion cells (RGCs). Building on a preparation they previously published, this study adds the use of optogenetic identification of inhibitory neurons (aka optotagging) to compare RGC connectivity to excitatory and inhibitory neurons in SC. Using this approach, the authors characterize connection probability, strength, and response correlation between RGCs and their target neurons in SC, finding several differences from what is observed in the retina-thalamus-visual cortex pathway. As such, this may be a useful dataset for efforts to understand retinocollicular connectivity and computations.

Recommendations:

Reviewer #1 (Recommendations For The Authors):

Some minor points.

Fig.1G shows a difference in mean firing rates between inhibitory and excitatory cells. Please plot the cumulative distribution of firing rates to be able to scrutinize the data better.

We have addressed this issue and updated panel G in Figure 1.

Fig. 2C. The black background color of this plot is black; it is not possible to decipher much, please change it to white

We have now changed panel C in Figure 2 to a white background.

Fig. 4D would be better represented as a histogram since most points overlap.

We now represent panel D in Figure 4 as a histogram.

Citations. I would cite some of the foundational work, in some instances, e.g., in the first sentence (SC receives input from the retina)

We have now addressed this issue and cited more foundational studies (e.g. line 68)

The discussion is a bit long; the last paragraph can be removed, mainly because the previous section conflates superficial SC with the entire SC, which is confusing (e.g., Ayupe et al.). In this way, there is more space to discuss the direct implication of the study within the context of known cell types.

We now shortened the discussion and provide more background about different SC cell types in the discussion (line 643).

Reviewer #2 (Recommendations For The Authors):

Minor correction: Whyland et al 2020 did not identify V1 input to horizontal cells. A more appropriate reference is Zingg et al Neuron 2017.

We thank the reviewer for this important point and have now corrected the citation in line 613 in the discussion to Zingg et al 2017.

Reviewer #3 (Recommendations For The Authors):

Regarding the degree of convergence from RGC to SC, the Crair lab (Furman 2013) performed a quantal analysis in slice that is worth citing.

We included this citation in the revised version of the manuscript (line 501).

I have lost track at this point, but many labs (Heimel, Meister, Farrow, Cang, Isa, maybe others?) have observed that neighboring SC neurons have similar tuning for direction/orientation, but the circuit mechanisms are not well understood. Given the relatively weak correlation between response tuning of RGC axons and their SC target neurons, a useful comparison might be that of SC neurons and their neighbors, and whether SC neurons that show weaker correlation to their RGC axons show stronger correlations with their SC neighbors, which could implicate local connectivity within SC.

We thank the reviewer for providing this interesting comment. With our recording approach we could study locally connected SC neurons. However, the focus of our study was to first characterize the retinocolliculuar connectivity and therefore investigating the intracollicular connectivity is beyond the scope of the current study. We thank the reviewer for the valuable suggestion and will consider to tackle this aspect in a separate study in the future.

Is it possible any of these measurements are biased by laminar targeting of their probe within superficial SC? Their schematic seems to suggest they targeted the deeper part of superficial SC. Do they know whether they recorded throughout superficial SC or targeted the deeper layers closer to stratum opticum?

Our recordings are in between the deeper and upper visual SC layer depending on the recording site on the Neuropixels probe as we use an angled insertion approach. Besides DiI staining (Author response image 7), we can estimate the location of the probe using functional measurements, i.e. visually driven channels and retinotopic locations of the recording sites. If the Neuropixels probe is inserted too superficial, the number of recording site with visually driven activity is low. If the Neuropixels probe is inserted too deep in the visual layers we see two separated regions on the probe with visually driven activity in which the retinotopy is non-continues (please refer to Figure 2 in (Sibille et al., 2022)). In the recordings included in this study, the number of visually driven channels was generally high and the retinotopy continues, suggesting that we covered a region within the deeper and upper visual layers.

Author response image 7.

Functional estimation of probe location. DiI staining of Neuropixels probe (middle) and multi-unit activity across channels in response to visual stimulation (bottom). The white dashed lines in the middle and bottom panels mark the rough boundaries of the visual SC layers.

In Fig. 4, the authors argue that firing in inhibitory neurons is less correlated with RGC input. Does their metric for contribution of retinal input control for the fact that inhibitory neurons have higher firing rates overall and, e.g., may be more depolarized at rest and likelier to fire spontaneous spikes but no less likely to be driven by retina? Or is the argument that their visual responses are more likely to be driven by V1 or local connections?

We thank the reviewer for bringing up that point. The contribution measure estimates the fraction of SC spikes that were preceded by an RGC spike and it is thus, in theory, independent of the firing rate of the SC neuron. In practice, however, we agree that high firing SC neurons may be more likely to have a lower contribution value simply because a larger fraction of their spikes is not preceded by the activity of the presynaptic RGC. But this is exactly what we aimed at characterizing with this analysis. Where these non-RGC driven SC spikes originate from, whether from a more depolarized state of the neuron or by other sources such as V1 or local connections, we can only speculate about. That said, please note that despite SC INs having higher firing rates, not all of them show low contribution. Likewise, we also see SC neurons with low firing rates and low contribution values (new Supp Fig. 3).

Minor point: The optotagging in the example cell doesn't cause the cell to fire for ~50 ms? That is odd. Typically, cells classified as optotagged fire within 5-10 ms of light onset. Is that a strange example cell or is there something different about the optotagging approach?

Unfortunately, transient LED light onsets and offsets can induce light artifacts on Neuropixels probes (Jun et al., 2017; Steinmetz et al., 2021) and therefore it is challenging to use brief LED pulses for optotagging with Neuropixels probes. To avoid this overlap of artefacts and LED evoked spikes, we opted for a longer stimulus duration of 100 ms to activate VGAT neurons (Bennett et al., 2019; Siegle et al., 2019). Moreover, instead of a square pulse, we used a slow ramping for light onsets and offsets to minimize the magnitude of induced artifacts. In Author response image 8 we present examples of individual activated VGAT neurons responding to a 100 ms blue light pulse.

Author response image 8.

Optotagging approach. Example traces of a single stimulation pulse and protocol used for optogenetic stimulation. Evoked activity in response to LED stimulation (100ms, 100 trials) for six example SC IN neurons.

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Author Response

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

We would like to thank the Reviewers for their careful reading and the many thoughtful suggestions to improve our manuscript, as well as both the Editors and Reviewers for the generally positive evaluations and encouraging statements.

Editorial assessment:

This important work presents an interesting perspective for the generation and interpretation of phase precession in the hippocampal formation. Through numerical simula- tions and comparison to experiments, the study provides solid evidence for the role of the DG-CA3 loop in generating theta-time scale correlations and sequences, which would be reinforced through the clarification of the concepts introduced in the study, in particular the notion of intrinsic and extrinsic sequences. This study will be of interest for the hippocampus and neural coding fields.

We appreciate that our work has been considered important. In our revision we made a considerable effort to improve on the presentation of our results and the justification of our model assumptions. Particularly we aimed to clarify the meaning of intrinsic and extrinsic sequences by ad- ditional figure panels as well as fleshing out their definition via spike-timing correlations being independent or dependent on the direction of the running trajectory, respectively. To address all the requests, we added 3 new Fig- ures, multiple new Figure panels and simulated a new model variant.

Reviewer #1 in their public review assessed ”The manuscript has the potential to contribute to the way we interpret hippocampal temporal coding for navigation and memory.”

They criticized

• The findings generally relate to network models of phase precession (re- viewed in e.g., Maurer and McNaughton, 2007, Jaramillo and Kempter, 2017). An important drawback of these models with respect to explaining specific experimentally observed features of phase precession, is that they cannot straightforwardly explain phase precession upon first exposure onto a novel track. This is because, specific connectivity in network models may re- quire experience-dependent plasticity, which would not be possible upon first exposure. This is essential, given that the manuscript addresses the possible origin of phase precession in terms of network models and at minimum, this weakness should be discussed.

We agree with Reviewer # 1 (and also with Reviewer # 2, who brought up a similar point) that models based on recurrence struggle to ex- plain how the recurrent connectivity matrix should come about. While we feel that a full model of how the 2-d topology in the recurrent weights can be learned goes far beyond the scope of this paper (and to our knowledge has not been solved so far in any existing model), we added a new model variant (new Figure 6 and Supplementary Figure 1), which explains the ba- sic phenomenology of extrinsic and intrinsic sequences without the need of recurrent connections, only using feed-forward synaptic facilitation. Thus, assuming recurrent connection is not necessary for our main findings. How- ever, we would like to point out that this does not exclude the possibility that recurrent connections, if set up in an appropriate way, also contribute to phase precession and theta sequences.

• An important and perhaps essential component of the manuscript, is the distinction between extrinsic and intrinsic models. However, the main con- cepts on which this hinges, namely extrinsic and intrinsic sequences (and the related extrinsicity and intrinsicity) could be better explained and illustrated. Along these lines, the result suggested by the title, namely, hippocampal theta correlations, may be important yet incidental in light of the new concepts (e.g., extrinsicity, intrinsicity) and computational models (e.g., DG-CA3 recurrent loop) that are put forward.

We have added substantial new explanatory material to the figures, captions and text to more didactically introduce the concepts of in- trinsicity and extrinsicity. We have also completely rewritten the abstract and added a subtitle: ”extrinsic and intrinsic sequences”

• The study seems to put forward novel computational ideas related to neural coding. However, assessing novelty is challenging as this manuscript builds on previous work from the authors, including published (Leibold, 2020, Yiu et al., 2022) and unpublished (Ahmadi et al., 2022. bioRxiv) work. For example, the interpretation of intrinsic sequences in terms of landmarks had been introduced in Leibold, 2020.

We agree with the reviewer that this paper touches on many related ideas from previous papers (not only of our lab) and is supposed to tie loose ends. Thus, the novel contribution is a biologically plausible mechanistic model of how intrinsic sequences and 2-d place maps interact on the level of interconnected spiking neurons. Such a level of explanation has not yet been available in previous work. We have considerably extended the Discussion section in our revision detailing the bigger picture underlying this theory. Also our addition of the non-recurrent model variant (see above) adds considerable novelty, since it provides an account of phase precession and preplay in novel environments.

• The significance of the readout tempotron neuron could be expanded on. In particular, there is room for interpretation of the output signal of that neuron (e.g., what is the significance of other neurons downstream? Why is the rationale for this output to being theta-modulated?)

We have added an additional Figure 8 to better illustrate the inner workings of the tempotron. We also extended the discussion to better explain the potential use of the tempotron output (see above). In short, we consider the tempotron to signal a unique behaviorally important context that is independent of remapping induced by changes of sensory cues, which is a new prediction of the model. Since the context signal is resulting from DG loops it requires a stable code to also exits in the DG. Evidence for such long-term stability in DG has been found in Hainmu¨ller & Bartos (2018).

Reviewer #2 in their public review find ”this research topic to be both important and interesting” and appreciates ”the clarity of the paper.”, com- mending our ”efforts to integrate previous theories into their model and con- duct a systematic comparison”.

We are very happy about these positive remarks and sincerely would like to thank the reviewer!

Reviewer #1 made the following specific recommendations for changes:

The abstract is somewhat difficult to parse. I have identified some words and/or sections that could be improved.

• ’ ....inherently 1 dimensional’. This statement seems to be related to an a priori interpretation of the authors. On the other hand, if offline sequences are trivially 1 dimensional because they are sequences (i.e., they constitute a vector), then online sequences would be 1-dimensional as well. What is the key difference between offline and online? Is it the omnidirectional place fields in two dimensions? Perhaps more importantly, how relevant is this fact with respect to the main results of the manuscript, which concern ex- trinsic and intrinsic sequences?

We indeed meant that the sequences are trivially 1-dimensional. The main challenge that we would like to address in this paper is how a 2-d topology of place cells (and direction dependent theta sequences) and a 1-d sequence topology of intrinsic theta correlations and during (p)replay can be reconciled. We hope this has become clearer in the rewritten abstract.

• The language in lines 36-38 is overly technical. I suggest modifying the language, the language was less technical and more understandable in the body of the manuscript, which should be also reflected in the Abstract.

We would would like to apologize for making the abstract too technical. Also in response to Reviewer #2, we decided to rewrite the ab- stract entirely.

The authors use a mixture of conductance based models and Izhikevich neurons, presumably for the spiking generating mechanism. The conductance component can be readily interpreted in terms of the underlying biophysics. The Izhikhevich neuron model, however, is phenomenological. I suggest you address i) the rationale for using Izhikevich model, 2) its biophysical inter- pretation, 3) and its combination with conductance-based currents.

The reviewer is correct that spike generation is modelled using Izhikevich’s model whereas synaptic integration is included in a conductance- based manner. As suggested by the reviewer, we have added further expla- nation in the Methods part, explaining that the Izhikevich approach allows to adjust burst firing properties with only few parameters by efficiently em- ulating the bifurcation structure of spike generation in the full biophysical model (1&2) and otherwise has no effect on the integration of conductance- based synaptic currents in a subthreshold regime (3).

Line 126: when you say preferred angle, do you mean preferred (heading) direction? If so, please maintain consistency throughout.

We thank the reviewer for pointing out the inconsistency. We have added the word ”heading” throughout the manuscript whenever ap- propriate. To further improve the consistency, we have clarified the meanings of ”best” (or ”worst”) direction and reserved the use of it solely for cases when trajectory direction is compared with the preferred heading direction, namely, ”best” (”worst”) direction when trajectory is along (opposite) the preferred heading direction.

Line 174: When discussing cross-correlation, sometimes you mean a cross-correlation function between two place fields and sometimes to the his- togram of all such correlations? Please clarify.

We used histograms to empirically estimate the underlying cross-correlation function. For clarity, we have specified that it is a cross- correlation histogram in the revised manuscript whenever we refer to the empirical estimate.

Figure 3:

Understanding the difference between extrinsic and intrinsic sequences is fundamental for the manuscript. I suggest that in the section that refers to Figure 3 (or Figure 3 itself), you kindly provide an example depicting how extrinsic and intrinsic sequences can

1) coexist yet be distinctly identified

2) depend on trajectory

3) depend on DG input

By coexistence, we meant the heterogeneous population of ex- trinsic and intrinsic cell pairs and, hence, the extrinsic and intrinsic theta correlations, as shown in Figure 3J. To improve the clarity, we added the following sentence in the section that refers to Figure 3: ”In our simula- tion, extrinsically and intrinsically driven cell pairs are both present in the population (Figure 3J), indicating a coexistence of extrinsic and intrinsic sequences.”. To illustrate how extrinsic and intrinsic sequences depend on both tra- jectory and DG recurrence, we have also added annotations in Figure 3F to mark the extrinsic and intrinsic part of the sequence.

Moreover, the caption of Figure 3 refers to the directionality of the theta sequences. How does this again relate to the extrinsic/intrinsic distinction?

We hope the highlighting in panel F of Figure 3 has resolved this problem.

Figure 5:

• This is a crucial figure that should illustrate the differences between extrinsic and intrinsic sequences, as the figure caption suggests. Surprisingly, it is not at all clear where (i.e., in which panel) and how (i.e., methodologi- cally) should one distinguish one type of sequence from another. I suggest that at least one such panel is dedicated to illustrating the difference and/or detection of these sequences in time and/or from phase precession plots. Moreover, there is significant visual crowding that makes the interpretation challenging (e.g., insert a space between G and E)

We would like to apologize that in the previous version of the manuscript, we seemed to have evoked the impression that the difference between intrinsic and extrinsic sequences should be mainly illustrated in Figure 5. We hope that our revisions of Figures 1 and 3 have made it sufficiently clear to this point. The main purpose of Figure 5 was (and is) to illustrate how intrinsic sequences can lead to out-of-field firing. We have modified the figure caption (and text) accordingly. To address the visual crowding problem in Figure 5, we have inserted a space between panels and also removed repeated labels.

Tempotron neuron and Figure 6:

From the reviewer’s questions on Figure 6, we feel that our presentation caused considerable confusion about the motivation and inter- pretation of the tempotron simulations. We therefore rewrote parts of the associated text and Figure caption. We hope that the revised presentation clarifies the issues. We therefore only briefly respond to the reviewer’s points here, because we think they largely resulted from misunderstandings.

• Intuitively, and as the manuscript results suggest, late phases are asso- ciated to extrinsic mechanisms while early phases are associated to intrinsic. Why not construct a simpler classifier readout based on this fact? How does it compare to a tempotron?

Opposite to the reviewer’s comment, extrinsic mechanisms are visible at early phases (late in the field), intrinsic mechanisms at late phases (early in the field). In fact, what the tempotron does is learning to identify the intrinsic (late phase) part and to disregard the extrinsic (early phase) part.

• What is the significance of theta-modulated output of the tempotron (readout) neuron?

The theta modulation of the tempotron output is a trivial re- sult of the theta-modulation of the input, i.e., the detection of the intrinsic sequence pattern is done once every cycle.

Suggestion for Figure 6 related to Tempotron readout: Focus on ’with DG loop condition’, as the challenge and most important point here is to identify extrinsic and intrinsic sequences. The No-loop condition could be left as a supplementary figure or side panel.

The no-loop condition is the essential control showing that the tempotron only responds to the previously learned intrinsic pattern and can- not identify spatial location based on the extrinsic pattern.

Further work/predictions.

Lines 196-198. ”Since intrinsic sequences can also propagate outside the trajectory (Figure 5) and activate place cells non-locally, our model predicts direction-dependent expansion of place fields.” If remote activation is ’suffi- ciently’ remote, wouldn’t this predict two separate place fields instead of an expansion?

The reviewer is completely correct. Out of field spiking can be also affecting remote locations, if the intrinsic sequences link to remote place fields. This would lead to double fields, however, the intrinsic part would only be active at late theta phases. For simplicity, we have not added such a case in our paper, but we would like to thank the reviewer for this comment, since it leads to a nice prediction of the model, which can be experimentally tested and therefore was included to the discussion.

Lines 556-558. ”In our model, firing rate is determined by both low-phase spiking from sensory input and high-phase spike arrivals of DG-CA3 loops, both producing opposing effects on the phase distribution.” Is it possible to make a differential prediction based on lesions here, e.g., along the lines of reduced range phase precession, for either high phases or for low phases?

We thank the reviewer for this great suggestion. Lesion of DG in the model does indeed reduce the phase range and mean spike phase. This further corroborates the effect of DG-loop on theta compression and high-phase spiking. We have included a new panel D in Figure 4 and a corresponding mention in the result section.

Line 570. ”We speculate that the functional roles of intrinsic sequences may not be limited to spatial memories.”. Is there any relationship to re- play and/or sleep-dependent memory consolidation? Some speculation in the Discussion section would be welcome and appropriate.

We have added some further speculative ideas to the last section of the Discussion. We propose that replay and preplay reflects the intrinsic sequences that express the current expectation of the animal. We have not yet thought well enough about their relation to memory consolidation to phrase this in the manuscript, but would suggest that they could serve to signal multimodal context information to the neocortex where it can evoke retrieval of unimodal memory traces.

The description of the results, as stated in the public review, can be im- proved. A key component is the definition and identification of extrinsic and intrinsic sequences.

Some comments:

• I think that the words ’extrinsic’ and ’intrinsic’ are problematic as both types of sequences/models rely on external (spatial) input, hence both are in some sense ’extrinsic’. On the other hand, both are network mechanisms, thus in some sense ’intrinsic’, where the asymmetry is either programmed directly onto the weights or due to synaptic depression. To add to the con- fusion, ’intrinsic’ mechanisms very often refer to cellular mechanisms in neurophysiology. I kindly ask you to, ideally, reconsider the terminology, or at the very least, be very thorough and precise when describing the mech- anisms. For example, sometimes extrinsic (intrinsic) ’models’ are referred to, sometimes ’sequences’, sometimes ’factors’, sometimes ’pairs’, etc.

We understand and appreciate the reviewers argument, but would like to stick to the terminology, since it was already used in our prior publication. We have made considerable effort to improve the explanation and illustration of extrinsic vs. intrinsic pairs in the main text, Figure 1 and 3 to highlight our definition that is based on pair correlations: Extrin- sic pairs flip the correlation lag with reversal of running direction, intrinsic pairs don’t. This is simply a functional definition and should not be con- fused with potential microscopic mechanisms. One of those (DG-loops) is suggested in our paper.

• As discussed in the public review, network mechanisms may require experience-dependent plasticity and hence cannot easily explain phase pre- cession on the first pass. Please discuss why and/or how your model fits with this observation.

We agree that the two models under consideration both require the recurrent network be set up appropriately and there is no theory so far that would explain how. The reason we chose these two models is because they are well known in the community and relatively similar. We reasoned that comparison between an intrinsic model and an extrinsic model would make most sense if the two are a similar as possible. Nevertheless, we ex- tended the manuscript by a new set of simulations in which we do not use re- current CA3 connections and obtain phase precession solely be feed-forward synaptic facilitation (new Figure 6 and supplementary Figure S1). The new simulations show that the basic phenomenology can also be obtained with- out using recurrent CA3 connections, however, as expected when removing one mechanisms of phase precession, the range of phase range is somewhat reduced as compared to the full model.

Along a similar vein, phase precession in Figure 1E only has a range of pi/2, which is about half of the typical range of phase precession for single runs. This should be characterized as a weakness of the intrinsic model.

The precession range in spiking models is highly sensitive to a large number of parameters such that it is hard to make such definite claims (see also above response). In the original Tsodyks et al. 1996 paper the phase range went up to 270 degrees with a slightly different implementation to ours in terms of current vs. conductance-based synapses, an exponen- tial instead of a Gaussian recurrent weight function, and 1-d (original) vs 2-d (ours). We chose conductance-based synapses, and a Gaussian weight profile for better comparison with the Romani and Tsodyks (2015) model. In the original non-spiking implementation by Romani and Tsodyks (2015), the phase range was hardly 70 degrees. Our model implementation of the Romani and Tsodyks (2015) model fits the experimentally reported phase ranges of about 70 to 180 degrees in CA3 (Harris et al., 2001).

Lines 282-284: ”...since phase precession properties change in relation to running directions, nor are they solely intrinsic since reversal of correlation is still observed in most of the sequences (Huxter et al., 2008; Yiu et al., 2022).”. To which extent is this a consequence of the phase precession model (extrinsic vs intrinsic) or the fact that place fields are sometimes directional?

The reversal of sequences with reversed running direction is how we define extrinsic correlation. We hope our changes in relation to Figure 1 has clarified this point.

Figure 2: Is it i) directional input or ii) short-term facilitation that gives rise to lower phase? (or perhaps both?) Please clarify.

It’s both. This is now clarified in the revised version of the Re- sults sections related to Figure 2: higher depolarization always yields earlier phases in spiking models, however, pair correlations are not affected by ei- ther of the two mechanisms.

Line 320. ”...onset of phase precession”. Do you mean in CA3/CA1/DG?

Thank you for pointing this out. We have clarified that this statement refers to CA3.

Line 323. ”....at a different location”. Please add rationale why it has to be at a different location and a reference to the appropriate equation.

The sequence rationale as well as the equation number have been added.

Line 384. ” ... predicting that loss of DG inputs is compensated for by the increase of release probability in the spared afferent synapses from the MEC.”. It wasn’t clear whether this was a ’homeostasis prediction’, or and implementation in the model. Please clarify.

Since the model explained the experimental observations by implementing an increased probability of release, the model predicts that in animals with DG lesion the probability of release should be enhanced. We have modified the wording to avoid confusion.

Line 428 ”...and near future locations) is obvious, the potential role of the lesser expressed intrinsic sequence contributions is not straightforward.”. Similar to my comments above regarding terminology, please clarify what are both contributions and why are intrinsic sequences ’lesser expressed’.

We have rewritten this passage to avoid unclear wording.

Line 474. ”...we showed that the trajectory-independent sequences”. Do you mean ’intrinsic sequences’?

We thank the reviewer for careful reading! We have changed the wording ”intrinsic sequences” in the revision.

Line 482. ”...field pairs being extrinsic”. Please clarify, as the usage of extrinsic now refers to field pairs.

Thank you for pointing this out. We went through the whole manuscript and clarified the terms.

Line 245 (heading). Consider rewriting as ’Dependence of theta se- quences on heading directions’. Extrinsic and Intrinsic models have not yet been introduced.

Since the main purpose of the first Results section is to explain the difference between extrinsic and intrinsic sequences we kept these terms in the heading but modified it to ”Dependence of theta sequences on head- ing directions: Extrinsic and intrinsic sequences”. Additionally, we have put more emphasis on introducing the terms ”extrinsic” and ”intrinsic” in this section.

Figure 1.

• I suggest using the same font - C and D, and F and G are too close to each other, consider adding space. For example, the exponent, 10-2 makes reading cumbersome. Line 300. Phase tail means offset phase? Phase tail may be too informal. Line 325: DG loop. Do you mean CA3-DG projection?

We thank the reviewer for the suggestions. In the revised manuscript, we have ensured that the same font is used in all of the fig- ures. To improve the readability of Figure 1, we have added space between panels as suggested, removed repeated axis label and downsized the text ”10-2”. Furthermore, we have rewritten the referenced line without using the word ”tail”, and also, clarified the meaning of DG loop as the short form of CA3-DG projection.

Figure 4 caption: ”DG lesion reduces temporal correlations...”. It is more precise to say that the lesion reduces the slope of the fitted lag vs dis- tance. And how is this related to sequence compression?

In the paragraph referring to Figure 4, we have elaborated on the meaning of theta compression and its relation with the the lag-distance plot. However, we argue that ”reduces the slope of the fitted curve” is not comprehensive enough to express our summarized conclusion in a caption title. We have modified the wording to be ”DG lesion reduces theta compression”.

In addition, we have changed the slope unit to be radians per cm rather than radians per maximum pair distance, in conformity to unit standards.

General comment about terminology with regards to tuning and connec- tivity: it is not formally correct to compare connectivity with trajectories (e.g., lines 388-395, caption of Figure 5A, etc). Perhaps compare tuning to particular directions/preference or receptive field?

We have corrected the wording such that the direction of DG- loop projection is compared to the direction of trajectory.

Line 470. ’...fixed recursive loop.” Sentence is not clear, do you mean recurrent loops?

The reviewer is correct. We corrected the wording

Reviewer #2 had the following recommendations.

M1. The abstract focuses on the differences between online and offline hippocampal replays. However, the replay topic is not touched upon in the rest of the manuscript. I found this very confusing when I first read the pa- per. I suggest the authors reconsider the best way to approach the opening or at least discuss if and how their model would incorporate replay phenomena.

Also in response to reviewer #1 we have rewritten the abstract focusing on the problem of how to generate 2-d topology from 1-d sequences. In addition, also in response to Reviewer#1 we added a paragraph in the discussion detailing a hypothesis on how er think replay and intrinsic se- quences work together.

m2. On lines 89-91, the authors provide the selection of neuronal pa- rameters for excitatory pyramidal cells and inhibitory cells in the Izhikevich model. While the choice of model is reasonable, it would be helpful to clarify the source of these neuronal parameters, especially for readers who are not familiar with the model.

Again, also in response to reviewer # 1, we have added more motivation for the Izhikevich model.

M3. On lines 94-98, the model considers a 2D sheet of CA3 neurons. One of the most significant assumptions is that each 2x2 tile of place cells is considered a unit with four directional angles. What is the basis for this assumption? Is there any experimental result supporting this, or is it a completely artificial design for the model? This is important since the or- ganization of CA3 cells also affects the network architecture discussed later and impacts the realism of the model.

This comment is related to Reviewer #1’s concern on experience- dependent plasticity: How is this connectivity pattern established? We fully agree that this is an open problem for the Tsodyks et al.-type networks. The main reason for choosing them (as argued in our response to reviewer #1) is to have two published models, representing one type of sequence each, that are similar enough for comparison. In addition, we added new simulations (new Figure 6 and Supplementary Figure S1), showing that the basic phe- nomenology can also be obtained in a model without recurrent connections (see also response to Reviewer # 1)

m4. Similarly, on lines 111 and 140, the model uses 500 ms for the timescales of short facilitation and short-term synaptic depression. The choices of these two timescales are vital for producing directionality in extrin- sic and intrinsic sequences, yet their experimental sources are not clarified.

In the Methods section of the revised manuscript, we have in- cluded the sources of previous experimental data and modelling work to support our choice of the time constants.

M5. On line 126, the authors assume that the synaptic strengths be- tween CA3 cells, Wij, are given by the distances between neurons and the similarity between their directional preferences. While this assumption seems reasonable in the sensory cortex, I am unsure if this is also the case in the hippocampus, and the authors should clarify the basis for this assumption.

The distance dependence simply reflects the original Romani and Tsodyks 2015 model (see response to M3) and we share the concern of the reviewers. The increased connectivity for neurons with the same di- rectional preference was necessary to recover the direction dependent phase precession properties (Figure 2) in the realm of the Romani and Tsodyks 2015 model. Please also see our new Figure 6 showing simulations without the recurrent matrix.

More importantly, the existing connections within CA3 and DG cells completely determine the ”intrinsic” sequences. But wouldn’t this be fragile when place cells undergo global remapping, which can take place within only a few seconds? The author should comment on this in the discussion.

We would like to thank the reviewer for bringing up this inter- esting point. In our thinking, the DG-CA3 connectivity is fixed (multiple 1-d trajectories, not necessarily requiring 2-d topology), i.e., the same in- trinsic sequence should show up in multiple environments (and should not remap), although it may just not be active in some environments). This is a prediction of our model and we have added it to the Discussion.

M6. I found the setup of DG place cells unreasonable. DG place cells are found to be granule cells rather than pyramidal cells. Moreover, the model does not consider recurrent connections between DG cells (These setups are closer to CA1 place cells).

We agree with the reviewer, DG granule cells should rather be modelled as high-input resistance EIF neurons. However, the feedback loop via the dentate is not a direct one. It involves hilar mossy cells plus multiple hierarchies of feedback inhibition (this is probably what the reviewer means with recurrent connections between DG neurons, because granule cells are not recurrently connected in the non-pathological state). To our knowledge a biologically realistic model of the hilar-DG network does not exist and it would be far beyond the scope of this paper to develop one. We therefore see our DG feedback model rather as phenomenological. The discussion paragraph on the anatomy of the dentate gyrus touches on these points.

Therefore, a significant concern is: Why should it be the DG feedback projection to CA3 responsible for the ”intrinsic” sequences instead of pro- jections from other brain areas?

The reviewer is generally correct, any brain structure which im- plements fixed sequences via a loop would do. The reason why we suggest the DG to be the best candidate is purely empirical referring to papers with dentate lesions: Sasaki et al. 2018 and Ahmadi et a. 2022. We have added a similar argument to the discussion.

m7. On line 166, the authors claim that there are no connections between inhibitory cells at all. While I understand that this is for simplification of the model, the lack of recurrent inhibition between interneurons may have limited the model’s ability to produce gamma-band dynamics (referring to PING and ING mechanisms), which are robust rhythms produced in CA3. I am very curious if the model can incorporate theta-gamma coupling by in- troducing connections between CA3 inhibitory cells.

We have omitted the gamma oscillation for simplicity, because we do not have a hypothesis for a functional role in the context of dis- tinguishing extrinsic from intrinsic sequences (Occam’s razor) and, as the reviewer correctly anticipates, they unavoidably show up when inhibitory in- terneurons connect to each other (e.g. Thurley et al. 2013). Of course, one could envision situations in which gamma for intrinsic sequences my have different frequency than for extrinsic ones, by differentially manipulating the CA3 and DG basket cell networks, but, as long as there is no experimental data, it would be pure speculation and thus we have not included it in the model.

m8. The authors should clarify the source of parameters in Table 1, especially the synaptic strengths. These values are vital for extrinsic and intrinsic theta sequences.

The weight values have been chosen to allow for large theta phase precession range, coexistence of extrinsic and intrinsic sequences, and stability of the network activity. A similar statement has been added to the manuscript.

M9. I have another concern regarding the measurements of ”extrinsic- ity” and ”intrinsicity” defined on lines 185-196. Are they the best measures? To distinguish the cause of spike correlations, the ”extrinsicity” and ”intrin- sicity” of a pair of spikes should not be high at the same time. However, this is clearly not the case in the model, according to Figs 3 and 5. Moreover, in the data analysis carried out later, spike pairs are considered extrinsic or intrinsic merely by comparing the two measurements. I suggest the authors consider counterfactual methods in causal inference. For example, would a spike pair (cell1, cell2) still exist if we change the sensorimotor inputs or the DG-CA3 projections? If this is difficult to implement, the authors should at least discuss how different choices of measurements would impact the con- clusions of the paper.

The problem the reviewer has identified arises from the funda- mental symmetry of theta phase quantification: if spikes of a pair of place fields have a phase difference of 180◦ one cannot say which cell leads and which cell follows, hence, the phase difference is both intrinsic (because the peak doesn’t flip) and extrinsic (because the peak flips and ends up at the same phase). The fact that in some cases extrinsicity as well as intrinsicity are high simply means that the field pair has a correlation peak lag close to 180◦. Since in the experimental data set in (Yiu et al. 2022) only field pairs were available, we have not been able to use a different quantification then and decided to apply the same quantification in our model for comparison. Moreover, Figure 5F nicely shows that the measures are able to retrieve the ground-truth intrinsic DG-loop structure when considered on the population level.

In our model, though, we can go beyond 2-nd order statistics and derive sequence similarity measures including multiple cells, e.g., Chenani et al. 2019. However, since, we already know the ground truth by construction, we decided to not use these methods. We added a paragraph in the discus- sion elaborating on beyond 2nd order sequence quantification.

m10. The authors begin discussing ”intrinsic sequences” from line 316. However, it is not defined before that (and in the rest of the paper as well), causing confusion when reading the paper. The exact definitions of extrinsic and intrinsic sequences should come earlier.

We hope that our changes to the beginning of the results section (Figure 1), also asked for by Reviewer # 1 could clarify the confusion.

m11. On lines 345-347, the authors claim that ”the intrinsic sequences are played out backward as determined by the direction of fixed recurrence (Figure 3F),” which is vague. If such sequences are present in that panel, it should be more explicitly indicated graphically.

Also in response to Reviewer #1, we have graphically high- lighted the two types of sequences.

M12. On lines 309, 356, 484, 495, 515, and possibly other instances, the authors repeatedly claim that the model simulations are in ”quantitative agreement” with their previous experimental paper. However, no experimen- tal data or comparison with the simulations are presented in this paper. The authors should at least create one figure to demonstrate the degree of consistency between them, instead of merely asking the reader to refer back to their previous paper.

We agree with the reviewer that the experimental data of our previous paper should be presented in the manuscript. However, creating more panels or figures is likely to clutter the already crowded visuals and ob- scure our main message. We therefore decided to give numerical comparisons the previous findings in the main text whenever appropriate, specifically, in the sections referring to Figures 2, 3 and in the Discussion.

Author Response

We thank Dr. Carlos Isales and Dr. Jenny Tung as well as the peer Reviewers for their critiques and comments concerning this manuscript and respond here to their key concerns. Some of the Reviewers’ questions raised fascinating points about naked mole-rat biology and social habits, which we are also curious about, but which are too far afield from the central themes of the manuscript to warrant new work or revision. The Reviewers also raised some concerns about our methodological assessments and data interpretation which may warrant further discussion and explanation. We address those comments below. In no case do we feel that the concerns raised undermine our conclusions, so we have not undertaken new analyses nor revised the manuscript.

Median survival and power.

A recurring theme in these reviews is that our conclusion that naked mole-rats do not experience actuarial senescence is spurious, as it is “incomplete for younger animals and inadequate for older animals” due to Kaplan-Meier survival failing to reach median lifespan. We counter that premise, for median survival is an arbitrary threshold with no special bearing on when the Gompertzian hazard increase (onset of actuarial senescence) should become apparent. This point is well illustrated in Figure 5 of our original manuscript (Ruby et al., 2018). For demographic data from lab mice, humans, and horses (panels B, C, and D, respectively), the Gompertzian hazard increase is readily apparent by the time median survival (indicated by vertical dotted lines) is reached.

Another concern raised in the reviews is uncertainty about the true increase in power for these updated data since our 2018 report. The Reviewers correctly point out that the distribution of those data, and not just their scale, are relevant to power. The distribution of all data, old and new, are clearly illustrated as a function of age in Figure 2A. The ~doubling of available observation data is consistent across age groups, with one exception: at ~8,000-10,000 days of age. However, we do not agree that is a shortcoming of the new data’s power for hazard calculation among older animals, given that the animals that formerly occupied that age bin have continued to age, without greater hazard, across the next five years. In other words, the lack of N increase in that particular age bin is balanced by the massive increase in available data at ~10,000-12,000 days of age - an advanced age bin that was previously almost empty.

More surprisingly is the insinuation that for an approximately 40 gram rodent species, median survival on an order of 30+ years, with no sign of an increase in age-related mortality hazard, is considered a reasonable expectation. Both here and in our 2018 manuscript, we have conservatively used Tsex (180 days) as our benchmark for allometric scaling. Alternatively, one could scale this to the predicted lifespan based on average body weight for the species. According to the equation of de Magalhaes et al. (2007), the maximum lifespan of H.glaber is expected to be merely six years. Here, the Reviewers suggest that we are under-powered to make any statements about demographic aging because we have not reached median lifespan - despite the fact that our observations extend out to seven times the expected maximum lifespan. This is the precise nature of our argument that Gompertzian demographic aging is defied: that the onset of actuarial senescence is not apparent even at ages many-fold beyond when one would expect Gompertzian trends to have wiped out the entire population.

Ironically, the Reviewers seem to have focused on the most striking manifestations of Gompertzian defiance - not reaching median lifespan after decades of population observation, or having few death events after tens of thousands of days of individual lifespan observation - as reasons to doubt the conclusions. Even if we quadrupled the number of sample points and included data for another 35 years, if we still did not detect the onset of actuarial senescence, the same critiques would still apply - and would be similarly illogical.

The appropriateness of Kaplan-Meier, with left & right censorship

Objections were raised about the appropriateness of Kaplan-Meier survival analysis for our data. Reviewer #3 asserts that “a Kaplan-Meier estimator can only take right-censored and uncensored records”, which is incorrect. This perhaps reflects a wider misunderstanding of Kaplan-Meier statistics that warrants further explanation.

Reviewer #3 asserts that “left-censoring occurs when your event can be repeated and some events occur before the start of the study”. This is an oversimplified and far too-limited description of when left-censoring should be applied. We will further explain how left-censorship is applied in various analyses of our data, but for further reading on how this practice can produce unbiased estimates, we recommend the Reviewers consult (Cain et al 2011). We will discuss left and right truncation and censorship in terms of the diagram from Figure 2 of that manuscript, which illustrates a study in which the timing of event Y after event X in an individual’s life is being analyzed, given enrollment in a study at age A and exit from the study at age B. We also remind the Reviewers that methods used previously by us are in the papers (Ruby et al, 2018 & 2019) which were referenced and cited in our manuscript and should also be consulted for a full description.

For our study, ages A and B from (Cain et al 2011) are akin to the edges of our hazard estimation windows: appropriate application of censorship and truncation allows us to accurately, unbiasedly estimate hazard within each age bin, allowing fair evaluation of changes (or lack thereof) as a function of age. For full Kaplan-Meier survival, age A is uniformly defined as Tsex (day 187), and B is not globally defined - rather, it is defined for each animal if observation ended due to exit from the collection (i.e., used in research studies (KFR), donated to another researcher, or continuing to be alive at the time of the study). Since none of the Reviewers seemed confused or concerned about our use of right-censorship in these cases, we will focus this discussion on left-censorship.

In our original analysis (Ruby et al., 2018), we did not apply left-censorship because Dr. Buffenstein had maintained the animals since they were born, therefore no events occurred (i.e. observations of an animal being alive or dead on a day) prior to the beginning of the study. In the parlance of (Cain et al, 2011): we knew when the initiating event X had occurred (Tsex), and the animals had been continuously observed thereafter, up until either their death or rightcensorship point. Animals were right-censored if they were removed from the study, e.g. due to sacrifice for research or donation to other researchers. Doing so reduced the population size moving forward (to the right) without modifying the survival value, allowing the impact of individual death events to be appropriately amplified (i.e. Kaplan-Meier analysis).

For left-censored data, the same operation occurs but in reverse order: for example, if an animal is left-censored at 457 days of age, then the population size is increased by one on that day, without modifying the survival value. In Kaplan-Meier survival estimation, for each observation period, the current survival value is multiplied by the fraction of animals surviving at that time interval divided by the number of animals in the population in that interval. Since the animal in question was not observed prior to 457 days of age, it would not be counted in the population size prior to that day: had it died, it would not have been in the study population at all. However, once it has entered the population, each day-of-age on which it is observed to be alive is included in the population size tally, since each day it could also perish and thereby impact the survival curve. If any of the Reviewers received animals from Dr. Buffenstein should they wish to extend this data set in the future using those animals, left-censoring them at their age when they were received (or after some acclimation period) would be the proper method to do so.

As stated above: in our original analysis (Ruby et al., 2018), we did not generally apply leftcensorship because Dr. Buffenstein had maintained the animals since they were born (although beginning the analysis at Tsex qualifies as population-wide left-censorship). In their commentary, Dammann et al. (2019) pointed out that loss of records could modify the hazard distribution through bias towards longer-term survivors: in other words, counting long-lived animals as part of the population in early life is unfair because the death events from the truly larger population at that time had been lost (in that case: perhaps back in the 1980’s). In the parlance of (Cain et al, 2011): loss of records would have been the equivalent of left truncation, which if unchecked could produce bias. For our reply (Ruby et al., 2019), we address this problem by applying a drastic left-censoring of all animal data on a date where we could be highly confident that all records had been securely maintained, thus removing any potential bias introduced by old, lost records - as illustrated by (Cain et al, 2011). That re-analysis does not change our results, negating loss of decades-old records as a confounder of our conclusions. In this new manuscript, we used this technique again, only analyzing data collected since those data reported in our prior publications. Again, our original conclusions were confirmed: quoting Reviewer #3, “the main figures are virtually the same, with some minor changes due to the extended dataset”.

Independence between studies

In this new manuscript, with substantially more data, we applied left-censorship again in order to conduct an analysis of just the newly-provided data. Importantly, no datum - i.e. no day of observation of an animal being either alive or dead - overlapped between that analysis and those from our original reports (Ruby et al., 2018 & 19), and data were collected across nonoverlapping periods of time. Reviewer #2 questions the independence of this analysis from the original, correctly citing that it is still our own collection whose demographic data we are surveying. We reply that it is as independent of a dataset as we could possibly provide: greater independence would require the publication of substantial demographic data from other members of the H.glaber research community, which we would be happy to see. We also want to remind the Reviewers that Sherman and Jarvis (2002) also reported negligible demographic senescence for animals >15 years of age under their care: a fully-independent observation that concurs with our conclusions, albeit with substantially fewer animals and less statistical power.

“Glossing over” reports of aging phenotypes

Reviewer #1 suggests that our review of our own prior publications in this manuscript has “glossed over data that don’t support our main interpretations”, specifically mentioning the papers by Edrey et al., (2011) and Andziak et al., (2006). However, this is not an accurate reflection of the content of those published papers. The reviewer highlights data pertaining to case studies of two animals, aged 29 and 30 years, exhibiting pathologies that are commonly associated with aging in the Edrey et al., (2011) paper that was entitled “Successful aging and sustained good health in the naked mole-rat……”. But, as per the title of that paper, those were atypical cases. Indeed, we reported that the majority of animals maintained good health and activity well into their third decade. The Andziak et al., (2006) paper revealed that young (2y), healthy naked mole-rats have higher levels of oxidative damage to lipids, proteins and DNA than observed in young mice; but the follow up paper Andziak and Buffenstein (2006) reported that unlike that observed in mice, in naked mole-rats the levels of such damage do not further increase with advancing age, supporting the premise of sustained tissue homeostasis. Routine pathological assessments undertaken by our group and from zoological specimens in the 12 years since Edrey et al., (2011) have revealed many more instances of “aging phenotype pathologies” - but again, with similar frequency across all age groups (Delaney et al., 2021). We have not “glossed over data that don’t support our main interpretations”: in fact, the data brought up by the Reviewer support our conclusions. Like natural death, “age-associated disease phenotypes” occur stochastically across all age groups of H.glaber, rather than being exponentially enriched in elderly animals as in other species.

Breeding status

Reviewer #1 also states that “this study fails to fully represent the literature with respect to the divergence in aging rates between breeders and non-breeders” This section of our discussion (lines 326-367) addresses the survival advantage in many cooperative breeding mammals in the wild and in captivity including other mole-rats and meerkats (Sharp and Clutton-Brock, 2010; Dammann et al., 2011, Cram et al., 2018). The lower survival of subordinates in captivity may be due to chronic stress associated with bullying by the dominant animals and their inability to disperse and avoid such unpleasant activities; often being injured and dying after losing fights for a more dominant position in the social hierarchy. Braude et al., (2021) similarly report that compared to subordinates who undertake the more precarious activities of burrow extension, foraging or dispersal, the breeding females remain in their study site for far longer periods.

In captivity, subordinates have two paths to becoming a breeder: If the breeding female dies, some subordinate females within the colony will fight to the death to establish breeding status and inherit the dominant role in the colony. This could imply that they are “higher-quality” individuals as suggested by Reviewer #1 with molecular and physiological mechanisms in place to outlive their “poorer- quality” conspecifics. However, the majority of breeding females in our colony arise through random pairing of a female and a male that has been isolated for a few days from their colony. As such there is no selection for “higher-quality” individuals with concomitant inheritance of better somatic maintenance mechanisms. Rather, breeding status appears to be accompanied by a phenoplastic switch, as suggested by the lower levels of DNA methylation in tissues of breeding females (Horvath et al., 2021) and altered growth patterns when a female changes her status to that of a breeder (O’Riain et al., 2000). This is possibly linked to moving up the dominance hierarchy with concomitant changes in stress, somatotropic, and reproductive hormones as well as augmented tissue repair pathways for the maintenance of homeostasis.

We have not undertaken in depth studies on behavior and social habits and the effect of age, but agree these would be of interest in future studies.

Analysis initiation at 6 months

Mortality rates are highest in the first three months of life, in keeping with increased mortality during the developmental period. While it is true that in captivity most animals continue to grow for the first eighteen months to two years of life and some individuals may continue to gain weight well into their third decade, we and others have shown that animals can successfully breed at 6 months of age, if given the opportunity to do so. Other demographic studies similarly use the age at which animals can reproduce as the starting point for their analyses. Nevertheless, even if we were to use 2 years as the starting point, the same trends will be evident for there was no increase in mortality risk even at ages beyond 30 years.

Colony size effects

It is intriguing that smaller colonies had higher mortality risk than larger colonies. In many cases smaller colonies represent younger colonies with possibly less well established breeders and a higher degree of social instability. In other cases, the breeding female may not be very successful in raising her young, and possibly is not producing “high-quality” offspring. We agree with the Reviewer, behavioral assessments are needed to evaluate if there is more fighting and competition for dominance or if other social dynamics or ‘poorer-quality’ offspring are at play, nevertheless these findings are intriguing and we have speculated as to why this is the case. Further work is needed to definitively tease out why this is indeed the case.

References cited here

Andziak et al., (2006) doi: 10.1111/j.1474-9726.2006.00237

Andziak and Buffenstein (2006) doi: 10.1111/j.1474-9726.2006.00246

Braude et al., (2021) doi: 10.1111/brv.12660

Cain et al (2011) doi: 10.1093/aje/kwq481

Cram et al., (2018) doi: 10.1016/j.cub.2018.07.021

Dammann et al., (2011) doi: 10.1371/journal.pone.0018757

Dammann et al., (2019) doi:10.7554/eLife.45415

Delaney et al., (2021) doi: 10.1007/978-3-030-65943-1_15

De Magalhaes et al., (2007) doi: 10.1093/gerona/62.6.583

Edrey et al., (2011) doi: 10.1093/ilar.52.1.41

Horvath et al., (2022) doi:10.1038/s43587-021-00152-1

O’Riain et al., (2000) doi: 10.1073/pnas.97.24.13194 Ruby et al., (2018) doi: 10.7554/eLife.31157

Ruby et al., (2019) doi: 10.7554/eLife.47047.

Sharp and Clutton-Brock,(2010) doi: 10.1111/j.1365-2656.2009.01616.

Sherman and Jarvis (2002) doi: 10.1017/S0952836902001437

Author Response

Reviewer #2 (Public Review):

The manuscript by Ramesh et al builds upon prior studies from the Sigrist group to examine synergistic interactions between the Spinophilin (Spn) and Syd-1 synaptic proteins and their role in regulating presynaptic homeostatic plasticity at Drosophila larval NMJs and adult olfactory memory in the Mushroom Body (MB). The authors show synergistic interactions between the two proteins in these processes, where late PHP and long-term memory are abolished in Spn mutants, but restored upon reduction of Syd-1 function in the mutants. The authors go on to show that Spn appears to act in PHP by regulating a late stage in AZ remodeling and longer-term increases in the readily releasable SV pool by controlling actin polymerization/dynamics through the Mical protein. Although key aspects of the overall bigger picture have been published before (Mical’s role in PHP, antagonism between Spn and Syd-1 in AZ development, AZ remodeling in MB-dependent memory), the current paper ties together many of these observations into a bigger picture of how PHP plasticity at the NMJ is established and provides support for a role for PHP-required proteins in promoting long-term memory in the adult MB through effects on AZ structure and AZ protein content/amount. The study also provides new links to the role of Spn in regulating local synaptic actin dynamics and how this alters the readily releasable pool and SV release. Some points of note are provided below.

1) I’m a bit confused about the time course experiments the authors describe that seem to be contradictory in Figures 1 and 2. The authors indicate control animals transiently increase BRP AZ levels during PHP at 10 mins, but by 30 minutes this increase is gone, even though PHP remains. As such, the data in these early figures suggests increases in BRP AZ levels may support an early aspect of the PHP effect (though I note this appears controversial, as other data indicate blocking the rapid AZ remodeling by several manipulations such as Arl8 transport disruption, permits early PHP, but disrupts late PHP). In contrast, the authors show that Spn mutants do not display AZ BRP increase at 10 mins, and still show early PHP, but lack late PHP. I assume the early PHP does not require AZ remodeling or an increase in the RRP at this early time point?

We thank the reviewer for this insightful question, which to a degree is reflected also in reviewer 1´s question concerning the variability of Spn mutants when tested for PHP at 10 min PhTx treatment and thus the temporally and likely functional entanglement of induction and maintenance mechanisms.

Let us start by once again describing our findings: BRP increase is clear at 10 min PhTx treatment but is no longer measurable at 30 min PhTx treatment. Genetic elimination of BRP does not restrict PHP at 10 min PhTx (Bohme et al. 2019). However, BRP mutants are neither able to maintain PHP when PhTx treatment is extended to 30 minutes as described in Turrel et al (Turrel et al. 2022), nor in a chronic PHP paradigm of BRP, GluRIIA double mutant (Bohme et al. 2019). We suggest that the transient increase of BRP, also previously described specifically in the MB γ-neurons (Zhang et al. 2018), triggers other, longer lasting AZ changes. Indeed, we found that the increase of the critical release factor Unc13A is still present at 30 min PhTx treatment and is dependent on the “transient” BRP increase (Fig. S3B) (Turrel et al. 2022). Turrel et al also uncovered a more transient upregulation of BRP when compared to Unc13A in the MB. Here, specifically upon paired olfactory conditioning, 1 h after training, animals displayed BRP and Unc13A level increases. At 3 h post training, however, BRP levels had already plateaued, whereas Unc13A levels had increased further (Figure 1B, (Turrel et al. 2022)).

We have now added to the discussion section: “We suggest that the transient increase of BRP, also previously described specifically in the MB γ-neurons (Zhang et al. 2018), triggers other, longer lasting AZ changes. Indeed, we found that the increase of the critical release factor Unc13A is still present at 30 min PhTx treatment and is dependent on the “transient” BRP increase (Fig. S3B) (Turrel et al. 2022). Turrel et al also uncovered a more transient upregulation of BRP when compared to Unc13A in the MB. Here, specifically upon paired olfactory conditioning, 1 h after training, animals displayed BRP and Unc13A level increases. At 3 h post training, however, BRP levels had already plateaued, whereas Unc13A levels had increased further (Fig. 1B, Turrel et al).” (Line 363)

RRP increase has been shown at 10 min PhTx (Weyhersmuller et al. 2011) treatment and remains high after 30 minutes of PhTx treatment (this study).

2) In relation to point 1 above, the time course seems different in MB neurons, where the AZ remodeling (noted by increases in AZ BRP) seems to take 2-3 hours. Do the authors have any ideas into why the time course of PHP AZ remodeling at larval NMJs can occur in 10 minutes, but MB neuron remodeling seems to take hours?

We thank the reviewer for this question. We specifically probed the time intervals of 10 and 30 min at the NMJ due to established protocols and technical reasons; and 1hr and 3hr in the brain due to our interest in MTM. Zhang et al (Zhang et al. 2018) previously showed that indeed BRP levels in the γ-lobe were significantly increased already after 20 min after conditioning. We in the moment can only suspect that the following differences might be relevant in this point: the differences in the peripheral and central nervous system in terms of glutamatergic motoneuron presynapses (NMJ) versus cholinergic (KC presynapses) might change temporal dynamics of AZ remodeling. Furthermore, the plasticity induction protocol, using PhTx, is potentially a somewhat more “heavy-handed” approach compared to the more subtle conditioning involving the activation of dopaminergic neurons. The more complex circuitry of the central brain might also be involved in maintaining this BRP levels increase over longer timescales than at the NMJ, which may serve some yet unknown physiological purpose in maintaining memories.

We use the NMJ PhTx assay to identify proteins involved in AZ remodeling that could also be involved in memory formation in adult flies. As of now, we have no experimental evidence of whether the AZ remodeling observed in the MB actually leads to synaptic depression or instead is a reaction to the initial short-term synaptic depression occurring. This study and Turrel et al. 2022 (Turrel et al. 2022) provide evidence for an overlap of the executory machinery involved in both mechanisms, NMJ PHP plasticity and MTM formation, as BRP, Spn, Arl8, IMAC and Aplip1 are involved specifically both in mid-term NMJ PHP (at 30 min after PhTx treatment) and in MTM.

3) Could the lack of rapid BRP accumulation during early PHP in Spn mutants be secondary to the larger # of AZs in those mutants and a known rate-limiting amount of BRP available that might not be enough to go to the extra Azs?

This per se might be a relevant concern. Notably, however, acute application of Latrunculin-B in Spn mutants allowed for an increase in BRP (Figure 5g-h). Thus, a limitation in the total pool of available BRP should not be responsible for Spn mutants’ inability to accumulate BRP under PhTx treatment.

4) There isn't any validation of the Spn co-IP results shown in Figure 3 through other assays, and a lot of proteins are being pulled down. I can't see some of these being real (mitochondrial translation proteins? - how could Spn gain access to the inside of the mitochondria since it's a cytosolic protein?). As such, I don't know how to value that huge group of pull-down interactions without further validation, making it difficult to sort out how relevant these really are. The genetic validation of similar phenotypes in the Mical mutant, together with rescues, supports that interaction. Not sure about the rest of that list.

We appreciate the opportunity to discuss our primary data and how we used them to generate testable hypotheses for our study. Firstly, the mitochondrial translation proteins which were identified in our Spn IPs are all nuclear encoded, means they are transcribed in the nucleus and translated in the cytoplasm. Interestingly, recent work indeed suggests that mitochondrial biogenesis in the synapse is supported by local translation (e.g. see (Kuzniewska et al. 2020)). As Spn IPs are also highly significantly enriched for cytosolic translation machinery, it is an appealing idea that Spn might be involved in coupling local translation, mitochondria and memory stabilization. As this clearly goes beyond the scope of this paper, we did not further discuss this point, and are prepared to remove these data if considered misleading.

Concerning unspecific proteins being pulled down in our IPs, we would like to emphasize that these IPs are the result of an established out protocol, which entails laborious synaptosome preparations which our lab worked out previously (Depner et al. 2014). For each condition, 4 biological replicates were performed, and mitochondrial ribosomal proteins were enriched with p<10-30 significance, and never observed in our extensive systematic work on active zone biochemistry for any other active zone protein.

In this study, we used the Spn IPs to identify putative interaction partners, with the intention to validate the physiological relevance of any positive hits through experiments, like we did in the case of Mical. We were also able to identify previously known interaction partners like Syd-1 and Nrx-1 (Muhammad et al. 2015). Obviously, we did not independently validate these findings for the large number of identified proteins, e.g. by using in vitro purified proteins (we do not consider Western probing of IPs to be independent proof of any complementary value to mass-spectrometry based quantification).

We have now added this sentence to our manuscript:

“As a validation of the list of proteins that were returned as interaction partners of Spn in this work, we were able to reconfirm previously known interactions (Muhammad et al. 2015), e.g., Syd-1 (Figure 3b) and Nrx-1 (not shown).” (Line 148)

5) Are the authors worried about the fact that the Actin-GFP line they use to look at synaptic actin dynamics is driven by a GAL4, and the 2nd top hit of their Spn IP pull downs are translation regulators? Could the changes in actin-GFP they see between control and Spn mutants have anything to do with a different translation of the exogenous UAS-actin-GFP? Would have been helpful to do an endogenous stain for actin levels with an anti-actin antibody so no transcription/translation issues of a transgene would be at play. This would be easy to do for the quantification of total actin levels at the synapse.

This is per se a fully justified concern, which is hard to be fully excluded. Indeed, when preparing this manuscript, we attempted to visualize and quantify the endogenous presynaptic actin through immunostaining. However, these attempts were unsuccessful, as the very bright muscle actin staining obscures the relatively low levels of actin present close to the presynaptic AZs, even when using super-resolution light microscopy. Still, we would like to emphasize that Spn and Syd-1 antagonized each others’ function concerning apparent F-actin level (using Gal4 expression of actin-GFP). Given the known connection of Spn operating as a compartment specific F-actin breaker (Chia, Patel, and Shen 2012; Ryan et al. 2005; Nakanishi et al. 1997), we are still rather confident about our finding and its interpretation.

Concerning the FRAP analyses, we are fully confident of our findings, as the intensity of actin-GFP is internally normalized within each NMJ. Therefore, the differences in FRAP experiments should be independent of the starting amounts of actin in control and mutant animals. As we can show that the Spn/Syd-1 antagonism functions on actin dynamics as well (Figure 4j), we are sure concerning the physiological relevance of our observations.

6) Are Mical levels normalized in the Spn, Syd1 double mutants, given PHP is recovered?

We thank the reviewer for the comment and agree that Mical levels should be expected to normalize upon Syd-1 heterozygosity in Spn mutants. We have now immunostained for Mical in wildtype, Spn mutants and Spn mutants with Syd-1 heterozygosity to address this question. We found that Mical levels in Spn mutants were indeed normalized upon Syd-1 heterozygosity (Figure 5 - Figure supplement 1 c-d).

Author response

Reviewer #1 (Public Review):

The usual strategy to combat antimicrobial drug resistance is to administer a combination of two drugs with distinct mechanisms. An alternative, however, would be to use two drugs that attack the same target, if resistance to one is incompatible with resistance to the other. The authors previously studied parasites resistant to the dihydroorotate dehydrogenase (DHODH) inhibitor DSM265 through an E182D mutation and found that resistance to another inhibitor, IDI-6273, resulted in a reversion to wild-type. Here, they screened various other inhibitors and found that TCMDC-125334 is more active on DSM265-resistant parasites than the wild-type. In this case, however, it was possible for the parasites to become resistant to both inhibitors, either by increasing the copy number of DSM-265-resistant DHODH genes (with a C276Y mutation) or by the emergence of a different mutation. The selection of wild-type parasites with both compounds resulted in resistance but this took considerably longer than for either compound alone. (The actual frequency of double resistance emergence was not measured.)

Overall the results suggest that for DHODH, when pre-existing resistant parasites are selected with another inhibitor, the results will depend on both the initial mutation and the new inhibitor. The data are solid and convincing and suggest that DHODH has considerable scope for resistance development. The observations do have relevance for other inhibitors and/or enzyme drug targets. However from the data so far, the sweeping statements that the authors make concerning double resistance, in general, are not supported.

The formatting of the Figures requires some improvement and in some cases, more details of the statistical analyses are needed.

We thank Reviewer 1 for their kind and helpful comments. We have answered their specific concerns below. In particular, we have improved the formatting of the figures based on their recommendations. We have also edited the discussion based on reviewer 1’s comments.

Reviewer #2 (Public Review):

This article focuses on drug resistance acquired by Plasmodium falciparum malaria parasites that have been pressured with different inhibitors of the essential enzyme DHODH (dihydroorotate dehydrogenase). The study focuses on collateral sensitivity between DSM265, which has been evaluated in a human clinical trial and found to select for resistance via the point mutation C276Y (C276F and G181S were also implicated; PMID 29909069), and the GSK compound TMCDC-125334, against which a panel of DHODH mutant parasites (including C276Y) were found to have increased sensitivity. The authors herein explore this case of "collateral sensitivity" by examining whether these two inhibitors, when used simultaneously, might preclude the selection of resistant parasites. The answer, in this case, is no; collateral sensitivity did not prevent parasites from acquiring a novel mutation (V532A) that mediated resistance to both. Culture competition assays provide evidence that this mutant retains normal fitness. The authors conclude that for this target the idea of combining these inhibitors is not a viable therapeutic strategy. The authors also illustrate how TMCDC-125334 can select for resistance via a separate mutation (I263S) or amplification of a chromosomal segment containing dhodh. They also present modeling data to examine binding poses and how mutations could impact drug binding, which is allosteric to the enzyme's substrates (orotate and FMN). The data are thorough and provide convincing evidence that in this case collateral sensitization by distinct chemotypes does not translate into a viable strategy to inhibit DHODH in a way that can preclude mutations that confer cross-resistance.

We thank the reviewer for their kind comments and helpful recommendations.

Reviewer #3 (Public Review):

'Collateral sensitivity' occurs when drug-resistance mutations render a drug target more sensitive to inhibition by another drug, which has been previously described in some detail for malaria parasite dihydroorotate dehydrogenase (DHODH - see refs 36, 46, and 47, for example). Although it has been suggested that combinations of such drugs could potentially suppress the emergence of resistance, cross-resistance-associated mutation (or copy-number variation, CNV) could render such combination strategies ineffective. In the current study, the authors assess a new pairing of DHODH-targeting drugs. Cross-resistant parasites with DHODH mutation or CNV arise following either sequential or combined drug selection, suggesting that the drug combination described would likely fail to effectively suppress the emergence of resistance.

The strength of the study is that it describes, for a particular drug combination, different mutations associated either with collateral sensitivity or with cross-resistance, and the authors conclude that "combination treatment with DSM265 and TCMDC-125334 failed to suppress resistance". They go on to say that this "brings into question the usefulness of pursuing further DHODH inhibitors." More specific interpretations and implications of the study are as follows:

a. Other combinations may also fail but there may be combinations that can effectively suppress resistance. A more exhaustive analysis of mutational space will likely be required to determine which combinations if any, would be predicted to succeed in a clinical setting.

b. It was previously reported that "a combination of [DHODH] wild-type and mutant-type selective inhibitors led to resistance far less often than either drug alone. ... Comparative growth assays demonstrated that two mutant parasites grew less robustly than their wild-type parent, and the purified protein of those mutants showed a decrease in catalytic efficiency, thereby suggesting a reason for the diminished growth rate" (Ref 46). Also, "selection with a combination of Genz-669178, a wild-type PfDHODH inhibitor, and IDI-6273, a mutant-selective PfDHODH inhibitor, did not yield resistant parasites" (Ref 36). It is possible that these previously tested combinations would also yield cross-resistant mutants if selected further.

c. Although increased DHODH copy number "confers only moderately reduced susceptibility" to the drug used for selection and although these clones were not assessed here for cross-resistance, it seems likely that CNV may represent a general mechanism that could undermine other collateral resistance strategies.

We thank the reviewer for their kind and helpful comments.

Author Response

Reviewer #1 (Public Review):

This study applies state-of-the-art single-cell transcriptome analysis to investigate the nature of drug tolerance, a phenomenon distinct from drug resistance, and a problem of considerable importance in the treatment of C. albicans infections. The authors first show that their transcriptomics platform can reveal sub-populations of untreated cells that display distinct transcription profiles related to metabolic and stress responses that are coupled with cell cycle regulation. They note the consistency of these findings with previous work indicating connections between cell cycle phase and expression of genes related to stress responses and metabolism and argue that this validates their experimental approach, which relies on a complex statistical analysis of sparse data from a relatively small number of single cells. They then proceed to analyze drug-treated cells, mostly focusing on fluconazole (FCZ; which targets ERG11, thus disrupting ergosterol biosynthesis and membrane integrity) and examining individual cells at 2-, 3-, and 6-days following treatment. Their primary finding is the identification of two major classes of cells, one of which they call the α response, characterized by high ribosomal protein (RP) gene expression and the absence of either heat shock or hyperosmotic stress gene expression as well as low expression of glycolytic, carbohydrate reserve pathway, and histone genes. The second survival state on day 2 (called the β response) instead displays low RP gene expression and high heat-shock stress response. Interestingly, the proportion of β cells clearly increases on day 3. In addition, responses to caspofungin (CSP) and rapamycin (RAPA) are examined and compared to FCZ or untreated cells. The main conclusion that the authors draw from their data is that the initial α response transitions to the β response, which is similar to a recently characterized ribosome assembly stress response (RASTR) in the budding yeast S. cerevisiae. They argue that the transcriptional state in α cells provokes the transition to the β state.

This manuscript presents an enormous amount of complex data whose significance will be difficult to evaluate for those (e.g., this reviewer) not immersed in the specialized analytical techniques used here. Taken at face value, however, the experimental findings are consistent with the authors' main conclusions. Nevertheless, and consistent with the complexity of the responses observed, there are many findings that remain to be explored in mechanistic detail and for which conclusions are less precise.

We thank Reviewer #1 for their excellent questions. The manuscript does have a large amount of complex data so this version of the manuscript has a tighter focus on the major findings (i.e. 𝛼/Rd versus β/Sd subpopulations in response to FCZ). We have tried to explore these subpopulations in greater depth with supporting data from complementary technologies and additional bioinformatic analyses. We agree that there still remains several observations in the manuscript that are not explored in mechanistic detail. We have tried our best to clearly delineate the evidence that we have for these findings in addition to their potential significance.

Towards the simplification of the manuscript, we have moved the discussion regarding “comets” to Appendix 2 [Changes L837-897] along with the detailed analysis of the response of cells to rapamyacin and caspofungin [Changes L899-963]. We have also removed from the manuscript a paragraph (and associated Figure 2 - figure supplement 5 in the original manuscript) from the Discussion that described our inability to assign DNA level chromosomal aberrations to either the Rd or Sd subpopulations using whole genome sequencing. Figures 5 and 6 of the original manuscript depicted GO analysis that compared changes in the molecular processes between 𝛼/Rd and β/Sd subpopulations at day 3 and 6 respectively. Although interesting, the figures do not advance the main findings of the manuscript and have been removed from this version.

Reviewer #2 (Public Review):

In this manuscript, Dumeaux et al. assess the heterogeneous cellular response of the fungal pathogen Candida albicans to antifungal agents, using single-cell RNA sequencing. The researchers develop and optimized single-cell transcriptomics platform for C. albicans, and exploit this technique to monitor the cellular response to treatment with three distinct antifungal agents. Through this analysis, they identify two distinct subpopulations of cells that undergo differential transcriptomic responses to antifungal treatment: one involving upregulation of translation and respiration, and the other involving stress responses. This work monitors how different and prolonged antifungal exposure alters and shifts fungal cell populations between these responses. This is an innovative study that exploits novel single-cell transcriptomic techniques to address a very interesting question regarding the heterogeneous nature of the fungal response to antifungal drug treatment. This work optimizes a protocol for single-cell RNA sequencing, which is a significant contribution to the fungal research community and will bolster future research efforts in this area. The identification of two distinct subpopulations of fungal cells with differential responses to antifungal treatment is an exciting and novel finding. While there are aspects of this manuscript that are of significant interest, there are also limitations to this work.

The research is framed as a method to study antifungal drug tolerance, but it is not clear how it does so, based on the methods. This work also compares very different populations of cells (rapidly growing untreated cells compared with cells grown in antifungal for several days), making it difficult to assess the role of antifungal treatment specifically in this analysis. This manuscript is also written with a great deal of highly technical language that makes it difficult to dissect the major findings and outcomes from the study.

We sincerely thank the reviewer for these comments and for making the effort to evaluate the manuscript. We have tried to address these criticisms by improving the introduction to better explain fungal drug tolerance [Changes L53-61] and to explain how our experimental design allows us to investigate this phenomenon (for example for UT cells L184-187, L142-149). We have also re-written subsections of the results to more intuitively explain technical concepts (especially surrounding single cell technologies and analyses) [L250-257, L368-373, L699-707]. Some subsections of the results have been moved to the appendices in order to better emphasize the major findings and outcomes (e.g. comets L837-897 and in depth analysis of RAPA and CSP treatment L899-963). We address each of the specific concerns below. We have also removed some complicated analyses that did not directly advance the major findings of the manuscript including the GO analysis in Figures 5 and 6 of the original manuscript.

Before proceeding, we would like to take this opportunity to underscore that these experiments were not primarily designed to investigate the differences between untreated (UT) and treated cells. The major findings (of the 𝛼/Rd and β/Sd subpopulations) are not dependent on the UT profiles. That is, the 𝛼/Rd and β/Sd subpopulations would be evident even if the UT profiles were removed from the manuscript entirely. Rather, the UT profiles/analyses are intended to contribute to the manuscript by helping establish the technical efficacy of the sc-profiling technique. For example, we might expect - a priori - that a large component of cell to cell heterogeneity in isogenic UT cells should correspond to differences in cell cycle, and, indeed, this is what we found.

Indeed, we did embed (via UMAP) and cluster (via Leiden clustering) the UT data alongside data for the drug-treated cells (Figure 3), which reveals that UT cells largely cluster separately from drug-treated cells. The reviewer is absolutely correct to question the sources underlying this separation; in addition to differential cellular responses to the drug itself, some of the separation may be due to differences in the amount of growth media, for example. (The fact that different drugs (FCZ, RAPA and CSP) largely separate from UT cells and from each other may suggest that at least some of this separation could be due to differences in the mode of action of each drug rather than to issues related to, for example, media depletion. However, this difference is not a major finding of the manuscript. Rather, we agree with the reviewer that “The identification of two distinct subpopulations of fungal cells with differential responses to antifungal treatment is an exciting and novel finding”. As such, the major results begin with data in panels 3D and E that reveal the two distinct cell types within the FCZ-treated sample (a distinction that is not dependent on the status of the UT cells).

Reviewer #3 (Public Review):

The authors described their extensive single-cell analysis of Candida undergoing (sub-inhibitory) antibiotic treatment versus no treatment. To do so, the authors used a microfluidics platform they had previously developed, and they optimized, characterized, and validated it for this particular application. Their findings included: (a) the transcription of untreated cells is driven mostly by cell cycle phase, (b) treated cells can be clustered into several major groups and a few outlier groups that the authors termed comets, (c) cells undergoing FCZ treatment can adopt one of two different states (possibly bistability). I found the results interesting and the approach to be sound, and much of the results confirmed my prior expectations. The authors provide a detailed depiction of what is going on in the transcriptome during sub-inhibitory treatment, although this did not always lead to a mechanistic explanation. The clinical relevance was unclear to me beyond a proof of concept application for single-cell transcriptomics. In my opinion, an interesting follow-up would be to follow the transcriptional trajectory of lineages undergoing antimicrobial switching (on and off). The main issues I identified were the author's use of the term tolerance versus resistance, interpretation of "comets", clustering approach, description of fitness, and comparison between time points.

We thank the reviewer for their time and effort with this manuscript. In the revised manuscript, we expanded the introduction to better delineate between resistance and tolerance, moved the “comets” section to the appendices, as it distracted from the major results and we provided more interpretive analysis of the findings. We also better defined the bioinformatic approaches. (Changes e.g. comets L837-897 and in depth analysis of RAPA and CSP treatment L899-963). With respect to comparisons between time points, we now address these concerns throughout the Response to Reviewer document. We have also moved a comparison of UT versus FCZ cells to Appendix 2 L828-836 as it was perhaps misleading readers of our intention. We only performed this comparison as a sort of “sanity” check to see if the single cell (sc)-profiling would detect differences between UT and drug treated cells.

Author response

Reviewer #1 (Public Review):

This careful study reports the importance of Rab12 for Parkinson's disease associated LRRK2 kinase activity in cells. The authors carried out a targeted siRNA screen of Rab substrates and found lower pRab10 levels in cells depleted of Rab12. It has previously been reported that LLOMe treatment of cells breaks lysosomes and with time, leads to major activation of LRRK2 kinase. Here they show that LLOMe-induced kinase activation requires Rab12 and does not require Rab12 phosphorylation to show the effect.

We thank the reviewer for their comments regarding the carefulness and importance of our work and for their specific feedback which has substantially improved our revised manuscript.

1) Throughout the text, the authors claim that "Rab12 is required for LRRK2 dependent phosphorylation" (Page 4 line 78; Page 9 line 153; Page 22 line 421). This is not correct according to Figure 1 Figure Supp 1B - there is still pRab10. It is correct only in relation to the LLOMe activation. Please correct this error.

We appreciate the reviewer’s comment around the requirement of Rab12 for LRRK2-dependent phosphorylation of Rab10 and question regarding whether this is relevant under baseline conditions or only in relation to LLOMe activation. Using our MSD-based assay to quantify pT73 Rab10 levels under basal conditions, we observed a similar reduction in Rab10 phosphorylation when we knockdown Rab12 as we also observed with LRRK2 knockdown (Figure 1A). Further, we see comparable reduction in Rab10 phosphorylation in RAB12 KO cells as that observed in LRRK2 KO cells using our MSD-based assay (Figure 2A and B). Based on this data, we believe Rab12 is a key regulator of LRRK2 activation under basal conditions without additional lysosomal damage. However, as the reviewer noted, we do observe some residual Rab10 phosphorylation upon Rab12 knockdown when assessed by western blot analysis (Figure 1D and Figure 1- figure supplement 1). A similar signal is observed upon LRRK2 knockdown, which may suggest that some small amount of Rab10 phosphorylation may be mediated by another kinase in this cell model. Nevertheless, we appreciate this reviewer’s point and have therefore modified the text to remove any reference to Rab12 being required for LRRK2-dependent Rab phosphorylation and now instead refer to Rab12 as a regulator of LRRK2 activity.

As noted by the reviewer, our data does suggest that Rab12 is required for the increase in Rab10 phosphorylation observed following LLOMe treatment to elicit lysosomal damage, and we now refer to this appropriately throughout the text.

2) The authors conclude that Rab12 recruitment precedes that of LRRK2 but the rate of recruitment (slopes of curves in 3F and G) is actually faster for LRRK2 than for Rab12 with no proof that Rab12 is faster-please modify the text-it looks more like coordinated recruitment.

The reviewer raises an excellent point regarding our ability to delineate whether Rab12 recruitment precedes that of LRRK2 on lysosomes following LLOMe treatment. As noted by the reviewer, we do see both the recruitment of Rab12 and LRRK2 to lysosomes increase on a similar timescale, so we cannot truly resolve whether Rab12 recruitment precedes LRRK2 recruitment in our studies. Based on this, we have modified the text to emphasize that this data supports coordinated recruitment, as suggested, and we have further removed any mention of Rab12 preceding LRRK2. The specific change is as follows “Rab12 colocalization with LRRK2 increased over time following LLOMe treatment, supporting potential coordinated recruitment of these proteins to lysosomes upon damage (Figure 3I). Together, these data demonstrate that Rab12 and LRRK2 both associate with lysosomes following membrane rupture.” and can be found on lines 460-463 of the updated manuscript.

3) The title is misleading because the authors do not show that Rab12 promotes LRRK2 membrane association. This would require Rab12 to be sufficient to localize LRRK2 to a mislocalized Rab12. The authors DO show that Rab12 is needed for the massive LLOME activation at lysosomes. Please re-word the title.

To address the reviewer’s concern regarding the title of our manuscript, we have modified the title from “Rab12 regulates LRRK2 activity by promoting its localization to lysosomes” to “Rab12 regulates LRRK2 activity by facilitating its localization to lysosomes” to soften the language around the sufficiency of Rab12 in regulating the localization of LRRK2 to lysosomes. We show that Rab12 deletion significantly reduces LRRK2 activity (as assessed by Rab10 phosphorylation on lysosomes) and significantly increases the localization of LRRK2 to lysosomes upon lysosomal damage. The updated title better reflects the regulatory role of Rab12 in modulating LRRK2 activity, and we thank the reviewer for their suggestion to modify this accordingly.

Reviewer #2 (Public Review):

This study shows that rab12 has a role in the phosphorylation of rab10 by LRRK2. Many publications have previously focused on the phosphorylation targets of LRRK2 and the significance of many remains unclear, but the study of LRRK2 activation has mostly focused on the role of disease-associated mutations (in LRRK2 and VPS35) and rab29. The work is performed entirely in an alveolar lung cell line, limiting relevance for the nervous system. Nonetheless, the authors take advantage of this simplified system to explore the mechanism by which rab12 activates LRRK2. In general, the work is performed very carefully with appropriate controls, excluding trivial explanations for the results, but there are several serious problems with the experiments and in particular the interpretation.

We appreciate the reviewer’s comments regarding the rigor of our work and the potential impact of our studies to address a key unanswered question in the field regarding the mechanisms by which LRRK2 activation is mediated. Our studies focused on the A549 cell model given its high endogenous expression of LRRK2 and Rab10, and this cell line provided a simple system to investigate the mechanism and impact of Rab12-dependent regulation of LRRK2 activity. We agree with the reviewer that future studies are warranted to understand whether similar Rab12-dependent regulation of LRRK2 occurs in relevant CNS cell types.

First, the authors note that rab29 appears to have a smaller or no effect when knocked down in these cells. However, the quantitation (Fig1-S1A) shows a much less significant knockdown of rab29 than rab12, so it would be important to repeat this with better knockdown or preferably a KO (by CRISPR) before making this conclusion. And the relationship to rab29 is important, so if a better KD or KO shows an effect, it would be important to assess by knocking down rab12 in the rab29 KO background.

The reviewer raises a good point regarding the importance of confirming that loss of Rab29 has no effect on Rab10 phosphorylation. To address potential concerns about insufficient Rab29 knockdown, we measured the levels of pT73 Rab10 in RAB29 KO A549 cells by MSD-based analysis. RAB29 deletion had no effect on Rab10 phosphorylation, confirming findings from our RAB siRNA screen and the observations of Dario Alessi’s group reported previously (Kalogeropulou et al Biochem J 2020; PMID: 33135724). We have included this new data into our updated manuscript in Figure 1- figure supplement 1 and comment on it on page 6 in the updated Results section.

Secondly, the knockdown of rab12 generally has a strong effect on the phosphorylation of the LRRK2 substrate rab10 but I could not find an experiment that shows whether rab12 has any effect on the residual phosphorylation of rab10 in the LRRK2 KO. There is not much phosphorylation left in the absence of LRRK2 but maybe this depends on rab12 just as much as in cells with LRRK2 and rab12 is operating independently of LRRK2, either through a different kinase or simply by making rab10 more available for phosphorylation. The epistasis experiment is crucial to address this possibility. To establish the connection to LRRK2, it would also help to compare the effect of rab12 KD on the phosphorylation of selected rabs that do or do not depend on LRRK2.

The reviewer raises an interesting question regarding whether Rab12 can further reduce Rab10 phosphorylation independently of LRRK2. Using our quantitative MSD-based assay, we observe that pRab10 levels are at the lower limits of detection of the assay in LRRK2 KO A549 cells. Unfortunately, this means that we are unable to detect whether there might be any additional minor reduction in Rab10 phosphorylation with Rab12 knockdown in LRRK2 KO cells. We cannot rule out that Rab12 may play a LRRK2-independent role in regulating Rab10 phosphorylation in other cell lines, and future studies are warranted to explore whether Rab12 knockdown can further reduce Rab10 phosphorylation in other systems, including in CNS cells.

Regarding exploring the effects of RAB12 knockdown on the phosphorylation of other Rabs, we also assessed the impact of RAB12 KO on phosphorylation of another LRRK2-Rab substrate, Rab8a. We observed a strong reduction in pT72 Rab8a levels in RAB12 KO cells compared to wildtype cells, suggesting the impact of RAB12 deletion extends beyond Rab10 (see representative western blot in Author response image 1). Due to potential concerns with the selectivity of the pT72 Rab8a antibody (potentially detecting the phosphorylation of other LRRK2-Rabs), we cannot definitively demonstrate that Rab12 mediates the phosphorylation of other Rabs. This question should be revisited when additional phospho-Rab antibodies become available that enable us to selectively detect LRRK2-dependent phosphorylation of additional Rab substrates under endogenous expression conditions.

Author response image 1.

A strength of the work is the demonstration of p-rab10 recruitment to lysosomes by biochemistry and imaging. The demonstration that LRRK2 is required for this by biochemistry (Fig 4A) is very important but it would also be good to determine whether the requirement for LRRK2 extends to imaging. In support of a causal relationship, the authors also state that lysosomal accumulation of rab12 precedes LRRK2 but the data do not show this. Imaging with and without LRRK2 would provide more compelling evidence for a causative role.

We thank the reviewer for their suggestion to assess Rab12 recruitment to damaged lysosomes with and without LRRK2 using imaging-based analyses to add confidence to our findings from biochemical approaches. To address this comment, we have imaged the recruitment of mCherry-tagged Rab12 to lysosomes (as assessed using an antibody against endogenous LAMP1) and observed a significant increase in Rab12 levels on lysosomes following LLOMe treatment. This occurs to a similar extent in LRRK2 KO A549 cells, suggesting that Rab12 is an upstream regulator of LRRK2 activity. This new data has been incorporated into the revised manuscript (Figure 3E) and is presented on page 20 of the updated manuscript.

Our conclusions on this are further strengthened by new data assessing Rab12 recruitment to lysosomes using orthogonal analysis of isolated lysosomes biochemically. Using the Lyso-IP method, we observed a strong increase in the levels of Rab12 on lysosomes following LLOMe treatment that was maintained in LRRK2 KO cells. These data have been added to the updated manuscript (new data added to Figure 3- figure supplement 1).

Together, these data support our hypothesis that Rab12 recruitment to damaged lysosomes is upstream, and independent, of LRRK2.

The authors also touch base with PD mutations, showing that loss of rab12 reduces the phosphorylation of rab10. However, it is interesting that loss of rab12 has the same effect with R1441G LRRK2 and D620N VPS35 as it does in controls. This suggests that the effect of rab12 does not depend on the extent of LRRK2 activation. It is also surprising that R1441G LRRK2 does not increase p-rab10 phosphorylation (Fig 2G) as suggested in the literature and stated in the text.

We agree with the reviewer that it is quite interesting that RAB12 knockdown significantly attenuates Rab10 phosphorylation in the context of PD-linked variants in addition to that observed in wildtype cells basally and after LLOMe treatment. As noted by the reviewer, we did not observe increased levels of phospho-Rab10 in LRRK2 R1441G KI A549 cells at the whole cell level (Figure 2G). However, we observed a significant increase in Rab10 phosphorylation on isolated lysosomes from LRRK2 R1441G KI cells compared to WT cells (Figure 4B). This may suggest that the LRRK2 R1441G variant leads to a more modest increase in LRRK2 activity in this cell model. Previous studies in MEFs from LRRK2 R1441G KI mice or neutrophils from human subjects that carry the LRRK2 R1441G variant showed a 3-4 fold increase in Rab10 phosphorylation (Fan et al Acta Neuropathol 2021 PMID: 34125248 and Karaye et al Mol Cell Proteomics 2020 PMID: 32601174), supporting that this variant does lead to increased Rab10 phosphorylation and that the extent of LRRK2 activation may vary across different cell types.

Most important, the final figure suggests that PD-associated mutations in LRRK2 and VPS35 occlude the effect of lysosomal disruption on lysosomal recruitment of LRRK2 (Fig 4D) but do not impair the phosphorylation of rab10 also triggered by lysosomal disruption (4A-C). Phosphorylation of this target thus appears to be regulated independently of LRRK2 recruitment to the lysosome, suggesting another level of control (perhaps of kinase activity rather than localization) that has not been considered.

The reviewer suggests an interesting hypothesis around the existence of additional levels of control beyond the lysosomal levels of LRRK2 to lead to increased Rab10 phosphorylation of lysosomes. Given the variability we have observed in measuring endogenous LRRK2 levels on lysosomes, we performed two additional replicates to assess lysosomal LRRK2 levels in LRRK2 R1441G KI and VPS35 D620N KI cells at baseline and after treatment with LLOMe. We observed a significant increase in LRRK2 levels on lysosomes in cells expressing either PD-linked variant and a trend toward a further increase in the levels of LRRK2 on lysosomes after LLOMe treatment in these cells (Figure 4D in the updated manuscript). We have updated the text on page 24 to reflect this change, suggesting that the PD-linked variants do not fully occlude the effect of lysosomal disruption on the lysosomal recruitment of LRRK2.

LLOMe treatment leads to a stronger increase in Rab10 phosphorylation on lysosomes from LRRK2 R1441G and VPS35 D620N cells compared to the modest increase in LRRK2 levels observed. This could suggest that, as the reviewer noted, additional mechanisms beyond increased lysosomal localization of LRRK2 may be driving the robust increase in Rab10 phosphorylation observed. We have modified the results section on lines 548-551 to highlight this possibility: “Rab10 phosphorylation showed a more significant increase in response to LLOMe treatment than LRRK2 on lysosomes from LRRK2 R1441G and VPS35 D620N KI cells, suggesting that there may be more regulation beyond the enhanced proximity between LRRK2 and Rab that contribute to LRRK2 activation in response to lysosomal damage.”

Reviewer #3 (Public Review):

Increased LRRK2 kinase activity is known to confer Parkinson's disease risk. While much is known about disease-causing LRRK2 mutations that increase LRRK2 kinase activity, the normal cellular mechanisms of LRRK2 activation are less well understood. Rab GTPases are known to play a role in LRRK2 activation and to be substrates for the kinase activity of LRRK2. However, much of the data on Rabs in LRRK2 activation comes from over-expression studies and the contributions of endogenously expressed Rabs to LRRK2 activation are less clear. To address this problem, Bondar and colleagues tested the impact of systematically depleting candidate Rab GTPases on LRRK2 activity as measured by its ability to phosphorylate Rab10 in the human A549 type 2 pneumocyte cell line. This resulted in the identification of a major role for Rab12 in controlling LRRK2 activity towards Rab10 in this model system. Follow-up studies show that this role for Rab12 is of particular importance for the phosphorylation of Rab10 by LRRK2 at damaged lysosomes. Increases in LRRK2 activity in cells harboring disease-causing mutants of LRRK2 and VPS35 also depend (at least partially) on Rab12. Confidence in the role of Rab12 in supporting LRRK2 activity is strengthened by parallel experiments showing that either siRNA-mediated depletion of Rab12 or CRISPR-mediated Rab12 KO both have similar effects on LRRK2 activity. Collectively, these results demonstrate a novel role for Rab12 in supporting LRRK2 activation in A549 cells. It is likely that this effect is generalizable to other cell types. However, this remains to be established. It is also likely that lysosomes are the subcellular site where Rab12-dependent activation of LRRK2 occurs. Independent validation of these conclusions with additional experiments would strengthen this conclusion and help to address some concerns that much of the data supporting a lysosome localization for Rab12-dependent activation of LRRK2 comes from a single method (LysoIP). Furthermore, there is a discrepancy between panel 4A versus 4D in the effect of LLoMe-induced lysosome damage on LRRK2 recruitment to lysosomes that will need to be addressed to strengthen confidence in conclusions about lysosomes as sites of LRRK2 activation by Rab12.

We thank the reviewer for their comments regarding our work that identifies Rab12 as a novel regulator of LRRK2 activation and the appreciation of the parallel approaches we employed to add confidence in this effect.

As suggested by the reviewer, we have updated our manuscript to now include independent validation of our conclusions using imaging-based analyses to complement our data from biochemical analyses using the Lyso-IP method. Specifically, we have included new imaging data that confirms that Rab12 levels are increased on lysosomes following membrane permeabilization with LLOMe treatment and demonstrates that this occurs independent of LRRK2, providing additional support that Rab12 is an upstream regulator of LRRK2 activity (Figure 3E in the updated manuscript).

Regarding the reviewer’s comment on a discrepancy between our findings in Figure 4A and Figure 4D, we have performed additional independent replicates in Figure 4D to assess the impact of lysosomal damage on the lysosomal levels of LRRK2 at baseline or upon the expression of genetic variants. We observed a significant increase in LRRK2 levels on lysosomes following LLOMe treatment in our set of experiments included in Figure 4A and a non-significant trend toward an increase in LRRK2 levels on isolates lysosomes in Figure 4D. As described in more detail below (in response to the second point raised by this reviewer), we think this variability arises because of a combination of low levels of LRRK2 on lysosomes with endogenous expression and variability across experiments in the efficiency of lysosomal isolation. Our observations of increased recruitment of LRRK2 to lysosomes upon damage are further supported by parallel imaging-based studies (Figure 3F-I) and are consistent with previous studies using overexpression systems.

We thank the reviewer for all of the suggestions which have added further confidence to our conclusions and substantially improved the manuscript.

Author Response

Reviewer #1 (Public Review):

This manuscript provides novel and intriguing experiments that aim to elucidate the mechanical properties of the Reissner fiber (RF) and to probe its interactions with the motile cilia in the central canal of the spinal cord. Using in vivo imaging in larval zebrafish, the authors show that the RF is under tension and oscillates dorsoventrally. Importantly, ablation of the RF triggered retraction and relaxation of the fiber cut ends. The retraction speed depends on where the fiber was ablated, with fastest retraction in the rostral side, indicating that tension in the RF builds up rostrally. The authors, based on observations from live imaging of intact and ablated RF and central canal, conjecture that numerous ependymal motile monocilia, that are tilted caudally and interact frequently with the RF, contribute to RF heterogenous tension via weak interactions.

The work is important. The experiments are thorough and intricate. The findings are fascinating and open up the prospect for future investigations and models. I'm particularly curious as to what future experiments can be used to test the hypothesis put forward by the authors about the role of ciliafiber interactions in the RF mechanical properties and function.

We thank Reviewer#1 for showing enthusiasm and support.

Reviewer #2 (Public Review):

The present manuscript by the Claire Wyart group analyses the behaviour of Reissner's fibre (RF) when it is cut, as well as the behaviour of cells touching RF when contact is interrupted. They show that RF is under tension that is higher in the rostral than in the caudal spinal cord. One of the proposed mechanisms is a caudally oriented movement of the cilia of ependymal radial glials cells (ERG) that is inherent rather than caused by the contact with RF. Kolmer Agduhr neurons that are also CSF contacting (CSF-cN), alter their activity when contact is lost through laser ablation of RF.

This is an interesting paper - RF has long been proposed to be a source of signalling molecules in the development and physiological function of neural cells in the spinal cord. Cilia are the main centre of signalling activity in ciliated cells (e.g. for sonic hedgehog signalling) and the fact that ERG cilia are in direct contact with RF is intriguing. Presumably, signalling molecules could be directly transferred from RF to ERG at the contact points.

Functionally, CSF-cN are augmenting spinal cord intrinsic sensory feedback on body curvature. This had been shown in vitro/ex vivo, but not clearly evaluated in the living animal. The data shown here demonstrate a possible mechanism for how the feedback can be mediated through contact with RF. This is of fundamental interest to understand the functioning of a locomotor network that is under evolutionary pressure to function early, since fish hatch at 3 days post fertilisation.

We thank Reviewer#2 for the interest in our work.

Interestingly, the authors propose (and discuss against the relevant literature) that the presence of RF in the central canal can influence the flow of the CSF, which should be investigated in further work.

To bring readers back in the context of the existing literature:

When using beads to track particles in the flow in the presence or in the absence of RF, we have not seen major difference in the bidirectional dorsoventral profile of the embryonic CSF flow (Cantaut-Belarif et al CB 2018 ; Sternberg et al., Nature Comm 2019 ; Thouvenin et al., eLife 2020).

However, we cannot exclude that there could be a very local impact of the RF on CSF flow, due to the fact that the flow has to be null on the surface of the fiber (of 200 nm diameter). With our methods for tracking fluorescent particles in single planes at a time (Cantaut-Belarif et al CB 2018 ; Sternberg et al., Nature Comm 2019 ; Thouvenin et al., eLife 2020), we are likely missing the fiber in the plane and the fine analysis of the domain surrounding the fiber is not resolved. However, a null flow at the surface of the RF would impose a sharp gradient around the fiber.

Note that our results estimating the effect of cutting the fiber on the beating frequency of motile cilia were not consistent across fish – half the cilia showing an increase while the rest show a decrease, making it hard to conclude. A finer analysis with higher temporal and spatial resolution in 3D will be necessary to decipher the role of the fiber on the beating of cilia and local CSF flow.

Overall, the results are clearly presented, and methods are thoroughly given, including some indication on the reduction of bias (by blinding movies before analysis). The authors also clearly state the limitations of their work, mostly derived from optical limitation (size of the RF in the larval fish, and speed of the recording in the laser-equipped microscope). This doesn't affect the fundamental statements.

Thank you again for your appreciation of our work.

Reviewer #3 (Public Review):

This manuscript by Bellegarda et al. examined the in vivo dynamic behavior of the Reissner fiber and its interactions with cilia and sensory neurons in the central canal of zebrafish larvae. The authors accomplished this by performing live imaging with a transgenic reporter zebrafish line in which the fiber is GFP-tagged and by finely tracking the movement of the fiber. Interestingly, they discovered that the fiber undergoes a dynamic vibratory-like movement along the dorsoventral axis. The authors then utilized a pulsed laser to precisely cut the fiber, which frequently resulted in a fast retraction behavior and a loss of calcium activity in sensory neurons in the central canal called CSFCNs. Mechanical modeling of the elastic properties of the fiber indicated that the fiber is a soft elastic rod with graded tension along the rostrocaudal axis. Finally, by performing live imaging of motile cilia and the fiber in the central canal, they found that the two interact in close proximity and that cilia motility is affected when the fiber was cut. The authors concluded that the Reissner fiber is a dynamic structure under tension that interacts with sensory neurons and cilia in the central canal.

Strengths:

1) The study utilizes state-of-the-art microscopy techniques and beautiful transgenic zebrafish tools to characterize the in vivo behavior of the Reissner fiber and found that it exhibits surprising dynamic movements along the dorsal-ventral axis. This observation has important implications for the physiology and function of the Reissner fiber.

2) By performing a series of clever laser cutting experiments, the authors reveal that the Reissner fiber is under tension in the central canal of zebrafish. This finding provides direct experimental evidence to support the hypothesis that the Reissner fiber functions in a biomechanical manner during spinal cord development and body axis straightening.

3) By developing a mechanical model of the Reissner fiber and its retraction behavior, the authors estimate the elastic properties of the fiber and found that it is more akin to an elastic polymer rather than a stiff rod. This is a useful finding that illuminates the biophysical properties of the fiber.

4) Through calcium and cilia imaging studies, the authors demonstrate that the Reissner fiber likely interacts with motile cilia and regulates the activity of ciliated sensory neurons (CSF-CNs). The authors propose a model in which fiber-cilia interactions may occur via weak interactions or frictional forces. This model is plausible and opens several new doors for additional investigation.

We thank Reviewer#3 for the support.

Weaknesses:

1) All the live imaging experiments appear to be performed with animals paralyzed via the injection of a chemical agent (bungarotoxin). Does paralysis and/or bungarotoxin negatively impact the behavior of the Reissner fiber? Some data from non-paralyzed animals would ameliorate this concern.

We performed very few experiments on non paralyzed fish as the position of the Reissner fiber were difficult / impossible to analyze in 3D. In a movie added to our revision as Movie 3, it is obvious that skeletal muscle contractions result in very large jumps of the fiber that cannot be corrected for using single plane imaging. Without being able to monitor and correct for muscle contractions, an accurate estimation of the fiber motion in this context would be artefactual.

2) Although the authors convincingly demonstrate that the Reissner fiber is under graded tension, it remains unclear what is the relevance and function of tension on this structure. The photoablation data presented do not delineate between the relevance of the fiber being intact or tension on the fiber as cutting the fiber impacts both. Is fiber tension required for body straightening? At the site of fiber photoablation, does a spinal curvature develop? If cultured, do the ablated animals exhibit a scoliotic phenotype?

We thank Reviewer#3 for asking these important questions. We did ask ourselves the same questions, but had to restrain the ambition of our study as for technical reasons, the ablation experiments performed on an inverted microscope required to mount the fish closed to the bottom coverslip and were extremely difficult to perform while safely removing the animal from the imaging cuvette and not affecting the alignment of its body axis.

3) One of the most potentially impactful conclusions of the paper is that the Reissner fiber interacts with cilia, but the evidence is insufficient to support this. Although some motile cilia are near the fiber (Figure 3A), many cilia are not near the fiber. The provided images and videos do not clearly demonstrate that cilia physically contact or influence the behavior of the Reissner fiber. Further, the data is lacking to conclude that the Reissner fiber directly impacts cilia motility as they did not observe an overall statistically significant difference before and after ablation (Supplemental Figure 1A). Higher magnification, higher resolution, higher acquisition rate and/or colocalization analyses of fiber-cilia interactions could alleviate this concern.

We agree with the reviewer but could not yet perform for technical reasons more spatially- and temporally- resolutive experiments. Further analysis of cilia and RF translational motion is displayed on the Figure 4 - Supplemental Figure 2 and presented in the Results sections.. We observed that for 7 out of 15 dorsal cilia and 4 out of 9 ventral cilia, the preferred position of the cilium was correlated with a position of the fiber – suggesting that they could interact. However, our current dataset in 2 D is too incomplete to draw strong conclusions on the nature of interactions between fiber and cilia. A future study relying on 3D analysis of the fiber and cilia should resolve how collective interactions of cilia may determine the position of the fiber.

4) Similarly, how does the Reissner fiber interact with CSF-CN sensory neurons? The authors suggest that the fiber interacts with CSF-CN sensory neurons by modulating their spontaneous calcium activity via weak interactions or frictional forces from motile ciliated ependymal radial glial cells. While the calcium imaging data of the CSF-CNs is convincing and sound, the exact nature of the fiber-neuron interaction is unclear. Do cilia or apical extensions on CSF-CN sensory neurons sense the fiber or forces through a mechanosensing or chemosensing mechanism?

This question is of great interest to us and will be the topic of a future investigation, as it is very difficult to image CSF-cN motile cilium (see Bohm et al., Nature Comm 2016) and even more with the Reissner fiber.

There is some additional confusion as the authors appear to focus their cilia experiments on ependymal radial glial cells in section 4, rather than CSF-CNs. The addition of an illustrative cartoon would add clarity.

We agree and we added a schematic in the last figure (Figure 4A).

Overall, the conclusions of the study are well supported by the data presented. However, the strength of the conclusions could be enhanced by additional controls, alternative experimental approaches and clarifications.

This manuscript is an important contribution to the fields of spinal cord development and body axis development, which are fundamental questions in neurobiology, developmental biology, and musculoskeletal biology. In recent years, the Reissner fiber and motile cilia function have been linked to cerebrospinal fluid flow signaling and body straightening, but the precise form and function of the fiber remain unclear. This study provides new insight into the dynamic and biophysical properties of the Reissner fiber in vivo in zebrafish and proposes a model in which the fiber interacts with cilia and sensory neurons. This study provides novel insight into the cellular mechanisms that underlie the pathogenesis of disorders such as idiopathic scoliosis.

We thank the Reviewer #3 and added further analysis of cilia and RF motion displayed on the figures below added as well as extended data figures in the main manuscript.

Author response

Reviewer #1 (Public Review):

The potential role of the CaMKII holoenzyme in synaptic information processing, storage, and spread has fascinated neuroscientists ever since it has been described that self-phosphorylation of CaMKII at T286 (pT286) can maintain the kinase in an activated state beyond the initial Ca2+ stimulus that induced kinase activation and pT286. The current study by Lučić et al utilizes biochemical and biophysical methods to re-examine two pT286 mechanisms and finds:

(1) that a previously proposed activation-induced subunit exchange within the holoenzyme can not provide pT286 maintenance or propagation; and

(2) that pT286 can occur not only within a holoenzyme but also between two holoenzymes, at least at sufficiently high concentrations.

For the observation regarding the subunit exchange, the authors go above and beyond to demonstrate that a previously proposed activation-induced subunit exchange does not actually occur in their hands and that the previous appearance of such a subunit exchange may instead be due to activation-induced interactions between the kinase domains of separate holoenzymes. This provides important clarification, as the imagination about the possible functions of this subunit exchange has been running wild in the literature.

By contrast, pT286 between holoenzymes at sufficiently high concentrations was largely predicted by the previously reported concentration-dependence of pT286 between monomeric truncated CaMKII (although these previous experiments did not rule out that such pT286 could have been excluded for intact full-length holoenzymes). Notably, the reaction rate reported here for pT286 between two holoenzymes is more than two orders of magnitude slower compared to the previously described rate of the pT286 reaction within a holoenzyme.

The only point on which we disagree (and we think it’s unarguable) is that the current consensus is that inter-holoenzyme phosphorylation simply doesn’t happen (whether or not monomers can phosphorylate each other). The reviewer is of course right that this view seems now less and less likely. We now performed new experiments to investigate this critical point further (see below).

The probable reason for the discrepancy in reported half-time of phosphorylation measured in earlier reports and in our paper is the fact that earlier reports (for example Bradshaw et al., 2002) measured autophosphorylation rate of wild-type CaMKII holoenzymes, at catalytically-competent enzyme concentrations of 0.1-5 µM. We are reporting the phosphorylation rate of 4 µM kinase-dead CaMKII, which is only a substrate, by 10 nM catalytically competent enzyme (CaMKII wild-type). There is up to 500 times less catalytically competent enzyme in our reactions, which is probably the reason why the reaction itself is several orders of magnitude slower.

In summary, this study contains two somewhat disparate parts: (1) one technical tour-de-force to provide evidence that argues against activation-induced subunit exchange, which was a tremendous effort that provides influential novel information, and (2) another set of experiments showing the somewhat predictable potential for pT286 between holoenzymes, but without indication for the functional relevance of this rather slow reaction. Unfortunately, in the current/initial title of the manuscript, the authors chose to emphasize the weaker part of their findings.

We agree with the reviewer that the title should be modified to emphasize both findings of our study. We also hope that our new experiments do bolster our findings with regard to pT286 between holoenzymes, as the reviewer puts it.

The seemingly slow inter-holoenzyme phosphorylation is only slow under conditions in which one of the proteins is kinase-dead. In situation in which all CaMKII holoenzymes are wild-type and therefore capable of performing phosphorylation (both intra- and inter-holoenzyme) the reaction rates for pT286 are expected to be orders of magnitudes faster, than those reported here for the phosphorylation of T286 on kinase-dead protein.

Reviewer #2 (Public Review):

This well-written manuscript provides a technical tour-de-force to provide a novel mechanism for sustaining CaMKII autophosphorylation through an interholoenzyme reaction mechanism the authors term inter-holoenzyme phosphorylation (IHP). The authors use molecular engineering to create designer molecules that permit detailed testing of the proposed interholoenzyme reaction mechanism. By catalytically inactivating one population of enzymes, they show using standard assays that the inactive enzyme can be phosphorylated by active holoenzymes. They go on to show that in cells, the inactive enzyme is phosphorylated only in the presence of co-expressed active CaMKII and that this does not appear to be due to active and inactive subunits mixing within the same holoenzyme. The authors suggest reasons for why previous experiments failed to expose IHP and in some experiments provide evidence that reproduces and then extends earlier studies. Some noted differences from earlier experiments are the reaction temperature, the time course of the reactions, and that significantly higher concentrations of the inactive (substrate) kinase in the present study amplify the IHP. These are plausible reasons for earlier studies not finding significant evidence for IHP and the presented data is well-controlled and of high quality.

The authors then take on the idea of subunit exchange employing multiple strategies. Using genetic expansion, they engineer an unnatural amino acid into the hub domain of the kinase (residue 384). In the presence of the photoactivatable crosslinker BZF and UV illumination, a ladder of subunits was generated indicating intraholoenzyme crosslinks were established. Using this cross-linked enzyme, presumably incapable of subunit exchange, the authors show significant phosphorylation of the kinase-dead mutant. This further supports that IHP is the cause of phosphorylation and not subunit exchange. Extending these experiments, they could not find evidence when CaMKIIF394BZF was mixed with the kinase-dead mutant and exposed to UV light, that there was evidence of the kinasedead subunits exchanged into CaMKIIF394 (active) enzymes.

Just a note, instead of residue 384, this should read 394.

With an entirely different approach, the authors use isotopic labeling of different pools of wt CaMKII (N14 or N15) followed by bifunctional cross-linking and mass spec to assess potential intra- and interholoenzyme contacts. Several interesting findings came of these studies detailed in Figure 4, mapped in detail in Figure 5, and extensively documented in supplementary tables. Critically, numerous crosslinks were found between different domains of the enzyme (catalytic, regulatory, hub) that are themselves a nice database of proximity measurements, but critical to the hypothesis, no heterotypic cross-links were found in the hub domains at any activated state or time point of incubation. This data supports two findings, that catalytic domains come into close proximity between holoenzymes when activated, supporting the potential for IHP, but that no subunit exchange occurs.

The authors then pursue the approach used originally to provide evidence of subunit mixing, single molecule-based fluorescence imaging. Using pools of CaMKII labeled with spectrally separable dyes, the authors reproduce the earlier findings (Stratton et al, 2016) showing that under activating conditions, but not basal conditions, colocalized spots were detected. Numerous controls were done that confirm the need for full activation (Ca2+/CaM + Mg2+/ATP) to visualize co-localized CaMKII holoenzymes. Extending these studies, the authors mix holoenzymes, fully activate them, and after sufficient time for subunit exchange (if it occurs), the reactions were quenched, and then samples were analyzed. The result was that no evidence of dual-colored holoenzymes was present; if subunits had mixed between holoenzymes, dual-colored spots should have been evident after quenching the reactions. This was not the case. Further, experiments repeated with pools of differentially labeled kinase dead enzymes produced no colocalization, as predicted, if activation of the catalytic domains is necessary to establish IHP.

Finally, the authors employ mass photometry to investigate the potential for interholoenzyme interactions. At basal conditions, only a mass peak consistent with CaMKII dodecamers was evident. Upon activation, a small fraction of dimeric complexes was evident (with Ca2+/CaM bound) but the majority of the peak was a dodecamer with 12 associated CaM molecules, and importantly, a significant fraction of a mass population was found consistent with a pair of holoenzymes with associated CaM. As an aside, the holoenzyme population appeared to be modestly destabilized as evidence of a minor fraction of dimers appeared as the authors diluted the enzyme, but the pools of holoenzyme and pairs of holoenzymes (with CaM) remained the dominant species when activated under all three enzyme concentrations assessed. Supporting the importance of activation for interactions between holoenzymes, the catalytically dead kinase even under activating conditions, shows no evidence of dimers of holoenzymes.

Each of the approaches is well-controlled, the data is of uniformly high quality, and the authors' interpretations are generally well-supported.

We are very grateful for these supportive comments.

Reviewer #3 (Public Review):

CaMKII is a multimeric kinase of great biologic interest due to its crucial roles in long-term memory, cardiac pacemaking, and fertilization. CaMKII subunits organize into holoenzymes comprised of 1214 subunits, adopting a donut-like, double-ringed structure. In this manuscript, Lucic et al challenge two models in the CaMKII field, which are somewhat related. The first is a longstanding topic in the field about whether the autophosphorylation of a crucial residue, Thr286, can be phosphorylated between intact holoenzymes (inter-holoenzyme phosphorylation). The second is a more recent biochemical finding, which tested the long-running theory that CaMKII exchanges subunits between holoenzymes to create mixed oligomers. These two models are connected by the idea that subunit exchange could facilitate phosphorylation between subunits of different holoenzymes by allowing subunits to integrate into a different holoenzyme and driving transphosphorylation within the CaMKII ring. Here, the authors attempt to show that one intact holoenzyme phosphorylates another intact holoenzyme at Thr286. The authors also provide evidence suggesting that subunit exchange is not occurring under their conditions, and therefore not driving this phosphorylation event. The authors propose a model where instead of exchanging subunits, two holoenzymes interact via their kinase domains to enable transphosphorylation at Thr286 without integrating into the holoenzyme structure. In order for the authors to successfully convince readers of all three facets of this new model, they need to provide evidence that 1) transphosphorylation at Thr286 happens when subunit exchange is blocked, 2) subunit exchange does not occur under their conditions, and 3) there are interactions between kinases of different holoenzymes that lead to productive autophosphorylation at Thr286.

Strengths:

The authors have designed and performed a battery of cleverly designed and orthogonal experiments to test these models. Using mutagenesis, they mixed a kinase-dead mutant with an active kinase to ask whether transphosphorylation occurs. They observe phosphorylation of the kinase-dead variant in this experiment, which indicates that the active kinase must have phosphorylated it. A few key questions arise here: 1) whether this phosphorylation occurred within a single CaMKII holoenzyme ring (which is the canonical mechanism for Thr286 phosphorylation), 2) whether the phosphorylation occurred between two separate holoenzyme rings, and 3) why was this not observed in previous literature? To address questions 1 and 2, the authors implemented an innovative strategy introducing a geneticallyencoded photocrosslinker in the oligomerization domain, which when crosslinked using UV light, should lock the holoenzyme in place. The rate of phosphorylation was the same when comparing uncrosslinked and crosslinked CaMKII variants, indicating that phosphorylation is occurring between holoenzymes, rather than through a subunit exchange mechanism that would require some type of disassembly and reassembly (presumably blocked by crosslinking). The 3rd question remains as to why this has not been previously observed, as it has not been for lack of effort. The authors mention low temperature and low concentration as culprits, however, Bradshaw et al, JBC v. 277, 2002 carry out a series of careful experiments that indicated that autophosphorylation at T286 is not concentration-dependent (meaning that the majority of phosphorylation occurs via intra-holoenzyme), and this is done over a concentration and temperature range. It is possible that due to the mutants used in the current manuscript, it allows for the different behavior of the kinase-dead domains, which will have an empty nucleotide-binding pocket. Further studies will need to elucidate these details, and importantly, understand what physiological conditions facilitate this mechanism.

We thank the reviewer for their assessment of our work.

The paper cited by the reviewer (Bradshaw et al, JBC v. 277, 2002) is indeed a carefully designed biochemical investigation of CaMKII activity. As the reviewer pointed out, one of the conclusions of the paper is that the autophosphorylation of CaMKII is not concentration dependent, implying that it has to occur exclusively intra-holoenzyme. However, there are some limitations which colour the interpretation of this classic paper. Bradshaw and colleagues used only CaMKII wild-type protein, so the autophosphorylation which is taking place in their reactions is possible both within holoenzymes and between holoenzymes, but this is impossible to distinguish. The authors of the cited paper then used “Autonomous activity assay” (not any measurement of pT286 on CaMKII itself) in which they first stopped the initial autophosphorylation reaction at T286 by adding a quench solution which contained a mixture of EDTA and EGTA, and then measured phosphorylation of the peptide-substrate of CaMKII (autocamtide-2), in the absence of Calmodulin binding (autonomous activity). They also diluted the autophosphorylation reaction to 10 nM CaMKII before adding it to the “Autonomous activity assay”.

As a side point, each reaction was quenched and diluted to the same final CaMKII concentration of 10 nM. They measured the activity of this dilution with phosphorylation of a peptide-substrate (autocamptide-2), in the absence of CaM binding. The authors contend that autonomous activity reported in this way reflects the amount of pT286, which is not impossible, but it is not a direct measure of pT286.

All this adds up to allowing the autophosphorylation of wild-type CaMKII at various concentrations ranging from 0.1 to 4.6 µM in the presence of 10 µM Ca/CaM and 500 µM Mg/ATP. This is a very fast reaction, concentrations of enzyme (CaMKII wild-type), activator (Ca/CaM) and ATP/Mg are all high at the beginning of the autophosphorylation reaction and would expect to allow for maximal autophosphorylation in very short times (seconds). Most importantly, this experiment does not exclude a inter-holoenzyme reaction slower than the intra-holoenzyme one. It certainly could not detect it.

In any case, to relate these concepts to our experiments and current understanding of CaMKII, we performed a new set of experiments modelled on the Bradshaw paper. Critically, we used CaMKII wild-type as the enzyme, and CaMKII kinase-dead, as the substrate. Intraholoenzyme phosphorylation cannot occur in this reaction, which was designed to detect a concentration-dependent phosphorylation reaction. We used a fixed concentration of the substrate kinase (4 µM), and 4 different concentrations of CaMKIIWT ranging from 0.5 -100 nM. In our assay, the level of phosphorylation on substrate CaMKII(CaMKIIKD) was dependent on concentration of enzyme CaMKII (CaMKIIWT) (Figure 1-figure supplement 3), adding more evidence to the hypothesis that CaMKII autophosphorylation can occur inter-holoenzyme.

The possibility that empty nucleotide binding pocket is influencing the phosphorylation status of T286 in the regulatory domain of kinase-dead CaMKII is highly unlikely. One could maybe envision that empty nucleotide binding pocket might expose the regulatory domain in kinase-dead CaMKII for phosphorylation, which would be prevented in CaMKIIWT, but in all available structures of CaMKII (Chao et al, 2011; Myers et al., 2017, Buonarati et al., 2021), the regulatory domain is docked to the kinase domain of CaMKII, although the nucleotide binding pocket is empty (either by mutation of residue K42 and/or simply by not adding the ATP/Mg to reduce chemical dispersity of the sample). The only time the regulatory domain was not docked on the kinase domain is when CaMKII was in complex with Calmodulin (Rellos et al., 2010). Finally, in our crosslinking mass spectrometry experiments, we used both heavy and light forms of CaMKII wild-type, and there we can clearly see interactions between kinase/regulatory domains of two different species of CaMKIIWT, which are dependent on activation.

The most convincing data that subunit exchange does not occur is from the crosslinking mass spectrometry experiment. The authors created mixtures of 'light' and 'heavy' CaMKII holoenzymes, either activated or not and then used a Lys-Lys crosslinker (DSS) to trap the enzyme in its final state. The results of this experiment indicate that subunit exchange is not occurring under their conditions. A caveat here is that there are not many lysines at hub-hub interfaces, which is the crux of this experiment. If there is no subunit exchange under their conditions, how does transphosphorylation occur between holoenzymes? The authors show very nice mass photometry data indicating that there are populations of 24-mers, which corresponds to a double-holoenzyme. Paired with the data from their crosslinking mass spectrometry which shows crosslinks between kinase domains of different holoenzymes, this indicates that perhaps kinases between holoenzymes do interact, and they do so in a competent manner to allow transphosphorylation to occur.

It is true that there are “only” 6 Lysines in the hub domain of CaMKII. However, it is clear from our crosslinking mass spectrometry data that we can detect hub:hub peptides coming from the same holoenzymes (homocrosslinks, either 14N: 14N or 15N: 15N species), but never between holoenzymes (14N with 15N). The fact that peptides can be detected in the homocrosslinks speaks to the validity of using Lysine crosslinkers in this experiment.

Weaknesses:

The authors should be commended for performing three orthogonal experiments to test whether CaMKII holoenzymes exchange subunits to form heterooligomers. However, there are technical issues that dampen the strength of the results shown here. For simplicity, let's consider that CaMKII holoenzymes are comprised of two stacked hexameric rings. It has been proposed that the stable unit of CaMKII assembly and perhaps also disassembly and subunit exchange is a vertical dimer unit (comprised of one subunit from each hexameric ring). In the UV crosslinking data shown in this paper, the authors have a significant number of monomers, some crosslinked dimers (of which there are two populations), and fewer higher-order oligomers. To effectively block subunit exchange, robust crosslinking into hexamers is necessary, which the authors have not done. Incomplete crosslinking results in smaller species that can still exchange (and/or dissociate), confounding the results of this experiment. In addition, Figure 3 shows a trapping experiment, where if the exchange was occurring, there would be an oligomeric band in Lane 8, which is visible and highlighted with a blue arrow by the authors. This result is explained by nonspecific UV effects, however by eye it is not clear if there is an equivalent band in lane 10. The overall issue here is inefficient crosslinking.

We agree with the reviewer that the robustness of the UV-induced crosslinking is not extremely high. However we do observe higher order oligomers on the gel (Figure 2 and Figure 3B, pT286 blot), which states that at least a portion of the holoenzymes is crosslinked. On the other hand, the UVinduced crosslinking is not slowing down the trans-phosphorylation reaction, which would be expected if the subunit exchange would be the prevailing mechanism for spread of kinase activity between holoenzymes.

In figure 3, lanes 8 and 10 show a small portion of dimers (less than 5% by densitometry), and at the absolute limit of detection. This dimer band is most likely due to unspecific UV-induced disulfide bridging (we already lessened it by adding 50 mM TCEP prior to UV treatment (Figure 3-figure supplement 1B and C). Previous reviewers of this manuscript criticized the small dimer band in lane 8, and we wanted to address this transparently in the submission to eLife.

Unfortunately, if we absolutely crank up the contrast to see this band in lane 10, we start to see other features in the noise as well. We have now edited the image in Figure 3B to highlight these minor bands more clearly, but this is also not ideal.

With regard to the trapping experiment, the overall problem is not inefficient crosslinking, because we see that P-T286 signal is quite nicely represented in higher order bands from F394BzF protein, but kinase dead protein (Avi-tagged signal in Figure 3) is almost entirely absent. Any crosslinking of Avitagged protein (possibly corresponding to subunit exchange) is a minor process at the limit of detection on WB.

Unfortunately we did not yet find any better crosslinking sites than the two we report (we have tried about 10). But the results we did obtain encouraged us to employ other techniques to probe subunit exchange (for example, the MS X-linking).

The authors also employ a single-molecule TIRF experiment to further interrogate subunit exchange. Upon inspection of the TIRF images, it is not clear that the authors are achieving single molecule resolution (there are evident overlapping and distorted particles). The analysis employed here is Pearson's correlation coefficient, which is not sufficient for single molecule analysis and would not account for particle overlap, particles that are too bright, and/or particles that are too dim. For example, an alternative explanation for the authors' results is that activation results in aggregation (high correlation), and subsequent EGTA treatment leads to dissociation at these low concentrations (low correlation). However, further experimentation and analysis are necessary.

In the manuscript we present raw images, not processed. As we wrote in the material and methods, we thresholded the images for further processing. All colocalization methods have drawbacks, but we found that our thresholding combined with the Pearson coefficient was highly reproducible. We did also look at Manders coefficients, but these are less straightforward to understand, whilst still giving in our hands the same answer. We agree, there are more experiments that can be done, with particular predictions based on our new mechanism. And we are doing them and will report them when they are ready.

At the risk of repeating ourselves, the reversible loss of overlap of the two labelled populations is the key result and cannot be explained by spurious dim or bright particles, or by a few overlapping profiles.

Taken together, the authors have provided important food for thought regarding inter-holoenzyme phosphorylation and subunit exchange. However, given the shortcomings discussed here, it remains unclear exactly what mechanisms are at play within and between CaMKII holoenzymes once activated.

We thank the reviewer for their critical assessment of our manuscript. We will continue to investigate the relevant points and refine the overall picture of CaMKII, to better clarify the mechanisms.

Author Response

Reviewer #1 (Public Review):

The Authors of this study have investigated the consequence of knocking out protein 4.1B on hippocampal interneurons. They observed that in 4.1B KO mice, the myelinization of axons of PV and SST interneurons was altered. In addition, the molecular organization of the nodal, heminodal, and juxtaparanodal parts of the interneuron axons was disrupted in 4.1B KO mice. Further, the authors found some changes in spiking features of SST, but not PV interneurons as well as synaptic inhibition recorded in CA1 pyramidal cells. Lastly, 4.1B KO mice showed some impairment in spatial memory.

Strengths

One of the strengths of this MS is the multilevel approach to the question of how myelinization of interneuron axons can contribute to hippocampal functions. Further, the cell biological results support the claim of the reorganization of channel distributions at axonal nodes.

Weaknesses

1) Although the authors acknowledge that SST is expressed in different GABAergic cell types in the hippocampus, they claim that OLM cells, which express SST are subject to changes in 4.1B KO mice. However, this claim is not supported by data. Both OLM cells and GABAergic projection cells expressing SST have many long-running axons in the stratum radiatum, where the investigations have been conducted (e.g. Gulyas et al., 2003; Jinno et al., 2007). Thus, the SST axons can originate from any of these cell types. In addition, both these GABAergic cells have a sag in their voltage responses upon negative current injections (e.g. Zemankovics et al., 2010), making it hard to separate these two SST inhibitory cell types based on the single-cell features. In summary, it would be more appropriate to name the sampled interneurons as SST interneurons. Alternatively, the authors may want to label intracellularly individual interneurons to visualize their dendrites and axons, which would allow them to verify that the de-myelinization occurs along the axons of OLM cells, but not SST GABAergic projection neurons.

We agree and named the sampled interneurons as SST interneurons throughout the text. We acknowledge that SST GABAergic projection cells have long-running axons in the stratum radiatum (Gulyas et al., 2003; Jinno et al., 2007) that may be also dysmyelinated. See Results lanes 200 and 350.

2) Although both the cellular part and the behavioral part are interesting, there is no link between them at present. The changes observed in spatial memory tests may not be caused by the changes in the axonal de-myelinization of hippocampal interneurons. Such a claim can be made only using rescue experiments, since changes in 4.1B KO mice leading to behavioral alterations may occur i) in other cell types and ii) in other regions, which have not been investigated.

Alteration of spatial memory has not been previously reported in the 4.1B KO mice. Our results leave open the possibility that dysmyelination of inhibitory interneurons in the hippocampus may induce impaired cognitive ability (see preprint). We agree that future studies investigating a putative rescue of spatial memory by means of virus-mediated expression of 4.1B in hippocampal Lhx6 interneurons would be very informative.

Reviewer #2 (Public Review):

In this study, Pinatel et al. address the role of interneuron myelination in the hippocampus using a 4.1B protein mouse knockout model. They show that deficiency in 4.1B significantly reduces myelin in CA1 stratum radiatum, specifically myelin along axons of parvalbumin and somatostatin hippocampal interneurons. In addition, there are striking defects in the distribution of ion channels along myelinated axons, with misplacement of Na channel clusters along the nodes of Ranvier and the heminodes, and a pronounced decrease in potassium channels (Kv1) at juxtaparanodes. The axon initial segments of SST are also shorter. Because the majority of myelinated axons in the stratum radiatum of the hippocampus belong to PV and SST interneurons such profound changes in myelination are expected to affect interneuronal function. Interestingly, the authors show that PV basket cells' properties appear largely unaffected, while there are substantial changes in stratum oriens O-LM cells. Inhibitory inputs to pyramidal neurons are also changed. Behaviorally, the 4.1B KO mice exhibit deficits in spatial working memory, supporting the role of interneuronal myelination in hippocampal function. This study provides important insights into the role of myelination for the function of inhibitory interneurons, as well as in the mechanisms of axonal node development and ion channel clustering, and thus will be of interest to a broad audience of circuit and cellular neuroscientists. However, the claims of the specificity of the reported changes in myelination need to be better supported by evidence.

Strengths:

The authors combine a wide array of genetic, immunolabeling, optical, electrophysiological, and behavioral tools to address a still unresolved complex problem of the role of myelination of locally projecting inhibitory interneurons in the hippocampus. They convincingly show that changing myelination and ion channel distribution along nodes and heminodes significantly impairs the function of at least some interneuron types in the hippocampus and that this is accompanied by behavioral deficits in spatial memory.

Regarding the organization of myelinated axons, the lack of 4.1B causes striking changes at the nodes of Ranvier that are convincingly and beautifully presented in the Figures. While the reduction in Kv1 in 4.1B KO mice has been previously reported, the mislocalization of sodium channels at the nodes and heminodes had only been observed in developing but not adult spinal cords. This difference in the dependence of the sodium channel distribution on 4.1B in adult hippocampus vs spinal cord may hold important clues for the varying role of myelin along axons of different neuronal types.

The manuscript is very well written, the discussion is comprehensive, and provides detailed background and analysis of the current findings and their implications.

Weaknesses:

Because of the wide diversity of interneuron types in the hippocampus, and also the presence of myelinated axons from other neuron types as well, including pyramidal neurons, it is very difficult to disentangle the effects of the observed changes in the 4.1 B KO mouse model. While the authors have been careful to explore different possibilities, some of the claims of the specificity of the reported changes in myelination are not completely founded. For example, there is no compelling evidence that the myelination of axons other than the local interneurons is unchanged. The evidence strongly supports the claims of changes in interneuronal myelination, but it leaves open the question of whether 4.1B lack affects the myelination of hippocampal pyramidal neurons or of long-range projections.

This is an important question also raised by Reviewer 1. We have now quantified the density of paranodes in the alveus as shown in Figure 1I. Paranode density was not affected in the alveus nor in the stratum lacunosum-moleculare suggesting that myelinated axons connecting extra-hippocampal areas may be preserved. In particular, this is an indication that the axons of pyramidal neurons that run into the alveus should be properly myelinated.

To be able to better interpret the changes in the 4.1B KO mice, knowledge of the distribution of 4.1B in the hippocampus of control mice will be very helpful. The authors state that 4.1B is observed in PV neurons but not in pyramidal neurons, however, the evidence is not convincing. Thus, the lack of immunolabeling at the pyramidal neuron cell bodies does not indicate that 4.1B is missing at the axonal level. The analysis also leaves out the question of whether 4.1 B is seen in the axons of somatostatin neurons.

We agree and do not exclude that 4.1B may be expressed along the axons of pyramidal neurons. We performed double-staining for SST and 4.1B to show that 4.1B is localized along the internode and enriched at the paranodes of SST axons as observed for PV axons (Figure 4F). The enrichment of 4.1B in GABAergic neurons was previously observed in premyelinated hippocampal cell culture (Bonetto et al. 2019).

Reviewer #3 (Public Review):

Pinatel and colleagues addressed a currently understudied topic in neurobiology, namely, the architecture and function of myelination in subsets of Parvalbumin (PV)- and Somatostatin (SST)-positive GABAergic hippocampal interneurons and its dependence on juxtaparanodal organizer proteins. In order to elucidate the structural and functional implications of interneuron myelination, the authors visualized inhibitory neurons by utilizing a Lhx2-Lhx6 tdTomato reporter line in combination with mutants for crucial membrane and cytoskeletal linker proteins such as Contactin2/TAG-1, Caspr2, and Protein 4.1B. They then applied a comprehensive set of histological, electrophysiological, and behavioral experiments to dissect the role these proteins play in proper myelination and function of PV- and SST-interneurons.

The bulk of the study's data is based on immunofluorescence, which is presented in a number of figures comprised of high-quality images. As much as this is a strength of the study, the underlying image analysis as described in the methods falls short. All structural data rely on the measurements of physical parameters such as length of internodes, the distance between (juxta)paranode and node, the distance between node and myelin sheath, length of the axon initial segment (AIS), etc. In light of this, and considering the small physical dimensions of the nodal region in general, the methods remain unclear about the depth of 3D reconstruction/deconvolution applied to the samples. Measurements presented in the results show significant differences in sub-micrometer dimension, which at least according to the stated methods, are unlikely to be precise given that the confocal imaging parameters do not seem to reach Nyquist conditions. For a study in which a third of all data is aimed at elucidating (sub)micrometer changes, this is crucial and the study would benefit from a more rigorous method description by the authors.

Another methodological weakness is the somewhat small n, and its incoherence across the experiments and therefore, the statistics performed in some of the experiments. Statistics are based on either n for animals, or n for individual data points from several animals. Why is not all data represented as mean/animal? Also, the sampling in general with n = 3 animals is borderline acceptable; in some cases, it seems that only 2 animals were used, and in others, no number is given at all (please refer to author comments for details). This needs to be addressed, either by explaining why so few animals were used, or by adding more data from individual animals.<br /> Assigning structures (AIS, nodes) as n results in overstating effects, since especially for AIS, there is significant heterogeneity in the length across neurons from the same type, and this is masked when 100 AIS are considered as individual n instead 100 AIS per animal, and the animal is (correctly) the n.

Since the study seems to switch back and forth between these assignments, it would be helpful to level these data across all experiments unless there are specific reasons not to do so, which then need to be explained. As outlined in the methods, all values are given as means {plus minus} SEM; this needs to be corrected for those cases where the standard deviation is the appropriate choice (e.g. all graphs showing n = individual structure, and not the mean of an animal).

As far as the analysis of geometrical AIS changes is concerned, the method section should be extended to address how, if at all, AIS length and position were analyzed in 3D, also considering the somewhat "spotty" immunosignal outlined in Fig. 8D.

We agree with all these comments. We improved Fig.1 I and J by adding more data (n=4 mice). We would like to point out that the phenotype of the 4.1B KO mice is highly penetrant. The selective loss of myelin in the hippocampus was observed in the two different genetic background (4.1B-/- and 4.1B-/-;Lhx6;tdTomato mice) and at all the ages examined (P25P180).

For the quantitative morphological analysis: We considered “n=number of animals” in Figure 1 to describe the massive and selective alteration of myelin in the hippocampus of 4.1B KO mice. In the following Figures, we considered n=ROIs (Figure 2, Figure 3, Figure 6) for the density of SST and PV interneurons or oligodendroglial cells and n=individual structures (Figure 4, Figure 5, Figure 8) for a more precise sampling of the structure heterogeneity (internode, node, AIS). Means ± SEM are indicated in the text corresponding to plot boxes and distribution plots in the Figures.

Concerning AIS measurements, we considered “n” as individual AIS in a coherent manner with the electrophysiological recordings in which “n” is the individual cells. We hope that we have now better illustrated the AIS of SST cells in the stratum oriens in the new Figure 8 with single channel images. In contrast to the AIS of pyramidal neurons that display sinuous feature, the AIS of SST neurons (and especially O-LM cells which axons run straight across the stratum radiatum) show a rather straight organization.

We improved our measurements of the AIS structural parameters (onset, length) of SST neurons of the stratum oriens using confocal imaging with a 20x objective, 0.54 µm steps, Nyquist conditions. Indeed, these new measurements confirmed that the AIS of SST neurons was significantly shorter in the 4.1B KO mice.

The observed AIS length change is then discussed in the context of a study conducted in a pharmacological model of myelin loss, however, that particular study (Hamada & Kole, 2015) found not only a length change but a position change after cuprizone-induced AIS plasticity. The authors should therefore discuss this finding in a bit more detail than simply stating "Adaptation of the AIS has been reported in the cuprizone chemical model of demyelination" (p. 14, ll. 512).

We added these sentences in the Discussion:

Lane 527: Supporting this notion, previous studies have reported an adaptive response of the AIS of cortical pyramidal neurons in the cuprizone chemical model of demyelination. Specifically, it was observed that the length of the AIS is reduced together with a more proximal site of the onset. These changes reduce the AIS excitability suggesting a compensatory mechanism to ectopic action potentials generated in demyelinated axons (Hamada and Kole, 2015).

Lane 556: Interestingly, in cortical pyramidal neurons, demyelination induced by cuprizone causes the restructuring of AIS and reduces excitability at this site. “Acute demyelination leads to a more proximal onset of AIS without a change in the length of ßIV spectrin expression. However, the AIS of these acutely demyelinated axons display a reduced length of Nav1.6 channel expression and extended Kv7.3 channel expression at the distal site (Hamada and Kole, 2015).”

Similarly to the points made about structural data above, the data from electrophysiological recordings should be presented in such a way that e.g. the number of cells and/or animals is readily accessible from the graph or legend. In its current form, this information - while available - needs to be pieced together from in-text information supplemented by figure legends. Sometimes, the authors do not include the number of animals behind individual cell data (for details please see author comments). Please carefully review all figures and edit accordingly.

The behavioral data presented in the study is interesting, but the conclusions drawn are not supported by the data presented, as many unknown factors remain in place that could contribute to the observed phenotype.

Author Response

Reviewer #3 (Public Review):

Wernet et al. show that there are intrinsic protein oscillations at the hyphal tips of A. flagrans, a nematode trapping fungus, that become coordinated when two hyphae become close. They create a mathematical model of this synchronization phenomenon, and then go on to show that calcium is critical to the functioning of these oscillations and hyphal fusion. The concept of interhyphal communication through signal synchronization is fascinating, and the visual matching of the output of the model to the data is compelling. However, given that the authors already showed synchronized oscillations in the SofT protein in A. flagrans in Hammadeh et al. 2022 (Figure 4), this diminishes the novelty of the findings in this study. Additionally, as it also has been established that calcium drives other oscillatory communications, the characterization of calcium dependence is not especially novel or bringing new insights into the problem especially since it is unclear if the chelation is having effects due to loss of intracellular supplies and/or because it is the key signal in the dialogue. Right now the mathematical model feels a bit vague with discussion of hypothetical molecules, so the paper would be greatly strengthened if any key regulatory molecules that promote desychronization could be identified or there were some manipulations of the core known proteins that examined consequences of altering the oscillations. As it is, the reader is left intrigued but there are few concrete conceptual advancements.

We thank Reviewer #3 for the thoughtful comments on our manuscript! We would like to emphasize that the main finding of this paper is the discovery of a monologue of individual hyphae before fusion and the transition into a dialogue. This had not been shown in any fungus, and it explains nicely the onset of the communication. During the revision process, we performed co-localization of SofT-GFP and MakB-mCherry in the same hyphae and observed that both proteins were oscillating in the same phase without other hyphae in vicinity, which is the opposite of the so far observed anti-phasic oscillations observed during the cell dialogue. Additionally, we observed that decoupling of the oscillations into the anti-phasic cell dialogue occurred during the transitory phase. We included our results in (L167) and updated the figures to create a new figure 3 and supplementary figure Fig. SS.

We agree that it would be great to isolate the signaling molecule. However, this has been tried by several groups, so far without success. Therefore, we think that this one main finding is exactly the scope of short reports for eLife.

Author Response

Reviewer #1 (Public Review):

The idea that because the hippocampal code generates responses that match the most needed variable for each task (time or distance) makes it a predictive code is not fully proved with the analyses provided in the manuscript. For example, in the elapsed time task, there are also place cells and in the fixed-distance travel there are also cells that encode other features. This, rather than a predictive code, can be a regular sample of the environment with an overrepresentation of the more salient variable that animals need to get in order to collect rewards.

We concur with the Reviewer’s reservation. Claims about predictive coding were removed and the following possible account explanation for over-representation was suggested instead:

"These results underscore the flexible coding capabilities of the hippocampus, which are shaped by over-representation of salient variables associated with reward conditions. " (page 1 line 23, page 4 line 27)

In addition, the analysis provided in the manuscript are rather simple, and better controls could be provided. Improving the analytical quantification of the results is necessary to support the main claim.

We improved the quantification, as suggested below by specific comments of the reviewer.

What is the relationship of each type of cell with the speed of the animal?

The cells were assigned to the different types according to their responses while running across all speeds. However, we checked how the speed of the animal affects the peak firing rate of the cells, for each type of cell. Results of this analysis are presented in Author response image 1. Bars represent maximum firing rate of all cells of a given type across runs with the specified speed range (𝒎𝒆𝒂𝒏 ± 𝑺𝑬𝑴).

Author response image 1.

We did not find a significant interaction effect of the speed and the cell-type over the max firing rate (2-way Anova p>0.98).

What is the relationship with the n of trial that the animal has run (first 10 trials, last 10 trials..)?

Some of the animals were subjected to only one type of session. Moreover, they were sometimes trained without recording. Therefore, to answer this question we restricted our analysis to recording sessions where the animal switched from fixed-time to fixed-distance or vice versa. We checked the 20 first runs vs. the last 20 runs (data from 10 runs is not powerful enough for analysis) in See the results in Author response table 1.

Author response table 1.

To assess the dynamics of the coding flexibility, we defined the Time-Distance index (TDI), quantifying the balance between the proportion of distance cells and of time cells at a given time. as (NDistanceCells/NTimeCells)/(NDistanceCells+NTimeCells). The is in the range of [0 ,1] if the majority of cells are classified as distance cells, and in the range of [-1, 0] if the majority of cells are classified as time cells. Chi-square testing for differences in proportions did not reveal significant differences (after correction for multiple comparisons).

The shaded boxes in Author response table 1 indicate the sessions which followed a transition between session types

What is the average firing rate of each neuron?

This information was now added to the titles of the panels in Figure 2 and Figure 2-figure supplement 1.

Is there any relationship between intrinsic firing rate and the type of coding that the cell develops in each task?

In Author response image 2 is a comparison of the firing rates of the Time cells vs the Distance cells.

The distributions are similar (p = 0.975 ,and p = 0.675 for peak firing rate and mean firing rate, respectively, Kolmogorov-Smirnov (KS) test).

Author response image 2.

This figure was added to the supplementary figures (figure 3 - figure supplement 3)

What is the relation of the units of each type with LFP features (theta phase, ripple recruitment)?

We had LFP recordings for 15 out of 18 sessions. A large proportion of the cells showed phase precession (see Author response table 2). An example is shown in Author response image 3. We could not find a significant relation between phase precession and the cell type or the trial type.

The table on the left shows the total cells analyzed, and on the right we show the percentage of cells that had a significant linear fit of the theta phase within 80% of the field width, when analyzed per time (topright) or per distance (bottom-right). FDist/Ftime are Fixed-distance and fixed-time trials and Dist/Time are the cell type.

We did not identify ripple events during treadmill runs.

Author response table 2

Author response image 3

Reviewer #3 (Public Review):

Weaknesses:

The original study of Kraus et al. consisted of 3 rats for which all sessions, including both training and recording, were of one type. Another 3 rats had a hybrid mixture of distance and time sessions. This is mentioned very briefly in the main text.

It would appear that the theory of reward might lead to different predictions that could be verified by comparing these animals session to session at a finer grain. For example, are there examples of cells switching or transforming their “predictive” representations when a large number of trials in on session type is followed by a large number of trials of the opposite type?

For another example, the transition from training to recording could give similar opportunities. It seems at least possible that ignoring these issues could cause a loss of power.

We could not compare a particular cell for switching between encodings since the different types of trial were performed on different days. As an alternative, we compared the populations of cells within the first 20 vs. last 20 trials in recording sessions where the animal switched from fixed-time to fixed-distance or vice versa (see table below). The “Time-Distance balance index” (TDI) is defined as (#DistanceCells#TimeCells)/(#DistanceCells+#TimeCells) and is ranges between 0 and 1 if the majority of cells are classified as distance cells while between -1 to 0 if the majority of cells are classified as time cells.

In all three animals there seems to be a change between the first 20 runs and last 20 runs of the same session, following a switch between trial types. However, this change is significant and with the expected trend only in one of the animals (BK49, p=0.02, chi-square test).

The grayed boxes in Author response table 1 indicate the sessions which followed a transition between session types

Some circularities in the construction and interpretation of the time-cell and distance-cell classifiers are not clearly addressed. The classifiers currently appear to be fit to predict the type of session a cell’s response patterns are observed within. But it is tautological to use the session type to define the cell type. I sense this is ultimately reasonable because of how the classifier is built, but this concern is not addressed or explained.

We regret that the term ‘classifiers’ was not sufficiently precise. We used this term to describe the metrics designed to express the relation between the firing-time and the velocity, in order to classify cells, rather than classifiers that are fit to predict the type of session. We believe this to be the source of the apparent circularity. To circumvent this confusion, we now replaced all places where the term “classifier” was mentioned, with the term “metric”

Author Response

Reviewer #1 (Public Review):

The paper reports important work in which the Fub-1 boundary of the Drosophila bithorax complex is characterized in detail. Fub-1 separates the bxd/pbx regulatory domain, which is active in PS6/A1, from the abx/bx regulatory domain, which is active in PS5/T3. The work presented provides compelling evidence that Fub-1 consists of two key elements: an insulating boundary region called HS1, which is regulated by an adjacent region called HS2. HS2 contains a promoter that is activated in PS6/A1 by enhancers in the bxd/pbx region. Read-through of HS1 by transcripts from the HS2 promoter blocks the insulating activity of HS1, allowing the bxd/pbx regulatory regions to activate Ubx transcription in PS6/A1. It has long been appreciated that boundary elements within the BX-C are regulated in a segment-specific fashion. The work presented in the Ibragimov manuscript provides a very nice example of how this segment-specific regulation can take place. For the most part, the work is very thorough and the conclusions are well-supported. However, there are a few important issues that should be addressed.

First, throughout the manuscript, it is stated that the read-through transcription of HS1 eliminates its blocking activity. Missing, however, is a test of whether the direction of transcription of HS1 is important. That is, no construct is tested in which HS1 is inverted so that RNAs from the HS2 promoter are transcribed from the opposite strand of HS1. If read-through transcription of HS1 is all that is required to abrogate its blocking activity, such a construct should behave identically to constructs in which HS1 is not inverted. However, if the structure of the F1HS2 RNA is critical to preventing the blocking activity of HS1, inversion of HS1 relative to HS2 may render it immune to inactivation by transcripts initiated at HS2.

This is a good point. The sequence/structure of the transcript could be important—e.g., it recruits a factor that disrupts boundary activity.

While we didn’t do such an experiment, this scenario seems unlikely. As noted above we have replaced Fub-1 with two other BX-C boundaries Mcp and Fab-8. Their sequences are different from other and from Fub-1. Both block bxd/pbx from regulating Ubx and give an A1 LOF phenotype. To test the effects of transcription on boundary activity, we placed a P-element promoter upstream of both boundaries (so transcripts from the P-element promoter would read through boundaries towards bxd/pbx. We found that inclusion of the P-element promoter rescued the LOF phenotypes.

Second, the terminology used to designate the constructs tested is very hard to follow and needs simplification. Since the orientation of HS1 in isolation is unimportant, perhaps just HS1 HS2, HS1 Inv(HS2), HS2 HS1, and Inv(HS2) HS1 could be used.

We wanted to keep the terminology consistent in so far as possible with publications on other BX-C boundaries.

Third, in many places in the manuscript genotypes are shown in which the HS1 insulator is placed into F7attP50. For these genotypes, H1 is said to block the interaction between iab-6 and iab-7, but not to support bypass activity. Readers need some help here, as they will not understand why A5 and A6 tergites are black in these genotypes, as this implies that iab-5 is able to act over the HS1 element to activate Abd-B. One explanation may be that iab-5 can promote pigmentation by acting on abd-A.

The likely explanation is that the Fab-6 boundary is able to "bypass" the intervening HS1 insulator and target iab-5 enhancers to Abd-B promoter. There are other Fab-7 replacements in which the iab-5 enhancers are also blocked. The likely explanation is that the Fab-6 boundary is able to "bypass" the intervening HS1 insulator and target iab-5 enhancers to Abd-B promoter. We added an explanation and a review article describing to the text.

Fourth, a more complete description of the HS1248 HS2505R genotype is needed. In this genotype, the H1 insulator is constitutively active, as H2 is inverted. Do animals of this genotype show a bxd phenotype in the larval cuticle? Do adults show a transformation of the halteres like that shown by classical bxd mutations? Answers to these questions would shed light on when H1 is active as an insulator, and whether it is active throughout PS6/A1.

Phenotype of larval cuticle indicates a LOF transformation towards T3. We added a supplementary Figure 6-figure supplement 5 showing this. The haltere shows evidence of an LOF phenotype (Figure 6-figure supplement 6).

Author Response

Reviewer 2 (Public Review):

Weaknesses: The paper is largely written within the 'accidental virulence' framework, ref [2]. This is a valuable framework, but it is worth noting that the ideas overlap with the earlier concept of 'coincidental selection for virulence', first developed by Bruce Levin and C Svanborg-Eden (1990) Parasitology 100, S103-S115 (more recent experimental work in this thread is reviewed by ref [1]).

We wholeheartedly agree. As noted above, the manuscript has been updated to reflect this omission.

Missing this thread leads to a number of statements that are just not supported by the literature. Some examples -

Summary: 'The existence of microbes that are not normally pathogenic, yet are well-suited to host exploitation, is an evolutionary paradox. ' - No, this is potentially explained by coincidental selection for virulence, which has been documented in several studies

Summary: "Our results support the idea that selection in the environment for a trait unrelated to virulence can inadvertently generate opportunistic, "accidental" pathogens." - The trait is not unrelated to virulence, as they are correlated, likely shaped by adhesion behaviors. This correlation is not surprising as 'adhesins' are a classic category of virulence factor, presenting a potential common cause between sticking to a bead and killing an insect more rapidly.

Line 26 "hypothesis has not been directly tested experimentally". - this is probably the main concern, as the paper currently does not address related prior experimental work that has been developed within the co-incidental selection tradition. Please see refs that are cited by paper [1] for a start, and then follow forward for more recent work. One recent study comes to mind as it looks at correlated effects of in vitro bead attachment -- https://www.nature.com/articles/s41396020-0652-0 (virulence was not directly assayed, but of interest also noted a shift in antibiotic resistance following bead-attachment selection without drugs or a host).

We agree with these suggested edits and have updated the manuscript in the appropriate places.

Turning to experimental choices, the use of a 'no bead' experimental control is an important point of comparison, to ensure that the evolutionary effects of interest are particular to the presence of the bead. But if there were no beads, how are you measuring 'cells on bead' (y-axis in Figure 1)? I assume this is an oversight and you're measuring cells per x volume.

This is a good question. To be clear, Figure 1 does not represent measurements taken throughout the course of the experiment; rather, it represents a large phenotyping effort after the experiment ended. Ancestors and evolved populations from multiple timepoints (including the control populations) were started from cryopreserved stocks, then challenged to grow in the presence of a bead. As can be seen in the figure, both ancestors had some plastic adherence ability, which was maintained in the control populations.

Moving into the key virulence assays, I was expecting a similar and simple design: compare the virulence of ancestor versus 'evolved with bead' versus 'evolved without bead'. This would allow answers to the key question of whether bead attachment leads to the evolution of increased virulence, with appropriate controls for adaptation to the general passaging environment. Why not use this simple and standard design?

Instead, we get a more complex design, contrasting isolates that are filtered on the adhesionrelated traits (biofilm, etc), but sampled across timepoints. This does establish that less adhesive and less biofilmy isolates are less virulent so this remains useful information, but the motivation for only using this design is not well spelled out. In principle, you could do this purely on standing variation and not require an experimental evolution step.

We understand and respect this criticism. Please see the response above (in the section responding to the editor’s summary).

As for the question of using standing variation, it is true that a large part of the evolution observed in this experiment is from the sorting of standing genetic variation. We did not anticipate the evolved phenotypes we observed. Perhaps if we had known they were possible, we could have searched for them in the standing genetic variation in F1 offspring/segregants. Related to this idea, we have investigated 350+ segregants from each of these clinical backgrounds (that were generated in order to map the genetic basis of plastic adherence for a manuscript in preparation). The evolved populations occupy different phenotypic space than the mapping population, although there is obviously overlap. Thus, in order to get to the hypermulticellular phenotype observed in the experiment, either multiple rounds of recombination were required to get many high alleles into one background, or new mutations were required.

Concerning the role of plastic, I would encourage caution in the interpretation, given the experimental design. Consider this line from the discussion "In this experiment, favoring the ability to adhere to plastic, a surface that is alarmingly common in industrial, medical, and domestic settings [69], led to a suite of aggregative phenotypes and increased virulence." - by bringing up applied consequences of plastic exposure, this really raises the stakes. At present, the data does not separate the role of bead attachment from the specific role of plastic as a material. What would happen if you repeated with glass beads? I suspect a similar pattern, again driven by adhesin changes. The data at present does not resolve this issue.

We respect this note of caution, which is in opposition to Reviewer #1, who thinks we should add more information about the increase in microplastics. We agree that the results are likely due to selection for adherence, rather than specifically adherence to plastic. That being said, the experiment does show that plastic is a surface on which these yeast can be selected to adhere. And it is also true that this surface is increasingly common. As a compromise, we took out the word alarming and added references to the effect of microplastics on other microbes.

Author Response

Reviewer #1 (Public Review):

Sučević and Schapiro investigated a neurobiologically inspired model of human hippocampal structure and computation in category learning. In three separate simulations, the model (CHORSE) is presented with learning tasks defined by various category structures from prior work and evaluated for its ability to learn the category structure, generalize categorization to novel stimuli, and accurately recognize previously encountered stimuli. Although originally conceived of as a computational model of associative memory, C-HORSE is demonstrated to quite naturally account for human-like learning of the three category tasks. Notably, the authors characterize the mechanisms underlying the model's learning by way of additional simulations in which "lesions" to the model's monosynaptic pathway (MSP; direct connections between ERC and CA1) are contrasted with lesions to its trisynaptic pathway (TSP; pathway connecting ERCDG-CA3-CA1). These in silico lesions offer key insight into the computational principles underlying theorized hippocampal functions in category learning: whereas MSP provides incremental learning of shared features diagnostic to category membership that are important for category generalization, TSP learns item-specific information that drives recognition behaviour. The authors propose that C-HORSE's successful account of a broad set of category learning datasets provides clear support for the role of complementary hippocampal functions mediated by MSP and TSP in category learning. This work adds compelling computational evidence to a growing literature linking hippocampus to a broader role in cognition that extends beyond declarative memory.

The model simulations are clear and properly conducted. The three datasets examined offer a relatively broad set of findings from the category learning literature; that the models provide reasonable accounts of human performance in all three speaks to the model's generalizability. Overall, I find this work exciting and an important step in linking longstanding well-established formal learning theories of psychology with neurobiological mechanism. Several weaknesses dampen this excitement, each of which are detailed below:

1) C-HORSE is presented as a new entry into a rich field of formal computational models of category learning. As noted above, the datasets examined span a broad range of learning contexts and structures and the model's ability to account for learning behaviour is compelling. However, no other models are leveraged to perform a direct evaluation. In other words, CHORSE's predictions are compelling, but is it better than other competing models in the literature? To be clear, C-HORSE offers a novel alternative with its fundamental mechanisms originating from anatomical structure and connectivity. As such, a proof-of-concept showing that such a neurobiologically inspired framework can account for category learning behaviour is a worthwhile contribution in its own right and a clear strength of this paper. However, how to consider this model relative to existing theoretical frameworks is not well described in the manuscript.

We very much appreciate this point — see response to Editor summary point #3 above.

2) Relatedly, C-HORSE is evaluated in terms of qualitative fit to behaviour measures from prior studies and in all three simulations restricted to measure of end of learning performance. Again, an appeal to the proof-of-concept nature of the current work may provide an appropriate context for this paper. But, a hallmark of well-established category learning models (e.g., SUSTAIN, DIVA, EBRW, SEA, etc.) is their ability to account for both end of learning generalization (and in some cases, recognition) and behaviour throughout the learning process. C-HORSE does provide predictions of how learning unfolds over time, but how well this compares to human measures is not considered in the current manuscript. Such comparisons would strengthen the support for C-HORSE as a viable model of category learning and help position it in the busy field of related formal models.

We completely agree about the value of this, and we have added empirical timecourse data for comparison with all simulations, as described in response to Editor summary point #7, above.

3) A consistent finding across all three simulations is that the TSP provides item-specific encoding. Evidence for this can be inferred by contrasting categorization and recognition performance across the TSP- and MSP-only model variants. In the discussion, the authors draw a parallel between exemplar theories of category learning and the TSP, which is a compelling theoretical position. However, as noted by the authors, unlike exemplar theories, the TSP-only model was notably impaired at categorization. The author's suggestions for extensions to CHORSE that would enable better TSP-based categorization are interesting. But, I think it would be helpful to understand something about the nature of the representations being formed in the TSP-only model. For example, are they truly item-specific, are the shared category features simply lost to heightened encoding of item-unique features, are category members organized similarly to the intact model just with more variability, and so on. Characterizing the nature of these representations to understand the limitations of the TSP-only model seems important to understanding the representational dynamics of C-HORSE, but are not included in the current manuscript.

The RSA results, now included for Simulations 2 and 3 in addition to Simulation 1, provide the information needed to characterize the nature of the TSP representations. Generally speaking, they are truly item specific, meaning that each item is represented by its own distinct set of units. This is a demonstration of the classic pattern separation function of this pathway, taking similar inputs and projecting them to orthogonal populations of neurons. Simulation 1 is the clearest example of this, where there is virtually no similarity and very low variability in the item similarity structure in DG and CA3. The new Simulation 3 RSA shows us where the limit is to this pattern separation ability of the TSP, with highly typical items being represented by somewhat overlapping populations of neurons in DG and CA3. To the extent that the TSP can succeed in generalization, it seems to involve this pattern separation failure.

We have made these points more explicit in new discussion of the RSA results:

• Simulation 1: “In the initial response, there was no sensitivity at all to category structure in DG and CA3 — items were represented with distinct sets of units. This is a demonstration of the classic pattern separation function of the TSP, applied to this domain of category learning, where it is able to take overlapping inputs and project them to separate populations of units in DG and CA3.” • Simulation 3: “As in the prior simulations, DG and CA3 represented the items more distinctly than CA1, and settled activity after big-loop recurrence increased similarity, especially in CA1. This simulation was unique, however, in that DG and CA3 showed clear similarity structure for the prototype and highly prototypical items. There is a limit to the pattern separation abilities of the TSP, and these highly similar items exceeded that limit. This explains why, at high typicality levels, the TSP could be quite successful on its own in generalization (Figure 5e), and why it struggled with atypical feature recognition for these items (Figure 5f).”

4) In general, a detailed description that links model mechanisms and analyses to the learning constructs of interest for the different simulations is lacking. For example, RSA results for simulation 1 are contrasted for initial and settled representations, but what is meaningful about these two timepoints is not directly stated (moreover, what initial and settled response mean in terms of the current model is not explained). The authors do briefly suggest that differences between initial and settled representations may reflect encoding dynamics before and after bigloop recurrence, but this is not established as a key metric for evaluating the nature of the model representations. In general, more motivation is needed to understand what the chosen analyses reveal about the nature of the model's learning process and representations.

We have added more description of the motivation for our analyses. See response to Editor summary point #6 above.

5) I appreciate the comparison in the discussion to extant models of categorization. Certainly, the exemplar and prototype models are fixtures of the category learning literature and they somewhat align with the type of learning that TSP and MSP, respectively, provide. REMERGE and SUSTAIN are also briefly mentioned, but their discussion is limited which is unfortunate as they are actually more functionally equivalent to C-HORSE. I think, however, that the authors are missing an opportunity to discuss how C-HORSE offers a means for bridging levels of analysis to connect neurobiological mechanisms with these notably successful psychological models of category learning. Rather than framing C-HORSE as a competitor to existing models, it should be viewed as an account existing on a different level of analysis. In this sense, it complements existing approaches and potentially extends a theoretical olive branch between the psychology and neuroscience of category learning.

We love this point about bridging levels of analysis and have added it to our discussion of the model’s relationship to other models, see Editor summary point #3 above.

6) The discussion takes a broad perspective on covering evidence concerning hippocampal contributions to category learning. Although comprehensive, some sections are not well connected back to the main thrust of the paper. For example, a section on neuropsychological accounts of the hippocampus and category learning summarizes central aspects of this literature but is never reflected on through the lens of the current findings. I do think this prior work is relevant, especially since it a central theme of the hippocampus not being necessary for category/concept learning, but its connection back to the current study is not well argued. Similarly, the section on consolidation and sleep is relevant, but in its current form does not seem to fit with the rest of the paper.

We have implemented these suggestions through very significant revisions to the Discussion. We now better connect the sections to the main argument of the paper and made cuts throughout, including removing the section on consolidation and sleep.

Reviewer #2 (Public Review):

The authors present a model of the hippocampal region that incorporates both the (indirect) trisynaptic and (direct) mono-synaptic pathways from entorhinal cortex (EC) to CA1 - the former incorporating projections from EC to dentate gyrus (DG), DG to CA3, and CA3 to CA1, and exhibiting a higher learning rate. They demonstrate that exposing this network to stimuli consistent with standard empirical tests of category learning (e.g. where within-category exemplars share a set of common features) allows the network to reliably assign both novel and previously encountered stimuli to the correct category (e.g. the network can learn to classify stimuli and generalise this knowledge to new examples). They show that the tri-synaptic pathway (TSP) preferentially supports the encoding of individual exemplars (e.g. analogous to episodic memory) while the mono-synaptic pathway (MSP) preferentially supports category learning.

The manuscript is well written, the simulation details appear sound, and the results are clearly and accurately presented. This model builds on a long tradition of computational modelling of hippocampal contributions to human memory function, strongly grounded in anatomical and electrophysiology data from both rodents and humans, and is therefore able to link phenomena at the level of individual cells and circuits to emergent behaviour - a major strength of this, and similar, work. However, I have two major concerns relating to the relationship between these findings and previously published work by the same and other authors.

First, it is not clear to me - from the manuscript - whether these results represent a significant novel advance on previous publications from the same senior author. Figures 1 and 3D are almost identical to figures published in Schapiro et al. (2017) Phil Trans B, and the take-home message (that the MSP might support statistical learning) is the same. In brief, it seems that the authors have subjected an identical network to some new (but related) tasks and reached the same set of conclusions. I see no distinction between learning to extract 'statistical regularities' (in previous work) and learning 'the structure of new categories' (described here). As an aside, demonstrating that an autoencoder network can learn stimulus categories and generalise to new exemplars is also well established.

We appreciate the opportunity to better articulate the novelty and importance of applying the model to the domain of category learning. There are crucial differences between statistical learning and category learning that make these simulations nontrivial (it did not have to be the case that the results would replicate for these category learning paradigms), and, importantly, many of the insights in the current work are category-learning specific (e.g., the effects of atypical features, trade-offs between generalization and recognition of exemplar-specific features). On the other hand, we of course agree that there are principles in common between statistical learning and category learning that are leading to the consistent findings. We added new material to the Introduction to explain the importance of these new simulations in the domain of category learning, and the value we see in demonstrating convergence across domains. See response to Editor point #1 above.

Second, I have some concerns with the relationship between the properties of this hippocampal network model and well described properties of single cells in the rodent and human hippocampus. In particular, the CA1 units in this model (and to some extent, also the CA3 units) come to respond strongly to all exemplars from within each category (e.g. as shown in Figure 3D, bottom right panel). This appears to be at odds with the known properties of place and concept cells from the rodent and human hippocampus, respectively, which show little generalisation across related concepts (i.e. the Jennifer Aniston neuron does not fire in response to other actors from Friends, for example). If the emergent properties of this model are not consistent with existing data, then it is not a valid model.

We appreciate the opportunity to discuss connections to the physiology literature. See response to Editor summary point #2 above.

More generally, the authors are clear that this model is "a microcosm of [the] hippocampusneocortex relationship" and that the properties of the MSP "mirror those of neocortex". Why not assume that category learning is supported by an interaction between hippocampus and neocortex, then, as in the complementary learning systems (CLS) model? Aside from some correlational fMRI data and partial deficits in hippocampal amnesics - either of which could have a myriad of different explanations - what empirical data is better accounted for by this model than CLS? Put differently, what grounds are there for rejecting the CLS model? To some extent, this model appears to account for less empirical data than CLS, with the exception of a few recent neuroimaging studies (which are hard to interpret at the level of single cells)

This is an important point for us to clarify, so we very much appreciate this comment. The crucial issue with CLS that motivated the microcosm theory is that the neocortex in the CLS framework learns far too slowly to support the kind of category learning studied in these paradigms, which unfolds over the course of minutes or hours. The neocortex in CLS was proposed to learn novel structure across days, months, and years.

We have added the following to the Introduction:

• “Despite its analogous properties, the MSP is not redundant with neocortex in this framework: the MSP allows rapid structure learning, on the timescale of minutes to hours, whereas the neocortex learns more slowly, across days, months, and years. The learning rate in the MSP is intermediate between the TSP (which operates as rapidly as one shot) and neocortex. The proposal is thus that the MSP is crucial to the extent that structure must be learned rapidly.”

We also have this description in the Discussion:

• “The MSP in our model has properties similar to the neocortex in that framework, with relatively more overlapping representations and a relatively slower learning rate, allowing it to behave as a miniature semantic memory system. The TSP and MSP in our model are thus a microcosm of the broader Complementary Learning Systems dynamic, with the MSP playing the role of a rapid learner of novel semantics, relative to the slower learning of neocortex.”

Reviewer #3 (Public Review):

The current work aimed to determine how the hippocampus may be able to detect regularities across experiences and how such a mechanism may serve to support category learning and generalization. Rapid learning in the hippocampus is critical for episodic memory and encoding of individual episodes. However, the rapid binding of arbitrary associations and one-shot learning was long thought suboptimal for finding regularities across experiences to support generalization, which were instead ascribed to other, slower-learning memory systems. More recent work has started to highlight hippocampal role in generalization, renewing the question of how generalization can be accomplished alongside memory for episodic details within a single memory structure. The current paper offers a reconciliation, presenting a biologically-inspired model of the hippocampus that is able to learn categories alongside stimulus-specific information comparably to human performance. The results convincingly demonstrate how distinct pathways within the hippocampus may differentially serve these complementary memory functions, enabling the single structure to support both episodic memory and categorization.

Major strengths and contributions

The paper includes simulation of three distinct categorization tasks, with a clear explanation of the unique aspects of each task. The key results are consistent across tasks, lending further support to the main conclusions of the role of distinct hippocampal pathways in learning specific details vs. regularities. Together with prior work on how the same architecture can support statistical learning in other types of tasks, this work provides important evidence of the broad role of the hippocampus in rapid integration of related information to serve many forms of cognition.

Throughout the paper, the authors nicely explain in conceptual terms how the same underlying computations may serve all three categorization tasks as well as statistical learning and episodic inference tasks. Thus, the paper will be of broad interest, beyond researchers focused on modeling and/or categorization.

On a conceptual level, this work provides a fruitful framework for understanding hippocampal functions, representations and computations. It provides a highly plausible mechanistic explanation of how category learning and generalization can be accomplished in the hippocampus and how distinct types of representations may emerge in distinct hippocampal subfields. The framework can be used to derive new testable predictions, some of which the authors themselves introduced. It also provides new insights into how the outputs of different pathways influence each other, providing a more nuanced view of the division of labor and interactions between hippocampal subfields. For example, the big loop recurrence would eventually lead to category influences even on the initially sparse, pattern separated representations in the CA3, which is an idea consistent with empirical observations.

The presented computational model of the hippocampus is currently the most detailed and biologically plausible hippocampal model easily applicable in the area of cognitive neuroscience and behavioral simulations. The commonalities and differences with other related models (conceptual and computational) are well explained. Both the conceptual and technical descriptions of the model are exceptionally clear and detailed. The model is also publicly available for download for any researcher to use with their own task and data. All these aspects make it likely that other researchers may adopt the model in a wider range of tasks, stimulating new discoveries.

The autoencoder nature of the model and the use of categorization tasks meant that some measures of interest, like recognition of exemplar-specific information, could not be evaluated by direct reading of the output layer to compare with some label (like old/new). The authors however came up with clever ways how to evaluate recognition performance in each task that was sensible and highlighted the multiple ways how one may think about information contained in neural representations in each layer. This approach can also be utilized by others for evaluating item-specific and category information in activation patterns, for example in analyses of fMRI.

Finally, I thought the current paper and provided model may also serve as an excellent introduction to computational modeling for those new to this approach. The exceptional clarity of the conceptual and technical description of this model and the clear logic of how one may model a cognitive task and interpret results made this paper fairly accessible. Furthermore, the paper offered new insights and predictions based on analyzing the model's hidden layers, lesion performance, and/or noting some patterns of behavior unique to specific tasks. This was also instructive for highlighting the distinctive contributions that the computational modeling approach can have for furthering our understanding of cognition and the brain.

We are extremely appreciative of the value the Reviewer sees in this work.

Weaknesses

The paper's strengths far outnumbered the weaknesses, that are minor. For one, the selected categorization tasks nicely complemented each other, but only covered stimuli with discretevalue dimensions (features like color, shape, symbol, etc). The degree to which the results generalize (or not) to continuous-value stimuli and different category structures (for instance information-integration or rule-based in COVIS framework) is not clear. How the model could be adjusted for continuous-value stimuli was not specified.

We agree that the simulation of only discrete valued dimensions is a limitation. We chose to do this simply because it is easier to use discrete values in the model as currently implemented, but future work will certainly need to test whether the model can simulate the various paradigms that make use of continuous-valued dimensions. We have added an explicit acknowledgement of this issue in the Methods:

• “The inhibition simulates the action of inhibitory interneurons and is implemented using a set-point inhibitory current with k-winner-take-all dynamics (O’Reilly, Munakata, Frank, Hazy, & Contributors, 2014). All simulations involved tasks with discrete-valued dimensions, as these are more easily amenable to implementation across input/output units whose activity tends to become binarized as a result of these inhibition dynamics. It will be important for future work to extend to implementations of category learning tasks with continuous-valued dimensions.”

There is compelling evidence for the dissociation between different hippocampal pathways and subfields (CA1 vs. CA3) that the model is based on. As the authors noted, there is also compelling evidence for functional dissociations along the long hippocampal axis, with anterior portions more geared towards coarse, generalized representations while posterior towards more detailed, specific representations. The authors nicely pointed out that these proposals of withinhippocampus division of labor are less orthogonal than they may first appear, as there is greater proportion of CA1 in the anterior hippocampus. However, it is premature to imply that this resolves the CA1/CA3 vs. anterior/posterior question; the idea that existing anterior findings may be simply CA1 findings is currently only speculation. Furthermore, first studies indicating that anterior/posterior representational gradients may exist within each subfield are beginning to emerge.

We completely agree that this is speculative at this point, which needed acknowledgment. See response to Editor summary point #2 above.

Author Response

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

Reviewer 1

Question 1: While the CTD human brain organoids show a decrease in Cr (in absence of Cr in the culture medium) as compared to control organoids (4 times less), they are not devoid of Cr. Do these organoids express the two enzymes allowing Cr synthesis (AGAT and GAMT), and in which brain cell types? If yes, how to explain the decrease in Cr in the CTD organoids?

There is a lack of functional CRT in the CTD human brain organoids. The basal level of creatine in CTD human brain organoid is significantly lower than in healthy human brain organoids. The intracerebral creatine synthesis is due to different expression of the AGAT and GAMT enzymes and relies on functional CRT for the transport of the GAA intermediate. Literature pointed out that both enzymes are rarely co-expressed (Braissant et al., 2001, PMID: 11165387) meaning that GAA intermediate needs to be transported by CRT to neurons for complete creatine synthesis. Even if we evidenced a slight mRNA expression of AGAT and GAMT enzymes, the creatine synthesis is not effective since the GAA intermediate could not be transported in cell expressing GAMT due to the non-functional creatine transporter in the CTD human brain organoids.

Question 2. The rescue experiment, re-establishing a functional Cr transporter (CRT or SLC6A8) in the CTD human brain organoids, is very interesting, as this may help the design and development of new treatments for CTD. However, authors claim that the functional CRT expressed in the rescued CTD organoids was expressed in each cell. This may be a difficulty in the development of new CTD treatments, as CRT should be expressed in neurons and oligodendrocytes, but not in astrocytes. Authors may want to comment on this point.

As shown in Figure S2C, the whole brain organoid in the rescue experiment shows the expression of the GFP protein, thus also the co-expressed wild-type CRT. In these experiments, we did not make a detailed cellular characterization of the rescued organoids, and this may be the aim of a separate study that will carry out experiments for an exact characterization of the cell-specific CRT expression and function in the rescued brain organoids. Accordingly, we corrected in the revised version of manuscript the statement on page 6 to the following: “SLC6A8 expressing brain organoids showed GFP fluorescence in the whole area of the organoid (Fig S2C).”

Reviewer #1 (Recommendations for The Authors):

• Authors may cite the recent review by Fernandes-Pires (2022) exposing the challenges to treat CTD (introduction, lines 57-58 for example).

Reference has been added, lines 57-58 of the revised version

• Authors may precise in their introduction (lines 60-61) that, while creatine (Cr) supplementation is not effective to treat CTD male patients, a proportion of female CTD patients is responsive to Cr supplementation (due to the differential inactivation of one of the X chromosome depending on the cells).

Treating CTD appears simple: transport creatine into the brain cells. In individuals with creatine synthesis disorders, increasing brain creatine levels thanks to oral supplementation of creatine monohydrate and/or precursors improves neurodevelopmental outcomes. This task has proven more daunting than expected in CTD since oral creatine supplementation does not increase brain creatine concentrations. Literature and more specially data reported by Van de Kamp “X-linked creatine transporter deficiency: clinical aspects and pathophysiology. J Inhert Metab Dis 37 (5):715-733) describes 3 females CTD patients without improvement of clinical outcomes. Bruun et al., 2018 “Treatment outcome of creatine transporter deficiency: international restrospective cohort study: Metab. Brain Dis: 33:875-884 reports 2/3 CTD females with improvement of clinical outcome. Taken together the sentence has been modified in the revised version of the manuscript as follows: “Several combinations of nutritional supplements or Cr precursors l-arginine and l-glycine, have been studied as therapeutic approaches for CTD, but they have shown limited success (Bruun et al., 2018, Valayannopoulos et al., 2013) (lines 61-63, Page 4)

• When comparing their new in vitro CTD model of human brain organoids with existing in vivo rodent models, authors may add the citation of the rat model of Duran-Trio et al (2021 & 2022), in particular for its description of CNS tissue alterations (dendritic spines density for example).

The reference Duran-Trio et al (2021) has been added (page 4, line 70). The reference Duran-Trio et al (2022) has been added (page 11) and the sentence has been modified in the revised version of the manuscript as follows: “Reduced cortical spine density and reductions in protein levels of several synaptic markers have been observed in the brains of Slc6a8-/y mice and rats (Chen et al., 2021; Duran-Trio et al., 2022)”.

Reviewer #2 (Recommendations For The Authors):

There are only minor suggestions for improvement in this manuscript. The authors strongly link creatine uptake, the GSK3β pathway, and intellectual disability. Enhancing this claim with data on phosphorylation differences between organoids derived from healthy individuals and those from CTD patients could solidify this foundation and facilitate a more holistic understanding of the disease. In addition, the in vitro model based on organoids might be closer than other experimental setups; however, proving that those differences are also present in vivo would greatly benefit the story.

As shown in Fig 6A-B, GSK3β is less phosphorylated on Ser9 in CTD brain organoids compared to healthy organoids, indicating that GSK3β is more active in organoids with reduced creatine levels. Studying the level of GSK3β phosphorylation in the mouse brain could be part of next experiments and another story.

There is also some uncertainty around the rescue experiment using the exogenous SLC6A8 gene. Could the difference in creatine uptake between the rescue iPSCs and the healthy control be due to CRT overexpression? Higher levels of the transporter may explain the elevated levels of intracellular creatine. Thus, a comparison using Western blotting experiments could be a valuable addition to evaluating the expression levels of this protein.

For the rescue experiment, we used a vector where SLC6A8 and eGFP were connected by an IRES2 sequence, providing simultaneous, but independent expression of the two proteins. CTD-rescue iPSC clones were selected based on high eGFP fluorescence. These clones probably have several copies of transgene in their genome, which could result in a higher abundance of SLC6A8 compared with healthy iPSCs. The difference in creatine uptake between the CTD-rescue iPSCs and the healthy control is probably due to CRT overexpression. However, there are no satisfactory anti-SLC6A8 antibodies commercially available to quantify CRT by western-blot. We would like to add that, although creatine uptake is higher in CTD-rescue iPSCs than in healthy control, the basal level of creatine (which corresponds to culture conditions for the rest of the experiments) is similar.

Overall, this study provides valuable insights into CTD and potential therapeutic targets. It enriches our understanding of CTD and opens up new avenues for future research in this field.

We thank the reviewer for their kind words and hope this study will be useful for other researchers in the CTD field.

Author Response

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

We appreciate the thoughtful feedback provided by the editor and the three reviewers and have addressed their comments, which we believe have results in significant improvements to the manuscript. A point-by-point response to the comments is included below.

Reviewer #1

Line 229: The wording of "highly valuable" seems slightly vague. Consider rephrasing to something more specific, such as: "...using individual animal recorders provide valuable new insight into locomotor behavior when ..."

Thank you for your advice. The sentence was revised as you suggested.

Lines 518-527: Consider adding quantitative details for the four conditions. It is apparent in Figure 4 (dashed lines associated with peaks of the distributions), but in the text it would be helpful to add the speeds and heights chosen to sort the data.

Quantitative descriptions were added in the Materials and Methods section. We also moved detailed information about the curve fitting function from the Result section to Materials and Methods section.

“Threshold values were decided based on the peak in the curve of the fitted probability density distribution (wind speed: 6.0 m/s, wave height 2.8 m). Weibull distribution and log normal distribution were used as the fitting function for wind speed and wave height, respectively (Ferreira and Guedes Soares, 2000; Carta et al., 2009).”

Reviewer #2

Line 51 - Climatic models - climatic model cannot, by definition, provide prediction of specific weather conditions as they focus on large and long-term values and trends. I suggest the authors to review their use of climatic conditions throughout the manuscript, and use instead weather conditions, where appropriate.

Thank you for informing us the usage of terminology. Most of the phrases “climatic models” in the manuscript were replaced by “mathematical weather models”, for example, line 51, 226, 230, 312. We also checked that the phrase “climatic condition” never appears in the manuscript.

Lines 59-61 require editing. It is true that take-off is associated with high rate of energy expenditure, but it is phrased in an unclear way. I suggest writing instead "Therefore, the high energy expenditure associated with take-off is strongly influencing the total energy expenditure of wandering albatross during the foraging trip, unlike the duration or distance of the flight (Shaffer et al., 2001).

Thank you for your advice. As you suggested the phrasing was not proper to describe the previous study. The sentence was revised following your suggestion.

“Therefore, the high energy expenditure associated with take-off strongly influences the total energy expenditure of wandering albatross during the foraging trip, unlike flight duration or distance (Shaffer et al., 2001a)”

Line 213 - I suggest "Among the LMMS, models..."

The sentence was revised as you suggested.

Line 286 - I suggest using the word "difference" or "delta" AIC instead of variation which is confusing.

The sentence was revised as follows.

“For instance, the AIC difference in running speed between the best model and the second-lowest AIC model was only 0.27.”

Line 385 - Please provide actual percentage even if it is < 1%.

We added actual mass percentage of both small and large types of the recorders in line 385 and 386.

“Small Ninja-scans weighed 28 g, which is 0.3 ~ 0.4% of wandering albatross body mass, and are expected to record for 7 h. Large Ninja-scans weighed 91 g, which corresponds to 0.8 ~ 1.3% of wandering albatross body mass, and are expected to record for 65 h.”

Reviewer #3

Thank you for the marked-up manuscript and a lot of comments on it. Most of your grammatical advises and rephrases are reflected in the new version and we double-checked the whole manuscript using English proofreading service. Please refer to the below for the answer to each major comments.

Line 304 – not sure volume is best word choice.

We changed the word “volume” to “amplitude”.

Line 309 – Are you sure that Pennycuick 1982 didn’t document this?

His article mainly focused on the morphology and steady flight mechanism of albatrosses and petrels. There were no descriptions on take-offs of seabirds.

Line 320 – add after Weimerskirch citation, and similar to predicted best glide speeds (Shafer et al. 2001, Funct, Ecol 15)

Thank you for the beneficial information. We added the phrase and the citation in the sentence.

“The mean air speed of wandering albatrosses at the end of the running phase was close to the average flight speed (approximately 15 m/s) (Weimerskirch et al., 2002), and similar to predicted best glide speeds, (Shaffer et al., 2001b) indicating that wandering albatrosses gain sufficient lift at the end of the running phase and efficiently utilize ocean wind.”

Line 684 – citation information incomplete.

Thank you for finding the incomplete citation. Authors of the reference paper were corrected. “Weimerskirch H, Bonadonna F, Bailleul F, Mabille G, Dell’Omo G, Lipp H-P. 2002. GPS tracking of foraging albatrosses. Science 295:1259–1259. doi:10.1126/science.1068034”

Fig.4. – In Part B, reorient the y-axis labels to match the other figures. Change the orientation of y-axis labels like shown in Figure 3.

We rearranged the labels and ticks in Fig.4B to improve the readability and match the graphs with Fig3.

Author Response

Reviewer #1 (Public Review):

[...] Based on these results, the authors support a model whereby kinetic regimes are encoded in the cis-regulatory sequences of a gene instead of imposed by an evolving trans-regulatory environment.

The question asked in this manuscript is important and the eve locus represents an ideal paradigm to address it in a quantitative manner. Most of the results are correctly interpreted and well-presented. However, the main conclusion pointing towards a potential "unified theory" of burst regulation during Drosophila embryogenesis should be nuanced or cross-validated.

We thank the reviewer for their careful and insightful assessment of our manuscript. The reviewer is right in that our claims should have been more nuanced. Indeed, our proposed unified strategy only concerns even-skipped transcription under the variable conditions that exist in ectopic and endogenous eve expression regions.

Our results and those of others suggest that different developmental genes follow unified—yet different—transcriptional control strategies whereby different combinations of bursting parameters are regulated to modulate gene expression: burst frequency and amplitude for eve (Berrocal et al., 2020), and burst frequency and duration for gap genes (Zoller et al., 2018). In light of the aforementioned works, we can only claim that our results suggest a unified strategy for eve, our case of study, as we observe that eve regulatory strategies are robust to disruption of enhancers and binding sites. In the Discussion section of our revised manuscript, we will emphasize that the bursting control strategy we uncovered for eve does not necessarily apply to other genes, and speculate in more detail that genes that employ the same strategy of transcriptional bursting may be grouped in families that share a common molecular mechanism of transcription.

In addition to the lack of novelty (some results concerning the fact that koff does not change along the A/P axis/the idea of a 'unified regime' were already obtained in Berrocal et al 2020),...

Unfortunately, we believe there is a misunderstanding in terms of what we construe as novelty in our work. In our previous work (Berrocal et al., 2020), we observed that the seven stripes of even-skipped (eve) expression modulate transcriptional bursting through the same strategy—bursting frequency and amplitude are controlled to yield various levels of mRNA synthesis, while burst duration remains constant. We reproduce that result in our paper, and do not claim any novelty. However, what was unclear is whether the observed eve bursting control strategy would only exist in the wild-type stripes, whose expression—we reasoned—is under strong selection due to the dramatic phenotypic consequences of eve transcription, or if eve transcriptional bursting would follow the same strategy under trans-regulatory environments that are not under selection to deliver specific spatiotemporal dynamics of eve expression. Our results—and here lies the novelty of our work—support the second scenario, and point to a model where eve bursting strategies do not result from adaptation of eve activity to specific trans-regulatory environments. Instead, we speculate that a molecular mechanism constrains eve bursting strategy whenever and wherever the gene is active. This is something that we could not have known from our first study in (Berrocal et al., 2020) and constitutes the main novelty of our paper. To put this in other words, the novelty of our work does not rest on the fact that both burst frequency and amplitude are modulated in the endogenous eve pattern, but that this modulation remains quantitatively indistinguishable when we focus on ectopic areas of expression. We will make this point clearer in the Introduction and Discussion section of our revised manuscript.

… note i) the limited manipulation of TF environment;...

We acknowledge that additional genetic manipulations would make it possible to further test the model. However, we hope that the reviewer will agree with us that the manipulations that we did perform are sufficient to provide evidence for common bursting strategies under the diverse trans-regulatory environments present in wild-type and ectopic regions of gene expression. In the Discussion section of our revised manuscript, we will elaborate further on the kind of genetic manipulations (e.g., probing transcriptional strategies that result from swapping promoters in the context of eve-MS2 BAC; or quantifying the impact on eve transcriptional control after performing optogenetic perturbations of transcription factors and/or chromatin remodelers) that could shed further light on the currently undefined molecular mechanism that constrains eve bursting strategies, as a mean to motivate future work.

… ii) the simplicity with which bursting is analyzed (only a two-state model is considered, and not cross-validated with an alternative approach than cpHMM) and…

Based on our previous work (Lammers et al., 2020), and as described in the SI Section of the current manuscript: Inference of Bursting Parameters, we selected a three-state model (OFF, ON1, ON2) under the following rationale: transcription of even-skipped in pre-gastrulating embryos occurs after DNA replication, and promoters on both sister chromatids remain paired. Most of the time these paired loci cannot be resolved independently using conventional microscopy. As a result, when we image an MS2 spot, we are actually measuring the transcriptional dynamics of two promoters. Thus, each MS2-fluorescent spot may result from none (OFF), one (ON1) or two (ON2) sister promoters being in the active state. Following our previous work, we analyzed our data assuming the three-state model (OFF, ON1, ON2), and then, for ease of presentation, aggregated ON1 and ON2 into an effective single ON state. As for the lack of an alternative model, we chose the simplest model compatible with our data and our current understanding of transcription at the eve locus. With this in mind, we do not rule out the possibility that more complex processes—that are not captured by our model—shape MS2 fluorescence signals. For example, promoters may display more than two states of activity. However, as shown in (Lammers et al., 2020 - SI Section: G. cpHMM inference sensitivities), model selection schemes and cross-validation do not give consistent results on which model is more favorable; and for the time being, there is not a readily available alternative to HMM for inference of promoter states from MS2 signal. For example, orthogonal approaches to quantify transcriptional bursting, such as smFISH, are largely blind to temporal dynamics. As a result, we choose to entertain the simplest two-state model for each sister promoter. We appreciate these observations, as they point out the need of devoting a section in the supplemental material of our revised manuscript to clarify the motivations behind model selection.

… iii) the lack of comparisons with published work.

We thank the reviewer for pointing this out. In the current discussion of our manuscript, we compare our findings to recent articles that have addressed the question of the origin of bursting control strategies in Drosophila embryos (Pimmett et al., 2021; Yokoshi et al., 2022; Zoller et al., 2018). Nevertheless, we acknowledge that we failed to include references that are relevant to our study. Thus, our revised Discussion section must include recent results by (Syed et al., 2023), which showed that the disruption of Dorsal binding sites on the snail minimal distal enhancer results in decreased amplitude and duration of transcription bursts in fruit fly embryos. Additionally, we have to incorporate the study by (Hoppe et al., 2020), which reported that the Drosophila bone morphogenetic protein (BMP) gradient modulates the bursting frequency of BMP target genes. References to thorough studies of bursting control in other organisms, like Dictyostelium discoideum (Tunnacliffe et al., 2018), are due as well.

Reviewer #2 (Public Review):

The manuscript by Berrocal et al. asks if shared bursting kinetics, as observed for various developmental genes in animals, hint towards a shared molecular mechanism or result from natural selection favoring such a strategy. Transcription happens in bursts. While transcriptional output can be modulated by altering various properties of bursting, certain strategies are observed more widely. As the authors noted, recent experimental studies have found that even-skipped enhancers control transcriptional output by changing burst frequency and amplitude while burst duration remains largely constant. The authors compared the kinetics of transcriptional bursting between endogenous and ectopic gene expression patterns. It is argued that since enhancers act under different regulatory inputs in ectopically expressed genes, adaptation would lead to diverse bursting strategies as compared to endogenous gene expression patterns. To achieve this goal, the authors generated ectopic even-skipped transcription patterns in fruit fly embryos. The key finding is that bursting strategies are similar in endogenous and ectopic even-skipped expression. According to the authors, the findings favor the presence of a unified molecular mechanism shaping even-skipped bursting strategies. This is an important piece of work. Everything has been carried out in a systematic fashion. However, the key argument of the paper is not entirely convincing.

We thank the reviewer, as these comments will enable us to improve the Discussion section and overall logic of our revised manuscript. We agree that the evidence provided in this work, while systematic and carefully analyzed, cannot conclusively rule out either of the two proposed models, but just provide evidence supporting the hypothesis for a specific molecular mechanism constraining eve bursting strategies. Our experimental evidence points to valuable insights about the mechanism of eve bursting control. For instance, had we observed quantitative differences in bursting strategies between ectopic and endogenous eve domains, we would have rejected the hypothesis that a common molecular mechanism constrains eve transcriptional bursting to the observed bursting control strategy of frequency and amplitude modulation. Thus, we consider that our proposition of a common molecular mechanism underlying unified eve bursting strategies despite changing trans-regulatory environments is more solid. On the other hand, while our model suggests that this undefined bursting control strategy is not subject to selection acting on specific trans-regulatory environments, it is not trivial to completely discard selection for specific bursting control strategies given our current lack of understanding of the molecular mechanisms that shape the aforesaid strategies. Indeed, we cannot rule out the hypothesis that the observed strategies are most optimal for the expression of eve endogenous stripes according to natural selection, and that these control strategies persist in ectopic regions as an evolutionary neutral “passenger phenotype” that does not impact fitness. We recognize the need to acknowledge this last hypothesis in the updated Introduction and Discussion sections of our manuscript. Further studies will be needed to determine the mechanistic and molecular basis of eve bursting strategies.

Reviewer #3 (Public Review):

In this manuscript by Berrocal and coworkers, the authors do a deep dive into the transcriptional regulation of the eve gene in both an endogenous and ectopic background. The idea is that by looking at eve expression under non-native conditions, one might infer how enhancers control transcriptional bursting. The main conclusion is that eve enhancers have not evolved to have specific behaviors in the eve stripes, but rather the same rates in the telegraph model are utilized as control rates even under ectopic or 'de novo' conditions. For example, they achieve ectopic expression (outside of the canonical eve stripes) through a BAC construct where the binding sites for the TF Giant are disrupted along with one of the eve enhancers. Perhaps the most general conclusion is that burst duration is largely constant throughout at ~ 1 - 2 min. This conclusion is consistent with work in human cell lines that enhancers mostly control frequency and that burst duration is largely conserved across genes, pointing to an underlying mechanistic basis that has yet to be determined.

We thank the reviewer for the assessment of our work. Indeed, evidence from different groups (Berrocal et al., 2020; Fukaya et al., 2016; Hoppe et al., 2020; Pimmett et al., 2021; Senecal et al., 2014; Syed et al., 2023; Tunnacliffe et al., 2018; Yokoshi et al., 2022; Zoller et al., 2018) is coming together to uncover commonalities, discrepancies, and rules that constrain transcriptional bursting in Drosophila and other organisms.

Author Response

Reviewer #1 (Public Review):

This article is interested in how butterfly, or more precisely, butterfly wing scale precursor cells, each make precisely patterned ultrastructures made of chitin.

To do this, the authors sought to use the butterfly Parides eurimedes, a papilionid swallowtail, that carries interesting, unusual structures made of 1) vertical ridges, that lack a typical layered stacking arrangement; and 2) deep honeycomb-like pores. These two features make the organism chosen a good point of comparison with previous studies, including classic papers that relied on electronic microscopy (SEM/TEM), and more recent confocal microscopy studies.

The article shows good microscopy data, including detailed, dense developmental series of staining in the Parides eurimedes model. The mix of cell membrane staining, chitin precursor, and F-actin staining is well utilized and appropriately documented with the help of 3D-SIM, a microscopy technique considered to provide super-resolution (here needed to visualize sub-cellular processes).

The key message from this article is that F-actin filaments are later repurposed, in papilionid butterflies, to finish the patterning of the inter-ridge space, elaborating new structures (this was not observed so far in other studies and organisms). The model proposed in Figure 6 summarized these findings well, with F-actin reshaping it itself into a tulip that likely pulls down a chitin disk to form honeycombs. These interpretations of the microscopy data are interesting and novel.

There are two other points of interest, that deserve future investigation:

1) The authors performed immunolocalizations of Arp2 and pharmacological inhibitions of Arp2/3, and found some possible effect on honeycomb lattice development. The inter-ridge region of the butterfly Papilio polytes, which lacks these structures, did not seem to be affected by drug treatments. Effects where time-dependent, which makes sense. These data provide circumstantial evidence that Arp2/3 is involved in the late role of F-actin formation or re-organisation.

2) The authors perform a comparative study in additional papilionids (Fig. 6 in particular). I find these data to be quite limited without a dense sampling, but they are nonetheless interesting and support a second-phase role of F-actin re-organisation.

The article is dense, well produced and succinctly written. I believe this is an interesting and insightful study on a complex process of cell biology, that inspires us to look at basic phenomena in a broader set of organisms.

We thank the reviewer for the positive appraisal.

Reviewer #2 (Public Review):

The manuscript by Seah and Saranathan investigates the cell-based growth mechanism of so called honeycomb-structures in the upper lamina of papilionid wing scales by investigating a number of different species. The authors chose Parides eurimedes as a focus species with the developmental pathway of five other papilionid as a comparative backup. Through state-of-the-art microscopy images of different developmental steps, the author find that the intricate f-actin filaments reorganise, support cuticular discs that template the air holes that form the honeycomb lattice. The manuscript is well written and easy to follow, yet based on a somewhat limited sample size for their focus species, limiting attempts to suppress expression and alter structure shape.

The fact that the authors find a novel reorganisation mechanism is exciting and warrants further research, e.g. into the formation of other microscale features or smaller scale structures (e.g. the mentioned gyroid networks).

We thank the reviewer for the positive appraisal.

The authors place their results in the discussion in the light of current literature (although the references could be expanded further to include the breadth of the field). However, the mechanistic explanation completely ignores the mechanical properties of the membranes as an origin of some of the observed phenomena (see McDougal's work for example) and places the occurence of some features into Turing patterns and Ostwald ripening, which I find somewhat unlikely and I suggest that the authors discover this aspects further in the discussion.

We thank the reviewer for these suggestions. We have added more references from the current literature to more accurately reflecting the breadth of the field. McDougal et al. 2021. discuss the nature of biomechanical forces (differential growth and buckling) on the membrane and deposited cuticle shaping the formation of longitudinal ridges. However, here it is the invagination of the plasma membrane bearing the deposited cuticle that is our main concern. Nevertheless, we agree future studies should indeed consider the mechanical properties of the membranes, in addition to explain some of the observed features. We have clarified this in our discussion.

I have little concerns regarding the experimental approach beyond the somewhat limited sample size. One thing the authors should more clearly mention are the pupation periods for all investigated species as only the periods for two species are named.

Yes, unfortunately, we were only able to obtain pupae with pupation dates for two species. We have clarified this point in the methods.

Author Response

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

Reviewer #1 (Public Review):

This study by Sokač et al. entitled "GENIUS: GEnome traNsformatIon and spatial representation of mUltiomicS data" presents an integrative multi-omics approach which maps several genomic data sources onto an image structure on which established deep-learning methods are trained with the purpose of classifying samples by their metastatic disease progression signatures. Using published samples from the Cancer Genome Atlas the authors characterize the classification performance of their method which only seems to yield results when mapped onto one out of four tested image-layouts.

Major recommendations:

• In its current form, GENIUS analysis is neither computationally reproducible nor are the presented scripts on GitHub generic enough for varied applications with other data. The GENIUS GitHub repository provides a collection of analysis scripts and not a finished software solution (e.g. command line tool or other user interface) (the presented scripts do not even suffice for a software prototype). In detail, the README on their GitHub repository is largely incomplete and reads analogous to an incomplete and poorly documented analysis script and is far from serving as a manual for a generic software solution (this claim was made in the manuscript).

We apologize for this oversight, and we have now invested considerable resources into making the documentation more detailed and accurate. We have created a new GitHub repository (https://github.com/mxs3203/GENIUS) that contains a small set of example data and all the necessary scripts to run GENIUS. The README file guides the user through each step of the GENIUS framework but it also contains a bash script that runs all the steps at once. When a user would like to use it on their own data, they need to replace the input data with their data but in the same format as the example input data. This is now fully documented in the README file. All scripts have arguments that can be used to point to custom data. The entire pipeline using example data can be run using run_genius.sh script. This script will produce CSV files and PNG files inside the ExtractWithIG folder containing attribution scores for every cancer type tested.

The authors should invest substantially into adding more details on how data can be retrieved (with example code) from the cited databases and how such data should then be curated alongside the input genome to generically create the "genomic image".

Data for analysis can be sourced from multiple locations, what we have used in our examples and for development was based on data from the TCGA. It can be retrieved from the official TCGA data hub or through Xena Browser (https://xenabrowser.net/). However, the data formats are generic, and similar data types (mutation, expression, methylation, copy number) can be obtained from multiple sources. We have added example data to demonstrate the layout, and we have a script included that creates the layout from standard mutation, expression, methylation and copy number data formats. We have substantially improved the annotations, including detailed descriptions of the data layout along with examples, and we have, as part of our validation, had an independent person test run the scripts using TCGA example data we provided on the new GitHub page.

In addition, when looking at the source code, parameter configurations for training and running various modules of GENIUS were hard-coded into the source code and users would have to manually change them in the source code rather than as command line flags in the software call. Furthermore, file paths to the local machine of the author are hard-coded in the source code, suggesting that images are sourced from a local folder and won't work when other users wish to replicate the analysis with other data. I would strongly recommend building a comprehensive command line tool where parameter and threshold configurations can be generically altered by the user via command line flags.

Apologies, we have changed the code and removed all hard-coded paths. All paths are now relative to the script using them. Furthermore, we made the config file more visible and easier to use. The example run can be found on the new github repository we linked in the previous comment.

We also inserted the following text in the manuscript

The GitHub repository contains example data and instructions on how to use the GENIUS framework.

A comprehensive manual would need to be provided to ensure that users can easily run GENIUS with other types of input data (since this is the claim of the manuscript). Overall, due to the lack of documentation and hard-coded local-machine folder paths it was impossible to computationally reproduce this study or run GENIUS in general.

Apologies, we have completely reworked the code base, and extensively annotated the code. We have also made highly detailed step-by-step instructions that should enable any user to run GENIUS on their own or public data.

• In the Introduction the authors write: "To correct for such multiple hypothesis testing, drastic adjustments of p-values are often applied which ultimately leads to the rejection of all but the most significant results, likely eliminating a large number of weaker but true associations.". While this is surely true for any method attempting to separate noise from signal, their argument fails to substantiate how their data transformation will solve this issue. Data transformation and projection onto an image for deep-learning processing will only shift the noise-to-signal evaluation process to the postprocessing steps and won't "magically" solve it during training.

The data transformation does not solve the problem of multiple hypothesis testing but it facilitates the use of computer vision algorithms and frameworks on rich multi-omics data. Importantly, transforming the data into genome images, training the model, and inspecting it with integrated gradients can be interpreted as running a single test on all of the data.

Analyzing multiomics data using classical statistical methods typically means that we perform extensive filtering of the data, removing genes with poor expression/methylation/mutation scores, and then e.g. perform logistic regression against a desired outcome, or alternatively, perform multiple statistical tests comparing each genomic feature independently against a desired outcome. Either way, information is lost during initial filtering and we must correct the analysis for each statistical test performed. While this increases confidence in whichever observation remains significant, it also undoubtedly means that we discard true positives. Additionally, classical statistical methods such as those mentioned here do not assume a spatial connection between data points, thus any relevant information relating to spatial organization is lost.

Instead, we propose the use of the GENIUS framework for multiomics analysis. The GENIUS framework is based on deep neural nets and relies on Convolutions and their ability to extract interactions between the data points. This particularly considers spatial information, which is not possible using classical statistical methods such as logistic regression where the most similar approach to this would include creating many models with many interactions.

Furthermore, integrated gradients is a non-parametric approach that simply evaluates the trained model relative to input data and output label, resulting in attribution for each input with respect to the output label. In other words, integrated gradients represent the integral of gradients with respect to inputs along the path from a given baseline to input. The integral is described in Author response image 1:

Author response image 1.

More about integrated gradients can be read on the Captum webpage (https://captum.ai/docs/introduction) or in original paper https://arxiv.org/abs/1703.01365.

Since we transformed the data into a data structure (genome image) that assumes a spatial connection between genes, trained the model using convolutional neural networks and analyzed the model using integrated gradients, we can treat the results without any parametric assumption. As a particular novelty, we can sort the list based on attribution score and take top N genes as our candidate biomarkers for the variable of interest and proceed with downstream analysis or potentially functional validation in an in vitro setting. In this manner, the reviewer is correct that the signal-to-noise evaluation is shifted to the post-processing steps. However, the benefit of the GENIUS framework is particularly that it enables integration of multiple data sources without any filtering, and with constructing a novel data structure that facilitates investigation of spatial dependency between data points, thus potentially revealing novel genes or biomarkers that were previously removed through filtering steps. However, further downstream validation of these hits remains critical.

We added the following paragraph to make this more clear

"Integrated Gradients is a non-parametric approach that evaluates the trained model relative to input data and output label, resulting in attribution scores for each input with respect to the output label. In other words, Integrated Gradients represent the integral of gradients with respect to inputs along the path from a given baseline. By using Integrated Gradients, we provide an alternative solution to the problem posed by performing multiple independent statistical tests. Here, instead of performing multiple tests, a single analysis is performed by transforming multiomics data into genome images, training a model, and inspecting it with Integrated Gradients. Integrated Gradients will output an attribution score for every gene included in the genome image and those can be ranked in order to retrieve a subset of the most associated genes relative to the output variable."

In addition, multiple-testing correction is usually done based on one particular data source (e.g. expression data), while their approach claims to integrate five very different genomic data sources with different levels and structures of technical noise. How are these applications comparable and how is the training procedure able to account for these different structures of technical noise? Please provide sufficient evidence for making this claim (especially in the postprocessing steps after classification).

The reviewer is correct that there will be different technical noise for each data source. However, each data source is already processed by standardized pipelines used for interpreting sequence-level data into gene expression, mutations, copy number alterations and methylation levels. Thus, sequence-level technical noise is not evaluated as part of the GENIUS analysis. Nevertheless, the reviewer is correct that sample-level technical noise, such as low tumor purity or poor quality sequencing, undoubtedly can affect the GENIUS predictions, as is true for all types of sequence analysis. As part of GENIUS, an initial data preprocessing step (which is performed automatically as part of the image generation), is that each data source is normalized within that source and linearly scaled in range zero to one (min-max scaling). This normalization step means that the impact of different events within and between data sources are comparable since the largest/smallest value from one data source will be comparable to the largest/smallest value from another data source.

Additionally, deep neural networks, particularly convolutional networks, have been shown to be very robust to different levels of technical noise (Jang, McCormack, and Tong 2021; Du et al. 2022). In the manuscript we show the attribution scores for different cancer types in figure 3B of the paper. Here, the top genes include established cancer genes such as P53, VHL, PTEN, APC and PIK3CA, indicating that the attribution scores based on GENIUS analysis is a valid tool to identify potential genes of interest. Furthermore, when focusing the analysis on predicting metastatic bladder cancer, we were able to show that of the top 10 genes with the highest attribution scores, 7 showed significant association with poor outcome in an independent validation cohort of mostly metastatic patients (shown in figure 4).

• I didn't find any computational benchmark of GENIUS. What are the computational run times, hardware requirements (e.g. memory usage) etc that a user will have to deal with when running an analogous experiment, but with different input data sources? What kind of hardware is required GPUs/CPUs/Cluster?

We apologize for not including this information in the manuscript. We added the following section in to the manuscript:

"Computational Requirements

In order to train the model, we used the following hardware configuration: Nvidia RTX3090 GPU, AMD Ryzen 9 5950X 16 core CPU, and 32Gb of RAM memory. In our study, we used a batch size of 256, which occupied around 60% of GPU memory. Training of the model was dependent on the output variable. For metastatic disease prediction, we trained the model for approximately 4 hours. This could be changed since we used early stopping in order to prevent overfitting. By reducing the batch size to smaller numbers, the technical requirements are reduced making it possible to run GENIUS on most modern laptops."

• A general comment about the Methods section: Models, training, and validation are very vaguely described and the source code on GitHub is very poorly documented so that parameter choices, model validation, test and validation frameworks and parameter choices are neither clear nor reproducible.

Apologies, we have updated the methods section with more details on models, training and validation. Additionally, we have moved the section on evaluating model performance from the methods section to the results section, with more details on how training was performed.

We also agree that the GitHub page is not sufficiently detailed and well structured. To remedy this, we have made a new GitHub page that only has the code needed for analysis, example input data, example runs, and environment file with all library versions. The GitHub repository is also updated in the manuscript.

The new GitHub page can be found on: https://github.com/mxs3203/GENIUS

Please provide a sufficient mathematical definition of the models, thresholds, training and testing frameworks.

We sincerely apologize, but we do not entirely follow the reviewers request on this regard. The mathematical definitions of deep neural networks are extensive and not commonly included in research publications utilizing deep learning. We have used PyTorch to implement the deep neural net, a commonly used platform, which is now referenced in the methods. The design of the deep learning network used for GENIUS is described in figure 1, and the relevant parameters are described in methods. The hyper parameters are described in the methods section, and are as follows:

"All models were trained with Adagrad optimizer with the following hyperparameters: starting learning rate = 9.9e-05 (including learning rate scheduler and early stopping), learning rate decay and weight decay = 1e-6, batch size = 256, except for memory-intensive chromosome images where the batch size of 240 was used."

• In chapter "Latent representation of genome" the authors write: "After successful model training, we extracted the latent representations of each genome and performed the Uniform Manifold Approximation and Projection (UMAP) of the data. The UMAP projected latent representations into two dimensions which could then be visualized. In order to avoid modeling noise, this step was used to address model accuracy and inspect if the model is distinguishing between variables of interest.". In the recent light of criticism when using the first two dimensions of UMAP projections with omics data, what is the evidence in support of the author's claim that model accuracy can be quantified with such a 2D UMAP projection? How is 'model accuracy' objectively quantified in this visual projection?

We apologize for not clarifying this. The UMAP was done on L, the latent vector, which by assumption should capture the most important information from the “genome image”. In order to confirm this, we plotted the first two dimensions of UMAP transformation and colored the points by the output variable. If the model was capturing noise, there should not be any patterns on the plot (randomized cancer-type panel). Since, in most cases, we do see an association between the first two UMAP dimensions and the output variable, we were confident that the model was not modeling (extracting) noise.

To clarify this, we changed the sentence in the manuscript so it is more clear that this is not an estimation of accuracy but only an initial inspection of the models:

The UMAP projected latent representations into two dimensions which could then be visualized. In order to avoid modeling noise, this step was used to inspect if the model is distinguishing between variables of interest.

• In the same paragraph "Latent representation of genome" the authors write: "We observed that all training scenarios successfully utilized genome images to make predictions with the exception of Age and randomized cancer type (negative control), where the model performed poorly (Figure 2B).". Did I understand correctly that all negative controls performed poorly? How can the authors make any claims if the controls fail? In general, I was missing sufficient controls for any of their claims, but openly stating that even the most rudimentary controls fail to deliver sufficient signals raises substantial issues with their approach. A clarification would substantially improve this chapter combined with further controls.

We apologize for not stating this more clearly. Randomized cancer type was used as a negative control since we expect that model would not be able to make sense of the data if predicting randomized cancer type. As expected, the model failed to predict the randomized cancer types. This can be seen in Figure 2C, where UMAP representations (based on the latent representation of the data, the vector L) are made for each output variable. Not seeing any patterns in UMAP shows that, as expected, the model does not know how to extract useful information from “genome image” when predicting randomized cancer type (as when randomly shuffling the labels there is no genomic information to decipher). Similar patterns were observed for Age, indicating that patient age cannot be determined from the multi-omics data. Conversely, when GENIUS was trained against wGII, TP53, metastatic status, and cancer type, we observed that samples clustered according to the output label.

Reviewer #2 (Public Review):

In this manuscript, Birkbak and colleagues use a novel approach to transform multi-omics datasets in images and apply Deep Learning methods for image analysis. Interestingly they find that the spatial representation of genes on chromosomes and the order of chromosomes based on 3D contacts leads to best performance. This supports that both 1D proximity and 3D proximity could be important for predicting different phenotypes. I appreciate that the code is made available as a github repository. The authors use their method to investigate different cancers and identify novel genes potentially involved in these cancers. Overall, I found this study important for the field.

The major points of this manuscript could be grouped in three parts:

1) While the authors have provided validation for their model, it is not always clear that best approaches have been used.

a) In the methods there is no mention of a validation dataset. I would like to see the authors training on a cancer from one cohort and predict on the same cancer from a different cohort. This will convince the reader that their model can generalise. They do something along those lines for the bladder cancer, but no performance is reported. At the very least they should withhold a percentage of the data for validation. Maybe train on 100 and validate on the remaining 300 samples. They might have already done something along these lines, but it was not clear from the methods.

Apologize for not being sufficiently clear in the manuscript. We did indeed validate the performance within the TCGA cohort, using holdout cross validation. Here, we trained the network on 75% of the cohort samples (N = 3825), and tested on the remaining 25% (N = 1276).

To make this more clear, we have rewritten section “GENIUS classification identifies tumors likely to become metastatic” as such:

"The omics data types included somatic mutations, gene expression, methylation, copy number gain and copy number loss. Using holdout type cross-validation, where we split the data into training (75%) and validation (25%), we observed a generally high performance of GENIUS, with a validation AUC of 0.83 for predicting metastatic disease (Figure 2B)."

We also added the following sentence in the legend of Figure 2:

"The x-axis represents epochs and y-axis represents AUC score of fixed 25% data we used for accuracy assessment within TCGA cohort."

The accuracy of GENIUS could not be validated on the other two bladder cohorts since they do not contain all the data for the creation of five-dimensional genome images. However, we were able to investigate if the genes with the highest attribution scores towards metastatic bladder cancer obtained based on the TCGA samples also showed a significant association with poor outcome in the two independent bladder cancer cohorts. Here, we observed that of the top 10 genes with the highest attribution scores, 5 were associated with poor outcome in the early stage bladder cancer cohort, and 7 were associated with poor outcome in the late stage/metastatic bladder cancer cohort.

b) It was not clear how they used "randomised cancer types as the negative control". Why not use normal tissue data or matched controls?

In the study, we built six models, one for each variable of interest. One of them was cancer type which performed quite well. In order to assess the model on randomized data, we randomized the labels of cancer type and tried predicting that. This served as “negative control” since we expected the model to perform poorly in this scenario. To make this more clear in the manuscript, we have expanded the description in the main text. We have also added the description of this to each supplementary plot to clarify this further.

While normal tissue and matched controls would have been an optimal solution, unfortunately, such data is not available.

c) If Figure 2B, the authors claim they have used cross validation. Maybe I missed it, but what sort of cross validation did they use?

We apologize for not being sufficiently clear. As described above, we used holdout cross-validation to train and evaluate the model. We clarified this in the text:

"Using holdout type cross-validation, where we split the data into training (80%) and validation (20%), we observed a generally high performance of GENIUS, with a mean validation AUC of 0.83 (Figure 2B)"

2) Potential improvement to the method

a) It is very encouraging the use of HiC data, but the authors used a very coarse approach to integrate it (by computing the chromosome order based on interaction score). We know that genes that are located far away on the same chromosome can interact more in 3D space than genes that are relatively close in 1D space. Did the authors consider this aspect? Why not group genes based on them being located in the same TAD?

We thank the reviewer for this suggestion and we will start looking into how to use TAD information to create another genome representation. In this study, we tried several genome transformations, which proved to be superior compared to a flat vector of features (no transformation). We are aware that squared genome transformation might not be optimal, so we designed the network that reconstructs the genome image during the training. This way, the genome image is optimized for the output variable of choice by the network itself. However, we note that the order of the genes themselves, while currently based on HiC, can be changed by the user. The order is determined by a simple input file which can be changed by the user with the argument “all_genes_included”. Thus, different orderings can be tested within the overall square layout. This is now detailed in the instructions on the new GitHub page.

The convolutional neural network uses a kernel size of 3x3, which captures the patterns of genes positioned close to each other but also genes that are far away from each other (potentially on another chromosome). Once convolutions extract patterns from the image, the captured features are used in a feed-forward neural network that makes a final prediction using all extracted features/patterns regardless of their location in the genome image.

We also inserted the following sentence in discussion:

"Given that spatial organization improved the prediction, we recognize that there may exist a more optimal representation of multi-omics data which should be explored further in future work. Potential methods for organizing gene orientation in a 2D image could consider integrating topologically associating domains[39] along with the spatial information from HiC. This is already possible to explore with the current implementation of GENIUS, where gene layout can be set manually by the user."

b) Authors claim that "given that methylation negatively correlates with gene expression, these were considered together". This is clearly not always the case. See for example https://genomebiology.biomedcentral.com/articles/10.1186/s13059-022-02728-5. What would happen if they were not considered together?

We thank the reviewer for this insightful comment. We agree with the reviewer that methylation does not always result in lower expression, although methylation levels in most cases should correlate negatively to RNA expression, but with a gene-specific factor. Indeed, there are tools developed that infer RNA expression based on methylation, making use of gene-specific correction factors. E.g. Mattesen et al (Mattesen, Andersen, and Bramsen 2021).

However, upon reflection we agree with the reviewer that we cannot assume for all genes that methylation equals low expression. Therefore, we have performed an analysis where we compared the methylation level to gene expression levels for all tested genes within bladder cancer. We computed Pearson’s correlation of 16,456 genes that have both methylation and expression scores. Of these, 8528 showed a negative correlation. After p-value correction, this resulted in 4774 genes where methylation was significantly negatively associated with expression. For these genes we performed the subsequent analysis in bladder cancer, where methylation and expression were considered together. This updated analysis has been included in supplementary figure 10, and the results section has been amended to reflect this. Overall, this analysis resulted in 4 of 10 genes being replaced in the downstream analysis. However, we note that the final results did not materially change, nor did the conclusions.

Author response image 2.

Correlation between gene-level methylation and gene expression in TCGA BLCA cohort

3) Interesting results that were not explained.

a) In Figure 3A methylation seems to be the most important omics data, but in 3B, mutations and expression are dominating. The authors need to explain why this is the case.

We apologize for not explaining this in more detail. Figure 3B shows the attribution scores scaled within the cancer type, where Figure 3A shows raw attribution scores for each data source included. The reason for this is that methylation and expression have in general, smaller attribution scores but more events where a single mutation often is characterized with large attribution scores and the rest of them with very small attribution. In order to make those numbers comparable and take into account biological differences between the cancer type, we scaled the scores within each cancer type.

To make this more clear we modified the first sentence in “Interpreting the GENIUS model classifying metastatic cancer biology” section:

"Analysing raw attribution scores we concluded the most informative data type overall regarding the development of metastatic disease was methylation (Figure 3A). …We also noticed that mutation data often had a single mutation with large attribution score where expression and methylation showed multiple genes with high attribution scores… … The normalization step is crucial to make results comparable as underlying biology is different in each cancer type included in the study."  

Reviewer #1 (Recommendations For The Authors):

• While I appreciate the creative acronym of the presented software solution (GENIUS), it may easily be confused with the prominent software Geneious | Bioinformatics Software for Sequence Data Analysis which is often employed in molecular life science research. I would suggest renaming the tool.

We appreciate the comment but prefer to keep the name. Given that the abbreviation is not exactly the same and the utility is different, we are confident that there will be no accidental mixup between these tools.

• A huge red flag is the evaluation of the input image design which clearly shows that classification power after training is insufficient for three out of four image layouts (and even for the fourth AUC is between 0.70-0.84 depending on the pipeline step and application). Could the authors please clarify why this isn't cherry-picking (we use the one layout that gave some form of results)? In light of the poor transformation capacity of this multi-omics data onto images, why weren't other image layouts tried and their classification performance assessed? Why should a user assume that this image layout that worked for this particular input dataset will also work with other datasets if image transformation is performing poorly in most cases?

We apologize for not describing this further in the manuscript. We wrote in the manuscript that we could not know what genome representation is optimal as it is difficult to know. A flat vector represents a simple (or no) transformation since we simply take all of the genes from all of the data sources and append them into a single list. Chromosome image and square image are two transformations we tried, and we focused on the square image since in our hands it showed superior performance relative to other transformations.

Reviewer #2 (Recommendations For The Authors):

Minor points:

1) Legends of supplementary Figures are missing.

We thank the reviewer for this comment and apologize for missing it. All legends have been added now.

2) For some tests the authors use F1 score while for other AUC, they should be consistent. Report all metrics for all comparisons or report one and justify why that only metric.

We apologize for not being sufficiently clear. AUC is a standard score used for binary classification, while the F1 score is used for multiclass classification. We have now described this in the methods section, and hope this is now sufficiently clear.

"When predicting continuous values, the model used the output from the activation function with the mean squared error loss function. When predicting multi-class labels, the performance measure was defined by the F1 score, a standard measure for multiclass classification that combines the sensitivity and specificity scores and is defined as the harmonic mean of its precision and recall. To evaluate model performance against the binary outcome, ROC analysis was performed, and the area under the curve (AUC) was used as the performance metric."

3) not sure how representation using UMAP in Figure 2C is helping understand the performance.

Apologies for the poor wording in the results section. The purpose of the UMAP representation was to visually inspect if the model was distinguishing between variables of interest, not to estimate model performance. We have rephrased the text in the methods section to make this clear:

"After successful model training, we extracted the latent representations of each genome and performed the Uniform Manifold Approximation and Projection (UMAP) of the data for the purpose of visual inspection of a model."

And

"In order to avoid modeling noise, this step was used to inspect if the model is distinguishing between variables of interest."

And also in the results section:

"In order to visually inspect patterns captured by the model, we extracted the latent representations of each genome and performed the Uniform Manifold Approximation and Projection (UMAP) of the data to project it into two dimensions."

4) Instead of pie chart in 3A, the authors should plot stacked barplots (to 100%) so it would be easier to compare between the different cancer types.

We thank the reviewer for the suggestion; however, since we wanted to compare the relative impact of each data source with each other, we used pie charts. Piecharts are often better for describing relative values, whereas bar plots are better for absolute values.

References

Du, Ruishan, Wenhao Liu, Xiaofei Fu, Lingdong Meng, and Zhigang Liu. 2022. “Random Noise Attenuation via Convolutional Neural Network in Seismic Datasets.” Alexandria Engineering Journal 61 (12): 9901–9.

Jang, Hojin, Devin McCormack, and Frank Tong. 2021. “Noise-Trained Deep Neural Networks Effectively Predict Human Vision and Its Neural Responses to Challenging Images.” PLoS Biology 19 (12): e3001418.

Mattesen, Trine B., Claus L. Andersen, and Jesper B. Bramsen. 2021. “MethCORR Infers Gene Expression from DNA Methylation and Allows Molecular Analysis of Ten Common Cancer Types Using Fresh-Frozen and Formalin-Fixed Paraffin-Embedded Tumor Samples.” Clinical Epigenetics 13 (1): 20.

Author Response

Joint Public Review

“Using computational modeling, this manuscript explores the effect of growth feedback on the performance of gene networks capable of adaptation. The authors selected 425 hypothetical synthetic circuits that were shown to achieve nearly perfect adaptation in two earlier computational studies (see Ma et al. 2009, and Shi et al. 2017). They examined the effects of cell growth feedback by introducing additional terms to the ordinary differential equation-based models, and performed numerical simulations to check the retainment and the loss of the adaptation responses of the circuits in the presence of growth feedback. The authors show that growth feedback can disrupt the gene network adaptation dynamics in different ways, and report some exceptional core motifs which allow for robust performance in the presence of growth feedback. They also used a metric to establish a scaling law between a circuit robustness measure and the strength of growth feedback. These results have important implications in the field of synthetic biology, where unforeseen interactions between designed gene circuits and the host often disrupt the desired behavior. The paper’s conclusions are supported by their simulation results, although these are presented in their summary formats and it would be useful for the community if the detailed results for each topology were available as a supplementary file or through the authors’ GitHub repository.”

We will update our GitHub repository with detailed results for each topology, along with other simulation details and results that might be of interest to the readers.

Strengths: “This work included a detailed investigation of the reasons for adaptation failure upon introducing cell growth to the systems. The comprehensiveness of the analysis makes the work stand out among studies of functional screening of network topologies of gene regulation.” “The authors’ approaches for assessment of robustness, such as the survival ratio Q, can be useful for a wide range of topologies beyond adaptation. The scaling law obtained with those approaches is interesting.”

We are grateful to the referees and editors for their positive assessment of our work.

Weaknesses 1: “The title suggests that the work investigates the ’effects of growth feedback on gene circuits’. However, the performance of ’nearly perfect adaptation’ was chosen for the majority of the work, leaving the question of whether the authors’ conclusion regarding the effects of growth feedback is applicable to other functional networks.”

We will change the title of the paper from “Effects of growth feedback on gene circuits: A dynamical understanding” to “Effects of growth feedback on adaptive gene circuits: A dynamical understanding,” because the focus of our current work was on gene circuits with adaptation. Our work provided a framework that can be readily generalized to investigate the effects of growth feedback in other functional networks such as bistable gene circuits.

Weaknesses 2: “This work relies extensively on an earlier study, evaluating only a selected set of 425 topologies that were shown to give adaptive responses (Shi et al., 2017). This limited selection has two potential issues. First, as the authors mentioned in the introduction, growth feedback can also induce emerging dynamics even without existing function-enabling gene circuits, as an example of the ”effects of growth feedback on gene circuits”. Limiting the investigation to only successful circuits for adaptation makes it unclear whether growth feedback can turn the circuits that failed to produce adaptation by themselves into adaptation-enabling circuits. Secondly, as the Shi et al. (2017) study also used numerical experiments to achieve their conclusions about successful topologies, it is unclear whether the numerical experiments in the present study are compatible with the earlier work regarding the choice of equation forms and ranges of parameter values. The authors also assumed that all readers have sufficient understanding of the 425 topologies and their derivation before reading this paper.”

We will make the following revisions.

1. We will modify the title of the paper as discussed above. The reviewers/editors are insightful that growth feedback could turn a non-adaptive circuit into an adaptation-enabling one - an interesting possibility worth further study.

2. We will provide details of all the pertinent numerical simulations, highlighting the differences from those in the previous work (Shi et al., 2017). Briefly, our adaptation criteria are stricter than those utilized in that work. As a result, out of the 425 topologies, random sampling based on our criteria identified adaptation in 414 topologies. For the remaining 11 topologies, either our more strict criteria have eliminated the possibility for the gene circuits to be adaptive, or the adaptive region in the high-dimensional parameter space is too small to be detected by random sampling.

3. We will describe the 425 topologies utilized in our study and provide more detail in the GitHub repository, including the topological structures and the parameter sets leading to adaptation.

Weaknesses 3: “The authors’ model does not describe the impact of growth via a biological mechanism: they model growth as an additional dilution rate and calculate growth rate based on a phenomenological description with growth rate occurring at a maximum (kg) scaled by the circuit ’burden’ b(t). Therefore, the authors’ model does not capture potential growth rate changes in parameter values (e.g., synthetic protein production falls with increasing growth rate; see Scott & Hwa, 2023).”

We considered dilution due to cell growth as the dominant factor of growth feedback. In fact, we studied the adaptive circuits without growth and their ability to maintain their adaptive behaviors after dilution into a fresh medium, based on a recent work [Zhang, et al., Nature Chemical Biology 16.6 (2020): 695-701]. A higher growth rate can change synthetic protein production. However, the dynamic roles of the dilution and growth-affected production rate should be analogous, given that they both act as inhibitory factors arising from cell growth as mentioned by the reviewers/editors. Taking the growth effect on the production rate into account would require a more comprehensive study. We will elaborate on the limitation of our modeling framework and include the pertinent references (e.g., Scott & Hwa, 2023).

Weaknesses 4: “The authors made several claims about the bifurcations (infinite-period, saddle-node, etc) underlying the abrupt changes leading to failures of adaptations. There is a lack of evidence supporting these claims. Both local and global bifurcations can be demonstrated with semi-analytic approaches such as numerical continuation along with investigations of eigenvalues of the Jacobian matrix. The claims based on ODE solutions alone are not sound.”

We will add this material to our next version of the paper. A further semi-analytic analysis can better justify the numerically discovered bifurcations.

Weaknesses 5: “The impact of biochemical noise is not evaluated in this work; the author’s analysis is only carried out in a deterministic regime.”

Our work focused on uncovering the deterministic dynamical mechanisms underlying growthfeedback induced circuit failures in situations where all protein concentrations are high so that neglecting the effects of biochemical noises can be justified. Incorporating noises into our analysis will significantly complicate the study and likely prevent the dynamical origin of the failures from being unveiled. Nonetheless, the effects of biochemical noises are important and we will provide a discussion in the revised manuscript.

Author Response

We would like to express our sincere gratitude for the detailed examination of our manuscript titled "Specific Modulation of CRISPR Transcriptional Activators through RNA-Sensing Guide RNAs in Mammalian Cells and Zebrafish Embryos." We deeply appreciate the time and effort put into the review process, especially considering the unforeseen delays. Your insightful comments and recommendations have provided critical perspectives that we believe will significantly enhance the quality of our work. In this letter, we will address the reviewers' concerns and outline the revisions we will make in response to the feedback.

eLife assessment

The authors aim to develop a CRISPR system that can be activated upon sensing an RNA. As an initial step to this goal, they describe RNA-sensing guide RNAs for controlled activation of CRISPR modification. Many of the data look convincing and while several steps remain to achieve the stated goal in an in vivo setting and for robust activation by endogenous RNAs, the current work will be important for many in the field.

We wish to acknowledge and thank you for the thoughtful eLife assessment, which succinctly summarizes our ambition to create a CRISPR system controlled by RNA sensing. The synopsis provided encapsulates the essence of our research, emphasizing both the progress we have made and the challenges that lie ahead. This assessment fully resonates with our views.

Reviewer #1 (Public Review):

This paper describes RNA-sensing guide RNAs for controlled activation of CRISPR modification. This works by having an extended guide RNA with a sequence that folds back onto the targeting sequence such that the guide RNA cannot hybridise to its genomic target. The CRISPR is "activated" by the introduction of another RNA, referred to as a trigger, that competes with this "back folding" to make the guide RNA available for genome targeting. The authors first confirm the efficacy of the approach using several RNA triggers and a GFP reporter that is activated by dCas9 fused to transcriptional activators. A major potential application of this technique is the activation of CRISPR in response to endogenous biomarkers. As these will typically be longer than the first generation triggers employed by the authors they test some extended triggers, which also work though not always to the same extent. They then introduce MODesign which may enable the design of bespoke or improved triggers. After that, they determine that the mode of activation by the RNA trigger involves cleavage of the RNA complexes. Finally, they test the potential for their system to work in a developmental setting - specifically zebrafish embryos. There is some encouraging evidence, though the effects appear more subtle than those originally obtained in cell culture.

Overall, the potential of a CRISPR system that can be activated upon sensing an RNA is high and there are a myriad of opportunities and applications for it. This paper represents a reasonable starting point having developed such a system in principle.

The weakness of the study is that it does not demonstrate that the system can be used in a completely natural setting. This would require an endogenous transcript as the RNA trigger with a clear readout. Such an experiment would clearly strengthen the paper and provide strong confidence that the method could be employed for one of the major applications discussed by the authors. The zebrafish data relied on exogenous RNA triggers whereas the major applications (as I understood them) would use endogenous triggers.

Related, most endogenous RNAs are longer than the various triggers tested and may require extensive modification of the system to be detected or utilised effectively. While additional data would clearly be beneficial, there should nevertheless be a more detailed discussion of these caveats and/or the strengths and applications of the system as it is presented (i.e. utility with synthetic triggers).

We would like to thank Reviewer #1 for the thoughtful and comprehensive analysis of our work as well as for the constructive feedback provided. We agree with the observation regarding the subtler effects in the zebrafish embryos and the reliance on exogenous RNA triggers. Indeed, the utilization of endogenous transcripts as triggers in a natural setting is a logical next step. We further acknowledge the need to delve deeper into the complexities and challenges of our system, particularly concerning the detection of endogenous RNA, thus offering valuable insights for researchers looking to adapt our system for various applications. In the final version of our paper, we will indeed discuss these challenges in detail and provide a clear path for future users who might be interested in employing this system. Our expanded discussion will encompass the considerations required for high-throughput screens, combining both quantitative and experimental approaches for identifying endogenous RNAs that could act as triggers. We will also elaborate on the potential biotech applications related to the detection of synthetic RNA triggers. This includes its use in Synthetic Biology circuit design and the implementation of logic gates for mammalian cell engineering.

Reviewer #2 (Public Review):

In this work, the authors describe engineering of sgRNAs that render Cas9 DNA binding controllable by a second RNA trigger. The authors introduce several iterations of their engineered sgRNAs, as well as a computational pipeline to identify designs for user-specified RNA triggers which offers a helpful alternative to purely rational design. Also included is an investigation of the fate of the engineered sgRNAs when introduced into cells, and the use of this information to inform installation of modified nucleotides to improve engineered sgRNA stability. Engineered sgRNAs are demonstrated to be activated by trigger RNAs in both cultured mammalian cells and zebrafish.

The conclusions made by the authors in this work are predominantly supported by the data provided. However, some claims are not consistent with the data shown and some of the figures would benefit from revision or further clarification.

Strengths:

• The sgRNA engineering in this paper is performed and presented in a systematic and logical fashion. Inclusion of a computational method to predict iSBH-sgRNAs adds to the strength of the engineering.

• Investigation into the cellular fate of the engineered sgRNAs and the use of this information to guide inclusion of chemically modified nucleotides is also a strength.

• Demonstration of activity in both cultured mammalian cells and in zebrafish embryos increases the impact and utility of the technology reported in this work.

Weaknesses:

• While the methods here represent an important step forward in advancing the technology, they still fall short of the dynamic range and selectivity likely required for robust activation by endogenous RNA.

• While the iSBH-sgRNAs where the RNA trigger overlaps with the spacer appear to function robustly, the modular iSBH-sgRNAs seem to perform quite a bit less well. The authors state that modular iSBH-sgRNAs show better activity without increasing background when the SAM system is added, but this is not supported by the data shown in Figure 3D, where in 3 out of 4 cases CRISPR activation in the absence of the RNA trigger is substantially increased.

• There is very little discussion of how the performance of the technology reported in this work compares to previous iterations of RNA-triggered CRISPR systems, of which there are many examples.

We are very grateful to the Reviewer #3 for the meticulous examination of our work, highlighting both the systematic approach in sgRNA engineering and areas for improvement. The insights offered in this review are extremely useful, and we are committed to addressing these points in the following sections of our response.

Concerning the methods falling short of the dynamic range and selectivity required for robust activation by endogenous RNA, we acknowledge this limitation and recognize the need for improvement in this area. In the final version of our manuscript, we will provide a detailed discussion on how the selection of appropriate triggers might partially improve dynamic ranges and selectivity. This includes an exploration of various strategies and considerations that may enhance the robustness of our system. Regarding the inconsistent performance of the modular iSBH-sgRNAs, as observed in Figure 3D, we recognize this discrepancy and will clarify it in the following iteration. For the concern about the lack of comparison with previous iterations of RNA-triggered CRISPR systems, we recently published a comprehensive literature review on the existing systems for activation of CRISPR in response to RNA detection (doi/full/10.1089/crispr.2022.0052). In the final version of our manuscript, we will include a comparison between our system and existing technologies, thereby addressing this valid observation.

Thank you once again to the entire review team for the meticulous examination and for your thoughtful and constructive feedback. Your insights are instrumental in refining our research, and we look forward to incorporating these changes as we finalize our manuscript.

Author Response

We are very grateful to the editors and reviewers for their valuable comments of our manuscript. We carefully consider all the comments and will provide a revised manuscript with our point-by-point responses as soon as possible. In the meantime, we will try our best to carry out additional experiments to bolster our conclusions. Here, we would like to respond provisionally to the public reviews.

We appreciate the concerns raised by Reviewer 1 regarding the identification of cell types in our study. Specifically, they noted that the high proportion of NSCs within the astroglial lineage clusters is inconsistent with classic histology studies. We apologize for not clearly specifying in the text and figure legend that the data presented in Figure 2C were obtained from neonatal samples, which may explain the higher presence of NSCs. To rectify this issue, we will revise the text to ensure clarity regarding the age group from which the data in Figure 2C were obtained. Additionally, we commit to providing additional UMAP plots and quantitative analysis separately for different age groups to support our findings. This will allow a more accurate representation of the cell type composition, taking into consideration any potential variations that may occur with age.

We appreciate Reviewer 2's acknowledgment that the finding of our study is interesting and relevant to a broader audience. However, he raised two major concerns that could weaken the conclusions drawn from our study. First, the reviewer noted that the number of sequenced nuclei in our study is lower than the calculated number required for detecting rare cell types. We noticed that according to the computational modeling conducted by Tosoni et al. (Neuron, 2023), at least 21 neuroblast cells (NBs) can be identified out of 30,000 granule cells (GCs) from a total of 180,000 dentate gyrus (DG) cells. In our dataset, we sequenced 24,671 GC nuclei and 92,966 total DG cell nuclei, which also includes neonatal samples. The number of nuclei we sequenced is 4.5 times higher than that of Wang et al. (Cell Research, 2022), who also detected NBs. Therefore, it is reasonable to conclude that we were able to detect NBs. Moreover, the presence of these rare cell types has been demonstrated in our study through immunostaining techniques, which provides further evidence. Secondly, Reviewer 2 raised concerns about the low number of donors included in some of the groups, with only one donor (n=1) being represented in certain cases. We acknowledge these limitations and understand that the inclusion of a larger number of donors would strengthen the statistical power and generalizability of our findings. However, due to the scarcity of stroke or neonatal human samples, it is not feasible to collect a larger sample size within the expected timeframe. Although one sample is not enough to show the precise changes in cells and molecular mechanisms caused by stroke, it can provide a typical example to demonstrate our hypothesis that neural stem cells could be activated under conditions of injury. The latter is what we really want to address in the manuscript. Regrading to the donor’s information, we will provide more details about the donors, including any clinical characteristics available, to enhance the transparency of our study. Importantly, we have implemented strict quality control measures to support the reliability of our sequencing data. These measures include: 1) Immediate collection of tissue samples after postmortem (3-4 hrs) to ensure the quality of isolated nuclei. 2) Only nuclei expressing more than 200 genes but fewer than 5000-8600 genes (depending on the peak of enrichment genes) were considered. On average, each cell detected around 3000 genes. 3) The average proportion of mitochondrial genes in each sample was approximately 1.8%, with no sample exceeding 5%.

Author Response:

Reviewer #1 (Public Review):

Summary:<br /> In this study, the authors generate a Drosophila model to assess disease-linked allelic variants in the UBA5 gene. In humans, variants in UBA5 have been associated with DEE44, characterized by developmental delay, seizures, and encephalopathy. Here, the authors set out to characterize the relationship between 12 disease-linked variants in UBA5 using a variety of assays in their Drosophila Uba5 model. They first show that human UBA5 can substitute all essential functions of the Drosophila Uba5 ortholog, and then assess phenotypes in flies expressing the various disease variants. Using these assays, the authors classify the alleles into mild, intermediate, and severe loss-of-function alleles. Further, the authors establish several important in vitro assays to determine the impacts of the disease alleles on Uba5 stability and function. Together, they find a relatively close correlation between in vivo and in vitro relationships between Uba5 alleles and establish a new Drosophila model to probe the etiology of Uba5-related disorders.

Strengths:<br /> Overall, this is a convincing and well-executed study. There is clearly a need to assess disease-associated allelic variants to better understand human disorders, particularly for rare diseases, and this humanized fly model of Uba5 is a powerful system to rapidly evaluate variants and relationships to various phenotypes. The manuscript is well written, and the experiments are appropriately controlled.

Reviewer #2 (Public Review):

Relative simplicity and genetic accessibility of the fly brain make it a premier model system for studying the function of genes linked to various diseases in humans. Here, Pan et al. show that human UBA5, whose mutations cause developmental and epileptic encephalopathy, can functionally replace the fly homolog Uba5. The authors then systematically express in flies the different versions of the gene carrying clinically relevant SNPs and perform extensive phenotypic characterization such as survival rate, developmental timing, lifespan, locomotor and seizure activity, as well as in vitro biochemical characterization (stability, ATP binding, UFM-1 activation) of the corresponding recombinant proteins. The biochemical effects are well predicted by (or at least consistent with) the location of affected amino acids in the previously described Uba5 protein structure. Most strikingly, the severity of biochemical defects appears to closely track the severity of phenotypic defects observed in vivo in flies. While the paper does not provide many novel insights into the function of Uba5, it convincingly establishes the fly nervous system as a powerful model for future mechanistic studies.

One potential limitation is the design of the expression system in this work. Even though the authors state that "human cDNA is expressed under the control of the endogenous Uba5 enhancer and promoter", it is in fact the Gal4 gene that is expressed from the endogenous locus, meaning that the cDNA expression level would inevitably be amplified in comparison. The fact that different effects were observed when some experiments were performed at different temperatures (18 vs. 25) is also consistent with this. While I do not think this caveat weakens the conclusions of this paper, it may impact the interpretation of future experiments that use these tools, and thus should be clearly discussed in the paper. Especially considering the authors argue that most disease variants of UBA5 are partial loss-of-functions, the amplification effect could potentially mask the phenotypes of milder hypomorphic alleles. If the authors could also show that the T2A-Gal4 expression pattern in the brain matches well with that of endogenous RNA or protein (e.g. using HCR-FISH or antibody), it would help to alleviate this concern.

We thank the reviewer for pointing out this limitation.

Regarding the humanization strategy we used in the study, we agree that this is a binary system which may lead to overexpression of the target protein. However, as the

reviewer also points out, this temperature-sensitive system also enables us to flexibly adjust the expression level of the target protein, which is especially useful to study

partial LoF variants such as the UBA5 variants in this study. In our study we have successfully compared the relevant allelic strength of most of the variants, which

supports the use of our system in future studies. However, we do agree that the gene dosage effect could vary widely, so it is difficult to directly predict the effects of one variant in humans based upon results obtained in a model organism.

We agree with the reviewer that a masking effect may exist in our system due to its gene overexpression nature. However, we cannot conclude that this masking effect

really affects the interpretation of Group IA variants in our tests. The three variants are mild LoF, which is also supported by the biochemical assays. Hence, the variants may not cause any phenotype even when they are expressed at a physiological level.

Regarding the temporal and spatial expression pattern of the T2A-GAL4, the Bellen lab has generated T2A-GAL4 lines for more than 3,000 genes. The expression pattern of the vast majority of these GAL4 lines faithfully reflects the expression pattern of the endogenous genes, which has been documented in our previous publications (PMIDs 25824290, 29565247, 31674908, 35723254).

Reviewer #3 (Public Review):

Summary:<br /> Variants in the UBA5 gene are associated with rare developmental and epileptic encephalopathy, DEE44. This research developed a system to assess in vivo and in vitro genotype-phenotype relationships between UBA5 allele series by humanized UBA5 fly models and biochemical activity assays. This study provides a basis for evaluating current and future individuals afflicted with this rare disease.

Strengths:<br /> The authors developed a method to measure the enzymatic reaction activity of UBA5 mutants over time by applying the UbiReal method, which can monitor each reaction step of ubiquitination in real time using fluorescence polarization. They also classified fruit fly carrying humanized UBA5 variants into groups based on phenotype. They found a correlation between biochemical UBA5 activity and phenotype severity.

Weaknesses:<br /> In the case of human DEE44, compound heterozygotes with both loss-of-function and hypomorphic forms (e.g., p.Ala371Thr, p.Asp389Gly, p.Asp389Tyr) may cause disease states. The presented models have failed to evaluate such cases.

We agree with the reviewer that our model did not reflect the situation of the individuals who are compound heterozygous for a Group IA variant (p.Ala371Thr, p.Asp389Gly, or p.Asp389Tyr) and a strong LoF variant. However, we argue that our results do show that the Group IA variants alone do not cause disease. As discussed in the manuscript, individuals homozygous for the p.Ala371Thr variant are healthy and do not present with obvious phenotype. This is consistent with our findings in flies, and shows that the p.Ala371Thr variant is a mild LoF variant.

Author Response

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

We greatly appreciate the thoughtful suggestions made by the Reviewers. We have addressed all of their comments below, with our responses bulleted and in italics. We believe these changes have helped clarify the manuscript and strengthen it overall.

Reviewer 1

1) Figures 1B and Supp. Figure 1A: It would be worth mentioning that the wave-form in the 129 strain in response to QLA starts out like AJ and B6, but transitions to looking like the wild-derived strain. So, although not quite as drastic as the NZO and NOD strains, it is not quite like the other classical inbred strains.

• We thank the reviewer for pointing this out. We have added further language to clarify the point:

“Additionally, even with the clear separation between the clusters, inter-strain variation was still observed within the clusters (e.g. more 129 islets had plateau responses to 8G/QLA than the B6 or AJ).”

2) The figures are generally excellent and really help to clarify the work in the paper. For Figure 2A, it would help even further if you could number the six different Ca++ parameters that are measured. They're all there, but it takes a bit of time to find them on the figure and numbering will make it easier on your reader.

• We appreciate this suggestion and have implemented it in our revised Figure 2A. The Ca2+ parameters are now numbered, and the description of this figure has been adjusted accordingly in the results section.

We added the revised text in the results section:

“To elucidate strain differences in Ca2+ dynamics, we focused on six parameters of the Ca2+ waveform (Figure 2A): 1) peak Ca2+ (the top of each oscillation); 2) period (the length of time between two peaks); 3) active duration (the length of time for each Ca2+ oscillation measured at half of the peak height, also known the oxidative “secretory” phase, or “MitoOx” (8); 4) pulse duration (active duration plus extra time for Ca2+ extrusion); 5) silent duration (the electrically-silent “triggering” phase, also known as “MitoCat” (8), which culminates in KATP closure and membrane depolarization); and 6) plateau fraction (the active duration divided by the period, or the fraction of time spent in the active “secretory” phase).”

3) Figure 4A, B: I was expecting to see Ca++ vs insulin parameters in the different strains/sexes. In addition to the heat maps, it would be useful to see the regression plots, showing where each strain and sex falls for the insulin and Ca++ parameters.

• This is an excellent suggestion, and we have added a new Supplemental Figure 5 to provide examples of various strain/sex patterns that drive the correlations used for the heatmap and histogram in Figure 4A and B.

We added text in the results section referring to this point:

“Clustering the Ca2+ responses into distinct groups based on our observations of the waveforms (Figure 1B, Figure 4C-E, and Supplemental Figures 1 and 2) also occurs when correlating individual Ca2+ parameters to ex vivo secretion and clinical data (Supplemental Figure 5). For example, the anticorrelation between the 1st frequency component in 8G and percent insulin secreted in 8.3G/QLA (Supplemental Figure 5A) separates the classic inbred, wild-derived, and diabetes-susceptible strains into distinct groups despite the variability in the trait. Correlation between the silent duration in 8G/QLA to insulin secretion in 8.3G/QLA, likewise groups by strain (Supplemental Figure 5B). Finally, some correlations, such as that between 8G/QLA/GIP silent duration and plasma insulin at sacrifice (Supplemental Figure 5C), can be strongly influenced by outlier strains; e.g., NZO. Collectively, these data demonstrate that genetics has a profound influence on key parameters of islet Ca2+ oscillations.”

4) Please include methods for the insulin measurements collected in Fig. 4.

• Thank you for pointing out this missing information. We have clarified that prior insulin measurements (plasma insulin and ex vivo static insulin secretion that were used in Figure 4 for correlation analysis) were completed in another previously published cohort of mice (reference 17: Mitok KA, Freiberger EC, Schueler KL, Rabaglia ME, Stapleton DS, Kwiecien NW, et al. Islet proteomics reveals genetic variation in dopamine production resulting in altered insulin secretion. The Journal of biological chemistry. 2018;293(16):5860-77).

We added this new text (highlighted) to the results section to help clarify this point:

“Fasting blood glucose and insulin levels were measured in mice at 19 weeks of age, except for the NZO males which were measured at 12 weeks of age. Glucose was analyzed by the glucose oxidase method using a commercially available kit (TR15221, Thermo Fisher Scientific), and insulin was measured by radioimmunoassay (RIA; SRI13K, Millipore). This is the same assay that was used to measure plasma insulin for the previously published cohort used for the correlation analysis in Figure 4 (17).”

5) In the methods, please include details on the four conditions used for Ca++ imaging of the islets, and the timing for each condition.

• We appreciate this guidance in clarifying our manuscript, and we have now included the conditions and timing for each condition in the methods section.

We added the following text to the results section to help clarify this:

“The solutions included 8 mM glucose (8G), 8 mM glucose + 2 mM glutamine, 0.5 mM leucine, and 1.5 mM alanine (8G/QLA), 8G/QLA + 10 nM glucose-dependent insulinotropic polypeptide (8G/QLA/GIP), and 2 mM glucose (2G), each of which were kept in a 37°C water bath.”

Reviewer 2

One major critique is that the authors studied "the human orthologues of the correlated mouse proteins that are proximal to the glycemia-associated SNPs in human GWAS". This implies two assumptions - (1) human and mouse proteins do not differ in terms of islet physiology and calcium signaling; (2) the proteins proximal to the SNPs are the causal factors for functional differences, though the SNPs could affect protein/gene function distant from the SNPs.

• Thank you very much for highlighting this limitation in our study. We think this is very important to address which we have done in our discussion section.

We have added the following text to discuss this important issue:

“Our approach to merge human GWAS with our findings in mouse assumes that the glycemic-related SNPs we nominated alter the abundance or function of the human orthologues. Most SNPs that are strongly associated with phenotypes in human GWAS are noncoding, residing within introns, promoters, 3’UTRs, or intergenic regions (e.g. Figure 6). Therefore, a limitation of our approach is the assumption that SNPs regulate the gene they are proximal to, which is not always accurate (76-78). To infer a more direct link between SNPs and potential target genes, we incorporated human islet chromatin data (37). Physical contact between a region containing SNPs and a distal gene supports a regulatory role, as for ACP1 (Figure 6B). Additionally, SNPs within regions of open chromatin (ATAC-seq) and actively transcribed regions (histone markers) suggest a higher likelihood of regulating transcription factor access. While this approach does not conclusively show a link between the SNPs and expression of the orthologue for our candidate proteins, these chromatin data more strongly suggest that the orthologue expression may be regulated by the candidates’ SNPs.”

Author Response

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

In response to the eLife assessment that “the analysis of the data is inadequate”, we strongly disagree and we to point out that in fact we follow the latest IUPHAR community guidelines on bias identification and quantification (Kolb et al, 2022). These protocols are not yet being used in the RTK and FGF fields, and thus the reviewer is not familiar with them, or with the concept of ligand bias. Our responses to the technical comments start at the bottom of page 7 of this document.

We have edited the paper by adding a scaling step-by-step protocol in the Supplementary Data. We have also expanded the Discussion to help readers understand what is measured and how it is very novel. We have also changed the title of the manuscript. The edits in the Manuscript are marked in yellow. Our response to the reviewer is given below.

Question/comment: 1. Previous studies have demonstrated that the variability of signal transduction stimulated by different FGF family members originates from their preferential activation of different members of the FGFR family (Ornitz et al., 1996). For example, it was previously shown that members of the FGF8 subfamily preferentially activate FGFR3c, whereas members of the FGF4 subfamily activate FGFR1c more potently than other FGFs. Moreover, it was shown that FGF18, a member of the FGF8 subfamily, preferentially binds to and activates the FGFR3c isoform. Indeed, this can be seen in the data shown in Figure 3 in this manuscript, where maximum levels of FGFR1 pY653/4 and pFRS2 are reached at different concentrations when stimulated with increasing concentrations of each ligand in HEK293T cells.

The reviewer is correct that there are differences in the signaling of the different FGFRs, however these differences are not relevant for this work. This paper is only about FGFR1c, as this is the only FGF-receptor which is expressed in the mesenchyme of the developing limb bud (early limb bud stage, before the onset of mesenchymal condensations) and encounters different FGF ligands. In the article, we analyze the mechanism by which one FGFR recognizers and responds to three different FGFs.

The reviewer also correctly points out that differences in our work “can be seen in the data shown in Figure 3 in this manuscript, where maximum levels of FGFR1 pY653/4 and pFRS2 are reached at different concentrations when stimulated with increasing concentrations of each ligand in HEK293T cells”. This is correct, but this is a statement about the potencies of the ligands, which is just one of three characteristics we explore here, namely potencies, efficacies, and bias. To determine if ligand bias exists or not, we need to compare two ligands and two responses (such as growth arrest and ECM degradation, or pY653/4 and pFRS2 phosphorylation). Ours is the first report of ligand bias in FGFR1 signaling, and the presence of bias goes far beyond simply differences in potencies (Kolb et al, 2022). Ligand bias in FGFR1 has never been demonstrated before. In part, this is because there have been no cell lines that give us the opportunity to compare two functional responses to FGF stimulus, via just one endogenously expressed FGFR variant. Notice that the paper that the reviewer is citing, (Ornitz et al., 1996), compares only 1 (one) type of response, when induced by different ligands, i.e. proliferation, and thus cannot answer the question if ligand bias exists or not. We have edited the Discussion to emphasize this fact. We have also changed the title.

Two studies meant to characterize FGF binding to the FGFRs (Ornitz et al., 1996; Zhang et al., 2006) have defined the main rules of the FGF-FGFR interaction, such as exclusivity of the FGF3 subfamily (FGF3, FGF7, FGF10) for the ‘b’ variants of the FGFR1 and FGFR2. These studies however do not measure ligand binding. These studies were carried-out in BAF/3 cells, where the transfected FGFRs are treated with exogenous FGFs, to cause cell proliferation. As such, the studies have several limitations. In BAF/3 cells, the cell proliferation is used as a surrogate for FGF binding on FGFR. The FGFRs activate cell proliferation via RAS-ERK MAP kinase pathway. However, many other pathways of downstream signaling are initiated by FGFRs, regulating cell differentiation, migration, metabolism and apoptosis, in biological contexts. Using single cellular response (cell proliferation) as a surrogate for FGF binding to their receptors will favor FGF ligands causing cell proliferation. FGFs which have preference for other responses will incorrectly appear weakly binding and weakly activating in BAF/3 cells. Further, an FGF ligand binding with high affinity to the receptor but inducing a lower proliferative response will be recognized as a less ‘preferential’ for the particular receptor in the BAF/3 assay. Second, the significant diversity of signaling of 18 FGFs through seven FGFR variants in mammalian development suggests that many previously unappreciated nodules of FGF-FGFR signaling exist, including the recently discovered FGF signaling towards primary cilia, or interaction with insulin receptor system (Kunova Bosakova et al., 2019; Neugebauer et al., 2009; Nies et al., 2022). This diversity is not reflected in BAF/3 assay, which respond to FGFs with only one phenotype. This is why we have used the RCS cells in the manuscript. In RCS cells, at least two qualitatively different cell responses can be induced by the FGF signaling, making the cell model ideal for elucidating biased signaling.

The so called ‘binding preferences’ based on the Ornitz articles are not binding measurements and should not be used universally to describe the FGF interactions with FGFRs, because we do not know what the term really means, nor what is it based on; the molecular basis of the FGFR signaling BAF/3 is poorly characterized. In our article, we model the processes occurring in every developing mammalian limb, where three FGF ligands (FGF4, FGF8, FGF9), released by the ectoderm at the surface of the limb bud, signal to the underlying mesenchymal cell expressing just one FGF-receptor, the FGFR1c (Mariani and Martin, 2003; Tabin and Wolpert, 2007). Unlike the BAF/3 cells engineered to ectopically express one FGFR and treated by recombinant FGFs in the lab, all three FGFs are recognized by cells expressing FGFR1c, and each of the three FGFs delivers unique morphogenetic information. The mechanisms underlying differential signaling of multiple FGFs via one FGFR are poorly defined, as the term ‘preferential signaling’ does not provide mechanistic explanation. Our article is a step towards understanding the complex processes of FGF ligand recognition and response. In our article, we evaluate the potency, the efficacy, the FGFinduced FGFR1c oligomerization and downregulation, and conformation of the active FGFR1c dimers in response to FGF4, FGF8 and FGF9. We show that FGF4, FGF8, and FGF9 are biased ligands, and that bias can explain differences in FGF4, FGF8 and FGF9-mediated cellular responses in development.

References

Kolb P, Kenakin T, Alexander SPH, Bermudez M, et al. Community guidelines for GPCR ligand bias: IUPHAR review 32. Br J Pharmacol. 2022;179, 3651-3674.

Kunova Bosakova M, Nita A, Gregor T, Varecha M, et al. Fibroblast growth factor receptor influences primary cilium length through an interaction with intestinal cell kinase. Proc Natl Acad Sci U S A. 2019;116(10):4316-4325.

Mariani FV, Martin GR. Deciphering skeletal patterning: clues from the limb. Nature. 2003;423(6937):319-25.

Nies VJM, Struik D, Liu S, Liu W, et al. Autocrine FGF1 signaling promotes glucose uptake in adipocytes. Proc Natl Acad Sci U S A. 2022;119(40):e2122382119.

Neugebauer JM, Amack JD, Peterson AG, Bisgrove BW, Yost HJ. FGF signalling during embryo development regulates cilia length in diverse epithelia. Nature. 2009;458(7238):651-4.

Ornitz DM, Xu J, Colvin JS, McEwen DG, et al. Receptor specificity of the fibroblast growth factor family. J Biol Chem. 1996;271(25):15292-7.

Tabin C, Wolpert L. Rethinking the proximodistal axis of the vertebrate limb in the molecular era. Genes Dev. 2007;21(12):1433-42.

Zhang X, Ibrahimi OA, Olsen SK, Umemori H, Mohammadi M, Ornitz DM. Receptor specificity of the fibroblast growth factor family. The complete mammalian FGF family. J Biol Chem. 2006;281(23):15694-700.

Question/comment: In order to be sure that the 'biased agonist' described in this manuscript for FGF8 binding is not caused by binding preference towards different FGFR members, the authors should present data comparing cell signaling via FGFR3c stimulated by FGF4, FGF8, and FGF9.

Here, we study signaling by FGFR1, which is the only receptor that is expressed in the mesenchyme of the developing limb bud. FGFR3 is not expressed there, and thus we do not study FGFR3 in this paper. FGFR3 is important regulator of skeletal development, but is not involved in the early stages like FGFR1. When the bones are formed, FGFR3 regulates chondrocyte proliferation and differentiation in the growth plate cartilage (Colvin et al., 1996). In fact, we are currently performing experiments with FGFR3 and multiple FGF ligands, and we see that it also engages in biased signaling. However, these FGFR3 studies have no relevance to the current work and will be published separately.

The so called ‘binding preferences towards different FGFR members’, based on the Ornitz articles (Ornitz et al., 1996; Zhang et al., 2006) provides no mechanistic explanation about differential FGF signaling via the activation of a single FGFR. Our article is a step forward towards the mechanism, by demonstration, for the first time, that ‘ligand bias’ may explain differential signaling by FGF4, FGF8 and FGF9 via FGFR1c.

References

Colvin JS, Bohne BA, Harding GW, McEwen DG, Ornitz DM. Skeletal overgrowth and deafness in mice lacking fibroblast growth factor receptor 3. Nat Genet. 1996;12(4):390-7.

Ornitz DM, Xu J, Colvin JS, McEwen DG, MacArthur CA, Coulier F, Gao G, Goldfarb M. Receptor specificity of the fibroblast growth factor family. J Biol Chem. 1996;271(25):15292-7.

Zhang X, Ibrahimi OA, Olsen SK, Umemori H, Mohammadi M, Ornitz DM. Receptor specificity of the fibroblast growth factor family. The complete mammalian FGF family. J Biol Chem. 2006;281(23):15694-700.

Question/comment: 2. It is well-established that FGFR signaling by canonical FGF family members including FGF4, FGF8, and FGF9 is dependent on interactions of heparin or heparan sulfate proteoglycans (HSPG) to the ligand the receptors. Differential contributions of heparin to cell signaling mediated by FGF4, FGF8, and FGF9 binding and activation of different FGFRs expressed in RCS cells as this cell express endogenous HSPG molecules. This question should be addressed by comparing cell signaling via FGFRs ectopically expressed in BAF/3 cells (which do not possess endogenous FGFRs and HSPG) stimulated by FGF4, FGF8, and FGF9 in the absence or presence of different heparin concentrations. This approach has been applied many times in the past to explore and establish the role of heparin in control of ligand induced FGFR activation.

The work cannot be done with BAF/3 cells, since the topic of the study is ligand bias so we need to compare at least two measurable responses. In RCS cells, the two functional responses are growth arrest and extracellular matrix degradation. In BAF/3 cells, ligand stimulation leads to one single response: proliferation.

The HSPG and other sulphated proteoglycans work as low affinity FGF co-receptors. They stabilize the FGF secondary structure, present the FGFs to the FGFRs, and participate in FGFFGFR interactions (Yayon et al., 1991; Schlessinger et al., 2000; Zakrzewska et al., 2009). In the FGF field, the FGF-FGFR interaction is commonly supported by addition of exogenous heparin, which is highly sulphated glycosaminoglycan capable of full substitution of the cell-bound HSPGs in their function as low affinity FGF co-receptors.

Most cells produce proteoglycans, including BAF/3 cells. The analysis of expression of FGFR overexpressed in BAF/3 cells demonstrated that FGFR1, FGFR2 and FGFR3 migrate as proteins of approximately 130-150 kDa (Ornitz et al., 1996; Fig. 1A), which implies extensive glycosylation in Golgi. For instance, the full-length amino acid sequence for human FGFR3 is 806 residues, which on acrylamide gel migrates as a band of approximately 85 kDa; heavier FGFR3 variants are Golgi-glycosylated proteins. The treatment with de-glycosylation enzymes reduces the molecular weight to the one expected from the amino acid sequence.

To carry-out the BAF/3 experiment with FGF4, FGF8, and FGF9 in the absence or presence of different heparin concentrations, as the referee suggests, makes no sense. In BAF/3 cells, all FGF stimulations were done in the presence of 2 g/ml heparin (Ornitz et al., 1996; Zhang et al., 2006), because without heparin there would be no signaling. Even if the BAF/3 cells produce ample HSPGs, the heparin would still have to be used, because without it many of the FGFs would likely cause no response, regardless of the FGFR variant expressed. We and other have demonstrated, that most of the FGFs require stabilization by heparin to elicit signaling in cells expressing abundant amounts of HSPG (Buchtova et al., 2015; Chen et al., 2012).

Why should we compare the FGF signaling in BAF/3 transfected with FGFR1, with the RCS cells which express endogenous FGFR1? In RCS cells, several cellular phenotypes caused by FGF signaling can be easily detected and quantified, in comparison with BAF/3 cells, which only respond to the FGF signaling by proliferation. No bias in signaling can be established in cells with display only single type of response. The RCS cells used in our paper represent one of the most tractable cellular models of FGFR signaling. There are more than 40 articles exploring the mechanisms of FGF-FGFR signaling in RCS cells, including mechanisms of FGF signal transduction, FGF regulation of cell cycle, cell proliferation, differentiation, premature senescence, loss of extracellular matrix, interaction of FGF signaling with WNT, cytokine and natriuretic peptide signaling, and others (Raucci et al., 2004; Priore et al., 2006; Kamemura et al., 2017; Kolupaeva et al., 2013; Krejci et al., 2005; Krejci et al., 2007; Krejci et al., 2010; Dailey et al., 2003; Rozenblatt-Rosen et al., 2002; Fafilek et al., 2008). In addition, the three treatments to inhibit pathological FGFR signaling which are now in human trials (RBM007, meclozine) or FDAapproved (vosoritide), were initially developed in RCS cells, benefiting from the well characterized molecular mechanisms of FGF signaling (Krejci et al., 2005; Wendt et al., 2015; Kimura et al., 2021; Matsushita et al., 2013). In comparison with RCS cells, very little is known about the mechanisms of the FGF signaling in BAF/3 cells, as the BAF/3 proliferation assay is used mostly to evaluate FGFR agonists and antagonists (Yamada et al., 2020; Kamatkar et al., 2019; Motomura et al., 2008). We have edited this information to the revised Discussion.

References

Buchtova M, Oralova V, Aklian A, Masek J, et al. Fibroblast growth factor and canonical WNT/βcatenin signaling cooperate in suppression of chondrocyte differentiation in experimental models of FGFR signaling in cartilage. Biochim Biophys Acta. 2015 May;1852(5):839-50.

Buchtova M, Chaloupkova R, Zakrzewska M, Vesela I, et al. Instability restricts signaling of multiple fibroblast growth factors. Cell Mol Life Sci. 2015 Jun;72(12):2445-59.

Chen G, Gulbranson DR, Yu P, Hou Z, Thomson JA. Thermal stability of fibroblast growth factor protein is a determinant factor in regulating self-renewal, differentiation, and reprogramming in human pluripotent stem cells. Stem Cells. 2012 Apr;30(4):623-30.

Fafilek B, Balek L, Bosakova MK, Varecha M, et al. The inositol phosphatase SHIP2 enables sustained ERK activation downstream of FGF receptors by recruiting Src kinases. Sci Signal. 2018 Sep 18;11(548):eaap8608.

Kamemura N, Murakami S, Komatsu H, Sawanoi M, et al. Biochem Biophys Res Commun. 2017 Jan 29;483(1):82-87.

Kamatkar N, Levy M, Hébert JM. Development of a Monomeric Inhibitory RNA Aptamer Specific for FGFR3 that Acts as an Activator When Dimerized. Mol Ther Nucleic Acids. 2019 Sep 6;17:530-539.

Kimura T, Bosakova M, Nonaka Y, Hruba E, Yasuda K, et al. An RNA aptamer restores defective bone growth in FGFR3-related skeletal dysplasia in mice. Sci Transl Med. 2021 ;13(592):eaba4226.

Kolupaeva V, Daempfling L, Basilico C. The B55α regulatory subunit of protein phosphatase 2A mediates fibroblast growth factor-induced p107 dephosphorylation and growth arrest in chondrocytes. Mol Cell Biol. 2013 Aug;33(15):2865-78.

Krejci P, Masri B, Salazar L, Farrington-Rock C, et al. Bisindolylmaleimide I suppresses fibroblast growth factor-mediated activation of Erk MAP kinase in chondrocytes by preventing Shp2 association with the Frs2 and Gab1 adaptor proteins. J Biol Chem. 2007;282(5):2929-36.

Krejci P, Masri B, Fontaine V, Mekikian PB, et al. Interaction of fibroblast growth factor and C-natriuretic peptide signaling in regulation of chondrocyte proliferation and extracellular matrix homeostasis. J Cell Sci. 2005 Nov 1;118(Pt 21):5089-100.

Krejci P, Prochazkova J, Smutny J, Chlebova K, et al. FGFR3 signaling induces a reversible senescence phenotype in chondrocytes similar to oncogene-induced premature senescence. Bone. 2010;47(1):102-10.

Matsushita M, Kitoh H, Ohkawara B, Mishima K, et al. Meclozine facilitates proliferation and differentiation of chondrocytes by attenuating abnormally activated FGFR3 signaling in achondroplasia. PLoS One. 2013;8(12):e81569.

Motomura K, Hagiwara A, Komi-Kuramochi A, Hanyu Y, et al. An FGF1:FGF2 chimeric growth factor exhibits universal FGF receptor specificity, enhanced stability and augmented activity useful for epithelial proliferation and radioprotection. Biochim Biophys Acta. 2008 Dec;1780(12):1432-40.

Ornitz DM, Xu J, Colvin JS, McEwen DG, MacArthur CA, Coulier F, Gao G, Goldfarb M. Receptor specificity of the fibroblast growth factor family. J Biol Chem. 1996;271(25):15292-7.

Priore R, Dailey L, Basilico C. Downregulation of Akt activity contributes to the growth arrest induced by FGF in chondrocytes. J Cell Physiol. 2006 Jun;207(3):800-8.

Raucci A, Laplantine E, Mansukhani A, Basilico C. Activation of the ERK1/2 and p38 mitogen-activated protein kinase pathways mediates fibroblast growth factor-induced growth arrest of chondrocytes. J Biol Chem. 2004;279(3):1747-56.

Robinson JW, Egbert JR, Davydova J, Schmidt H, et al. Dephosphorylation is the mechanism of fibroblast growth factor inhibition of guanylyl cyclase-B. Cell Signal. 2017;40:222229.

Rozenblatt-Rosen O, Mosonego-Ornan E, Sadot E, Madar-Shapiro L, et al. Induction of chondrocyte growth arrest by FGF: transcriptional and cytoskeletal alterations. J Cell Sci. 2002 Feb 1;115(Pt 3):553-62.

Schlessinger J, Plotnikov AN, Ibrahimi OA, Eliseenkova AV, et al. Crystal structure of a ternary FGF-FGFR-heparin complex reveals a dual role for heparin in FGFR binding and dimerization. Mol Cell. 2000 Sep;6(3):743-50.

Wendt DJ, Dvorak-Ewell M, Bullens S, Lorget F, et al. Neutral endopeptidase-resistant Ctype natriuretic peptide variant represents a new therapeutic approach for treatment of fibroblast growth factor receptor 3-related dwarfism. J Pharmacol Exp Ther. 2015 Apr;353(1):132-49.

Yamada R, Fukumoto R, Noyama C, Fujisawa A, et al. An epidermis-permeable dipeptide is a potential cosmetic ingredient with partial agonist/antagonist activity toward fibroblast growth factor receptors. J Cosmet Dermatol. 2020 Feb;19(2):477-484.

Yayon A, Klagsbrun M, Esko JD, Leder P, Ornitz DM. Cell surface, heparin-like molecules are required for binding of basic fibroblast growth factor to its high affinity receptor. Cell. 1991 Feb 22;64(4):841-8.

Zakrzewska M, Wiedlocha A, Szlachcic A, Krowarsch D, et al. Increased protein stability of FGF1 can compensate for its reduced affinity for heparin. J Biol Chem. 2009 Sep 11;284(37):25388-403. doi: 10.1074/jbc.M109.001289.

Zhang X, Ibrahimi OA, Olsen SK, Umemori H, Mohammadi M, Ornitz DM. Receptor specificity of the fibroblast growth factor family. The complete mammalian FGF family. J Biol Chem. 2006;281(23):15694-700.

Question/comment: It is impossible to interpret the FGFR binding characteristics and cellular activates of FGF4, FGF8, and FGF9 in the absence of information about the role of heparin in their binding and activation.

We do not measure ligand binding to FGFR1 in this study. We record biological responses when we treat with FGF different ligands, and thus we measure the efficacy and the potency of each ligand to induce a response, and then we compare 2 ligands and 2 responses to determine if bias exists or not. We do not ask questions about the role of heparin, as it is always there no matter if we treat with FGF4, FGF8, or FGF9.

Why it is not possible to interpret our cellular data? In our article, the RCS cells were treated with FGFs in the presence of 1 g/ml heparin, as clearly stated in Methods section. Using heparin at 1 or more μg/ml, to stabilize FGFs and negate the effect of endogenous HSPG, is a standard approach in the FGF field. This includes the two articles, which the whole field have used for more than 20 years as a basic reference for FGF-FGFR interactions (Ornitz et al., 1996; Zhang et al., 2006). In these studies, 2 μg/ml of heparin along with FGFs was used to treat BAF/3 cells; no experiments were conducted without heparin, as is does not make sense. Most likely, without heparin the obtained FGF-FGFR ‘preferences’ would, in fact, be the differences in FGF thermal stability, as we clearly demonstrate in our previous study (Buchtova et al., 2015). The latter article gives a detailed information about the role of heparin in the signaling of multiple FGFs in RCS cells.

References

Buchtova M, Chaloupkova R, Zakrzewska M, Vesela I, Cela P, Barathova J, Gudernova I, Zajickova R, Trantirek L, Martin J, Kostas M, Otlewski J, Damborsky J, Kozubik A, Wiedlocha A, Krejci P. Instability restricts signaling of multiple fibroblast growth factors. Cell Mol Life Sci. 2015 Jun;72(12):2445-59.

Ornitz DM, Xu J, Colvin JS, McEwen DG, MacArthur CA, Coulier F, Gao G, Goldfarb M. Receptor specificity of the fibroblast growth factor family. J Biol Chem. 1996;271(25):15292-7. <br /> Zhang X, Ibrahimi OA, Olsen SK, Umemori H, Mohammadi M, Ornitz DM. Receptor specificity of the fibroblast growth factor family. The complete mammalian FGF family. J Biol Chem. 2006;281(23):15694-700.

Technical Comments/Answers

Question/comment: 3. It is not clear how some of the experimental data were analyzed. Blots in Figures 3A and 3B should include controls (total FGFR1 for pY653/4 and total FRS for pFRS2). How are the data shown in Figure 3C normalized? It does look like the level of phosphorylation was all normalized against the strongest signals irrespective of which ligand was used. Each data representing each ligand should be separately normalized.

The reviewer is correct that most often in the RTK literature “each data representing each ligand is separately normalized”. But this approach will eliminate all the information about ligand efficacies and about ligand bias; it will only yield information about the potencies. Here we are not only interested in the potencies, as we are also interested to determine if bias exists or not. As such, we follow scaling protocols that have been established and are currently recommended for ligand bias studies (Kolb et al, 2022).

One way to explain why the scaling that the reviewer is recommending is not correct for this work is to look at equation 2. What the reviewer is suggestion is to set all values of Etop to 1. In this case, the bias coefficient will depend only on the measured potencies, EC50. But this contradicts the very definition of bias, as it is NOT a difference in potencies only. In the literature, differences in potencies are called “quantitative differences”, while ligand bias describes differences which are called “qualitative” or “fundamental” (Kenakin, 2019).

To eliminate confusion, we have added a scaling protocol to the Supplement of the paper.

References

Kolb P, Kenakin T, Alexander SPH, Bermudez M, et al. Community guidelines for GPCR ligand bias: IUPHAR review 32. Br J Pharmacol. 2022;179, 3651-3674.

Kenakin T. Biased Receptor Signaling in Drug Discovery. Pharmacol Rev 2019;71, 267315.

Question/comment: 4. In page 6, authors used the plot shown in Figure 3 for 'FGFR downregulation' to conclude that "the effect of FGF4 on FGFR1 downregulation is smaller when compared to the effects of FGF8 and FGF9. However, it is unclear how the data shown in the plot was normalized - none of the data seem to reach "1.0". Moreover, the plot seems to suggest that FGF4 can strongly downregulate FGFR as it can downregulate FGFR with higher potency.

The Western blots assessing FGFR1 expression are easy to scale, as the value in the absence of ligand is set to 1. The expression decreases as a function of the ligand concentration. We plot FGFR1 downregulation, so we subtract 1 from the scaled FGFR1 band intensities. The total amount of FGFR1 never becomes undetectable (i.e. zero), as the ligand concentration is increased. Thus, a value of 1 in the downregulation curve is never obtained.

We have added a protocol for this scaling in the Supplement.

Question/comment: 5. The structural basis of FGFR1 ligand bias and the different dimeric configurations and interactions between the kinase domain of FGFR1 dimers are not warranted (Figure 6). In the absence of any structural experimental data of different forms of FGFR dimers stimulated by FGF ligands the model presents in the manuscript is speculative and misleading.

This statement about Figure 6 is not fully correct because Figure 6A and B show experimental data. These are FRET experiments which show that the biased ligand, FGF8, induces different FGFR1 transmembrane domain conformation, as compared to FGF4 and FGF9.

The rest of the panels in Figure 6 show modeling using PyRosetta. These are indeed not experimental data, but to the best of our knowledge this is the very first time PyRosetta has been used to predict kinase-kinase interfaces.

Author Response

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

Reviewer #1 (Public Review):

The present study examined the physiological mechanisms through which impaired TG storage capacity in adipose tissues affects systemic energy homeostasis in mice. To accomplish this, the authors deleted DGAT1 and DGAT2, crucial enzymes for TG synthesis, in an adipocyte-specific manner. The authors found that ADGAT DKO mice substantially lost the adipose tissues and developed hypothermia when fasted; however, surprisingly, ADGAT KO mice were metabolically healthy on a high-fat diet. The authors found that it was accompanied by elevated energy expenditure, enhanced glucose uptake by the BAT, and enhanced browning of white adipose tissues. This unique animal model provided exciting opportunities to identify new mechanisms to maintain systemic energy homeostasis even in a compromised energy storage capacity. Overall, the data are compelling and well support the conclusion of this paper. The manuscript is clearly written.

We thank the reviewer for the time invested to critically review our paper.

Reviewer #2 (Public Review):

Here, Chitraju et al have studied the phenotype of mice with an adipocyte-specific deletion of the diglycerol acyltransferases DGAT1 and DGAT2, the two enzymes catalyzing the last step in triglyceride biosynthesis. These mice display reduced WAT TG stores but contrary to their expectations, the TG loss in WAT is not complete and the mice are resistant to a high-fat diet intervention and display a metabolically healthier profile compared to control littermates. The mechanisms underlying this are not entirely clear, but the double knockout (DKO) animals have increased EE and a lower RQ suggesting that enhanced FA oxidation and WAT "browning" may be involved. Moreover, both adiponectin and leptin are expressed in WAT and are detectable in circulation. The authors propose that "the capacity to store energy in adipocytes is somehow sensed and triggers thermogenesis in adipose tissue. This phenotype likely requires an intact adipocyte endocrine system...." Overall, I find this to be an interesting notion.

We thank the reviewer for the time invested to critically review our paper.

Reviewer #3 (Public Review):

In this study, the authors sought to test the hypothesis that blocking triglyceride storage in adipose tissue by knockout of DGAT1 and DGAT2 in adipocytes would lead to ectopic lipid deposition, lipodystrophy, and impaired glucose homeostasis. Surprisingly, the authors found the opposite result, with DGAT1/2 DKO in adipocytes leading to increased energy expenditure, minimal ectopic lipid deposition, and improved glucose homeostasis with HFD feeding. These metabolic improvements were largely attributed to increased beiging of the white fat and increased brown adipose tissue activity. This study provides an interesting new paradigm whereby impairing fat storage, the major function of adipose tissue, does not lead to severe metabolic disease, but rather improves it. The authors provide a comprehensive assessment of the metabolism of these DKO mice under chow and HFD conditions, which support their claims. The study lacks in mechanistic insight, which would strengthen the study, but does not detract from the authors' major conclusions.

We thank the reviewer for the time invested to critically review our paper.

The conclusions of this paper are mostly well-supported, but some aspects should be clarified and extended.

1) The authors claim the beiging of WAT of ADGAT DKO mice is partially through the SNS; however, housing these mice at thermoneutrality did not block the beiging, which seems to negate that claim. Is there evidence of increased cAMP/PKA activation in the adipose tissues of ADGAT DKO to support the premise that the beiging is activated by the SNS, even at thermoneutrality? Alternatively, if the authors block beta-adrenergic receptors with antagonists, such as propranolol, does this block the beiging?

We are currently unsure of the mechanism(s) for WAT beiging and whether it requires the SNS. We attempted denervation experiments to ablate SNS input; however, the results were consistent with partial denervation and not clearly interpretable, so we elected not to include them in the manuscript. Unfortunately, we did not measure cAMP/PKA activation or utilize beta blockers in attempt to block SNS activation. Due to a recent laboratory move, there are no study mice available to perform these experiments.

2) It's been shown that autocrine FGF21 signaling is sufficient to promote beiging of iWAT (PMID 34192547). The authors show Fgf21 mRNA is increased in iWAT of chow-fed ADGAT DKO mice. Is Fgf21 also increased in iWAT of HFD-fed mice? This and measurement of local FGF21 secretion by adipocytes would strengthen this study.

We thank the reviewer for this question. Unfortunately, we did not measure Fgf21 mRNA levels in iWAT of HFD-fed mice or FGF21 secretion by adipocytes and mice are not currently available. We agree, however, that FGF21 is a candidate for mediating this phenotype. Testing this idea would likely require crossing the ADGAT DKO mice with FGF21 KO mice. Arguing against FGF21 as contributing systemically, plasma levels were similar in HF-fed ADGAT DKO mice and controls.

3) The primary adipocytes in Figure 5–figure supplement 2A do not appear to have any depletion in TG stores, suggesting this may not be an appropriate model to study the cell autonomous effects of ADGAT DKO on beiging. The authors should use DGAT inhibitors instead to corroborate or investigate this question.

We agree with the reviewer that primary adipocytes from ADGAT DKO mice may not be the best model to study the cell autonomous effects of beiging, particularly since they are accumulating lipids. On the other hand, it’s not likely that DGAT inhibitors would be any better than the genetic deletions of the enzymes. Presumably, the neutral lipids are being synthesized by enzymes other than DGAT1 or DGAT2.

4) Multiple studies have shown the importance of lipolysis for the activation of brown and beige thermogenic programs (PMID 35803907, 34048700) and can be potentiated by HFD feeding (PMID 34048700). In the absence of DGAT activity in ADGAT DKO mice, it seems plausible that free fatty acids could be elevated, especially in the context of HFD. Are free fatty acids elevated in the adipose tissues, which could promote thermogenic gene expression?

We thank the reviewer for pointing this out. Although we cannot exclude this mechanism, arguing against it, we found lower levels of almost all free fatty acid species in iWAT of chow diet fed ADGAT DKO (Figure 5–figure supplement 1, metabolomics). Additionally, plasma FFA were reduced in these mice.

5) The lack of ectopic lipid deposition in the ADGAT DKO mice is striking, especially under HFD conditions. Can the increased energy expenditure fully account for the difference in whole body fat accumulation between Control and DKO mice or have the mice activated other energy disposal mechanisms? Please discuss or include measurement of fat excretion in the feces to strengthen this study.

Although decreased lipid absorption may conceivably contribute to energy loss, we would not expect this to occur in adipocyte-specific knockout mice, and we did not measure the lipid content in the feces. We have added a discussion point to the manuscript.

Reviewer #1 (Recommendations for the Authors):

The authors wish to clarify the following points to strengthen this exciting work further.

1) The authors demonstrated that DKO mice exhibited enhanced browning of WAT even under a thermoneutral condition, and this occurred in a non-cell autonomous fashion. Accordingly, the authors suggested the possibility that SNS activity was enhanced in DKO mice. It would be intriguing to examine the extent to which lipolysis is indeed enhanced in DKO mice. For instance, do DKO mice have higher FFA and glycerol levels than controls in circulation? This could explain a part of the phenotype, as a recent work suggested that WAT lipolysis triggers beige progenitor cell proliferation in WAT.

We thank the reviewer for this question. Although this is an interesting idea, we found that ADGAT DKO mice have lower levels of free fatty acids and glycerol in the circulation, indicating lipolysis not likely the underlying mechanism for increased beiging in ADGAT DKO mice. FFA were also reduced in the iWAT of the ADGAT DKO mice (as shown in supplemental data for Figure 5).

2) The authors suggested the possibility that other candidates in the DGAT2 gene family might compensate for the lack of DGAT1 and DGAT2. It will be insightful if the authors elaborate on this part - e.g., discussing any transcriptional changes of DGAT2 family members in the WAT of DKO mice.

We thank the reviewer for this question. Previous studies showed (Yen et al., 2005), monoacylglycerol acyl transferase (MGAT) enzymes also possess some TG synthesis activity. We found increased mRNA expression of MGAT1 and MGAT2 enzymes in white adipose tissue of ADGAT DKO mice. We now included this data in Figure 1–figure supplement 1G.

3) Minor: Statistics of the AUC for the GTT and ITT (Fig. 3G and 3H).

We thank the reviewer for this point. We have now updated the figures with statistics of the AUC for GTT and ITT.

Reviewer #2 (Recommendations for the Authors):

1) The authors suggest that the DKOs are protected against a high-fat diet due to an intact endocrine function combined with increased FA oxidation and WAT browning. This phenotype is interesting but as the authors write, the underlying mechanisms remain unclear. Furthermore, how important is retained endocrine function, in relation to WAT browning, in explaining the resistance to a high-fat diet in the DKOs? As these mice are born with the double DGAT KO and it is possible that compensatory mechanisms explain some of the observed effects. What happens with the endocrine function/browning effect if DGAT1/2 is inhibited in cells that already contain full TG stores? While I understand that studies in an inducible KO model are outside the scope of this study, data in cells where the effects of DGAT inhibition are studied early and late during differentiation would be interesting and could at least be discussed.

We thank the reviewer for this interesting question. It is possible that ADGAT DKO have adipose tissue-derived factors that act in endocrine or paracrine manner to induce beiging. Unfortunately, we do not have data addressing this point, but added discussion of this point to the revised manuscript.

2) While the possibility to dissociate TG storage from the endocrine function of WAT is attractive, the authors have only studied two adipokines. Do they have data on any other adipokine(-s) supporting the claim that the secretory function is intact?

We thank the reviewer for this question. Regrettably we did not measure additional adipokines, and the mice are no longer available for study due to a recent lab move.

Reviewer #3 (Recommendations for the Authors):

Minor comments/suggestions:

1) The authors show multiple phospholipid species were increased by ADGAT DKO. Cardiolipin has been shown to promote brown fat thermogenesis (PMID 29861389). Were cardiolipin levels changed by ADGAT DKO?

We thank the reviewer for this question. We found cardiolipin levels were increased in iWAT of ADGAT DKO mice. However, we have not measured cardiolipin levels in brown fat.

2) A recent study (PMID 36914626) has shown that inhibition of lipogenesis in adipose tissue impairs autophagy and also causes beiging of white adipose tissue. Is autophagy affected by ADGAT DKO? Are de novo lipogenesis enzymes affected by the DKO?

We thank the reviewer for this interesting suggestion. We did find that mRNA levels of genes involved in de novo lipogenesis (Srebp1c, Acc, Fas) were decreased in iWAT of ADGAT DKO mice, as expected from some of our other studies involving DGAT inactivation. Unfortunately, we did not measured autophagy per se in iWAT of ADGAT DKO mice.

Author Response

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

We thank the editors and reviewers for their thoughtful consideration of our manuscript. Here, we addressed the reviewers’ points.

Reviewer #1 (Public Review):

Tomasi et al. performed a combination of bioinformatic, next-generation tRNA sequencing experiments to predict the set of tRNA modifications and their corresponding genes in the tRNAs of the pathogenic bacteria Mycobacterium tuberculosis. Long known to be important for translation accuracy and efficiency, tRNA modifications are now emerging as having regulatory roles. However, the basic knowledge of the position and nature of the modifications present in a given organism is very sparse beyond a handful of model organisms. Studies that can generate the tRNA modification maps in different organisms along the tree of life are good starting points for further studies. The focus here on a major human pathogen that is studied by a large community raises the general interest of the study. Finally, deletion of the gene mnmA responsible for the insertion of s2U at position 34 revealed defects in in growth in macrophage but in test tubes suggesting regulatory roles that will warrant further studies. The conclusions of the paper are mostly supported by the data but the partial nature of the bioinformatic analysis and absence of Mass-Spectrometry data make it incomplete. The authors do not take advantage of the Mass spec data that is published for Mycobacterium bovis (PMID: 27834374) to discuss what they find.

1) The authors say they took a list of proteins involved in tRNA modifications from Modomics and added manually a few but we do not know the exact set of proteins that were used to search the M. mycobacterium genome.

Thank you for pointing out this issue. We added the complete list of proteins used for the BLAST query as Supplemental Table 1.

2) The absence of mnmGE genes in TB suggested that the xcm5U derivatives are absent. These are present in M. bovis (PMID: 27834374). Are the MnmEG gene found in M. bovis? If yes, then the authors should perform a phylogenetic distribution analysis in the Mycobacterial clade to see when they disappeared. If they are not present in M. bovis then maybe a non-orthologous set of enzymes do the same reaction and then the authors really do not know what modification is present or not at U34 without LC-MS. The exact same argument can be given for the xmo5U derivatives that are also found in M.bovis but not predicted by the authors in M. tuberculosis.

The reviewer raises a valid point. In M. bovis mnm5U and cmo5U derivatives were observed in LC-MS analysis. However, we did not identify candidate genes known to be involved in the biogenesis of mnm5U and cmo5U in the Mycobacteriaceae, including M. bovis and Mtb, suggesting that if these modifications are indeed present, they are not synthesized through canonical biogenesis pathways in this family. There are several examples where the same modification is generated by distinct modification enzymes (Kimura, 2021). These observations raise the interesting possibility that in the Mycobacteriaceae and most species in actinomycetota (except for Bifidobacterium, Corynebacterium and Rhodococcus species), major wobble modifications are generated by biosynthesis pathways that are distinct from those employed by well-characterized organisms. Future studies will examine this hypothesis.

3) Why is the Psi32 predicted by the authors because of the presence of the Rv3300c/Psu9 gene not detected by CMC-treated tRNA seq while the other Psi residues are? Members of this family can modify both rRNA and tRNA. So the presence of the gene does not guarantee the presence of the modification in tRNAs

Thank you very much for the careful read. We did not include RluA in the list of query proteins because it is not classified as a tRNA modification enzyme in Modomics. Additionally, the CMC-coupled tRNA-seq is imperfect for detection of all pseudouridylated positions. Due to this limitation, we only assigned modifications that are both predicted by the presence of putative biosynthetic enzymes and RT-derived signatures. As the reviewer points out, we cannot rule out that this homolog targets only rRNAs. We clarified this possibility in the revised manuscript by adding the following sentence: “Additionally, CMC treatment may not identify  at all positions, thus, the targets of Rv3300 and Rv1540 remain unclear. Since these genes are similar to E. coli rluA, which also targets rRNA, these genes may target rRNAs instead of tRNAs” (lines 298-300)

In the revised manuscript, RluA was added to the BLAST query for creating Fig. 2. Interestingly, Rv3300c is more similar to Pus9 than RluA, while Rv1540 is the Mtb gene most similar to E. coli RluA suggesting that these two genes encode pseudouridylases that target different species of tRNAs/rRNAs.

4) What are tsaBED not essential but tsaC (called sua5 by the authors) essential?

Thank you for pointing out this interesting observation. We are also curious about differences in the essentiality among t6A biogenesis genes. We speculate that TsaC has critical roles in cell viability other than t6A synthesis. TsaC synthesizes threonylcarbamoyl-AMP as an intermediate for t6A biogenesis. Thus, it is possible that this intermediate has a role in other essential cellular activities besides t6A biogenesis. Further study of these factors in Mtb could reveal interesting crosstalk between modification synthesis and other cellular activities.

Reviewer #2 (Public Review):

In this study, Tomasi et al identify a series of tRNA modifying enzymes from Mtb, show their function in the relevant tRNA modifications and by using at least one deleted strain for MnmA, they show the relevance of tRNA modification in intra-host survival and postulate their potential role in pathogenesis.

Conceptually it is a wonderful study, given that tRNA modifications are so fundamental to all life forms, showing their role in Mtb growth in the host is significant. However, the authors have not thoroughly analyzed the phenotype. The growth defect aspect or impact on pathogenesis needs to be adequately addressed.

• The authors show that ΔmnmA grows equally well in the in vitro cultures as the WT. However, they show attenuated growth in the macrophages. Is it because Glu1_TTC and Gln1-TTG tRNAs are not the preferred tRNAs for incorporation of Glu and Gln, respectively? And for some reason, they get preferred over the alternate tRNAs during infection? What dictates this selectivity?

Thank you very much for raising this excellent point. As the reviewer suggests, the attenuation of ΔmnmA Mtb growth inside of macrophages could be caused by disparate codon usage between genes required for in vitro growth and intracellular growth. Among multiple codons encoding Glu, Gln, or Lys, s2U modification-dependent codons might be preferentially distributed in genes associated with intracellular growth. For example, Mtb has two tRNA isoacceptors, Glu1_TTC and Glu2_CTC, to decipher two Glu codons, GAA and GAG. According to the wobble pairing rule, GAA is only decoded by Glu1_TTC, whereas GAG is decoded by both Glu1_TTC and Glu2_CTC; i.e., GAG can be deciphered by an s2U-independent tRNA. Thus, genes required for intracellular growth might be enriched with GAA, an s2U-dependent codon. Similar codon usage differences could be present in Gln and Lys codons deciphered by s2U-containing tRNAs. In the revised manuscript, we included a new paragraph in the discussion explaining the possibility that differences in codon usage could contribute to the intracellular fitness defect of the ΔmnmA Mtb mutant (lines 323-332).

• As such the growth defect shown in macrophages would be more convincing if the authors also show the phenotype of complementation with WT mnmA.

The reviewer raises a valid point. We note however, that Rv3023c, a putative transposase, is downstream of MnmA and unlike MnmA, Rv3023c appears to be dispensable for in vivo growth, according to the Tn-seq database (reference 44 and 45). Therefore, it is likely that the intracellular growth defect is caused by loss of mnmA.

An important consideration here is the universal nature of these modifications across the life forms. Any strategy to utilize these enzymes as the potential therapeutic candidate would have to factor in this important aspect.

This is a valid point. Targeting a pathogen-specific system enables avoidance of the adverse side effects caused by many therapeutic reagents. There are a couple of Mtb modification enzymes that are specific to bacteria and critical for Mtb fitness (e.g., TilS). These enzymes represent ideal potential therapeutic targets to impede Mtb intracellular growth.

Reviewer #3 (Public Review):

The work presented in the manuscript tries to identify tRNA modifications present in Mycobacterium tuberculosis (Mtb) using reverse transcription-derived error signatures with tRNA-seq. The study identified enzyme homologs and correlates them with presence of respective tRNA modifications in Mtb. The study used several chemical treatments (IAA and alkali treatment) to further enhance the reverse transcription signals and confirms the presence of modifications in the bases. tRNA modifications by two enzymes TruB and MnmA were established by doing tRNA-seq of respective deletion mutants. Ultimately, authors show that MnmA-dependent tRNA modification is important for intracellular growth of Mtb. Overall, this report identifies multiple tRNA modifications and discuss their implication in Mtb infection.

Important points to be considered:

• The presence of tRNA-based modifications is well characterised across life forms including genus Mycobacterium (Mycobacterium tuberculosis: Varshney et al, NAR, 2004; Mycobacterium bovis: Chionh et al, Nat Commun, 2016; Mycobacterium abscessus: Thomas et al, NAR, 2020). These modifications are shown to be essential for pathogenesis of multiple organisms. A comparison of tRNA modification and their respective enzymes with host organism as well as other mycobacterium strains is required. This can be discussed in detail to understand the role of common as well as specific tRNA modifications implicated in pathogenesis.

The reviewer raises a fair point. However, with the exception of Chionh et al., the other studies cited here are not genome-wide characterization of tRNA modification. Re-analysis showed that the distribution of the tRNA modifying enzymes are very similar across mycobacterium strains, e.g., Mycobacterium smegmatis, Mycobacterium tuberculosis, and Mycobacterium abscessus, suggesting that modifications related to pathogenesis in Mtb may have different physiological roles in other Mycobacterium species. We included the distribution of tRNA modification enzymes across multiple mycobacterium species in a revised Fig. 1.

• Authors state in line 293 "Several strong signatures were detected in Mtb tRNAs but not in E. coli". Authors can elaborate more on the unique features identified and their relevance in Mtb infection in the discussion or result section.

Thank you for the suggestion. However, the identity of these RT signatures and the relevance of these modifications for Mtb pathogenicity remains speculative at this point.

• Deletion of MnmA is shown to be essential for E. coli growth under oxidative stress (Zhao et al, NAR, 2021). In similar lines, MnmA deleted Mtb suffers to grow in macrophage. Is oxidative stress in macrophage responsible for slow Mtb growth?

This is an excellent hypothesis which we have added to the revised manuscript (lines 320-322). “In fact, the absence of mnmA is reported to sensitize E. coli to oxidative stress, raising the possibility that s2U modification promotes Mtb growth under oxidative stress elicited by the host.”

• Authors state in line 311-312 "Mtb does not contain apparent homologs of the tRNA modifying enzymes that introduce the additional modifications to s2U". This can be characterised further to rule out the possibility of other enzyme specifically employed by Mtb to introduce additional modification.

The reviewer raises a valid point. As discussed above (Reviewer #1, pt 2), Mtb may employ distinct enzymes to generate certain tRNA modifications. Future mass spec-based analyses of Mtb tRNAs will be carried out to identify the precise chemical structure of the sulfurated uridine, and subsequent studies will attempt to determine the enzymes that account for the biogenesis of these modifications.

Kimura, S. (2021). Distinct evolutionary pathways for the synthesis and function of tRNA modifications. Brief Funct Genomics, 20(2), 125-134. doi:10.1093/bfgp/elaa027

Reviewer #1 (Recommendations For The Authors):

Additional data and Analyses

The Modomics database is far from complete so it would be more rigorous to give the full set of genes that was used to do the searches as supplemental data.

Thank you for the suggestion. We added the list of the query genes as Supplemental Table 1. Minor points to be fixed

1) The authors name the psi32 synthase Rv3300c Pus9 when it is a member of the RluA family. It is not clear why the yeast/eukaryotic name was used.

We included enzymes from diverse species in our query, including eukaryotic genes. Indeed, we found that Rv3300c showed the lowest E-value among our query genes, therefore, we name Rv3300c as Pus9.

2) The sua5 gene name was used it should be tsaC to follow the accepted nomenclature.

We renamed Sua5 to TsaC2.

3) The statement lines 203-296 was totally unclear. I did not understand what the authors were trying to say at all.

This paragraph described how sequence context can result in different reverse transcription-derived signatures from dihydrouridine (D). We added a schematics describing this paragraph as Supplemental Fig. 6.

4) In reference, names with special characters should be fixed such as Börk.

We fixed the names with special characters.

Reviewer #2 (Recommendations For The Authors):

The authors state that at least some of tRNA modifying enzymes, while redundant for growth in vitro, may play a role during growth inside the macrophages, mostly due to the diverse stresses they could encounter.

We added a sentence, “In fact, the absence of mnmA is reported to sensitize E. coli to oxidative stress, suggesting that s2U modification is required for Mtb growth under oxidative stress elicited by the host” in the discussion.

• Ideally, authors could have tested the impact of diverse intracellular stresses that Mtb encounters, like redox stress, nitrosative, pH or nutritional stress, to check whether any of these stresses cause in vitro growth defects in ΔmnmA strain.

Thank you for the suggestion. This point will be addressed in future experiments.

This would be a wonderful way to show that under stress, the essentiality of tRNA modification enzymes changes.

Reviewer #3 (Recommendations For The Authors):

• In general, the clarity of the presentation can be improved.

• Authors state that "MiaA, is non-essential in E. coli, but apparently essential in Mtb". While MiaA is shown to be critical for the fitness and virulence of extraintestinal pathogenic E. coli (Fleming et al, NAR, 2022). This can be clarified.

We rephrase as follows: “Unexpectedly, one modifying enzyme, MiaA, is non-essential in E. coli grown in nutrient-rich medium, but apparently …”

• Line numbers 130-132 is a repetition of line numbers 103-105

We repeated these sentences because the same claim was deduced from different experiments, i.e., BLAST search and tRNAseq.

• Line number 228: The presence of U at position 55 in the tRNAs can be included in the text for a better understanding.

We changed the text as following: “… Termination signatures derived from position 55, which is exclusively uridine in all tRNA species, increased in most tRNA species, suggesting …”

• A detailed pictorial depiction on comparing the modifications and enzymes from E. coli and Mtb can be included for easy understanding.

We created an E. coli tRNA modification map in the same format as Figure 2C and added it to the revised manuscript as a new Supplementary Fig. 1.

Author Response

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

Reviewer #1 (Public Review):

“First, I agree with the authors of this manuscript that conformational changes in the XFEL structures with 2.8 A resolution are not reliable enough for demonstrating the subtle changes in the electron transfer events in this bacterial photosynthesis system. Actually, the data statistics in the paper by Dods et al. showed that the high-resolution range of some of the XFEL datasets may include pretty high noise (low CC1/2 and high Rsplit) so the comparison of the subtle conformational changes of the structures is problematic.

The manuscript by Gai Nishikawa investigated time-dependent changes in the energetics of the electron transfer pathway based on the structures by Dods et al. by calculating redox potential of the active and inactive branches in the structures and found no clear link between the time-dependent structural changes and the electron transfer events in the XFEL structures published by Dods, R.et al. (2021). This study provided validation for the interpretation of the structures of those electron-transferring proteins.

The paper was well prepared.”

Thank you very much for your positive and insightful comment. We greatly appreciate your suggestion regarding the high noise levels of the XFEL structures, as indicated by the low CC1/2 and high Rsplit values reported by Dods et al. Including this information in the Introduction section will draw readers’ attention to the concerns about the reliability of these XFEL structures. We have incorporated the following sentences into the Introduction section:

“Furthermore, the data statistics provided by Dods et al. indicate that the high-resolution range of some XFEL datasets exhibit high levels of noise, as evidenced by low CC1/2 and high Rsplit values. These observations raise concerns about the reliable comparison of subtle conformational changes among these structures. Hence, caution must be exercised when interpreting these XFEL structures in terms of their ability to accurately capture relevant conformational changes.”

The following sentences have also been added to the Conclusions section:

“Hence, it is crucial to exercise caution when interpreting time-dependent XFEL structures, especially in the absence of comprehensive evaluations of the energetics and accompanying structural changes. This cautionary note should serve as a counterargument in the future, highlighting the potential pitfalls associated with presenting time-dependent XFEL structures of insufficient quality and drawing conclusive interpretations of protein structural changes that may not be distinguishable from significant experimental errors.”

Recommendations for the authors

“Figure 1 needs clear labels or detailed notes in the figure legend for the labels such as M, L, Pm, Pl, etc.”

In Figure 1, we have increased the size of the labels to improve visibility. Additionally, we have expanded the figure legend to include detailed explanations of the abbreviations used, such as M, L, PM, PL, etc. We believe that these modifications have significantly improved the clarity and comprehensibility of Figure 1.

Reviewer #2 (Public Review):

“The manuscript by Nishikawa et al. addresses time-dependent changes in the electron transfer energetics in the photosynthetic reaction center from Blastochloris viridis, whose time-dependent structural changes upon light illumination were recently demonstrated by time-resolved serial femtosecond crystallography (SFX) using X-ray free-electron laser (XFEL) (Dods et al., Nature, 2021). Based on the redox potential Em values of bacteriopheophytin in the electron transfer active branch (BL) by solving the linear Poisson-Boltzmann equation, the authors found that Em(HL) values in the charge-separated 5-ps structure obtained by XFEL are not clearly changed, suggesting that the P+HL- state is not stabilized owing to protein reorganization. Furthermore, chlorin ring deformation upon HL- formation, which was expected from their QM/MM calculation, is not recognized in the 5-ps XFEL structure. Then the authors concluded that the structural changes in the XFEL structures are not related to the actual time course of charge separation. They argued that their calculated changes in Em and chlorin ring deformations using the XEFL structures may reflect the experimental errors rather than the real structural changes; they mentioned this problem is due to the fact that the XFEL structures were obtained at not high resolutions (mostly at 2.8 Å). I consider that their systematic calculations may suggest a useful theoretical interpretation of the XFEL study. However, the present manuscript insists as a whole negatively that the experimental errors may hamper to provide the actual structural changes relevant to the electron transfer events. My concerns are the following two points:

Is the premise of the authors for the electron transfer energetics obviously valid?

Could the authors find any positive aspect(s) in the XFEL study?

The authors' argument is certainly due to their premise "Em(HL) is expected to be exclusively higher in the 5-ps and 20-ps structures than in the other XFEL structures due to the stabilization of the [PLPM]•+HL•- state by protein reorganization" as noted in the Results and Discussion (p. 12, lines 180-182); however, it is unknown whether this premise can be applied to the ps-timescale electron transfer events. The above premise is surely based on the Marcus theory, as the authors also noted in the Introduction "The anionic state formation induces not only reorganization of the protein environment (ref. 5: Marcus and Sutin, 1985) but also out-of-plane distortion of the chlorin ring (ref. 6: two of the authors, Saito and Ishikita, co-authored, 2012)"; however, it is unknown whether protein reorganization can follow the ps-timescale electron transfer events. Indeed, Dods et al. mentioned in the Nature paper (2021) "The primary electron-transfer step from SP (special pair PLPM) to BPhL (HL) occurs in 2.8 {plus minus} 0.2 ps across a distance of 10 Å by means of a two-step hopping mechanism via the monomeric BChL molecule and is more rapid than conventional Marcus theory". It was also mentioned, "By contrast, the 9 Å electron-transfer step from BPhL to QA has a single exponential decay time of 230 {plus minus} 30 ps, which is consistent with conventional Marcus theory". As for the primary electron-transfer step from PLPM to HL, Wang et al. (2007, Science 316, 747; cited as ref. 8 in the Nature paper 2021) reported, by monitoring tryptophan absorbance changes in various reaction centers in which the driving forces (namely, the Em gaps between PLPM and HL) are different, that the protein relaxation kinetics is independent of the charge separation kinetics on the picosecond timescale. On the other hand, in the EPR study cited by the authors as ref. 7 (Muh et al. (1998) Biochemistry 37, 13066), although the authors described "two distinct conformations of HL- were reported in spectroscopic studies" (p. 3, lines 44-45), it should be noted that conformation of HL- was formed by 1 or 45 s illumination prior to freezing, and hence the second-order reorganized conformations may differ from picosecond-order conformations observed by the XFEL study (Nature, 2021) and/or the transient absorption spectroscopy (Science, 2007).

Therefore, I consider there is a possibility that the authors' findings may reflect not experimental errors but the actual ps-timescale phenomena presented by the first-time XFEL study on the timescale of the primary charge-separation reactions of photosynthesis. Thus I would like to suggest that the authors reconsider the premise for the electron transfer energetics on the picosecond timescale.

In any case, to discuss the experimental errors in the XFEL study, it is better to calculate the Em(QA) changes in the 300-ps and 8-us XFEL structures, which showed distinctive structural changes even at the 2.8 Å resolution as discussed by Dods et al. Then, if the Em(QA) values are changed as expected from theoretical calculations, such calculated results may suggest a useful theoretical interpretation of the XFEL study as a positive aspect. If the Em(QA) values are not higher in the 300-ps and 8-us structures than in the other structures, it may be argued that the experimental errors would be so large that the XFEL structures are irrelevant to the electron transfer events expected from theoretical calculations.”

We appreciate the reviewer's constructive suggestions, which significantly contributed to the improvement of our manuscript. We have performed additional calculations to address the reviewer's suggestion. We calculated the changes in Em(QA) in the XFEL structures. The Em(QA) values in the 300-ps and 8-μs structures were not significantly higher than those in the other structures (Figure 8).

These findings align with the scenario proposed by the reviewer, suggesting that the experimental errors are substantial, rendering the XFEL structures irrelevant to the electron transfer events. The results further reinforce our argument that the observed structural changes in the XFEL structures are not directly linked to the expected changes in electron transfer events.

We have incorporated these important points into the revised version as follows:

“One might argue that the loss of the link between the formation of the charge-separated state and the Em(HL) change (Figure 5) is not due to experimental errors but rather represents the actual ps-timescale phenomena during the primary charge-separation reactions (e.g., Dods et al. noted that “the primary electron-transfer step to HL is more rapid than conventional Marcus theory” 8). However, even if this were the case, this hypothesis regarding the relevance of the XFEL structures to the electron-transfer events can be further explored by examining the changes in Em(QA) among the XFEL structures, considering the relatively slow electron-transfer step to QA that allows sufficient protein relaxation to occur (e.g., Dods et al. stated that “the electron-transfer step to QA has a single exponential decay time of 230 ± 30 ps, consistent with conventional Marcus theory” 8). That is, if the Em(QA) values are not higher in the 300-ps and 8-μs structures than in the other structures, it suggests that significant experimental errors exist, rendering the XFEL structures irrelevant to the electron transfer events. Consistent with this perspective, the present results demonstrate that the Em(QA) values in the 300-ps and 8-μs structures are not significantly higher than those in the other structures, including the dark state structure (Figure 8). Consequently, the lack of a clear relationship between the charge separated state and the changes in Em(QA) at 300 ps and 8-μs further strengthens the argument that the XFEL structures are irrelevant to the electron transfer events.”

Recommendations for the authors

“In addition to my main concerns, the following points should also be taken into consideration:

The authors presented from QM/MM calculations out-plane distortion of HL (and HM) induced upon the reduction using the dark structure for dataset a (Table 5). However, to compare with the XFEL structures corresponding to the charge-separated state [PLPM]+HL-, positive charge should be located at the special pair (or, either PL or PM). In the present work, it is noted that counter ions were added to neutralize the entire system (in Methods: p. 6, lines104-105), but the location(s) of the positive charge is unclear.”

We appreciate the valuable suggestion provided by the reviewer. To address this concern, we have calculated out-of-plane distortion of HL•– in the presence of PL•+. The results have been included in Table 5. Note that the results obtained in the presence of PL•+ are substantially the same as those obtained in PL0 (Table 5).

For clarity, we have rephrased the sentence referring to counter ions as follows:

“To neutralize the entire system, counter ions were added randomly around the protein using the Autoionize plugin in VMD 22.”

“In relation to the calculations, the authors showed the induced out-plane distortion of HM for dataset a; however, the results for HM seem not to be mentioned anywhere. Instead, the calculations for HL of the dark structure for dataset b should be useful, especially for comparing with the time-dependent changes in the dataset b XFEL structures as shown in Figure 7.”

We have made Table 6 to present the results for dataset b. The results are consistent with those for dataset a (Table 5).

Author Response

We express our gratitude to the editors for acknowledging the significance of our findings and facilitating the review process. We would also like to thank the reviewers for dedicating their time to thoroughly read the manuscript and provide valuable insights.

During the revision process, we will address the raised issues and concerns, confident that our revisions will enhance the clarity and strength of the paper.

In response to the reviewers' feedback, we acknowledge that some of the relevant information was previously presented in our published papers (Meng, Dev Cell. 2017; Xia, Elife. 2021). However, we recognize that in the current version of the manuscript, we may not have expounded on these details as clearly as needed. We will rectify this shortcoming in the revised version to provide a more comprehensive account of our research.

We also explain our perspective on why the discovery of MYRF controlling lin-4 upregulation is crucial in addressing unanswered key questions in developmental biology.

The Loss of Function Characteristics of myrf-1(ju1121 G274R)

We would like to present the evidence supporting the characteristics of myrf-1(ju1121) as a loss-of-function mutation affecting both myrf-1 and myrf-2. In our initial paper (Meng, Dev Cell. 2017), the nature of this mutation was a significant focus of our research.

Our investigation involved analyzing multiple alleles (tm, ok, gk alleles from CGC, and indel alleles made in-house) of myrf-1 and myrf-2, as well as their double mutants. Here is a summary of our current understanding based on these analyses:

1. myrf-1 single loss-of-function (l.f.) mutants exhibit penetrant arrest at the end of L1 or early L2 stages. However, they only display very mild deficiency in DD synpatic remodeling at 21 hours, primarily caused by a delay.

2. myrf-2 single l.f. mutants behave similarly to the wild type, exhibiting no significant developmental abnormalities, including synpatic remodeling.

3. myrf-1 and myrf-2 double l.f. mutants exhibit penetrant arrest during L2, occurring approximately half a stage later than in myrf-1 single mutants.

4. Remarkably, myrf-1 and myrf-2 double l.f. mutants exhibit severe blockage in synaptic remodeling, indicating that both genes act collaboratively to drive this essential process (Meng, Figure 5).

5. The myrf-1(ju1121 G274R) mutation exhibits severe synaptic remodeling blockage and arrest during L2, closely resembling myrf-1 myrf-2 double mutants (Meng, Figure 1 and 2).

Therefore, despite myrf-1's more significant role in development based on the arrest phenotype, synaptic remodeling requires the combined function of myrf-1 and myrf-2. This redundancy is further supported by the analysis of the new set of specific myrf-1 mutants (Xia, Figure 6).

Both myrf-1 and myrf-2 are broadly expressed (Meng, Figure 3 and S5), and they undergo developmentally regulated cell-membrane to nucleus translocation (Xia, Figure 4 and Supplement 1). Overexpressing N-MYRF-1 and full-length MYRF-2 in DD neurons leads to precocious synaptic remodeling (Meng, Figure 4 and 5). Interestingly, overexpressing full-length myrf-1 does not have the same effect, indicating potential regulatory differences between these two factors.

The myrf-1(ju1121 G274R) mutation is located in the N-terminal region of the Ig-fold type DNA-binding domain, specifically within the loop between a and b Ig-fold strands. This site is conserved across all metazoan MYRFs (Meng, Figure 1D and 6A). The mutant myrf-1(G274R) loses its DNA binding ability, as demonstrated by a gel mobility shift assay using the counterpart residue mutation in mammalian MYRF (Meng, Figure 6B).

MYRF-1(ju1121 G274R) mutant interfering with normal MYRF’s function has been supported by molecular genetics experiments (Meng, Figure 6C-E) and biochemical analysis. In essence, the MYRF-1(G274R) mutant does not impact MYRF trimerization or MYRF-1-MYRF-2 interaction, but blocks DNA binding. Substantial evidence has confirmed the physical binding of MYRF-1 and MYRF-2 both in vitro and in vivo (Meng, Figure 5G and S6; Xia, Figure 1A). Importantly, MYRF- 1(ju1121 G274R) is still able to bind to MYRF-2, as supported by coIP analysis (Meng, Figure S7), indicating that the G274R mutation does not disrupt the MYRF-1-MYRF-2 interaction. This observation is consistent with the characteristics of the MYRF structure (PMID: 28160598; PMID: 34345217). The critical interface of the MYRF trimer is located in the alpha-helix upstream of the ICE domain, the beta sheets of the ICE, and the beta-helix of the bridge region between ICE and DBD. Therefore, since MYRF-1(ju1121 G274R) is not situated in this critical interface of the MYRF trimer, it is unlikely that the mutation affects MYRF trimerization.

With all available evidence, we propose a reasonable model where myrf-1(ju1121) has two effects: rendering myrf-1 defective in DNA binding and negatively interfering with MYRF-2 by forming a non-functional trimer consisting of monomer MYRF-1(ju1121) and wild-type MYRF-2.

Regarding the potential neomorphic function of myrf-1(ju1121), the myrf-1(ju1121)/+ individuals appear superficially wild type and show no defects in synaptic remodeling. Furthermore, we have generated a myrf-1 minigene array that results in a complete rescue of the developmental phenotype in myrf-1(ju1121) (Meng, Figure 3A-D). Notably, the transgene is expected to be low copy numbered, as it was generated by injecting at a very low concentration of 0.1 ng/μl. The complete rescue of the phenotype strongly suggests that any potential aberrant effects caused by myrf-1(ju1121) mutants are minimal.

In summary, myrf-1(ju1121) behaves similarly to myrf-1 myrf-2 double mutants, and we utilized this allele for the convenience of analysis.

Due to the essential role of MYRF-controlled processes in larval development and the lack of detectable phenotypic effects in myrf-2 single loss-of-function mutants, it is evident that myrf-2 plays a minor role in these developmental events. Considering that development regulation rarely follows a simple linear or accumulative fashion, deciphering the relative contributions of each myrf-1 and myrf-2 in specific developmental events may not be straightforward. Consequently, our primary focus remains on investigating the functions of myrf-1.

Nevertheless, we concur that providing a clear description of the impact of myrf-1 and myrf-2 single mutants on lin-4 expression is crucial. We are actively conducting ongoing analyses, and the new findings will be incorporated in the revised version of our manuscript.

Characterizing myrf-1(syb1313, 1-700) as a Hyperactive Allele of myrf-1

The cleavage and release of N-MYRF are developmentally regulated and occur in late L1. We have substantial evidence supporting the interaction between the non-cytoplasmic region of MYRF and another transmembrane protein, PAN-1, which is crucial for delivering MYRF onto the cell membrane (Xia, Figure 1, 7, 8, 10, 11 and 13). The myrf-1(syb1313, 1-700) mutant lacks the non-cytoplasmic region of MYRF, which is the interaction site for PAN-1. Initial analyses revealed that in the mutants, MYRF-1(syb1313) remains in the cytoplasmic, ER-like structure, resulting in larval arrest during L2 (Xia, Figure 8).

However, a more careful analysis unveiled that a small amount of N-MYRF is processed and enters the nucleus, but this process is not dependent on the normal developmental timing and may take place during early-mid L1. Consequently, this leads to precocious yet discordant DD synaptic remodeling and M-cell lineage division (Xia, Figure 6 and 9). Considering the precocious development, the low quantity of nuclear N-MYRF, and the overall larval arrest phenotype observed in the mutants, we conclude that myrf-1(syb1313) represents an inconsistent, weak hyperactive form of MYRF-1. Moreover, the hyperactive function may be context-dependent, for instance, presence of myrf-1(syb1313) may be sufficient for certain needs in neurons but insufficient for epidermis. Our ongoing research to identify the downstream targets of MYRF also supports this notion.

Given that the myrf-1(syb1313) mutant has been thoroughly characterized and published, it is the most suitable option for use in our current investigations on lin-4 expression.

Furthermore, we employed the MYRF-1(delete 601-650) deletion mutant construct, which is a significantly more effective hyperactive MYRF-1 mutant when overexpressed. This reagent stems from our ongoing study, which is dedicated to identifying the self-inhibitory mechanisms of MYRF cleavage. The extensive volume of data that led to this discovery makes it impractical to include in the current manuscript. However, we are eager to share the substantial effects of MYRF-1(delete 601-650) mutants in activating lin-4 expression, which strengthens the role of MYRF in regulating lin-4. We will take care to revise this section to provide clearer references.

The lin-4p::nls::mScarlet(umn84) knock-in reporter is loss-of-function for lin-4; however, lin-4 mature microRNA does not affect lin-4 expression.

Indeed, the lin-4 knock-in reporter umn84 removes lin-4 coding sequence. As a result, the homozygous reporter strain is also lin-4 null mutants. Since both lin-4 and myrf-1 are located on Chr II and are less than 4 m.u. apart, the constructed strain is myrf-1 lin-4(umn84) / mIn1 (balanced by mIn1). Consequently, the myrf-1 homozygous animal is also lin-4 reporter homozygous.

Regarding the endogenous function of the "auto-regulating element," we are aware of the follow-up paper by Frank Slack's group, in which they concluded that the previously reported sequence is dispensable for lin-4 expression, and the loss of lin-4 does not affect the expression of its primary transcript (PMID: 29324872). To avoid confusion, we will remove or revise the introductory sentences as necessary to accurately reflect this information.

Additionally, besides analyzing the expression of the knock-in reporter of lin-4 (umn84), we also conducted a thorough analysis of mature microRNA expression using targeted qPCR and genomic analysis via microRNA sequencing. Both sets of results indicate severely defective upregulation of lin-4 mature microRNA in myrf-1(ju1121).

No evidence indicates that the 2.4 kb reporter of Plin-4-gfp (maIs134) is an inappropriate reporter for lin-4 transcription.

maIs134 is originated from the Ambros lab, and to date, there is no single evidence demonstrating that maIs134 cannot be regarded as a reliable transcription reporter for lin-4 expression. The Stec et al. (Curr Biol 2021. PMID: 33357451) paper suggests that the PCE or CEA site (at ~ -2.8 kb) outside the 2.4 kb region confers enhancing effects for lin-4 transcription, but no other published paper has studied lin-4 transcription and cited this finding.

While the Stec et al. paper provides elaborate mechanistic descriptions, the basic characterization of the importance of CE-A and blmp-1 to lin-4 expression is lacking. Deletion of CE-A in the lin-4 promoter reporter using an Ex array transgene resulted in highly variable reporter expression (Stec, Figure 4D). Notably, two high expression data points indicated that a transgene reporter without CE-A can be highly expressed, suggesting that CE-A is unnecessary for lin-4 transcription. Only when both CE-A and CE-D (within 2.4 kb) were deleted, the reporter expression was significantly decreased. Moreover, deletion of CE-C (proximal region) alone caused severe loss of reporter activity, supporting that proximal CE-C is the essential element, while CE-A is not.

It is important to note that the effect of CE-A on lin-4 expression has not been analyzed using stable transgenes or genetic deletions in the endogenous lin-4 region. Furthermore, there is no data on how blmp-1 mutants affect the expression of the wild-type lin-4 promoter reporter, CEA deletion reporter, or lin-4 mature microRNA, despite the paper’s main claim that blmp-1 boosts lin-4 expression. While CE-A can confer an enhancing effect in epidermal expression when fused to the gst-5 promoter, there is no data showing that CE-A is sufficient to drive lin-4 transcription by itself.

In summary, there is currently insufficient evidence to establish whether CE-A is necessary or sufficient for regulating lin-4 expression. In fact, the data presented in Stec et al. (Curr Biol 2021) suggest that CE-A is unnecessary for lin-4 expression. As such, I do not see any reason to consider the 2.4 kb reporter in maIs134 as inappropriate for analyzing lin-4 transcription. Furthermore, our presented data using the knock-in reporter of lin-4 (umn84) demonstrated that its regulation by myrf is essentially consistent with the observations drawn from the maIs134 analysis.

The Significance of the Finding: MYRF Regulating lin-4 Upregulation

We are grateful that the editors find our results valuable for those interested in lin-4 expression. However, we acknowledge that the editors may not share the same enthusiasm as we do, seeing this as a landmark discovery in understanding postembryonic development, a fundamental question in the field of developmental biology.

Importance of Understanding lin-4 Upregulation in Development

The foundation of developmental biology has been built on the principles derived from studying embryonic development in model organisms like Drosophila, exemplified by the Nobel laureates Lewis, Nusslein-Volhard, and Wieschaus. These principles explain what occurs during embryonic development, including patern formation, morphogenesis, and differentiation. However, these existing principles do not fully explain the phenomena of postembryonic development, including growth. For instance, during C. elegans development in L1, it remains unclear what controls the initiation of P cell division. If we may exclude dividing cells from the discussion, numerous stage-specific changes occur in non-dividing cells, including neurons. The extensive, systematic expression studies of transcription factors in C. elegans have failed to provide evidence that such developmental progression is driven by sequential activation of transcriptional cascades, as commonly observed during embryonic differentiation. A different approach to ask a similar question is to inquire how developmental timing is controlled, e.g., "why does it take a boy 12 years to reach adolescence?" This perspective highlights the need to identify potential unidentified checkpoints that control postembryonic stages (An example of insightful review: The Systemic Control of Growth. Cold Spring Harb Perspect Biol. 2015. PMID: 26261282)

The upregulation of lin-4 represents a system’s checkpoint during postembryonic development. Deciphering the mechanism controlling lin-4 expression is instrumental in understanding the principles of postembryonic development, even extending to adult development, including life span control.

Importance of the Finding: MYRF's Control of lin-4 Upregulation

To date, no other essential, positive regulator of lin-4 transcription has been identified, although several negative regulators have been reported. A landmark paper by Victor Ambros identified FLYWCH as a repressor of lin-4 expression during embryogenesis (PMID: 18794349). FLYWCH mutants fail to progress to normal hatched larvae, implying that FLYWCH is crucial. The paper indeed suggested that FLYWCH has additional functions beyond suppressing lin-4, although these functions have not been thoroughly characterized. The significance of the FLYWCH finding lies in the elaborate control during the transition from embryo to larval development, where lin- 4 is actively suppressed. This control may ensure the robustness of subsequent lin-4 activation. The process during the embryo-to-larvae transition, as well as the counterpart process in mammalian development perinatally, remains poorly understood.

Another negative regulator of lin-4 is lin-42, as reported in three papers in 2014 (PMID: 25319259; PMID: 24699545; PMID: 25032706). Lin-42 negatively regulates lin-4 expression, despite the main focus of the papers being lin-42's repression of let-7. However, the precise mechanisms by which this repression is achieved are not fully understood.

Amy Pasquinelli's lab conducted a genome-wide screen to identify factors responsible for driving lin-4 upregulation but did not identify a critical factor that promotes lin-4 transcription (PMID: 20937268).

In the recent paper by Stec et al. (Curr Biol 2021. PMID: 33357451), they reported blmp-1's role in enhancing lin-4 expression. However, the significance of blmp-1 in regulating lin-4 remains vaguely described, despite a large amount of data describing elaborate epigenetic controls. The paper did not provide data on how endogenous lin-4 expression is affected in blmp-1 mutants, nor did it demonstrate how full-length reporter expression is affected in blmp-1 mutants. The only relevant data appears to be on the CE-A-gst-5 promoter reporter in blmp-1 mutants. As a result, it remains unclear how blmp-1 affects lin-4 transcription.

In summary, no single factor has been identified, the loss of which leads to significant deficiencies in lin-4 upregulation. MYRF is the first and a critical factor identified in this context. This finding represents a significant advancement in our understanding of lin-4 regulation and its crucial role in development.

Author Response:

We thank eLife for carrying out the peer review of our preprint. In this letter, we will provide a response to the eLife assessment, and the editor’s public review, and will also address the major points raised in the peer-review of our study.

First, we wish to inform the readers that including this review, our manuscript has now been reviewed 5 times. These have included three reviews at an earlier journal, a review at eLife under the older model, and the current review at eLife under the new model. In an effort to provide transparency and increase the reader’s confidence in our study, all the prior reviews and our rebuttals to them have been uploaded to Biorxiv and are publicly available for all readers to peruse [1]. These reviews will show that we have responded comprehensively with additional data, and analyses over the last 3 years. Of the current reviewers, Reviewer #1 (who was also Reviewer #1 at the earlier journal) has reviewed our manuscript all 5 times. At the prior journal, an additional Reviewer (#2) carried out 3 cycles of review – and we responded fully and comprehensively to all the issues and comments of that Reviewer. It is our understanding that the prior Reviewer #2 did not respond to the review request from eLife, after which eLife recruited two new Reviewers (current Reviewers #2 and #3), who have now reviewed our work twice – once under the older model and now again under the newer model.

Next, to ease readability, we will respond to the review in three parts. Part A will be dedicated to the editors’ public review. Part B will be dedicated to the response to eLife assessment, and we will respond to the reviewers’ comments in Part C.

Part A: Response to editor’s public review: We thank the editor for his nuanced and fair read of our data and our inferences, and of the multiple back-and-forth cycles of reviews and rebuttals. The editor’s public review highlights key points put forth in our data, and succinctly discusses the evidence provided for our claims. Here, we respond to each of these highlights.

(i) The editor agrees that subject to the broader limits of lineage fate-mapping experiments, which are universal for every prior and current study of vertebrate development, we have provided sufficient evidence for the presence of a population of cells within the myenteric ganglia, which shows mesodermal and not neural crest derivation, and which expresses the pan-neuronal marker Hu among other neuronal and mesenchymal/mesodermal markers.

Given that the current accepted annotation for enteric neurons depends on their expression of pan-neuronal markers (which we show are expressed by MENs), expression of neurotransmitter-encoding genes and proteins (such as CGRP, NOS1, ChAT, etc, which we show are expressed by MENs), and their localization within the enteric plexuses (we show evidence of intra-ganglionic localization of MENs in the myenteric plexus), our data suggests that in describing MENs, ours is the first report describing the presence of a mesoderm-derived neuronal population in a significant neural tissue. By virtue of the continual expansion of the MENs population with maturation and aging, we show evidence that MENs contributes to the post-natal maturation and aging of the enteric nervous system (ENS), and by reducing the proportions of MENs in aging tissue, we can rejuvenate the ENS to normalize gut function in aging mice.

(ii) The editor comments on whether beyond the accepted norm of their intraganglionic localization and expression of pan-neuronal markers, MENs can be described as functional neurons. We agree that in our manuscript, we did not test how MENs function. This is expressly because the current report is the first step in the study of MENs and does not aim to understand how MENs regulate various gut functions. In this response however, we wish to put forth a few arguments that would clarify some of the existing evidence on the functional nature of MENs as well as the current state of knowledge on ENS functions. These would help the readers understand the current evidence on the functional nature of MENs, and in addition, why it would be premature to expect MENs to exhibit canonical neuronal behavior.

a. MENs generate neurotransmitters and neuropeptides: Enteric neurons release various neurotransmitters, and their ability to generate important neurotransmitters such as nitric oxide (NO) and acetylcholine depends on their expression of enzymes Nitric Oxide Synthase 1 (NOS1) and choline acetyltransferase (ChAT). Our work shows that sub-populations of MENs express these important neurotransmitter-generating enzymes (Fig 3). Further, our data also shows that MENs express CGRP, which is an important neuropeptide for regulating various gut functions (Fig 3). These important data show that at the protein level, many MENs have the same cellular machinery as that of NENs that can help carry out regulation of important gut functions.

b. MENs have been shown to be functional in a prior study: Recently, enteric neurons have been shown to carry out significant immunomodulatory functions. These have included the expression of cytokines such as IL-18, which regulates intestinal barrier (as shown by Jarret et al. [2]), and CSF1, which regulates macrophage recruitment [3]. Jarret et al shows that the enteric neuron-derived IL-18 regulates immunity at the mucosal barrier. We show that the IL-18 – expressing enteric neurons are MENS (Fig 4), and thus, the data from Jarret et al [2] provides evidence that MENs are indeed functional in the in vivo environment.

c. We do not quite know how many enteric neurons work at the electrophysiological level: Canonical vertebrate neurons exhibit resting membrane potentials (RMP) in the range of -70 to -80 mV, and during neuronal activation, an increase in membrane potential beyond the threshold of -55 mV activates their action potential [4]. By contrast, past and recent studies have shown that the average RMP of rodent and human enteric neurons is significantly more positive than -70 mV (for human ENS: -48 ± 8 mV, for mouse ENS: -46 ± 6 mV for S neurons, -56 ± 5 mV for AH neurons) [5, 6]. These data suggest that enteric neurons show significant departures from canonical neuronal behaviors and thus, expecting MENs to adhere to canonical neuronal behavior – when most of the ENS does not adhere to expected norms - would be incorrect.

d. A neuron is not defined by its ability to generate an action potential: Neuronal behavior does not require the presence of action potentials, as observed in the neurons in C. elegans [7], much in the same way that the presence of action potentials is not restricted to neurons as it occurs in nonneuronal cells, including in enteroendocrine cells of the mammalian gut [8]. Thus, the presence or absence of action potentials cannot be the basis for adjudicating whether or not a neurotransmitter-expressing cell in a neural tissue is a functional neuron.

(iii) The Editor, after reading the extensive prior and recent correspondence between the authors and the reviewers on whether the cells analyzed in the transcriptomic experiments are the same as those observed in tissues (called tissue MENs by a reviewer), opined that he found “the authors' assertions that they have described a cluster of cells that express both neuronal and mesodermal genes, and that this cluster corresponds to the tissue MENs described in lineage tracing, to be broadly sound”.

We are enthused by the Editor’s opinion, as we had previously argued that our data connecting the transcriptomic data to tissue MENs is robust on the basis of extensive immunohistochemical validations of marker genes found in our single cell transcriptomic analyses. The Editor notes some confusion on why some marker genes not specific to MENs were used for the analyses and further points to the prior rebuttals we have posted on Biorxiv [1], where detailed clarifications on the choice of marker genes have been made. In the interest of readability, we direct the readers to these prior rebuttals at Biorxiv for more details. Succinctly, we initially tested canonical neuronal genes by immunolabeling (such as NOS1, ChAT, CGRP, etc) in NENs and MENs before performing single cell transcriptomic experiments. After performing the transcriptomic experiment, we next chose to validate neuronal and mesenchymal genes that were found expressed in the MENs cluster (such as DCN, SLPI, IL-18, NT-3, etc). Finally, in previous cycles of review, on the reviewer’s insistence, we included data on the expression of a host of neuronal genes and their encoded proteins (including Vsnl1, Pde10a, etc) to provide further evidence of neuronal identity of MENs.

While without a significantly large cluster of NENs, it is impossible to know in our transcriptomic data, whether a gene expressed by MENs would be similarly expressed by NENs, it is important to note that lack of detection of a gene in the single cell experiments cannot be inferred as lack of its expression in those cells, and hence, our inferences on whether any marker gene was exclusively expressed by neurons of a particular lineage were determined by immunohistochemistry. Additionally, we wish to reiterate and inform the readers that our study provides detailed analysis of prior work by May-Zhang et al [9], where they have described a small cluster of Phox2b-expressing cells from the murine myenteric plexus that shows the expression of neuronal and mesenchymal markers. Our analyses shows that the transcriptomic profile of MENs matches the molecular signature of these cells. In the longitudinal muscle – myenteric plexus layer, only glial cells and neurons express Phox2b [10], suggesting that this cluster sequenced by May-Zhang et al are cells of the myenteric plexus. We provide evidence that the majority of the MENs were left unsequenced by MayZhang et al and that this minimized the representation of MENs in their data (Fig 5). These data together provide important confirmation of our argument that the transcriptomic MENs point to no other cell type but the tissue MENs.

(iv) The Editor opines that a weakness in our current data is the significant overrepresentation of MENs in the single cell experiment, while also noting that our “explanation - that some cells are more sensitive to manipulations required to prepare cells for sequencing - is certainly well-represented in the literature and is therefore plausible….But it isn't fully satisfactory”. In our prior arguments (as well as in Part C), we have provided explanations based on prior observations that the issues of disproportionate representation of cell types are a technical limitation of the single cell transcriptomic methodology, which is prevalent in other experimental conditions for ENS (including the gut cell atlas study by Elmentaite et al [11]), and for other cell types in various organs. Due to this limitation, proportions of cells in the single cell space should not be inferred as their proportions in tissues. We also agree with the Editor that owing to the low representation of NENs, our data does not allow for a detailed comparison of the similarities and differences between the neurons of the two lineages, and that “an ideal analysis would have more cells, deeper sequencing, and comprehensive validation of the identity of each cluster of cells.” While in this study our aim was to describe the existence of MENs and not to perform an in-depth characterization of their sub-populations, we agree that this is the logical next step in creating a better understanding of the true diversity of ENS neurons. To that, we are currently evolving the methodologies to allow for a deeper and a more comprehensive analyses and validation of the various MENs populations, and study how they differ from NENs. We aim to publish these data in our next study.

(v) We agree with the Editor’s assessment on our transcriptomic data that “these data and analyses bolster the authors' claims, without conclusively establishing them. That is, these data should neither be dismissed nor, on their own, considered definitive.” We have only used our single cell transcriptomic data to provide additional support for our claims (which are based on extensive lineage fate mapping and immunohistochemical analyses) and are not using these as a stand-alone definitive proof of a mesodermal origin. The data from the transcriptomic experiments were used to learn additional molecular markers, whose expression in MENs in tissue could be tested by immunohistochemistry. With this methodology, we provide data on the coexpression of neuronal and mesenchymal markers by MENs, and test by computational analyses whether similar neuronal population exists in other murine and human transcriptomic datasets.

In addition, we completely agree with the Editor that “at this stage in the history of single-cell analysis, the criteria for using single cell sequencing data to establish cell type and cell origin is are not well established, and that neither the presence nor absence of specific sets of genes in single cells should not, for both technical and biological reasons, be considered dispositive as to identity.” We are very mindful of this limitation of these analyses and hence have continually ensured that our study only uses transcriptomic data of postnatal MENs to define a preliminary molecular signature of MENs, and not to infer developmental origins of MENs.

(vi) We thank the Editor for his summary and for highlighting that despite using multiple lines of evidence to support our hypothesis, the current reviewers are not yet convinced of the mesodermal origin of MENs. Our study utilizes well established tools for lineage fate-mapping (which are the only tools that currently are widely disseminated and accepted in the field of developmental biology) to show that MENs are not derived from the (Wnt1-cre, Pax3-cre -expressing) neural crest and instead are derived from the (Mesp1-cre, Tek-cre -expressing) mesoderm. The reviewers agree that by using multiple lines of evidence, we have established that our results of lineage fate-mapping are real and not due to any artifact. With this rationale, the reviewers would agree that MENs observed in tissue do not show evidence of derivation from neural crest while showing evidence of derivation from the mesoderm. Despite this, we cannot ascertain the scientific rationale for why despite agreeing with our lineage fate-mapping methods and analyses, the reviewers remain unconvinced as to the developmental origins of MENs. We do not know what other experiment would pass the reviewers’ muster to definitively annotate the mesodermal origins of MENs.

We wish to highlight that a recent study in ctenophores, where the investigators show evidence of a syncytial neural net [12], shows that much of the dogmatic view of how neurons are supposed to work is being overturned and newer paradigms that support broader interpretations for the definitions of neurons and how they regulate functions are being established. Our work on the developmental origins of a large population of neurons of the ENS, which is regarded as a primordial and conserved neural tissue, should be viewed in a similar vein.

Part B: Response to eLife assessment: Ours is the first report on the mesodermal derivation of a large population of neurons in a significant nervous system in mammals. We show that this population of neurons, called MENs, is molecularly distinct from the canonical neural crest-derived lineage of neurons, and that the post-natal ENS shows evidence of increasing presence of MENs in the maturing and aging ENS. We show that the two neuronal lineages are sensitive to their own growth factors, which can be used to manipulate their proportions in tissue, and thereby provide a potential rejuvenating therapy for age-associated intestinal dysmotility. We also show that on the basis of MENs’ marker expression, MENs maybe present in the human ENS, and that disproportionate changes in their proportions are associated with chronic gut dysmotility disorders. Our work has profound implications in the multiple fields, including those of enteric and peripheral neurobiology, developmental biology, medicine, and aging. We are thankful that the eLife assessment found that we provide sufficient evidence for this important work.

Part C: Response to Reviewers: Here, we wish to note that all the comments of the reviewers have been sufficiently addressed in prior reviews. All prior reviews, and our extensive rebuttals are available at our preprint for the readers’ perusal [1]. In this response, we wish to succinctly address some comments that have continued to emerge in this round of peer-review.

(i) We wish to highlight that the Reviewers 1 and 2 agree that our lineage-fate mapping experiments are correct and the results are not a result of any artifact. In addition to the additional reviewer in the prior reviews at an earlier journal, whose comments were addressed in full, we have a total of three reviewers who agree that our results on lineage fate-mapping are robust. Reviewer 3 comments on the possibility of ‘cre mosaicism’ or the deleterious issues with long-term expression of cre. Our prior rebuttals have dealt with this comment at length, but succinctly, our results are (a) based on extensive cre and floxed reporter controls for both the lineages, and (b) replicate observations made by other labs – including the Pachnis, the Heuckeroth, and the Southard-Smith labs to provide confidence that these are not due to any artifacts in cre or reporter gene expression. Finally, cre in the two lineage fate mapping systems (Wnt1-cre and Mesp1-cre) is only developmentally expressed and thus, there is no reasonable possibility that our results would be impacted by long-term expression of cre. Thus, our results and inferences on lineage fate mapping, which is central to our annotation of the two distinct developmental lineages, correctly describe the developmental origin of MENs.

(ii) By using extensive immunolabeling for (~21) markers that were learnt from our transcriptomic experiments, we provide evidence of the firm connection between the cluster of cells we annotated as MENs in the single cell transcriptomic experiments and the MENs we observe in tissues. Thus, we have performed more validation for these neurons than any other studies that have traditionally used 2 - 3 markers to validate a cell cluster in the ENS.

In addition, by providing evidence of the expression of pan-neuronal marker Hu and other ENS markers that include NOS1, ChAT, CGRP, etc and ~40 neuronally significant genes, we have established the neuronal nature of MENs. With regards to annotation of MENs as neurons, we expected and understand the confusion in the field with our discovery of mesoderm-derived neurons that coexpress neuronal and mesenchymal markers. We wish to put forth the following arguments for the readers to consider.

a. The annotation of Hu-expressing cells within the myenteric ganglia has been traditionally accepted as an enteric neuron. In those terms, by virtue of their intra-ganglionic presence and expression of Hu (and our data shows that Hu antibodies do not discriminate between the three neuronal isoforms of Hu) and other neuronal markers such as NOS1, ChAT, and CGRP, MENs should be annotated as neurons. We had addressed the semantic nature of this question in our last rebuttal (review #3, reviewer 1), which is available on the preprint [1].

b. As the molecular data on MENs suggests that they have significantly different biology, it would not be unreasonable to expect that their neuronal behavior may be quite different. This is underscored by the fact that we observe many MENs to lack the expression the protein SNAP25, whose presence is thought to be central to canonical neuronal behavior. We also cite evidence that neurons without SNAP-25 expression occur in the CNS neurons as well. In light of these discoveries, gauging the biology and neuronal behavior of MENs is a significant undertaking as it cannot be assumed that the behavior of MENs will be similar to that of NENs.

c. It is not logical to say that “Expressing one of the Hu proteins (Elavl2) probably isn't enough to call these "neurons" especially when neurons usually express Elavl3-4 (HuC/D)” especially when there are currently no antibodies to discriminate between the three neuronal gene products.

d. While at the outset it maybe an easy proposition to suggest that we provide evidence of neuronal activity in MENs by calcium flux or by electrophysiological means, it is important to know that calcium flux exists in all cells of the gut wall, including in smooth muscles, enteric glia, neurons and thus studying calcium flux will not provide definitive proof of neuronal behavior in MENs. Further, we reiterate from Part A of this response letter that “neuronal behavior does not require the presence of action potentials, as observed in the neurons in C. elegans [7], much in the same way that the presence of action potentials is not restricted to neurons as it occurs in non-neuronal cells, including in enteroendocrine cells of the mammalian gut [8]. Thus, the presence or absence of action potentials cannot be the basis for adjudicating whether or not a neurotransmitter-expressing cell in a neural tissue is a functional neuron.”

(iii) Our identification and validation of the molecular identity MENs using single cell transcriptomic experiments helps us establish the congruency of our cell cluster with a similar cluster enteric neurons previously observed by the SouthardSmith lab in their analyses. Thus, similar to our observations on the lineage-fate mapping models, observations on our transcriptomic data are also in-line with the observations made by other labs in the field.

(iv) To address any remaining confusion in the minds of the reviewers and of the readers about the correct methodology for interpreting single cell transcriptomic data and the limitations of this technique, we wish to reiterate that:<br /> a. Single cell or nucleus RNA sequencing methods are biased towards sequencing transcripts that are abundant relative to all other transcripts for that individual cell (detection and amplification bias). Thus, while the same transcript may be equally expressed at an absolute level in two different cells, it will be more readily sequenced and detected in the cell where the transcript is relatively more abundant.

b. Correct interpretation of single cell/nucleus transcriptomic data relies on an understanding that not all transcripts of a cell can be sequenced and detected, and thus absence of the expression of transcripts in a cell does not imply absent gene expression. Together this shows the fallacy of an argument often put-forth by the reviewers that a lack of detection of a gene transcript (for e.g. Phox2b) in MENs in a scRNAseq experiment should be inferred as a lack of expression of this transcript, even though we provide evidence of the expression of PHOX2B protein in MENs, and the expression of this transcript in the MENs in the data from the Southard-Smith lab.

c. scRNAseq is not a technique where annotation of a previously unknown cluster should be biased by the detection of expression of one or two genes, and instead establishing identity or conferring novel annotation of that cluster is defined by co-expression of several genes which must be validated in tissue.

d. It is well known that enzyme-based dissociation methods are unequally tolerated by diverse cell types, which is known to cause over- or underrepresentation of several cell types in scRNAseq (Uniken Venema et al.[13], who showed that dissociation method drives detection and abundance of cells sequenced; Wu et al.[14], showed the existence of similar dissociation bias in the kidney; Tiklova et al.[15] showed that specific subpopulations of Dat-expressing neurons in the developing mammalian brain were underrepresented in scRNAseq). The Gut Cell Atlas study (Elmentaite et al.[16]) was not able to detect NENs in the adult intestinal tissue. The lack of detectable canonical enteric neurons (NENs) in the adult tissue in their study should not be viewed as an absence of NENs in those tissues, and with the same logic, a restricted abundance of NENs and a larger abundance of MENs in our dataset cannot and should not be viewed as a reliable indicator of their actual proportions in tissues. The aim of our study is not to provide a comprehensive molecular atlas for all cells that reside in the LM-MP tissue layer, but to use the information in this atlas to identify a cell cluster that best describes MENs, and then use additional tools to validate this information.

e. Without extensive validation by immunohistochemical or other means, detection of transcripts of a particular gene ‘Z’ (which is known to be expressed in cell type ‘X’) in a particular cell cluster ‘A’ of a single cell transcriptomic dataset does not directly imply that cell cluster ‘A’ points to cell type ‘X’. Thus, the detection of transcripts of the gene Wt1 (which is known to be expressed in mesothelial cells) in MENs, in itself does not mean that the MENs cluster comprises of mesothelial cells. It simply suggests that in addition to its expression in mesothelial cells, Wt1 gene is also expressed by MENs – an inference which is supported by data that show the expression of LacZ in myenteric ganglia cells in the WT1-cre transgenic mouse (Wilms et al 2005 [17]).

(v) Our study has performed two scRNAseq studies, first to establish the distinct molecular signature of MENs, and second to provide transcriptomic evidence of MENs-genesis. In the last and current review, Reviewer 2 opines that we should perform an additional single cell RNA sequencing experiment just to show that the MENs cluster is represented in the mesoderm-enriched transcriptomic data. There is no doubt that owing to the expression of various mesodermal-markers that we show are expressed by MENS (both transcriptomically in scRNAseq and at the level of proteins in tissues), the cluster of MENs is mesodermal in origin. Thus, we have already provided evidence and met a higher burden of proof on the mesodermal identity of MENs, and thus, we do not consider the costly scRNAseq experiment proposed by the reviewer a definitive experiment that would justify the time or the cost.

(vi) Our prior rebuttals have provided the reviewers with evidence that shows that our study has used standard bioinformatic pipelines to analyze our data, and our inferences of the transcriptomic data are sound and well validated by additional methods.

(vii) Many comments of the reviewers that required textual edits were already carried out after the prior review at eLife. While a revised version of our manuscript was submitted to eLife for the current review, it is unfortunate that the reviewers have not updated many of their comments. For the sake of brevity, we will not be responding further to the comments that we have already addressed at length in prior rebuttals or in form of textual edits.  

References

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Author Response

Many thanks for the detailed and sometimes sharp, yet appropriate criticism of our study. It was an incentive for us to carry out additional analyses and to devote more effort to an elaboration of concepts. The outcome is that the results have changed slightly and that we now give more space to a discussion of concepts. We first address here the points raised by more than one reviewer before responding to comments contributed by individual reviewers.

The points raised can be divided into three thematic groups, 1) conceptual issues, 2) experimental and analytical questions, and 3) comments challenging the novelty of our results. On the first theme, we think it is essential to make a clear distinction between the conceptual and observational domains. As such, the criteria defining a “mirror neuron” and what is meant by the term "mirror mechanism" belong to the conceptual domain. This understanding of terms requires agreement among scientists, but is not experimentally testable. Unfortunately, there is no agreement on how to define a “mirror neuron” and what is meant by “mirror mechanism”. Thus, for the present work, the only option is to refer to specific definitions or to use our own, definitions which try to capture what others, and here most importantly Rizzolatti and colleagues, probably meant. We have adjusted the introduction in an attempt to convey our understanding and usage of the two terms in a hopefully comprehensible manner. Briefly, we use a definition for "mirror neuron" that we take from the first paragraph of the results section of Gallese et al. (Brain, 1996). We do not consider the "properties of mirror neurons" described in that paper as defining a mirror neuron (MN). Classifying neurons as MNs only on the basis of the presence of a modulation of discharge rate during an executed and an observed action compared with a baseline is a common practice also in other single neuron studies on MNs, consistent with this definition. Regarding "mirror mechanism", we refer to Rizzolatti and Sinigaglia (2016) and make a distinction between a broad and a strict definition. Given our finding that there are almost no F5 MNs whose activity during observation is a motor representation according to our strict definition of a mirror mechanism, and also given the problem that the term “mirror mechanism” itself is not uniformly understood, the question arises whether and how the term "mirror neuron" should be used in the future. The answer to this may vary and belongs to the conceptual domain. We briefly address this question at the end of the discussion of the revised manuscript.

From that understanding of terms, conceptual hypotheses are to be distinguished, which of course must allow experimental predictions, i.e., must be falsifiable. We now distinguish more clearly between a "representation hypothesis" and an "understanding hypothesis". Both hypotheses focus on F5 MNs and are based on the strictly defined mirror mechanism. We test the “representation hypothesis” in our study, and just because it is the basis for the “understanding hypothesis”, falsifying the “representation hypothesis” would allow us to conclude that the “understanding hypothesis” is not valid. In contrast, confirmation of the “representation hypothesis” would not, of course, allow us to conclude that the “understanding hypothesis” holds. That would really be circular reasoning (this conclusion was drawn by some and rightly criticized). However, support for the “representation hypothesis” would be the necessary prerequisite for the “understanding hypothesis” to be true. These two hypotheses take up the original argument that a certain understanding of observed actions could follow from an equality of action-specific F5 MN activity during execution and observation. Because we considered the data on equality of action- specific F5 MN activity to be insufficient, we designed this study. Since our result largely argues against the "representation hypothesis" and thus against the "understanding hypothesis," we now discuss alternative concepts for the function of F5 MNs in more detail. It should be noted here that our fourth concept ("goal-pursuit-by-actor") could well represent the observed action without contradiction to our broad definition of a mirror mechanism, which in principle could also serve a subjective experience (which could be conceived as a kind of understanding). The way we structure the concepts in the discussion of this revised manuscript is, in our opinion, a useful overview of the concepts. The third concept is new in this context. We would like to emphasize that we focus on F5 MNs and intentionally avoid a discussion of mirror neurons beyond F5 in this paper. With the data from this study, we cannot say anything about MNs outside of F5.

Regarding the key question of how the "understanding hypothesis" is testable, or whether it may not be testable at all, we agree, of course, that for the conclusion of whether F5 MNs contribute to perception, only a manipulation of F5 MNs can clarify it. We now say that explicitly in the introduction. We agree with reviewer #2 that "understanding" here is not limited to "action recognition" or "action categorization”, which in principle could be implemented by purely sensory processing. Therefore, we also do not believe that the approach proposed by reviewer #3, which builds on the distinction of actions, would allow for a critical examination of the "understanding hypothesis”. But we disagree that the "understanding hypothesis" is not testable at all. Operationalization is necessary. If we accept that we can measure certain visual or auditory perceptions of an animal by operationalization (e.g., the subjective visual vertical, see for example Khazali et al., PNAS, 2020), then we must also accept that we can, in principle, measure other subjective experiences by operationalization, such as pain or aiming at a goal or even the co- experience of pain. An example of how to approach this is the study by Carrillo et al. (Curr Biol, 2019), which reviewer #2 and colleagues discussed in a recent review article (Bonini et al., TCS, 2022).

With regard to the second theme, experimental and analytical questions, we noticed while reading the comments that in our first version we did not distinguish clearly enough between statements about single neurons and statements about populations of neurons. Therefore, we now clearly separate single neuron analysis and population code analysis in the structure of the article. In view of the fact that statements about mirror neurons in the literature mostly refer to single neurons, we added extensive single neuron analyses, so that only now statistically reliable statements about single neurons are possible. This has led to the realization that the number of neurons with exclusively shared code is so small that these neurons should be considered a rare exception. Given the small number of time periods with shared code, we additionally tested against a hypothesis already rightly proposed as an alternative explanation by G. Csibra in 2005 (Mirror neurons and action observation: Is simulation involved? In: What do mirror neurons mean? Interdisciplines Web Forum 2005). We were able to reject this hypothesis based on two of three methods for testing for a shared code. This is the second piece of evidence besides the clustering of time periods with shared code already described in the first version that time periods with shared code cannot be considered random.

We discuss in more detail the question of whether neurons that exhibit a shared code at least at times support the representation hypothesis. To this end, we additionally examined whether certain action segments are more frequently represented with a shared than with a non-shared code, whether neurons with shared code differ from those with non-shared code in anatomical location, and whether an accuracy can be achieved with a time bin-wise selection of neurons with shared code by population cross-task classifiers as with within-task classifiers in the whole population.

Another issue was how to test for shared code and how to decide if a code has enough sharing. To answer the question, the exact hypothesis we intended to test here is crucial. The representation hypothesis states that the representation of the observed actions in F5 MNs corresponds to the representation as it occurs during the execution of the same actions. Therefore, the relationship between discharge rate and actions that holds during execution should also hold during observation, which is measurable with a classifier trained on execution trials and tested on observation trials. Moreover, the actions should not be more distinguishable during observation with a classifier other than the execution-trained classifier, because if that were so, it would mean that the representation of observed actions is different from that of executed actions. The detection of a cluster of time bins for which both conditions are satisfied confirms that it is possible to discover in this way the shared codes postulated by the representation hypothesis.

With respect to concerns that the monkey may not have used the cue at all when the action was executed, we added a comparison with control trials with a non-informative cue and also compared the duration of the approach phase between the three actions. Regarding oculomotor behavior, we verified that the monkey had actually directed his gaze toward the action during action observation for all three actions.

On the third issue, concerning the novelty of our results, we have now explained in more detail in the introduction why we felt it necessary to conduct a study we considered fundamental. As a result of our study, it can be clearly stated now that representations of observed actions as predicted by the strictly defined mirror mechanism are rare in F5 MNs, but nevertheless cannot be dismissed as random. This dispels the objection rightly raised by Csibra in 2005 and contradicts the currently prevailing view that such a representation can only be found at a population level. Even if these representations are ultimately explained by a concept other than the strictly defined mirror mechanism, their existence must be accounted for by any theory of the function of F5 neurons. Moreover, it is also shown that the observed actions are well discriminated with a non- shared code, at times even optimally. This contradicts the notion – which has been widespread for a long time since the work of Gallese et al. (Brain, 1996) – that mapping to motor representations in terms of broad congruence is simply not perfect. The applied cross-task decoding approach seems promising to test also in the future for a shared action code. Finally, reconsideration of alternative concepts has led us to highlight the possibility of a representation of a goal pursuit by the observer.

Reviewer #1 (Public Review):

The authors set out to investigate the hypothesis that mirror neurons in ventral premotor area F5 code actions in a common motor representation framework. To achieve this, they trained a linear discriminant classifier on the neural discharge of three types of action trials and test whether the thus trained classifier could decode the same categories of actions when observed. They showed that codes were fully matched for a small subset of neurons during the action epoch, while a wider set of "mirror neurons" showed only poorly matched codes for different epochs.

This is one of the descriptions of our results, where we realized that in our first version we did not distinguish clearly enough between statements about single neurons and statements about populations of neurons. This prompted us to perform a detailed single neuron analysis.

The authors controlled for potential visual object confounds by having identical objects be manipulated in three different ways and by having the animal carry out the motor execution in the dark. The main strength of the study lies in the clever decoding approach testing the matched tuning to behavioural categories in a model-free way. The central result is in the identification of the small sub-group of mirror neurons that show true matching during the execution epoch, which can dissociate the three types of action almost perfectly. This aligns well with some previous work while offering a novel avenue to identify and investigate those neurons. The underlying neuronal mechanism and behavioural relevance of these neurons remain an open question. It would have been interesting to understand better whether the specific motor representations at a recording site, for instance identified through microstimulation prior to recording (see Methods), the reaction times on individual trials or the specific gaze targets (object/hand) had a bearing on the decoding performance for a neuron/trial.

We agree that these are interesting questions.

In this study, the focus is on testing for a shared code according to a strictly defined mirror mechanism. We have now compared the anatomical locations of neurons with only time bins in which observed actions were discriminated with a shared code (according to one of the methods) to the locations of neurons with only time bins with non-shared code (see last paragraph in Results). We did not find any relevant difference and this is why one cannot expect topographically specific effects of microstimulation.

We do not expect the reaction time (i.e., the time interval between LED onset and start button release, or the duration of the approach epoch) during execution or observation to have any effect on our results on shared coding as the analysis was based on relative time bins. The observed actions were predominantly distinguished late in the approach epoch, but especially in the manipulation epoch. At this time, reaction time is not expected to have a relevant influence.

The relationship between gaze/eye position and the activity of mirror neurons, during execution or observation, is an interesting topic in itself. However, for testing for a shared code according to a strictly defined mirror mechanism, it is only relevant that the observing monkey actually observes the action. We have ensured this in our experiment by a fixation window and have now also confirmed that the monkey actually looked into the area of the object during all three actions (see Results, lines 209-219 in the manuscript with tracked changes).

Ultimately, the uncovered matched mirror representations should in future experiments be tested with causal interventions and linked trial-by-trial to action selection performance.

The authors put the focus of their discussion on the wider, less well-matched neuronal pool to support an action selection framework, which is of course a valid view and well established in motor representations. From a sensory perspective, sparse coding, as suggested by the small group of "true" mirror neurons identified with the decoding approach, should also be considered as the basis for a possible neuronal mechanism. A particular strength of the paper is that it could give new data and impetus to the important discussion about how motor and sensory coding frameworks come together in cortical processing.

We have expanded the discussion considerably and also address the possibility of sparse coding.  

Reviewer #2 (Public Review):

The paper by Pomper and coworkers is an elegant neurophysiological study, generally sound from a methodological point of view, which presents extremely relevant data of considerable interest for a broad audience of neuroscientists. Indeed, they shed new light on the mirror mechanism in the primate brain, trying to approach its study with a novel paradigm that successfully controls for some important factors that are known to impact mirror neuron response, particularly the target object. In this work, a rotating device is used to present the very same object to the monkey or the experimenter, in different trials, and neurons are recorded while the monkey (motor response) or the experimenter (visual response) performed a different action (twist, shift, lift) cued by a colored LED.

The results show that there is a small set of neurons with congruent visual and motor selectivity for the observed actions, in line with classical mirror neuron studies, whereas many more cells showed temporally unstable matched or even completely non-matched tuning for the observed and executed actions. Importantly, the population codes allow to accurately decode both executed and observed actions and, to some extent, even to cross-decode observed actions based on the coding principles of the executed ones.

In my view, however, the original hypothesis that an observer understands the actions of others by the activation of his/her motor representations of the observed actions constitutes circular reasoning that cannot be challenged or falsified, as the author may want to claim. Indeed, 1) there is no causal evidence in the paper favoring or ruling out this hypothesis (and there couldn't be), 2) there is no independent definition (neither in this paper nor in the literature) of what "action understanding" should mean (or how it should be measured). Instead, the findings provide important and compelling evidence to the recently proposed hypothesis that observed actions are remapped onto (rather than matched with) motor substrates, and this recruitment may primarily serve, as coherently hypothesized by the authors, to select behavioral responses to others (at least in monkeys).

1) One of the main problems of this manuscript is, in my view, a theoretical one. The authors follow a misleading, though very influential, proposal, advanced since the discovery of mirror neurons: if there are (mirror) neurons in the brain of a subject with an action tuning that is matched between observation and execution contexts, then the subject "understands" the observed action. This is clearly circular reasoning because the "understanding" hypothesis uniquely derives from the neuron firing features, which are what the hypothesis should explain. In fact, there is no independent, operational definition of the term "understanding". Not surprisingly there is no causal evidence about the role of mirror neurons in the monkey, and the human studies that have claimed to provide causal evidence of "action understanding" ended up using, practically, operational definitions of "recognition", "match-to-sample", "categorization", etc. Thus, "action understanding" is a theoretical flaw, and there is no way "to challenge" a theoretical flaw with any methodologically sound experiment, especially when the flaw consists of circular reasoning. It cannot be falsified, by definition: it must simply be abandoned. On these bases, I strongly encourage the authors to rework the manuscript, from the title to the discussion, by removing any useless attempt to falsify or challenge a circular concept and, instead, constructively shed new light on how mirror neurons may work and which may be their functional role.

Please see the response to all.

2) An important point to be stressed, strictly related to the previous one, concerns the definition of "mirror neuron". I premise that I am perfectly fine with the definition used by the authors, which is in line with the very permissive one adopted in most studies of the last 20 years in this field. However, it does not at all fulfill the very restrictive original criteria of the study in which "action understanding" concept was proposed (see Gallese et al. 1996 Brain): no response to object, no response to pantomimed action or tool actions, activation during execution in the dark and during the observation of another's action.

We do not agree that the enumerated "very restrictive original criteria" emerge from the Gallese et al. (Brain, 1996) study. Except for the first paragraph in the results section, there is no clear statement on how mirror neurons should be defined.

If the idea (which I strongly disagree with) was to simply challenge a (very restrictive) definition of mirroring (a very out-of-date one, indeed, and different from the additional implication of "action understanding"), the original definition of this concept should be at least rigorously applied. In the absence of additional control conditions, only the example neuron in Figure 2A could be considered a mirror neuron according to Gallese et al. 1996.

We have the impression that the question does not distinguish clearly enough between the definition of "mirror neuron" and the definition of "mirror mechanism". In defining "mirror mechanism", we refer to the work of Rizzolatti and Sinigaglia (Nat Rev Neurosci, 2016). We do not think that this definition is out-of-date (see for example the 2018 article by Rizzolatti and Rozzi in Handbook of Clinical Neurology). If the term "mirror mechanism" is to be defined differently, then another term should be used for a new definition or an annotation should be added (such as "version 2"). This would be necessary to avoid unnecessary confusion resulting from unclear terms.

Permissive criteria implies that more "non-mirror" neurons are accepted as "mirror": simply because they are permissively named "mirror", does not imply they are mirroring anything as initially hypothesized

Even for a neuron that would be classified as a "mirror neuron" according to your previously stated "very restrictive original criteria”, it does not follow that it "mirrors” according to a mirror mechanism. And, of course, it is quite possible that more neurons do not "mirror” according to a mirror mechanism if one tests more neurons.

(Example neuron in Fig 2B, for example, could be related to mouth, rather than hand, movements, since it responds strongly and similarly around the reward delivery also during the observation task, when the monkey should be otherwise still).

We agree, it is not excluded that this neuron has a relation to mouth movements. However, since the neuron meets the conditions to be classified as a "mirror neuron", an additional relation to mouth movements would not be relevant. If mouth movements are to be an exclusion criterion, then this would have to be included and justified in the definition of a "mirror neuron".

Clearly, these concerns impact all the action preference analyses. To practically clarify what I mean, it should be sufficient to note that 74% (reported in this study) is the highest percentage ever reported so far in a study of neurons with "mirror" properties in F5 (see Kilner and Lemon 2013, Curr Biol) and it is similar to the 68% recently reported by these same authors (Pomper et al. 2020 J Neurophysiol) with very similar criteria. Clearly, there is a bias in the classification criteria relative to the original studies: again, no surprise if by rendering most of the recorded neurons "mirror by definition" then they don't "mirror" so much. I suggest keeping the authors' definition but removing the pervasive idea to challenge the (misleading) concept of understanding.

We think that it is very important to clearly separate "mirror neuron" from "mirror mechanism". And the question arises whether one should not include a mirroring criterion, which is derived from a definition of a mirror mechanism, in the definition of mirror neurons. We address this briefly in the discussion. Ultimately, the point of our study is to find out how many of the - if you want to put it that way - "permissively defined" mirror neurons actually “mirror”. And the answer depends on how one defines “mirror mechanism”. We provide an answer by resorting to a “strictly defined mirror mechanism”. We have now also given throughout the results section the percentages of neurons with certain properties with respect to all measured F5 neurons. This is a reference that allows comparisons among studies, provided that no neurons were directly discarded during recording, which we avoided in our study.

3) It would be useful to provide more information on the task. Panel B in Figure 1 is the unique information concerning the type of actions performed by the monkey and the experimenter. Although I am quite convinced of the generally low visuomotor congruence, there are no kinematics data nor any other evidence of the statement "the experimental monkey was asked to pay attention to the same actions carried out by a human actor". First, although the objects were the same, the same object cannot be grasped or manipulated in the same way by a human and a macaque, even just because of the considerable difference in the size of their hands; this certainly changes the way in which monkeys' and experimenter's hands interact with the same object, and this is a quantifiable (but not quantified) source of visuomotor difference between observed and executed actions and a potential source of reduced congruency.

We agree, of course, that there are kinematic differences in how a monkey and how a human manipulate the same object. We have not measured the kinematics and thus cannot make a systematic statement about this. We now report in the results section the rather incidental observation that already the reaching trajectories for the three actions differed and show corresponding differences in the timing of the approach epoch. However, for the question of this study, how many neurons are eligible to represent observed actions according to a strictly defined mirror mechanism, the kinematic repertoire of the observed actor is irrelevant. The reference is the F5 mirror neuron activity during the monkey's own action, i.e., how the monkey approaches the object with his hand, how he grasps it, and how he brings it to a certain target position and holds it there. The observed action, according to the strictly defined mirror mechanism, is to be mapped to this reference. Therefore, we did not collect kinematic data. But it is of course a possible explanation for a non-shared code if the strictly defined mirror mechanism does not apply.

Second, there is little information about monkey's oculomotor behavior in the two conditions, which is known to affect mirror neuron activity when exploratory eye movements are allowed (Maranesi et al. 2013 Eur J Neurosci), potentially influencing the present findings: a {plus minus}7 (vertical) and {plus minus}5 (horizontal) window at 49 cm implies that the monkey could explore a space larger than 10 cm horizontally and 14 cm vertically, which is fine, but certainly leaves considerable freedom to perform different exploratory eye movements, potentially different among observed actions and hence capable to account for different "attention" paid by the monkey to different conditions and hence a source of neural variability, in addition to action tuning.

We agree that the topic of the relationship between F5 MNs activity and eye movements is interesting. And we know from the work of Maranesi et al. (2013) that at least larger eye movements during action observation are related to the activity of F5 MNs. In our study, we ensured that the observing monkey was actually observing the action. For this purpose, we used a fixation window. We now additionally verified that the monkey really looked into the area of the object during all three actions (see Results, lines 209-219 in the manuscript with tracked changes). In our study, the fixation window was so small that the monkey could not see the face of the human actor, in contrast to the study of Maranesi et al. (2013). It was mainly the face that attracted the monkey's attention in that study (measured by gaze position). In our study, the risk that the gaze of observing monkey was out of the fixation window was high when he looked at the human actor's hand above the wrist. The execution of the action by the monkey took place in darkness. We did not use a fixation window because the monkey's own execution of the action can be assumed to direct his attention to the action.

We cannot rule out the possibility that smaller eye movements during observation, larger eye movements during execution in darkness, covert shifts of spatial attention, or more generally attentional fluctuations have an influence on F5 MNs that might have counteracted a shared action code in our study. However, if this were the case, then the investigated hypothesis that the activity of F5 MNs during action observation is a motor representation according to the strictly defined mirror mechanism would also have to be rejected.

4) Information about error trials and their relationship with action planning. The monkey cannot really "make errors" because, despite the cue, each object can be handled in a unique way. The monkey may not pay attention to the cue and adjust the movement based on what the object permits once grasped, depending on online object feedback. From the behavioral events and the times reported in Table 1, I initially thought that "shift" action was certainly planned in advance, whereas "lift" and "twist" could in principle be obtained by online adjustments based on object feedback; nonetheless, from the Methods section it appears that these times are not at all informative because they seem to depend on an explicit constraint imposed by the experimenters (in a totally unpredictable way). Indeed, it is stated that "to motivate the monkey even more to use the LED in the execution task, another timeout was active in 30% (rarely up to 100%) of trials for the time period between touch of object to start moving the object: 0.15 (rarely 0.1) for a twist and shift, 0.35 (rarely 0.3s) for a lift". This is totally confusing to me; I don't understand 1) why the monkey needed to be motivated, 2) how can the authors be sure/evaluate that the monkeys were actually "motivated" in this way, and 3) what kind of motor errors the monkey could actually do if any. If there is any doubt that the monkeys did actually select and plan the action in advance based on the cue, there is no way to study whether the activity during action execution truly reflects the planned action goal or a variety of other undetermined factors, that may potentially change during the trials. Please clarify.

It is true that the three actions could in principle be performed without using the LED as an informative cue. While this is unlikely under the assumption that a monkey prefers the easiest and fastest way to get reward, it remains a possibility. For this reason, we introduced time constraints in a part of the trials. The selection of time constraints and the proportion of trials in which they were applied, was a pragmatic compromise between a time limit, at which the LED must be used as an informative cue for action selection in order to comply with the task, and a time span that allows the task to be completed even when overall motivation is low. The latter takes into account the general experimental experience that a monkey's engagement or motivation in such experiments varies across trials, sessions, and days. To evaluate whether the LED color was, indeed, used as a cue for action planning in the execution task, we randomly interleaved trials with a different LED, non-informative regarding the type of object, as a control in 5% of the trials. We compared the behavioral responses in trials with informative cues and those with a non-informative cue. The behavioral analysis established that both monkeys indeed used the informative cues to guide their choices (see Fig. 1D).

Further evidence that the monkey used the cue for action selection and planning is the finding that the type of action was encoded before the release of the start button and then further during the approach phase, i.e., much earlier than somatosensory feedback about the manipulability of the object was available (see Fig. 3A and Fig. 6A).

Regarding the question, which "motor errors" were possible: The answer can be found in the description of the cases in which a trial was aborted (see Material and methods): releasing the start button too early (< 100 ms after turning on the LED), manipulating the object too slowly after touching it (the time constraints mentioned), not holding the object until the reward was given, or not performing the task at all (10 s timeout).

5) Classification analysis. There seems to be no statistical criterion to establish where and when the decoding is significantly higher than chance: the classifier performance should be formally analyzed statistically. I would expect that, in this way, both the exe-obs and the obs-exe decoding may be significant. Together with the considerations of the previous point 2 about the permissive inclusion criteria for mirror neurons, this is a remarkable (even quite unexpected) result, which would prove somehow contrary to what the authors claim in the title of the paper. The fact that in any classification the "within task" performance is significantly better than the "between task" performance does not appear in any way surprising, considering both the inclusive selection criteria for "mirror neurons" and the unavoidably huge different sources of input (e.g. proprioceptive, tactile, top-down, etc. afferences) between execution and observation. So, please add a statistical criterion to establish and show in the figures when and where the classifications are significantly above chance.

We have added - in addition to the statistics already performed in the first version (Fig. 3A in the previous version, now Fig. 6A) - a number of analyses including statistics. This mainly concerns the analyses regarding a shared code at the single neuron level, in which we additionally tested against the null hypothesis proposed by Csibra in 2005 using permutation tests. And we have now also calculated confidence intervals for the population classifications that allow the comparison with chance level. We re-performed the classification analyses using eight-fold cross-validation. We also added a statistical analysis to the finding of clustering of time periods with shared code (Fig. 4). In Figure 5, we additionally compared the frequency of action segments with shared and non-shared codes, which is a descriptive, exploratory analysis. For this reason, it does not make sense to perform inferential statistics. Overall, these analyses represent a significant expansion of the analyses in the first version. We have done this primarily to arrive at statistically sound conclusions at the single neuron level.

Regarding the comparison between within-task classification (o2o) and cross-task classification (e2o), it is important to keep in mind that the goal was to test the hypothesis that the activity of F5 MNs during action observation is a motor representation of the observed action according to the strictly defined mirror mechanism. This hypothesis requires both, 1) an above chance level accuracy of the e2o classifier and 2) no better accuracy of the o2o classifier as compared to the e2o classifier. If the o2o classifier were better, then the actions would not be represented as they are executed. And the reference in this hypothesis is the motor representation, that is, the code at execution. Thus, the direction e2o classification is the crucial one, not the reverse direction (o2e). One explanation for the fact that o2o shows better accuracy in the population may be the different sensory inputs mentioned above. In this case, the tested hypothesis has to be rejected and replaced by another one, which should then have a different name.

Nevertheless, we also show the result of the o2e cross-task classification in Fig. 6 (yellow curve), which was already included in Fig. 3 of the first version. However, we do not address it in more detail in the main text because it is not relevant for the hypothesis to be tested. It is only a reportable additional result.

6) "As the concept of a mirror mechanism posits that the observation performance can be led back to an activation of a motor representation, we restricted this analytical step to a comparison of the exe-obs and the obs-obs discrimination performance". I don't understand the rationale of this choice. The so-called "concept" of mirror mechanism in classical terms posits that mirror neurons have a motor nature and hence their functioning during observation should follow the same principle as during action execution. But this logical consideration has never been demonstrated directly (it is indeed costated by several papers), and when motor neurons are concerned (e.g. pyramidal tract neurons, see Kraskov et al. 2009) their behavior during action observation is by far more complex (e.g. suppression vs facilitation) than that hypothesized for classical "mirror neurons". Furthermore, when across-task decoding for execution and observation code has been used, both in neurophysiological (e.g. Livi et al. 2019, PNAS) and neuroimaging (Fiave et al. 2018 Neuroimage) data, the visual-to-motor direction typical produce better performance than the opposite one. Thus, I don't see any good reason not to show also (if not even just) the obs-exe results. Furthermore, I wonder whether it is considered the possible impact of a rescaling in the single neuron firing rate across contexts, as the observation response is typically less strong than the execution response in basically all brain areas hosting neurons with mirror properties, and this should not impact on the matching if the tuning for the three actions remains the same (e.g. see Lanzilotto et al. 2020 PNAS). The analysis shown in Figures 4 and 5 is, for the rest, elegant and very convincing - somehow surprising to me, as the total number of "congruent" neurons (7.5%) is even greater than in the original study by Gallese et al. (5.4%).

As to the rationale of our approach, please see our response to the previous point.

On the issue of rescaling: the hypothesis tested here requires that the F5 MNs activity on observation is a motor representation of the observed action. Hence, from the activity during observation the action should be just as readable as from the execution-related activity. If we had to use rescaling to find a shared code, then observed actions would not be represented in F5 MNs in the same way as on execution. Additional information on whether the action is being executed or observed would be needed. This would of course be possible in principle, but would contradict the hypothesis. And we then not only have the difficulty of which readout is the physiological one (here we make a parsimonious assumption with a linear readout), but we would have to make an additional assumption about rescaling. For this study, we have now chosen the solution of performing the action preference analysis on a single neuron level in a statistically clean way. This represents a very liberal form of rescaling, as it only tests whether the action with the highest or lowest discharge rate is the same when executed and observed. That is, if the result here is not fundamentally different, which is the case, then it can also be assumed that one does not get qualitatively different results for other forms of rescaling.

7) The discussion may need quite deep revision depending on the authors' responses and changes following the comments; for sure it should consider more extensively the numerous recent papers on mirror neurons that are relevant to frame this work and are not even mentioned.

The discussion has been thoroughly revised considering the comments raised and suggestions of this and the other two reviewers.

Reviewer #3 (Public Review):

Mirror neurons are a big deal in the neuroscience literature and have been for thirty years. I (and many others) remain skeptical of whether they serve the functions often attributed to them - specifically, whether they are motor planning neurons that contribute to understanding the actions of others. Testing their functions, therefore, is of great interest and importance. The present study, however, is not a cogent or convincing test. I do not think this study helps to answer the questions surrounding mirror neurons. It purports to provide a crucial test, that comes out mostly against the mirror neuron hypothesis, but the test has too many weaknesses to be convincing.

Thank you for the clear words. We take from it, first of all, that in the first version of the manuscript we failed to convey the relevance of our study for the discussion of mirror neuron function. The concerns of this reviewer are in line with those of the others and are addressed in our response to all three reviewers.

First, consider that the motor tuning and the visual tuning match "poorly." How poor or good must the match be before the mirror neuron hypothesis is rejected? I do not know, and the study does not help here. Even a "poor" match could contribute significantly to a social perception function.

The specific hypothesis tested here assumes that an action-specific activity of F5 MNs evoked by observed actions corresponds to an action-specific activity of these actions if executed. The approach taken here to compare cross-task classification accuracy (execution-trained, tested in observation) with within-task classification accuracy (observation-trained, tested in observation) tests this hypothesis. The fact that we found a cluster of time periods of single neurons in which both accuracies are almost equal supports this approach and also the hypothesis for these time periods. In principle, of course, the decision for the presence of a difference or equality is always only a statistical statement and contains assumptions. For example, the assumption that a linear readout has physiological relevance enters here. But this problem exists in all studies that ultimately try to understand biological neuronal networks in order to explain perceptions and behavior. However, it is such studies that attempt to elucidate what information is contained in which neurons that set the stage for experiments that, in the optimal case, manipulate certain neurons in a particular way in order to then measure the behavior of an animal that is just right for those neurons.

Second, the results remind me in some ways of other multi-modal responses in the brain. For example, in the visual area MST, neurons are tuned to optic flow fields that imply specific directions of self-motion. Many of the same neurons are tuned to vestibular signals that also imply specific directions of self-motion. But the optic flow tuning and the vestibular tuning are not perfectly matched. There is considerable slop and complexity in how the two tunings compare within individual neurons. That complexity is not evidenced against multi-modal tuning. Instead, it suggests a hidden-layer complexity that is simply not fully understood yet. Just so here, the fact that the apparent motor tuning and apparent visual tuning match "poorly" is not evidence against both a motor planning and a visual encoding function.

We hope that it is now clearer, in contrast to the first version, that we tested a specific hypothesis that is only a prerequisite for the hypothesis of a very specific form of understanding. Referring to the example, the hypothesis analogous to ours would be that the representation of self-motion direction due to optic flow ("observation") corresponds to the representation of self-motion direction due to vestibular stimulation ("execution"). If it were then found that the self-motion direction due to optic flow cannot be predicted from a classifier trained on vestibular stimulation, and that another classifier trained on optic flow performs better, then the hypothesis would have to be rejected. This is then a reason to realize that "everything is a bit more complex" and to search for better explanations.

Third, the animals are massively over-trained in three actions. They perform these actions and see them performed thousands of times toward the same object. Surely, if I were in the place of the monkey, every time I saw the object, I'd mentally imagine all three actions. As I saw a person act on the object, I'd mentally imagine the alternative two actions at the same time. Even if the mirror neuron hypothesis is strictly correct, this experiment might still find a confusion of signals, in which neurons that normally might respond mainly to one action begin to respond in a less predictable way during all three trial types.

In our study, we tested a specific hypothesis related to the time an action is observed. Here, you suggest an alternative hypothesis. The question is whether this alternative hypothesis better explains the result of our study. The alternative hypothesis can be formulated as follows: the F5 MNs activity elicited by an observed action in this experiment corresponds to a mixture of the activities that occur when the other two actions are executed. This hypothesis is to be rejected because it fails to explain why a shared code occurs in single neurons and why cross-task population classifiers show an accuracy above chance level. A modified alternative hypothesis, which states that what is represented in the experiment during observation is a mixture of all three actions, cannot explain why the three actions are very well represented in the population and are optimally represented exactly when the target position of the object is reached.

Fourth, the experiment relies on a colored LED that acts as an instructional cue, telling the monkey which action to perform. What is to stop the neurons from developing a cue-sensitive response, as in classic studies from Steve Wise and others in the premotor cortex? Perhaps the neuronal signal that the experimenters are trying to measure is partly obscured by other, complex responses influenced in some manner by the instructional cue?

In principle, there is the possibility that purely sensory information is also represented in area F5, at least in some neurons or at certain points in time. We take your suggestion and discuss this as one of the alternative concepts (we call it "sensory concept"). However, several findings argue against this concept. For example, neural responses to cues usually represent the subsequent action, but not sensory information of the cue such as the color of the cue. In our study, it is evident from Figure 3A, 6A and 6B that during action execution, actions are discriminated even before the start button is released. Since this discrimination of actions occurs with a time delay after the cue and then increases continuously, this is evidence that the action to be executed is represented, but not the cue itself.

Fifth, finally, and most importantly, the fundamental problem with this study is that it is correlational. Studies that purport to test the function of a set of neurons, and do so by use of correlational measurements, cannot provide strong answers. There are always half a dozen different interpretations and caveats, such as the ones I raised here. Both sides of a debate can always spin the results, and the arguments are never resolved. To test the mirror neuron hypothesis properly would require a causal study. For example, lesion area F5 and test if the monkey is less able to discriminate the actions of others. Or, electrically microstimulate in area F5 and test if the stimulation interferes (either constructively or destructively) with the task of discriminating the actions of others. Only in this way will it be possible to answer the question: do mirror neurons functionally participate in understanding the actions of others? The present study does not answer that question.

We would like to reiterate that studies aimed at elucidating what information is contained in which neurons or areas are necessary to understand neural network processes and are a prerequisite for conducting well-considered experiments that measure behavioral effects through specific manipulation of the neural network. Without the work of Gallese, Rizzolatti and colleagues, the idea of associating F5 neurons with action understanding would not have occurred in the first place. The current tricky question is whether at all, and if so, to what understanding, to what perception, to what behavior that uses information about mental states of another, F5 MNs might be able to contribute. And for this, it helps to have a clearer idea of what information is contained in F5 MNs during action observation.

Author Response:

Reviewer #1 (Public Review):

This is a short but important study. Basically, the authors show that α-synuclein overexpression's negative impact on synaptic vesicle recycling is mediated by its interaction with E-domain containing synapsins. This finding is highly relevant for synuclein function as well as for the pathophysiology of synucleinopathies. While the data is clear, functional analysis is somewhat incomplete.

We will perform all additional functional analyses asked by the reviewer (listed in “recommendations for the authors”) and report that in the revised version. These include dissociation of exo/endocytosis in the context of synapsin-E domain, and further quantification of the rise and fall of pHluorin curves.

Reviewer #2 (Public Review):

In this manuscript the authors established synapsin's E-domain as an essential functional binding partner that allows α-syn functionality. They show very elegantly that only synapsin isoforms that have an Edomain bind α-syn and allow the inhibition mediated by α-syn. Deletion of the C-terminus (α-syn 96-110) eliminated this interaction. Hence, synapsin E-domain binds to α-syn enabling the inhibitory effect of αsyn on synaptic transmission.

The paper will be improved significantly if additional experiments are added to expand and provide a more mechanistic understanding of the effect of α-syn and the intricate interplay between synapsin, αsyn, and the SV. For an enthusiastic reader, the manuscript as it looks now with only 3 figures, ends prematurely. Some of the experiments above or others could complement, expand and strengthen the current manuscript, moving it from a short communication describing the phenomenon to a coherent textbook topic. Nevertheless, this work provides new and exciting evidence for the regulation of neurotransmitter release and its regulation by synapsin and α-syn.

We will address all the technical and conceptual points raised by the reviewer, and do all the necessary experiments (listed in “recommendations for the authors”) and report that in the revised version). These include quantification of the expression levels of various proteins, evaluation of the dispersion of synapsin and α-syn under the stimulation conditions used in our studies, and consideration of other proposed roles of α-syn.

Author Response:

We thank the reviewers for their very thoughtful suggestions. We will submit a revised manuscript addressing these comments and including a point-by-point response to reviewers. We will provide evidence that Wnt3a treatment increases macropinocytosis and that PMA increases this cellular response in cultured cells, but only in the presence of Wnt3a. This will be done using the current gold standard for macropinocytosis assays, the uptake of high molecular weight Dextran sensitive to the Na/H+ exchanger inhibitor EIPA. A time-lapse video of rapid macropinocytosis cup induction by PMA in colorectal cancer cells will also be provided. Other new experiments will show that levels of the upstream macropinocytosis regulator Rac1 are increased by β-catenin DNA, constitutively active Lrp6, or LiCl. The criticism that by taking a broad approach our study lacks mechanistic analysis depth is a valid one. The reason we used a multiplicity of approaches – Xenopus embryo assays, cancer calls in culture, colon cancer tissue arrays and mouse xenografts – was to validate, in as many different ways possible, a central finding: that the classical phorbol ester tumor promoters can act by potentiating Wnt/β-catenin signaling through membrane trafficking.

Author Response:

We are very grateful to the Editors and the three Reviewers for their valuable reviews of our submission. We will take into account all the comments and provide a revised manuscript with our point-by-point responses as soon as possible. In the meantime, we would like to respond provisionally to the reservation expressed in the eLife editorial assessment and by Reviewer #3 about the validity of our models to study of the neurobehavioral consequences of purine deficiency and the pathogenesis of Lesch-Nyhan disease (LND) in Drosophila.

Two enzymes are responsible for purine recycling in mammals: APRT and HGPRT. Only HGPRT deficiency causes neurobehavioral disturbances and LND in humans, while APRT deficiency leads to metabolic deficits without neurological or behavioral symptoms. In contrast, as we have been able to confirm, Drosophila expresses a single purine recycling enzyme, Aprt, and no HGPRT or HGPRT-like activity. Here we propose different ways to model LND in Drosophila, based either on Aprt deficiency or the expression of mutant HGPRT.

Although it may be difficult to accept that the inactivation of a different gene in a distant organism could be a good model for LND, we have found that, in contrast to humans, Aprt deficiency has both metabolic and neurobehavioral consequences in Drosophila. This suggested that Aprt, being the unique fly purine recycling enzyme, might share the enzymatic function of human APRT and the neurodevelopmental function of human HGPRT, because its inactivation should recapitulate all pathological consequences of a lack of purine recycling in this organism, and in particular in the brain.

The statement by Reviewer #3 that “it is unknown whether Aprt is also a structural homologue [of HGPRT]” is not accurate. APRT and HGPRT are known to be functionally and structurally related. Both human APRT and HGPRT belong to the type I PRTases family identified by a conserved phosphoribosyl pyrophosphate (PRPP) binding motif, which is used as a substrate to transfer phosphoribosyl to purines. This binding motif is only found in PRTases from the nucleotide synthesis and salvage pathways (see: Sinha and Smith (2001) Curr Opin Struct Biol 11(6):733-9. PMID: 11751055). The purine substrates adenine, hypoxanthine and guanine share the same chemical skeleton and APRT can bind hypoxanthine, indicating that APRT and HGPRT also share similarities in their substrate binding sites (Ozeir et al. (2019) J Biol Chem. 294(32):11980-11991. PMID: 31160323). Moreover, Drosophila Aprt and Human APRT are closely related as the amino acid sequences of APRTs have been highly conserved throughout evolution (shown in Fig. S3B of our paper). We apologize for not providing this information in our original submission. This point will be made clearer in the revised article.

Here we report a set of evidence that Drosophila can be used as a model to study LND. A strong argument, as we believe, is that the same drugs have been found effective in rescuing the seizure-like phenotype in Aprt-deficient flies (Figure 7 in our manuscript) and the viability of fibroblasts and neural stem cells derived from iPSCs of LND patients, in which de novo purine synthesis was prevented (as discussed on page 37). This is a good sign that Drosophila could be used to identify new genetic targets and pharmacological compounds capable to rescue HGPRT mutations in humans.

Finally, we would like to emphasize that Reviewer #1 and Reviewer #2 expressed confidence in the potential usefulness of our work to better understand and treat LND in their public reviews. Reviewer #1 indeed stated that: “The findings provide a new example of how manipulating specific genes in the fruit fly allows the study of fundamental molecular processes that are linked to a human disease”, and Reviewer #2 further wrote: "Altogether, these are very important and fundamental findings that convincingly demonstrate the establishment of a Drosophila model for the scientific community to investigate LND, to carry out drug testing screens and find cures”, and added: “To conclude, this is a fundamental piece of work that opens the opportunity for the broader scientific community to use Drosophila to investigate LND”.

Author Response:

We thank the reviewers for the constructive feedback and detailed reviews. To avoid any misunderstandings, we would like to add the following clarification. The comments from Reviewer 3 seem to indicate that in our simulator, synthspot, we mix cells from different data sets and even different species to create synthetic spots. The comment is the following:

The choice to blend mouse and human scRNA-seq datasets in the simulation setup for generating synthetic spots is not ideal due to its departure from a realistic biological scenario.

We would like to point out that the synthetic spots we create for the silver standard data sets are always sampled from the same scRNAseq or snRNAseq data set to keep the simulations as biologically plausible as possible.

For each of the 6 public data sets, we create 9 different synthetic data sets, resulting in a total of 54 synthetic data sets. Each of these 9 data sets correspond to a different abundance pattern with spots representing combinations of cells sampled from this same public data set. Hence, these synthetic data sets always reflect cell types that actually co-occur in the tissue sections used to generate the underlying public scRNAseq or snRNAseq data set.

Author Response:

Reviewer #1 (Public Review):

In this paper, Hui and colleagues investigate how the predictive accuracy of a polygenic score (PGS) for body mass index (BMI) changes when individuals are stratified by 62 different covariates. After showing that the PGS has different predictive power across strata for 18 out of 62 covariates, they turn to understanding why these differences and seeing if predictive performance could be improved. First, they investigated which types of covariates result in the largest differences in PGS predictive power, finding that covariates with larger "main effects" on the trait and covariates with larger interaction effects (interacting with the PGS to affect the trait) tend to better stratify individuals by PGS performance. The authors then see if including interactions between the PGS and covariates improves predictive accuracy, finding that linear models only result in modest increases in performance but nonlinear models result in more substantial performance gains.

Overall, the results are interesting and well-supported. The results will be broadly interesting to people using and developing PGS methods. Below I list some strengths and minor weaknesses.

Strengths:

A major impediment to the clinical use of PGS is the interaction between the PGS and various other routinely measured covariates, and this work provides a very interesting empirical study along these lines. The problem is interesting, and the work presented here is a convincing empirical study of the problem.

The result that PGS accuracy differs across covariates, but in a way that is not well-captured by linear models with interactions is important for PGS method development.

Thank you for all of the positive comments.

Weakness:

While arguably outside the scope of this paper, one shortcoming is the lack of a conceptual model explaining the results. It is interesting and empirically useful that PGS prediction accuracy differs across many covariates, but some of the results are hard to reconcile simultaneously. For example, it is interesting that triglyceride levels are associated with PGS performance across cohorts, but it seems like the effect on performance is discordant across datasets (Figure 2). Similarly, many of these effects have discordant (linear) interactions across cohorts (Figure 3). Overall it is surprising that the same covariates would be important but for presumably different reasons in different cohorts. Similarly, it would be good to discuss how the present results relate to the conceptual models in Mostafavi et al. (eLife 2020) and Zhu et al. (Cell Genomics 2023).

Thank you for the comments. We agree that more generalizable explanations would be useful, which may be worth exploring in future work. Specifically, if there is heteroskedasticity in the relationship between PGS and BMI (e.g., phenotypic variance increases for higher values of BMI while PGS variance does not, or at least by a different amount), then that may partially explain the performance differences when stratifying by covariates that have main effects on BMI – somewhat similarly to what is presented in Figure 2 of Mostafavi et al. Such results may imply that similar performance differences could occur when stratifying by the phenotype itself, although this still may not explain differences in PGS effects, and differences in performance when using nonlinear methods (such as in this work and in Figure 4 of Zhu et al.). While we observe discordant effects for certain covariates across datasets, the findings from the correlation analyses use all cohorts and ancestries, and we expect that these difference in effects across datasets may be due to differences in their relationship with BMI across datasets (triglyceride levels may be especially noisy due to their sensitivity to fasting which may have been controlled for differently across datasets).

Reviewer #2 (Public Review):

This work follows in the footsteps of earlier work showing that BMI prediction accuracy can vary dramatically by context, even within a relatively ancestrally homogenous sample. This is an important observation that is worth the extension to different context variables and samples.

Much of the follow-up analyses are commendably trying to take us a step further-towards explaining the underlying observed trends of variable prediction accuracy for BMI. Some of these analyses, however, are somewhat confounded and hard to interpret.

For example, many of the covariates which the authors use to stratify the sample by may drive range restriction effects. Further, the covariates considered could be causally affected by genotype and causally affect BMI, with reverse causality effects; other covariates may be partially causally affected by both genotype and BMI, resulting in collider bias. Finally, population structure differences between quintiles of a covariate may drive variable levels of stratification. These can bias estimation and confounds interpretations, at least one of which intuitively seems like a concern for each of the context variables (e.g., the covariates SES, LDL, diet, age, smoking, and alcohol drinking).

The increased prediction accuracy observed with some of the age-dependent prediction models is notable. Despite the clear utility of this investigation, I am not aware of much existing work that shows such improvements for context-aware prediction models (compared to additive/main effect models). I would be curious to see if the predictive utility extends to held-out data from a data set distinct from the UKB, where the model was trained, or whether it replicates when predicting variation within families. Such analyses could strengthen the evidence for these models capturing direct causal effects, rather than other reasons for the associations existing in the UKB sample.

Thank you for the comments. We agree there are certain biases that may be introduced in these analyses. For population structure between quintiles, the analyses are already stratified by ancestry and have the top 5 genetic principal components included, which may help with this issue. In the interaction models we included separate terms for the PGS of the covariate as well which was meant to better capture the environmental component of the covariates, which may partially ameliorate issues of collider bias as SNPs that are causally affecting both BMI and the covariate would be partially adjusted for. While range restriction effects could introduce bias, in the correlation analyses the relationship between main effects and interaction effects (which were estimated without range restriction) have strong and reproducible correlations with PGS R2 differences across datasets.

We agree the increased prediction performance using PGS created directly from GxAge GWAS effects is notable, as it is essentially “free” performance increase that doesn’t require any new data, and it likely generalizable to additional covariates. It would be useful to validate its performance in other datasets, especially ones that are outside of the 40-69 age of UKBB.

Reviewer #3 (Public Review):

Polygenic scores (PGS), constructed based on genetic effect sizes estimated in genome-wide association studies (GWAS) and used to predict phenotypes in humans have attracted considerable recent interest in human and evolutionary genetics, and in the social sciences. Recent work, however, has shown that PGSs have limited portability across ancestry groups, and that even within an ancestry group, their predictive accuracy varies markedly depending on characteristics such as the socio-economic status, age, and sex of the individuals in the samples used to construct them and to which they are applied. This study takes further steps in investigating and addressing the later problem, focusing on body mass index, a phenotype of substantial biomedical interest. Specifically, it quantifies the effects of a large number of co-variates and of interactions between these covariates and the PGS on prediction accuracy; it also examines the utility of including such covariates and interaction in the construction of predictors using both standard methods and artificial neural networks. This study would be of interest to investigators that develop and apply PGSs.

I should add that I have not worked on PGSs and am not a statistician, and apologize in advance if this has led to some misunderstandings.

Strengths:

• The paper presents a much more comprehensive assessment of the effects of covariates than previous studies. It finds many covariates to have a substantial effect, which further highlights the importance of this problem to the development and application of PGSs for BMI and more generally.
• The findings re the relationships between the effects of covariates and interactions between covariates and PGSs are, to the best of my knowledge, novel and interesting.
• The development of predictors that account for multiple covariates and their interaction with the PGS are, to the best of my knowledge, novel and may prove useful in future efforts to produce reliable PGSs.
• The improvement offered by the predictors that account for PGS and covariates using neural networks highlights the importance of non-linear interactions that are not addressed by standard methods, which is both interesting and likely to be of future utility.

Thank for the positive feedback.

Weaknesses:

• The paper would benefit substantially from extensive editing. It also uses terminology that is specific to recent literature on PGSs, thus limiting accessibility to a broader readership.
• The potential meaning of most of the results is not explored. Some examples are provided below: • The paper emphasizes that 18/62 covariates examined show significant effects, but this result clearly depends on the covariates included. It would be helpful to provide more detail on how these covariates were chosen. Moreover, many of these covariates are likely to be correlated, making this result more difficult to interpret. Could these questions at least be partially addressed using the predictors constructed using all covariates and their interactions jointly (i.e., with LASSO)? In that regard, it would be helpful to know how many of the covariates and interactions were used in this predictor (I apologize if I missed that). • While the relationship between covariate effects and covariate-PGS interaction effects is intriguing, it is difficult to interpret without articulating what one would expect, i.e., what would be an appropriate null. • The finding that using artificial neural networks substantially improves prediction over more standard methods is especially intriguing, and highlights the potential importance of non-linear relationships between PGSs and covariates. These relationships remain hidden in a black box, however. Even fairly straightforward analyses, based on using different combinations of the PGS and/or covariates may shed some light on these relationships. For example, analyzing which covariates have a substantial effect on the prediction or varying one covariate at a time for different values of the PGS, etc.
• The relationship to previous work should be discussed in greater detail.

Thank you for the comments. Regarding running LASSO with all covariates along with each of their interactions with PGS in one model, upon reading those sections of the text again it is a little unclear we agree; but we actually did something very similar already (related sections have been edited for clarity in our revised manuscript) with these results being presented later on in the neural network section (second paragraph, S Table 7 – those results specifically aren’t in Figure 5). We just looked at changes in prediction performance, and did not try to interpret the model coefficients. We agree that many of the covariates are probably correlated, but based on the correlation results (Figure 4) it doesn’t seem like any covariate is especially important separately from its effect on BMI itself i.e., whatever covariates were chosen by LASSO may still not be especially important. This explanation is related to the interpretation of the neural network results, where neural networks improved performance even over linear models with just age and sex and their interactions with PGS as additional covariates, which may suggest that increased performance is coming from nonlinearities apart from multiplicative interaction effects with the PGS. So observing the coefficients from LASSO but still with a linear model may still not substantially aid in explaining the relationships that increase prediction performance using neural networks (additionally, this analysis may be difficult to replicate since many of the covariates are not present in multiple datasets). But this replication would be nice to see in future studies if such datasets exist. In terms of the null relationship between covariate main and interaction effects, if they are from the same model they will inherently be correlated, but the main effects from Figure 4 are from a main effects model only. Regarding the other points, the text will be edited for clarity and elaboration on specific topics.

Author Response:

We would like to express our gratitude for the valuable feedback provided by the editors and reviewers. In response to the reviewer's comments, we have outlined a plan to carry out additional experiments to bolster our paper's strength. Our primary objectives are to explore the developmental roles of both Porl1F and Regnase-1 and to provide further clarification regarding the involvement of Regnase-1 in memory consolidation. We will utilize the newly available Polr1F RNAi transgenes and confirm the efficacy of both the previous and new RNAi lines through quantitative polymerase chain reaction (qPCR) analysis. Additionally, we aim to investigate the impact of Regnase-1 overexpression on sleep and memory consolidation. We will also clarify some points that may not have been clear to reviewers.

Author Response

Reviewer #1 (Public Review):

This paper has significant strengths in taking a rich, quantitative, neurally-grounded approach to the development of human walking. It provides a rich empirical dataset of EMG and kinematic data at this challenging age, as well as sophisticated analyses of these data in terms of motor primitives, which are a concept that has recently been usefully applied to understanding human walking and its development.

STRENGTHS

It builds on emerging literature in this field and adds data at the key age of infancy-toddlerhood.

It takes a longitudinal approach, sampling children at the ages of newborn, 3 months, and newly walking. This is still reasonably rare in developmental research and allows for a powerful, robust interpretation of data: the authors should be commended for taking this approach.

WEAKNESSES

Some aspects of the work could have been more clearly introduced. This includes neural aspects: the location of the CNS control centres at the spinal level, and which higher centres control them (e.g. brainstem); the justification for understanding primitives as modular (no cross-talk or feedback). It also includes developmental aspects: introducing the stepping reflex, and behavioural aspects of infant motor variability (e.g. Adolph, Hoch & Cole, TICS, 2018).

The patterns relate to walking in a stereotypical manner, yet children's walking is full of skips, jumps, and climbs - both in relation to external obstacles and on even ground. Indeed, it is a challenge to get children to 'walk normally' in a lab. Thus, variability is in fact greater than is discussed here and this should be acknowledged.

Thanks for the remarks. We reviewed the introduction and clarified these points. Mainly, we realized that we were not clear enough about the type of variability that we focused on, and added a paragraph at the top of the introduction to clearly define the different types of variability that exist during development and to specify that we only focus on the ability to produce a given coordination mode (like for example alternated leg movements) with various muscle activities (line 34-44). We also added some specification about the neural structures that are known to be involved in modularity in animals (line 53-58).

The analyses are based on a limited sample of the data. (1) I am not clear on what basis the coders selected cycles, and why 5 cycles were selected. (2) It is not clear why certain movement parameters (cycle duration and flexion/extension proportions) and not others (e.g. step length, double support time) were selected. In particular, it is not clear why the authors focus on temporal, rather than spatial, variability. (3) Some data are based on stepping, and some on kicking. Because it's not clear that these are really equivalent, and because there are small samples of each (n<10), it's not clear that there is enough data to allow us to come to strong conclusions. The sample size should be justified - on the basis of power analyses and/or previous work in this area (e.g. Dominici, Science, n=40). From the results, where p values often hover around p=0.06, the paper seems underpowered to detect a decrease in variability with age for stepping kinematics and primitives.

We initially limited to 5 the number of cycles to analyze in each individual and age in order to make the indexes of variability comparable across individuals and ages. However, as detailed in the general response above, in the new version of the manuscript we preprocessed (i.e. filtered and normalized) a different amount of data in each individual and age (i.e. between 5 and 22 cycles depending on what was available) and we reproduced every analysis of the paper for 5 randomly chosen combinations of 5 cycles when strictly more than 5 cycles were available (i.e. we used a bootstrapping approach, limiting the number of combinations to 5 because of the processing time of the algorithm). Therefore, every result presented in the paper correspond to an average value computed across these 5 random combinations (except when the number of available cycles was strictly equal to 5), which allowed to include a different number of steps in the analysis while keeping the indexes comparable across individuals and ages. This raised the number of cycles included in the analysis from 200 to 586.

We do not present data on step length and double support time because we wanted to apply our analyses on the two behaviors (i.e. stepping and kicking) and there are no step length or support phase in kicking. Moreover, we do not have access to these data. In fact, the available space on the skin on newborns was limited after having disposed EMG sensors, and we could not dispose enough 3D markers to analyze step length. Furthermore, we had to record toddler’s walking in a room that was not equipped with motion capture, therefore we did not have access to any marker’s position at walking onset. As such, we report kinematic parameters that were available for each behavior, which are stride duration, variability of stride duration and percentage of extension phase. This was clarified in the manuscript line 581-583.

As detailed in our general response, we had chosen a very conservative approach which reduced the amount of data that were presented in the original manuscript, however we systematically reviewed our data and we now present our analyses on 18 infants, of which 11 stepped at birth, 15 stepped at 3 months old, 15 kicked at birth, 15 kicked at 3 months old, and 15 were recorded at walking onset. Each infant was followed longitudinally and we only present data if they are available on at least two time points. The results were reinforced with this new number of included individuals, and the p values are stronger (see table S1 were all the p-values are reported, line 979).

There are some points of interpretation that could have been clearer, for example highlighting how one might distinguish between variability as incidental (motor noise) or purposeful (for exploration); and how studying the time around walking onset can contribute to the broader literature on this topic.

The main result of this study is that the structure of EMG variability evolves during the first year of life, but the origin of this variability (incidental or purposeful) remains unknown. Be it purposeful or incidental, variability might arise at any level of the nervous system (Dhawale et al., 2017), and here we propose that it arises at the level of primitives’ activation during early development. As this is coherent with the fact that different pharmacological or electrical stimuli applied to the spinal cord of neonatal rodents can generate variability (Kiehn and Kjærulff, 1996; Klein et al., 2010), we can hypothesize that such variability could be purposely generated at a supra-spinal level during early development. However, even if it is generated at this level, variability could result from an instability of the command rather than from purposeful explorations. Interestingly, the distinction itself might be challenging, because both types of variability (incidental or purposeful) might contribute to exploration: theoretically, variability might be useful for exploration and learning even if it has not been purposely generated by the individual (Dhawale et al., 2017). As such we used animal literature to make hypothesis about the origin of this variability but we are not aware or any protocol that could have helped to discriminate among the two. This was specified line 388-389: “As similar neurophysiological investigations cannot be conducted in human infants, discriminating among purposeful and incidental variability remains challenging,”.

The time around walking onset was chosen to match previous literature on the topic (mainly, Dominici et al., (2011), but it also matches the period that is more and more recommended as a period when to intervene in early therapy. This was discussed line 469-471: “Overall, when compared with adult values (Figure 3, Figure 5, Table S3), our results suggest an immaturity of the modular system before and around walking onset, which confirms that infancy should be an ideal period of plasticity to benefit from in therapy (Ulrich et al., 2010; Morgan et al., 2021).”.<br /> As the age of walking onset is highly variable across infants (Martorell et al., 2006), we also chose to focus on walking onset rather than age to standardize recruitment along experience rather than age, as EMG variability is known to rapidly evolve with experience after a few months of walking experience (Chang et al., 2006). In the new version of the manuscript, we highlighted this variability by allocating legends according to the age of walking onset (Figure 2, Figure 3 and Figure 5, see Figure 3E detailing this legend).

Reviewer #3 (Public Review):

Hinnekens et al. examined the development of humans' leg movements as they learn to step, kick, and independently walk during infancy. An established theory argues that motor movements can be composed of a finite set of building blocks ("motor primitives"), just like any word can be composed of a finite set of letters. In their paper, Hinnekens et al. follow up this theory by longitudinally recording muscle activations of infants using EMG (at three time points: a few days after birth, at 3 months, and shortly after they learned to walk independently). The authors examined two modules that underlie the infants' stepping and two modules that underlie toddler walking, all based on previous literature. The authors also examined different modules that underlie infants' upright stepping and supine kicking. The authors used supervised machine learning (an advanced version of factor analysis) to identify the modules and to track their change at the different developmental time points. The authors found that trial-to-trial variability in the structure of primitives reduces from newborns to toddlers, even though the number of primitives increased. The authors relate these findings to motor exploration by arguing that newborns generate high variability with a low number of primitives.

The paper has one clear strength - its longitudinal recordings. Unlike most papers in this area of research, the authors follow the same individuals from birth until they learn to walk and the comparison between the use of primitives is done on the same infants. This is certainly novel.

That said, the contribution of the paper to the literature is unclear and it suffers from some critical weaknesses that challenge the current conclusions in the paper, based on the existing data.

1) Although the data is based on longitudinal recordings, and this is certainly desirable, the paper is based only on 10 infants. Moreover, only seven infants contributed supine data at the first time points and only six infants contributed upright data at the different time points. The paper would benefit from a more reliable dataset that includes more infants and time points to compare. To conclude the authors' conclusions, much richer data is required.

As detailed in our general response, we had chosen a very conservative approach which reduced the amount of data that were presented in the original manuscript, however we systematically reviewed our data and we now present our analyses on 18 infants, of which 11 stepped at birth, 15 stepped at 3 months old, 15 kicked at birth, 15 kicked at 3 months old, and 15 were recorded at walking onset. Each infant was followed longitudinally and we only present data if they are available on at least two time points. The results were confirmed by those analyses that yielded stronger p-values (see table S1, line 979).

2) Relatedly, although the strength of longitudinal data is compared between individuals and has significant insights into individual differences in development, this was not clearly (sometimes not at all) discussed in the paper. The work would benefit from more focus on individual differences and a clear explanation of its contribution to the field from that aspect. The key arguments in the paper focus on the ratio between the number of primitives and the variability in each time point, but none of this from the lens of individual differences. This is challenging to do because there are not many individuals who contribute to the dataset but otherwise, it is not clear what the paper contributes to previous work and more critically.

Thanks for the suggestion. To follow this remark, we modified each figure of the paper so the 18 individuals would each have their own color and could be followed across figures. Also, as the age of walking onset was different across infants, we allocated colors to each infant based on when they started to walk (Figure 2, Figure 3, Figure 5). Moreover, increasing our cohort highlighted some interindividual differences in the development of kicking only between birth and three months old (Figure 3, Figure 5, Table S1). This was discussed in a new paragraph of the discussion (line 469-487).

3) The motivation for the paper is unclear. Why did the authors do what they did? Why is this important to do it the way they did? In the current manuscript, it is not clear why they used this design to get those conclusions.

The main rational of the paper was to explore a paradox of the literature on early locomotor development: on one hand, newborn infants produce a highly variable muscular activity (Teulier et al., 2012), but on the other hand authors report that they produce rhythmic movement with a small number of invariant modules (Dominici et al., 2011; Sylos-labini et al., 2020). As the latest studies were based on averaged or single-step data, our main goal was to assess both EMG variability and features of modularity in the same cohort, in an attempt to refute or explain this paradox. We reviewed and clarified the introduction on this matter by clarifying the place of our study among the broader literature on variability in development (line 34-44) and by deepening explanations about the abovementioned paradox in relation to previous studies on infants’ modularity (line 72-96).

4) The data selection process is also not clear. At each time point and from each infant, the authors examined 5 cycles from the same leg. The definition of a cycle was hip-flexion onset to another hipflexion onset on one side of hip extension. It is not clear what variability (measured by % of the cycle in flexion and extension) means in this case because infants hold their legs in one position for a long time. What are those 5 cycles? Why five? A lot of information is missing there about the arbitrary selection of analytic parameters. In addition, the authors argue they performed the same analyses with different parameters and that they got similar results. However, those results are not given in detail and it is hard to compare them with the authors' report.

We entirely reviewed our data and less selection were applied in the current manuscript. Here is the complete data selection process:

Among the 18 infants that we followed from birth on, 15 were followed until walking onset (among the other three, one had moved and the other two could not be seen around walking onset because of the covid pandemic). Around birth and three months old, in each infant we tried to elicit stepping (by holding the infant in an upright position with his feet above a surface) and kicking (by placing the infant in a supine position). Therefore, we systematically analyzed each video from every infant and every age to spot and count every alternated leg movement within the two behaviors. After this step, we checked the quality of EMG data for the 10 muscles that were recorded. As our analysis has to be based on the same number of muscles for each individual, if the quality of the signal was too low for even one muscle during a leg cycle, the cycle had to be removed from the analysis. After this check, if less than 5 alternated leg cycles were available, the whole trial was removed from the analysis. The rational is that the hypotheses that we tested were mainly about intra-individual variability and therefore analyses had to be based on a minimal number of cycles. In newborns this was particularly challenging because we were limited in recording time (1 to 2 minutes), moreover we did not always have qualitative EMG data because we always reduced the amount of adhesive surface on the skin for ethical reasons. Therefore for several babies we could not observe enough cycles to include them in the analysis, however in the current version of the manuscript we present data on 11 babies for newborn stepping, 15 babies for 3 mo stepping, 15 babies for newborn kicking, 15 babies for 3 mo kicking, and 15 babies for toddlers walking. The trials that were not included are grey in Table 1 of this document. For every other trial, the exact number of remaining cycles are reported in the same table.

In the previous version of the manuscript, as we wanted the indexes to be comparable across individuals and ages, we had systematically analyzed 5 cycles that were randomly chosen among the available one. However this created data loss. As detailed in the general response above, to be less selective and to include every available cycle, we now rely on a new approach: if more than 5 cycles were available, we computed every variable of the study 5 times (for 5 random combinations of 5 cycles that were randomly chosen among every available cycle). The variables were averaged afterwards. Thanks to this new approach, 586 cycles are now included in the analysis, which confirmed the robustness of our findings.

Infants can indeed hold their legs in one position for a long time but all of our results were obtained after having normalized each phase of flexion or extension by a given number of time points (see Figure 6, Temporal normalization). Our results were also verified with a different temporal normalization, directly normalizing the cycle instead of the phases. We choose not to report more results in the main text for the overall readability of the paper but here are the same table of p-value as in the appendix of the paper with a normalization based on cycles instead of phases.

5) The recording times are not common across individuals. One newborn was recorded after 1 day and the other after 21 days. Not sure this is comparable, especially if the main contribution of the paper is the longitudinal data. Moreover, the second recording was conducted between 74 days to 122 days. This range is too broad. Same for the third time point - one walk onset is not reported, some infants were recorded at <380 days and some >500 days. This difference challenges the reliability of the data.

Given the high inter-individual variability that relates to the age of walking onset (Martorell et al., 2006) it is often a challenge in developmental sciences to choose between standardizing recruitment according to the age or according to the experience. In the present study, we choose to recruit toddlers of similar experience (i.e. around walking onset) rather than on similar age because motor variability is known to depend a lot on experience, in particular regarding EMG data during the first months of walking (Chang et al., 2006). However, we agree with the reviewer that the age of walking onset is an important source of inter-individual variability and therefore we modified each figure of the paper so the 18 individuals would each have their own color which was ordered and allocated according to the age of walking onset (see Figure 3E detailing this legend).

Regarding the other recording points, and the experience after walking onset, the recording time can indeed vary across individual despite our efforts during data collection to prevent this phenomenon. Main reasons were benign diseases of infants or work constraints for parents that induced postponements of the appointments. However, we report the precise age of each infant for each recording as well as individual data underlying each global figure (see source data of Figure 2, Figure 3 and Figure 5). Based on these data we checked that the individual that were recorded later than the others (for example, subject 1 and subject 14 who were recorded at 21 days for the 1st time point) did not demonstrate aberrant values.

6) Conceptually, I'm not sure I understand why the authors selected leg alternation (and not other types of movements) as their modules. I was not convinced that leg alternations reflect their real-life locomotor experience (e.g., short bouts in all directions), and therefore the variability measured in this work does not reflect the variability of infants' natural locomotor behaviour.

We fully agree that leg alternation do not reflect the whole variability that underlies real-life locomotor experience of these infants, however we did not intend to focus here on all the variability that exists during development but more specifically on the variability that allows to produce a given type of behavior with different inputs. This variability is interesting to study because infants tend to use steadier and steadier patterns of coordination to produce a given movement (Teulier et al., 2012), suggesting that they explore among different possible muscular associations before choosing some. As we wanted to study this phenomenon, it appeared methodologically pertinent to fix other sources of variability (i.e. to study different behaviors separately and to study only one coordination mode), as is commonly done in other EMG-based studies of the field (Dominici et al., 2011; Sylos-labini et al., 2020; Teulier et al., 2012). This choice allowed to remain comparable between infants and toddlers. Indeed, while infants produce numerous coordinative patterns while stepping or kicking, such as parallel cycles or singles cycles for example, toddlers only produce alternated flexion and extension cycle of the lower-limb when walking. Therefore, by selecting alternating cycles of flexion and extension only in infants, we ensure that the differences of variability that we observe between ages is not due to the ability of producing various movement, but really due to the ability of producing a given movement with various muscle outputs. Accordingly, and following our results, it allows to conclude that the structure of variability evolve between birth and independent walking to command a given movement. To explain this notion that relates to the redundancy of motor control, we added a new paragraph at the top of the introduction to better explain the place of our studies among broader literature on infant variability (line 34-44). We also clearly wrote in the discussion that our conclusions did not apply to every developmental source of variability (line 393-395): “As we observed such structure within alternated leg movements, other studies are needed to explore the extent of these results to other early behaviors or coordination modes”.

7) There is not enough rationale for why the specific measurements (IEV, VAF, IRV, etc.) were used and why those are the appropriate ones for the address the questions in the paper. What is the justification for using those measurements?

As our main goal is to characterize how EMG variability can be generated in a modular system, we defined those metrics as directly representative of the different features that we wanted to study: variability of the EMG output, dimensionality of the underlying modular organization, variability of module activations and selectivity of the command (be it through module activations or within module themselves). While VAF is commonly used in muscle synergies studies, this study is the first to explore how cycle-to-cycle variability could be generated in a modular system, and therefore these indexes were defined for its proper needs. As such to clarify their role to a broad audience we included a new table at the beginning of the Results section (see Table 1 of the ms, line 176).

8) Some of the conclusions, especially those that relate to motor exploration, are not based on sufficient data. Motor exploration was not explicitly measured in this study, and how motor exploration is reflected by the current data and analyses is not clear.

We fully agree with the reviewer: while we observed that the structure of EMG variability evolves during the first year of life, the origin of this variability (incidental or purposeful) remains unknown. This was specified line 388-389 “As similar neurophysiological investigations cannot be conducted in human infants, discriminating among purposeful and incidental variability remains challenging,”.

Author Response

Reviewer #1 (Public Review):

Summary

While DNA sequence divergence, differential expression, and differential methylation analysis have been conducted between humans and the great apes to study changes that "make us human", the role of lncRNAs and their impact on the human genome and biology has not been fully explored. In this study, the authors computationally predict HSlncRNAs as well as their DNA Binding sites using a method they have developed previously and then examine these predicted regions with different types of enrichment analyses. Broadly, the analysis is straightforward and after identifying these regions/HSlncRNAs the authors examined their effects using different external datasets.

Strengths/weaknesses

By and large, the analysis performed is dependent on their ability to identify HSlncRNAs and their DBS. I think that they have done a good job of showing the performance metrics of their methods in previous publications. Thereafter, they perform a series of enrichment-type analyses that have been used in the field for quite a while now to look at tissue-specific enrichment, or region-specific enrichment, or functional enrichment, and I think these have been carried out well. The authors achieved the aims of their work. I think one of the biggest contributions that this paper brings to the field is their annotation of these HSlncRNAs. Thus a major revisionary effort could be spent on applying their method to the latest genomes that have been released so that the community could get a clean annotation of newly identified HSlncRNAs (see comment 2).

Comments

1) Though some of their results about certain HSlncRNAs having DBSs in all genes is rather surprising/suspicious, I think that broadly their process to identify and validate DBSs is robust, they have multiple lines of checks to identify such regions, including functional validation. These predictions are bound to have some level of false positive/negative rate and it might be nice to restate those here and on what experiment/validation data these were conducted. However, the rest of their analysis comprises different types of enrichment analysis which shouldn't be affected by outlier HSlncRNAs if indeed their FPR/FNR are low.

2) There are now several new genomes available as part of the Zoonomia consortium and 240 Primate consortium papers released. These papers have re-examined some annotations such as Human Accelerated Regions (HARs) and found with a larger dataset as well as better reference genomes, that a large fraction of HARs were actually incorrectly annotated - that is that they were also seen in other lineages outside of just the great apes. If these papers have not already examined HSlncRNAs, the authors should try and re-run the computational predictions with this updated set and then identify HSlncRNAs there. This might help to clarify their signal and remove lncRNAs that might be present in other primates but are somehow missing in the great apes. This might also help to mitigate some results that they see in section 3 of their paper in comparing DBS distances between archaics and humans.

3) The differences between the archaic hominins in their DBS distances to modern humans are a bit concerning. At some level, we expect these to be roughly similar when examining African modern humans and perhaps the Denisovan being larger when examining Europeans and Asians, but they seem to have distances that aren't expected given the demography. In addition, from their text for section 3, they begin by stating that they are computing two types of distances but then I lost track of which distance they were discussing in paragraph 3 of section 3. Explicitly stating which of the two distances in the text would be helpful for the reader.

(1) According to Figure 1A (according actually to Meyer et al., 2012, Prufer et al., 2017, and Prüfer et al., 2013), the phylogenetic distance from modern humans to Denisovan is shorter than the distance to Altai Neanderthal. However, also according to these studies, the branch of Denisovan is more remote to modern humans than Altai Neanderthal. Thus, it is not unreasonable to find that 2514 and 1256 DBSs have distances > 0.034 in genes in Denisovans and Altai Neanderthals, respectively. Probably, both the phylogenetic distances and DBS distances depend considerably on the sampled genomes of Altai and Denisovan who lived on the earth for quite long. When new samples are obtained, these distances may be somewhat changed.

(2) Regarding “they are computing two types of distances but then I lost track of which distance they were discussing in paragraph 3 of section 3”, the second type of distances were discussed in section 3, and the distances computed in the first way were not further analyzed because “This defect may be caused by that the human ancestor was built using six primates without archaic humans”.

4) Isn't the correct control to examine whether eQTLs are more enriched in HSlncRNA DBSs a set of transcription factor binding sites? I don't think using just promoter regions is a reasonable control here. This does not take away from the broader point however that eQTLs are found in DBSs and I think they can perform this alternate test.

Indeed, the TFs-TFBSs and lncRNAs-DBSs relationships are comparable, and which one contains more QTLs is an interesting question. In this sense, it is reasonable to use TFBSs as the control. However, for three reasons, we did not perform the comparison and use TFBSs as the control. First, most TFBSs are predicted by varied methods, making us concern the reliability of comparing two sets of predictions. Second, most QTLs in DBSs are mQTLs but most QTLs in TFBSs are eQTLs. Third, probably a greater portion of TFBSs than DBSs are not in promoters, and the time consumption of LongTarget made us unable to predict DBSs truly genome-wide. Nevertheless, this is an interesting question deserving further exploring.

5) In the discussion, they highlight the evolution of sugar intake, which I'm not sure is appropriate. This comes not from GO enrichment but rather from a few genes that are found at the tail of their distribution. While these signals may be real, the evolution of traits is often highly polygenic and they don't see this signal in their functional enrichment. I suggest removing that line. Moreover, HSlncRNAs are ones that are unique across a much longer time frame than the transition to agriculture which is when sugar intake rose greatly. Thus, it's unlikely to see enrichment for something that arose in the past 6000-7000 years would in the annotation that is designed to detect human-chimp or human-neanderthal level divergence.

Multiple sugar metabolism-related pathways, including “glucose homeostasis” and “glucose metabolic process”, are found to be enriched only in Altai Neanderthal but not in chimpanzees (Figure 2). Indeed, HS lncRNAs are across a much longer time frame than the transition to agriculture. However, given that apes and monkeys know picking the ripe, sugar-rich fruits at the right time and place, we conjecture that archaic humans as hunter-gatherer could effectively explore natural sugars.

Reviewer #2 (Public Review):

Lin et al attempt to examine the role of lncRNAs in human evolution in this manuscript. They apply a suite of population genetics and functional genomics analyses that leverage existing data sets and public tools, some of which were previously built by the authors, who clearly have experience with lncRNA binding prediction. However, I worry that there is a lack of suitable methods and/or relevant controls at many points and that the interpretation is too quick to infer selection. While I don't doubt that lnc RNAs contribute to the evolution of modern humans, and certainly agree that this is a question worth asking, I think this paper would benefit from a more rigorous approach to tackling it.

At this point, my suggestions are mostly focused on tightening and strengthening the methods; it is hard for me to predict the consequence of these changes on the results or their interpretation, but as a general rule I also encourage the authors to not over-interpret their conclusions in terms of what phenotype was selected for when as they do at certain points (eg glucose metabolism).

I note some specific points that I think would benefit from more rigorous approaches, and suggest possible ways forward for these.

1) Much of this work is focused on comparing DNA binding domains in human-unique long-noncoding RNAs and DNA binding sites across the promoters of genes in the human genome, and I think the authors can afford to be a bit more methodical/selective in their processing and filtering steps here. The article begins by searching for orthologues of human lncRNAs to arrive at a set of 66 human-specific lncRNAs, which are then characterised further through the rest of the manuscript. Line 99 describes a binding affinity metric used to separate strong DBS from weak DBS; the methods (line 432) describe this as being the product of the DBS or lncRNA length times the average Identity of the underlying TTSs. This multiplication, in fact, undoes the standardising value of averaging and introduces a clear relationship between the length of a region being tested and its overall score, which in turn is likely to bias all downstream inference, since a long lncRNA with poor average affinity can end up with a higher score than a short one with higher average affinity, and it's not quite clear to me what the biological interpretation of that should be. Why was this metric defined in this way?

Length is an important metric of DBS, but it has a defect – a triplex of 100 bp may have 50% or 70% of nucleotides bound; in the two situations, the binding affinity of DBD and DBS is very different.

2) There is also a strong assumption that identified sites will always be bound (line 100), which I disagree is well-supported by additional evidence (lines 109-125). The authors show that predicted NEAT1 and MALAT1 DBS overlap experimentally validated sites for NEAT1, MALAT1, and MEG3, but this is not done systematically, or genome-wide, so it's hard to know if the examples shown are representative, or a best-case scenario.

More details are described in the citation Wen et al. 2022. We will put the sites into Supplementary Tables in the revised version.

It's also not quite clear how overlapping promoters or TSS are treated - are these collapsed into a single instance when calculating genome-wide significance? If, eg, a gene has five isoforms, and these differ in the 3' UTR but their promoter region contains a DBS, is this counted five times, or one? Since the interaction between the lncRNA and the DBS happens at the DNA level, it seems like not correcting for this uneven distribution of transcripts is likely to skew results, especially when testing against genome-wide distributions, eg in the results presented in sections 5 and 6. I do not think that comparing genes and transcripts putatively bound by the 40 HS lncRNAs to a random draw of 10,000 lncRNA/gene pairs drawn from the remaining ~13500 lncRNAs that are not HS is a fair comparison. Rather, it would be better to do many draws of 40 non-HS lncRNAs and determine an empirical null distribution that way, if possible actively controlling for the overall number of transcripts (also see the following point).

(1) If, say, three transcripts of a gene share the same promoter region (i.e., they have the same TSS) but differ only in 3’UTR, the promoter region was used to predict DBSs just for once. Otherwise, if the three transcripts have different TSS, the three promoter regions were used to predict DBSs.

(2) A gene may have many DBSs if it has many transcripts, or few ones if it has just a few transcripts. We did not correct for this uneven distribution of transcripts, because our GTEx analysis was on the transcript level; it is well recognized that transcripts of the same gene can be expressed in different tissues.

(3) We randomly sampled a pair of non-HS lncRNA and a transcript for 10000 times (i.e., 10000 pairs). It is a point that multiple draws of 40 non-HS lncRNAs should be made to make the statistics more robust.

3) Thresholds for statistical testing are not consistent, or always well justified. For instance, in line 142 GO testing is performed on the top 2000 genes (according to different rankings), but there's no description of the background regions used as controls anywhere, or of why 2000 genes were chosen as a good number to test? Why not 1000, or 500? Are the results overall robust to these (and other) thresholds? Then line 190 the threshold for downstream testing is now the top 20% of genes, etc. I am not opposed to different thresholds in principle, but they should be justified.

The over-representation analysis using g:Profiler was performed taking the whole genome as the background. Analyzing more DBSs (especially weak DBSs) would generate more results, but the results could be less reliable. Thus, there is a trade-off between analyzing fewer DBSs with relatively high reliability and analyzing more DBSs with relatively low reliability. Inevitably, the handling of this trade-off is somewhat subjective, and to carefully compare the two classes of DBSs per can be an independent question. Although weak DBSs were not systematically analyzed, the results from the strong DBSs undoubtedly suggest that HS lncRNAs have contributed greatly to human evolution.

Likewise, comparing Tajima's D values near promoters to genome-wide values is unfair, because promoters are known to be under strong evolutionary constraints relative to background regions; as such it is not surprising that the results of this comparison are significant. A fairer comparison would attempt to better match controls (eg to promoters without HS lncRNA DBS, which I realise may be nearly impossible), or generate empirical p-values via permutation or simulation.

We examined Tajima’s D in DBSs (Supplementary Figure 9) and in HS lncRNA genes (Supplementary Figure 18). In both cases, we compared the Tajima’s D values with the genome-wide background.

4) There are huge differences in the comparisons between the Vindija and Altai Neanderthal genomes that to me suggest some sort of technical bias or the such is at play here. e.g. line 190 reports 1256 genes to have a high distance between the Altai Neanderthal and modern humans, but only 134 Vindija genes reach the same cutoff of 0.034. The temporal separation between the two specimens does not seem sufficient to explain this difference, nor the difference between the Altai Denisovan and Neanderthal results (2514 genes for Denisovan), which makes me wonder if it is a technical artefact relating to the quality of the genome builds? It would be worth checking.

We used the same workflow (and the same cutoff 0.034) to analyze Vindija and Altai Neanderthal and Denisovan. If a smaller cutoff was used, one would see more Vindija genes. The question again is that there is a trade-off. Analyzing epigenome and epigenetic regulation in archaic genomes is an interesting direction, and much more studies are needed before more reasonably setting related parameters and cutoffs.

5) Inferring evolution: There are some points of the manuscript where the authors are quick to infer positive selection. I would caution that GTEx contains a lot of different brain tissues, thus finding a brain eQTL is a lot easier than finding a liver eQTL, just because there are more opportunities for it. Likewise, claims in the text and in Tables 1 and 2 about the evolutionary pressures underlying specific genes should be more carefully stated. The same is true when the authors observe high Fst between groups (line 515), which is only one possible cause of high Fst - population differentiation and drift are just as capable of giving rise to it, especially at small sample sizes.

Author Response

The primary concern of Reviewer 1 is that Ne might affect gBGC and hence GC, and this might act as a confounding effect. The reviewer suggests that we should investigate how gBGC (with GC presumably as its proxy) might affect CAIS, and to what extent any relationship here could explain the relationship between CAIS and body mass. We believe that we have already dealt with this both in Supplementary Figure S5A (where we regret having inserted the wrong figure panel, a mistake we will correct), and its PIC-corrected counterpart in S5B. These two panels show (or will show) that CAIS is not correlated with GC. Note that we expect our genomic-GC-based codon usage expectations to reflect unchecked gBGC in an average genomic region, independently of whether that species has high or low Ne. Our working model is that mutation biases, including but not limited to the strength of gBGC, vary among species, and that they rather than selection determine each species’ genome-wide %GC. By correcting for genome-wide %GC, our CAIS thus corrects for mutation bias, in order to isolate the effects of selection.

Reviewer 1 also suggests that we examine the relationship between gene expression and GC corrected RSCU, as we would expect codon adaptation to be stronger in more highly expressed genes, as was previously shown in the non-GC corrected CAI metric (Sharp et al 1987). Correlations with gene expression are outside the scope of the current work, which is focused on producing a single value of codon adaptation per species. It is indeed possible that our general approach could be useful in future work investigating differences among genes.

One key difference between our work and that of Galtier et al. 2018 is that our approach does not rely on identifying specific codon preferences per species. Our approach thus remains appropriate even for scenarios e.g. where different cell types, different environmental conditions, and/or different genes have different codon preferences (Gingold et al. 2014 https://doi.org/10.1016/j.cell.2014.08.011). At a high level, our results are in broad agreement with those of Galtier et al., 2018, who found that gBGC affected all animal species, regardless of Ne, and who like us, found that the degree of selection on codon usage depended on Ne. Through use of a more sensitive methodology, we believe we have expanded our ability to detect codon adaptation into animals of somewhat higher Ne than in previous work.

We thank Reviewer 2 for explicitly laying out the math that was implicit in our Figures 1 and 2. In our revisions, we will more clearly acknowledge that the per-site codon adaptation bias depicted in Figure 1 has limited sensitivity to s*Ne. We believe our approach worked despite this because the phenomenon is driven by what is shown in Figure 2. I.e., where Ne makes a difference is by determining the proteome-wide fraction of codons subject to significant codon adaptation, rather than by determining the strength of codon adaptation at any particular site or gene.

Simulated datasets would be great, but we think it a nice addition rather than must-have, in particular because we are skeptical about whether our understanding of all relevant processes is good enough such that simulations would add much to our more heuristic argument along the lines of Figure 2. E.g. we believe the complications documented by Gingold et al. 2014 cited above are pertinent, but incorporating them into simulations would require a complex set of assumptions.

In response to the final comment of reviewer 2, the reason that we hard-coded genome-wide %GC values is that we took them from the previous study of James et al. (2023) https://doi.org/10.1093/molbev/msad073. As summarized in the manuscript, genome-wide %GC was a byproduct of a scan conducted in that work, of all six reading frames across genic and intergenic sequences available from NCBI with access dates between May and July 2019. The code used in the current work to calculate the intergenic %GC, as well as that used to calculate amino acid frequencies, is located at https://github.com/MaselLab/Codon-Adaptation-Index-of-Species. We agree that more user-friendly tools would be useful, but producing robust tools falls outside the scope of the current manuscript.

Author Response

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

eLife assessment

This important study addresses both the native role of the Plasmodium falciparum protein PfFKBP35 and whether this protein is the target of FK506, an immunosuppressant with antiplasmodial activity. The genetic evidence for the essentiality of FKBP35 in parasite growth is compelling. However, the conclusion that the role of FKBP35 is to secure ribosome homeostasis and the claim that FK506 exerts its antimalarial activity independently of FKBP35 rely on incomplete evidence.

We thank the Reviewers and Editors for their careful evaluation of our manuscript and the constructive criticism. We realized that some of our conclusions may be regarded/misunderstood as overstatements. This was by no means our intention and we apologize for the unnecessary inconvenience. The phenotype of FKBP35 knock-out parasites clearly centers on failing ribosomes and protein synthesis, which in our opinion, provides an important leap towards understanding the role of this drug target in P. falciparum biology. It is however correct that, at this point, we can only make evidence-based hypotheses about direct interaction partners and we will emphasize this more clearly in a revised version of the manuscript. In order to prevent misinterpretation of our work, and as detailed in the point-by-point responses to the reviewer comments, we propose changing the manuscript title to “Genetic validation of PfFKBP35 as an antimalarial drug target”. To address the criticism regarding the effects of FK506, we will perform specific additional experiments. We are convinced that this new data set will resolve any remaining ambiguities and allows for a conclusive assessment of FK506 drug activity in P. falciparum.

Reviewer #1 (Public Review):

In this study, the authors investigate the biological function of the FK506-binding protein FKBP35 in the malaria-causing parasite Plasmodium falciparum. Like its homologs in other organisms, PfFKBP35 harbors peptidyl-prolyl isomerase (PPIase) and chaperoning activities, and has been considered a promising drug target due to its high affinity to the macrolide compound FK506. However, PfFKBP35 has not been validated as a drug target using reverse genetics, and the link between PfFKBP35-interacting drugs and their antimalarial activity remains elusive. The manuscript is structured in two parts addressing the biological function of PfFKBP35 and the antimalarial activity of FK506, respectively.

The first part combines conditional genome editing, proteomics and transcriptomics analysis to investigate the effects of FKBP35 depletion in P. falciparum. The work is very well performed and clearly described. The data provide definitive evidence that FKBP35 is essential for P. falciparum blood stage growth. Conditional knockout of PfFKBP35 leads to a delayed death phenotype, associated with defects in ribosome maturation as detected by quantitative proteomics and stalling of protein synthesis in the parasite. The authors propose that FKBP35 regulates ribosome homeostasis but an alternative explanation could be that changes in the ribosome proteome are downstream consequences of the abrogation of FKBP35 essential activities as chaperone and/or PPIase. It is unclear whether FKBP35 has a specific function in P. falciparum as compared to other organisms. The knockdown of PfFKBP35 has no phenotypic consequence, showing that very low amounts of FKBP35 are sufficient for parasite survival and growth. In the absence of quantification of the protein during the course of the experiments, it remains unclear whether the delayed death phenotype in the knockout is due to the delayed depletion of the protein or to a delayed consequence of early protein depletion. This limitation also impacts the interpretation of the drug assays.

We thank the Reviewer for the compliments regarding our experimental setup and the clarity of our manuscript. We agree that the link between FKBP35 knock-out and ribosome homeostasis is indirect and we now emphasize this more clearly in the revised manuscript. To prevent a general misinterpretation of our manuscript, we will adapt the title accordingly.

We would still like to reiterate that the phenotype of FKBP35 knock-out parasites is best described by their defects in maintaining functional ribosomes. It is for several reasons that we believe the links between FKBP35 and ribosome function are purely evidence driven: First, pre-ribosomal and nucleolar factors are the first proteins (in generation 1 schizonts) to be affected upon knock-out of fkbp35 (Figure 2A, Table S1). We realized that Figure 2A falls short in showing this observation, which is why will update the figure accordingly. Second, the dysregulation of ribosomal factors and the general stall in protein synthesis is dominating the phenotype of FKBP35 knock-out parasites in generation 2. We thus believe it is appropriate to say that knock-out cells are most likely killed in response to defective ribosome maintenance – which is a consequence of reduced FKBP35 levels. We are aware that our experiments (and possibly any other reverse genetics approach) cannot rule out that FKBP35 affects ribosomal factors indirectly. Clearly, more work is required to disentangle this question in more detail in the future.

We agree with the Reviewer that it is not possible to tell if the delayed death-like phenotype is due to a “delayed protein depletion”. We would however like to note that the DiCre/loxP approach allows for an immediate knock-out at the genome level and is thus as precise as possible. Further, in addition to the substantial depletion of FKBP35 in knock-out cells during the phenotypically silent generation, knocking out of fkbp35 at earlier time points (TPs 24-30 and 34-40 hpi in the preceding generation) resulted in the very same phenotype cycle (Figure 1). Here, parasite death was delayed substantially longer, i.e. more than one complete cycle. Together with the dysregulation of early ribosome maturation in generation 1, these findings point towards a delayed death phenotype. It is of course still possible to explain the delayed death-like phenotype by remnant activity of proteins synthetized prior to the genomic knock-out. We address this possibility and describe the two scenarios mentioned by the Reviewer in lines 141-144. Disentangling the two possibilities in future experiments will be difficult, not only with regards to FKBP35, but regarding “delayed death” phenotypes in general.

In the second part, the authors investigate the activity of FK506 on P. falciparum, and conclude that FK506 exerts its antimalarial effects independently of FKBP35. This conclusion is based on the observation that FK506 has the same activity on FKBP35 wild type and knock-out parasites, suggesting that FK506 activity is independent of FKBP35 levels, and on the fact that FK506 kills the parasite rapidly whereas inducible gene knockout results in delayed death phenotype. However, there are alternative explanations for these observations. As mentioned above, the delayed death phenotype could be due to delayed depletion of the protein upon induction of gene knockout. FK506 could have a similar activity on WT and mutant parasites when added before sufficient depletion of FKBP35 protein. In some experiments, the authors exposed KO parasites to FK506 later, presumably when the KO is effective, and obtained similar results. However, in these conditions, the death induced by the knockout could be a confounding factor when measuring the effects of the drug. Furthermore, the authors show that FK506 binds to FKBP35, and propose that the FK506-FKBP35 complex interferes with ribosome maturation, which would point towards a role of FKBP35 in FK506 action. In summary, the study does not provide sufficient evidence to rule out that FK506 exerts its effects via FKBP35.

Noteworthy, we were also very much surprised by data indicating that the antimalarial activity of FK506 is independent of FKBP35. It is for this reason that we conducted a comprehensive set of experiments to disprove our initial observations, but couldn`t find any evidence for an FKBP35-dependent mode of action of FK506:

We were not able to see altered FK506 sensitivity in (i) inducible knock-down parasites, (ii) inducible overexpression parasites and (iii) inducible knock-out parasites. Parasites with altered FKBP35 levels (as assessed by Western blot and quantitative proteomics at 36-42 hpi, respectively) were equally sensitive to FK506. Importantly, at no sub-lethal FK506 concentration did lower FKBP35 levels lead to an altered response of FKBP35KO compared to the wild-type control population. Furthermore, (iv) induction of the knock-out in the cycle preceding FK506 exposure also had no effect on parasite sensitivity. As mentioned by the Reviewer, we also exposed the parasites to FK506 at 30-36 hpi and (v) did not see any effect, even though we measured a 19-fold difference in FKBP35 protein levels between the parasite populations at 36-42 hpi. At this point, parasite death induced by the knock-out cannot be a confounding factor (as it was mentioned by the Reviewer), because the FKBP35 knock-out has no effect on parasite survival in generation 1 in the absence of FK506 (Figure 1F). This demonstrates that the observed effect is only due to drug-mediated killing and not due to the FKBP35 knock-out.

To account for a scenario in which the drop in FKBP35 levels only occurs after 36 hpi, we will perform an additional set of experiments, in which we induce the knock-out at 0-6 hpi and treat the parasites at 36-42 hpi (i.e. the time point at which the 19-fold difference in protein levels was measured by quantitative proteomics). This setup will allow determining whether or not the parasite killing activity of FK506 depends on FKBP35 levels.

So far, our experiments cannot support any scenario in which FK506 kills P. falciparum parasites via inhibiting the essential role of FKBP35 and we would therefore want to insist that this statement is based on highly solid evidence. In this context, it is important to note that our conclusion includes two scenarios: “This indicates that either the binding of FK506 does not interfere with the essential role of PfFKBP35, or that PfFKBP35 is inhibited only at high FK506 concentrations that also inhibit other essential factors.” While this phrase is already present in our initial submission, we will emphasize this point more clearly in the revised manuscript. We are convinced that this information is of high importance for ongoing and future drug development.

Reviewer #2 (Public Review):

The manuscript by Thomen et al. FKBP secures ribosome homeostasis in Plasmodium falciparum and focuses on the importance of PfKBP35 protein, its interaction with the FK506 compound, and the role of PfKBP35 in ribosome biogenesis. The authors showed the interaction of the PfKBP54 with FK506, but the part of the FK506 and PfKBP54 in ribosome biogenesis based on the data is unclear.

The introduction is plotted with two parallel stories about PfKBP35 and FK506, with ribosome biogenesis as the central question at the end. In its current form, the manuscript suffers from two stories that are not entirely interconnected, unfinished, and somewhat confusing. Both stories need additional experiments to make the manuscript(s) more complete. The results from PfFBP35 need more evidence for the proposed ribosome biogenesis pathway control. On the other hand, the results from the drug FK506 point to different targets with lower EC50, and other follow-up experiments are needed to substantiate the authors' claims.

The strengths of the manuscript are the figures and experimental design. The combination of omics methods is informative and gives an opportunity for follow-up experiments.

We thank the Reviewer for the evaluation of the manuscript. We apologize for the fact that the Reviewer found the manuscript to be inaccessible. We will use the comments as an incentive to restructure the manuscript and do our best to clarify the presentation, interpretation and conclusion of the presented data in the revised version. We believe that the FKBP35 data are strongly interlinked with the findings on FK506. We will emphasize these links more clearly and are convinced that the complementary nature of the datasets are a particular strength of the presented work.

Reviewer #3 (Public Review):

The study by Thommen et al. sought to identify the native role of the Plasmodium falciparum FKBP35 protein, which has been identified as a potential drug target due to the antiplasmodial activity of the immunosuppressant FK506. This compound has multiple binding proteins in many organisms; however, only one FKBP exists in P. falciparum (FKBP35). Using genetically-modified parasites and mass spectrometry-based cellular thermal shift assays (CETSA), the authors suggest that this protein is in involved in ribosome homeostasis and that the antiplasmodial activity of FK506 is separate from its activity on the FKBP35 protein. The authors first created a conditional knockdown using the destruction domain/shield system, which demonstrated no change in asexual blood stage parasites. A conditional knockout was then generated using the DiCre system. FKBP35KO parasites survived the first generation but died in the second generation. The authors called this "a delayed death phenotype", although it was not secondary to drug treatment, so this may be a misnomer. This slow death was unrelated to apicoplast dysfunction, as demonstrated by lack of alterations in sensitivity to apicoplast inhibitors. Quantitative proteomics on the FKBP35KO vs FKBP35WT parasites demonstrated enrichment of proteins involved in pre-ribosome development and the nucleolus. Interestingly, the KO parasites were not more susceptible to cycloheximide, a translation inhibitor, in the first generation (G1), suggesting that mature ribosomes still exist at this point. The SunSET technique, which incorporates puromycin into nascent peptide chains, also showed that in G1 the FKBP35KO parasites were still able to synthesize proteins. But in the second generation (G2), there was a significant decrease in protein synthesis. Transcriptomics were also performed at multiple time points. The effects of knockout of FKBP35 were transcriptionally silent in G1, and the parasites then slowed their cell cycles as compared to the FKBP35WT parasites.

The authors next sought to evaluate whether killing by FK506 was dependent upon the inhibition of PfKBP35. Interestingly, both FKBP35KO and FKBP35WT parasites were equally susceptible to FK506. This suggested that the antiplasmodial activity of FK506 was related to activity targeting essential functions in the parasite separate from binding to FKBP35. To identify these potential targets, the authors used MS-CETSA on lysates to test for thermal stabilization of proteins after exposure to drug, which suggests drug-protein interactions. As expected, FK506 bound FKBP35 at low nM concentrations. However, given that the parasite IC50 of this compound is in the uM range, the authors searched for proteins stabilized at these concentrations as putative secondary targets. Using live cell MS-CETSA, FK506 bound FKBP35 at low nM concentrations; however, in these experiments over 50 ribosomal proteins were stabilized by the drug at higher concentrations. Of note, there was also an increase in soluble ribosomal factors in the absence of denaturing conditions. The authors suggested that the drug itself led to these smaller factors disengaging from a larger ribosomal complex, leading to an increase in soluble factors. Ultimately, the authors conclude that the native function of FKBP35 is involved in ribosome homeostasis and that the antiplasmodial activity of FK506 is not related to the binding of FKBP35, but instead results from inhibition of essential functions of secondary targets.

Strengths:

This study has many strengths. It addresses an important gap in parasite biology and drug development, by addressing the native role of the potential antiplasmodial drug target FKBP35 and whether the compound FK506 works through inhibition of that putative target. The knockout data provide compelling evidence that the KBP35 protein is essential for asexual parasite growth after one growth cycle. Analysis of the FKBP35KO line also provides evidence that the effects of FK506 are likely not solely due to inhibition of that protein, but instead must have secondary targets whose function is essential. These data are important in the field of drug development as they may guide development away from structure-based FK506 analogs that bind more specifically to the FKBP35 protein.

Weaknesses:

There are also a few notable weaknesses in the evidence that call into question the conclusion in the article title that FKBP35 is definitely involved in ribosomal homeostasis. While the proteomics supports alterations in ribosome biogenesis factors, it is unclear whether this is a direct role of the loss of the FKBP35 protein or is more related to non-specific downstream effects of knocking down the protein. The CETSA data clearly demonstrate that FK506 binds PfKB35 at low nM concentrations, which is different than the IC50 noted in the parasite; however, the evidence that the proteins stabilized by uM concentrations of drug are actual targets is not completely convincing. Especially, given the high uM amounts of drug required to stabilize these proteins. This section of the manuscript would benefit from validation of a least one or two of the putative candidates noted in the text. In the live cell CETSA, it is noted that >50 ribosomal components are stabilized in drug treated but not lysate controls. Similarly, the authors suggest that the -soluble fraction of ribosomal components increases in drug-exposed parasites even at 37{degree sign}C and suggests that this is likely from smaller ribosomal proteins disengaging from larger ribosomal complexes. While the evidence is convincing that this protein may play a role in ribosome homeostasis in some capacity, it is not sure that the title of the paper "FKBP secures ribosome homeostasis" holds true given the lack of mechanistic data. A minor weakness, but one that should nonetheless be addressed, is the use of the term "delayed death phenotype" with regards to the knockout parasite killing. This term is most frequently used in a very specific setting of apicoplast drugs that inhibit apicoplast ribosomes, so the term is misleading. It is also possible that the parasites are able to go through a normal cycle because of the kinetics of the knockout and that the time needed for protein clearance in the parasite to a level that is lethal.

Overall, the authors set out to identify the native role of FKB35 in the P. falciparum parasites and to identify whether this is, in fact, the target of FK506. The data clearly demonstrate that FKBP35 is essential for parasite growth and provide evidence that alterations in its levels have proteomic but not transcriptional changes. However, the conclusion that FKBP35 actually stabilizes ribosomal complexes remains intermediate. The data are also very compelling that FK506 has secondary targets in the parasite aside from FKBP35; however, the high uM concentrations of the drug needed to attain results and the lack of biological validation of the CETSA hits makes it difficult to know whether any of these are actually the target of the compound or instead are nonspecific downstream consequences of treatment.

We appreciate the detailed and valuable suggestions to improve the manuscript. We agree that CETSA could only identify potential targets of FK506 in the micromolar range, while FK506 showed a high affinity for FKBP35, consistent with earlier reports (2). We would however like to point out that FK506 kills P. falciparum at exactly these relatively high concentrations and not at those presumed from the high affinity interactions between FK506 and FKBP35. The relatively high FK506 concentration required to stabilize potential off target proteins is therefore not a concerning observation, but rather corroborates our conclusion that FK506 fails to inhibit the essential function of FKBP35 at concentrations that leave off targets unaffected. As mentioned in response to Reviewer 1, we will describe and discuss these data more clearly in the revised manuscript. We thank the Reviewer for pointing out the potential issues regarding the use of the term “delayed death phenotype”. We now refer to the FKBP35 phenotype as “delayed death-like” in the revised manuscript.

We believe that follow-up work on specific FK506 CETSA hits is out of scope of the current and already quite complex manuscript.

As mentioned in the response to Reviewer 1, we realize that the short title of the manuscript can be regarded as an overstatement. Again, this was clearly not our intention and we apologize that the Reviewers had to indicate this issue. While we believe that the message of the title holds true (see response to Reviewer 1), we recognize the misconception that might arise from it, which is why we propose the new title: “Genetic validation of PfFKBP35 as an antimalarial drug target”.

Reviewer #1 (Recommendations For The Authors):

1) Documentation of FKBP35 protein levels over time in knockout, knockdown and overexpressing parasites is missing here. Since the knockdown of PfFKBP35 has no phenotypic consequence, very low amounts of FKBP35 are probably sufficient for parasite survival and growth. In the absence of quantification of the protein during the course of the experiments, it remains unclear whether the delayed death phenotype in the knockout is due to the delayed depletion of the protein or to a delayed consequence of early protein depletion. This limitation also impacts the interpretation of the drug assays. In particular, the delayed death phenotype could simply reflect delayed protein depletion, contrasting with the immediate inhibition of FKBP35 by FK506. The quantification by mass spectrometry does indicate substantial depletion but provides no information on the kinetics and levels. What is 19 fold compared to the knockdown condition? Also, expression of FKBP35 in overexpressing parasites should be compared side by side with the iKD (in the presence of Shield).

We agree with the Reviewer that low FKBP35 levels are likely sufficient for parasite survival. This is addressed in the manuscript (lines 141-143). Assessing protein levels in the transgenic parasites side by side in time course experiments would be interesting. However, our conclusions are independent of the outcome of such experiments because the relative difference in FKBP35 levels resulting from conditional expression systems did not change the parasites` susceptibility to FK506. We believe that comparing isogenic populations is much more informative than comparing independent cell lines with each other.

2) The authors claim that FK506 fails at inhibiting the essential function of PfFKBP35 (line 103), however this is not directly supported by data. FK506 kills the parasite and so inhibits essential functions. The data indicate that FK506 antimalarial activity does not seem to be influenced by FKBP35 levels, which would support the authors claim. However, as mentioned above, it is important to better define experimentally FKBP35 expression levels. Also, in experiments where FK506 is added late after rapamycin treatment, the authors need to clarify how they could distinguish drug killing and death due to the knockout.

In the experiment described by the Reviewer, the FKBP35 knock-out was induced in young ring stages (0-6 hpi) and FK506 was added at 30-36 hpi, we measured the parasite survival from G1 to G2 (see figure 5A). In the absence of FK506, the FKBP35 knock-out has no effect on parasite survival (Figure 1), demonstrating that the observed effect is only due to drug killing and not due to the KO.

To address the concerns regarding delayed depletion of FKBP35, we have performed an additional set of experiments. This data corroborates that the effect of FK506 is independent of FKBP35 levels. We discuss this topic in more detail in the Public Review. In brief, the additional experiment included exposing knock-out parasites (KO induced 0-6 hpi) with FK506 at 36-42 hpi, i.e. at a time point when FKBP35 protein levels are reduced by more than 90% (19-fold difference compared to the control parasites based on quadruplicate quantitative mass spectrometry data). However, despite the clear difference, the IC50 of FK506 remained the same as determined before (see new figure 4F).

3) Since FK506 is known to inhibit FKBP35 PPIase activity, it could be relevant to compare the effects of FK506 versus KO on ribosomes and translation. This could provide further evidence supporting a FKBP35-independent activity of FK506.

We agree with the Reviewer that this would be very informative. However, it would be difficult to disentangle indirect downstream processes on translation caused by both the FK506 drug treatment and the FKBP35 knock-out in a cellular assay. Establishing a biochemical in vitro assay to study the role of PPIase activity in translation is out of scope of this manuscript.

Minor points

-The title is rather vague, which reflects the fact that the function of PfFKBP35 is not precisely defined in the study.

We thank the Reviewer for this assessment, which is in agreement with Reviewer 3. Based on these concerns, and in order to prevent misinterpretation of our manuscript, we propose changing the title to “Genetic validation of PfFKBP35 as an antimalarial drug target” (see public response above).

-The transcriptomics data (Fig 3) provide little information on the function of FKBP35 and could be included as supplemental material. On the contrary, data in FigS5 convey important information and should be moved to the main figures.

We believe that the transcriptomics data are important to characterize the effect of limiting FKBP35 levels in G2, as they show that, unlike certain homologs of other organisms (3), FKBP35 has no role in transcriptional control and its knock-out does not have any downstream consequences on the transcriptional level (except for the death-related stall in cell cycle progression). We would therefore would like to keep this dataset represented in the main figures. The updated Figure 4F now includes more information about the effect of adding FK506 at different time points, which was only addressed in Figure S5 in the previous version of the manuscript. We believe that the key message of Figure S5 is now covered in Figure 4.

-Line 30: "action" rather than "role"

We corrected this.

Reviewer #2 (Recommendations For The Authors):

I have no comments on data, code, or other issues.

General comments:

The introduction is plotted with two parallel stories about PfKBP35 and FK506, with ribosome biogenesis as the central question at the end. In its current form, the manuscript suffers from two stories that are not entirely interconnected, unfinished, and somewhat confusing. I recommend focusing only on one story - either characterizing PfBP35 and its role in Plasmodium falciparum biology - future investigation of PfBP35 control of cellular processes or focusing on the actual targets of the FK506 drug (identified in figure 4). Both stories need additional experiments to make the manuscript(s) more complete and ready for publication. The results from PfFBP35 need more evidence for the proposed ribosome biogenesis pathway control. On the other hand, the results from the drug FK506 point to different targets with lower EC50, and other follow-up experiments are needed to substantiate the authors' claims.

The strengths of the manuscript are the figures and experimental design. The combination of omics methods is informative and gives an opportunity for follow-up experiments.

Detailed points and suggestions for authors:

Line 99

There is no such thing as "protein translation"; it is mRNA translation or protein synthesis, which needs to be updated throughout the manuscript.

We thank Reviewer 2 for pointing out this error that we now corrected.

Line 174

The statement needs a reference(s).

We added an appropriate review reference.

Lines 229-235

While transcriptomics and proteomics data can argue that FKBP35 maybe acts at the post-transcriptional level, its function, as well as presented data, could point to post-translational mechanisms as well, cell cycle checkpoint misregulation, and multiple other pathways that control cell size, cell proliferation, translation, and ribosome biogenesis. More solid and direct evidence on ribosome biogenesis (rRNA processing, polysome profiles, or similar experiments) would be needed to show the function of FKBP35 in this cellular process.

We have changed the term “post-transcriptional processes” to “transcription-independent processes”. As detailed in the Public Review, we agree with the Reviewer and lowered our statements regarding the function of FKBP35 throughout the manuscript.

Lines 237-313

The authors showed again the interaction of PfFKBP35 with the FK506 drug, but the phenotype differs from the protein deletion. Moreover, EC50s for multiple other proteins (i.e., PF3D7_1138700 or PF3D7_1325900, among others) are lower than for PfFKBP35 but are never further tested. This would be necessary to characterize FK506 drug targets, and it would be a different study.

We believe that characterizing putative targets of FK506 is out of the scope of this already complex study and should be addressed, as suggested by the Reviewer, in a future and independent efforts.

Lines 293 - 301

The point of lower EC50 for PfFKBP35 and FK506 in in vitro cell lysate experiment compared to in vivo IC50 data is not surprising, given that drug delivery is not an issue in a lysate experiment. It is unclear why the authors pick some proteins and not others for further characterization of FK506 binding. There is no explanation for this selection. They did not follow up on the best targets of FK406 drugs from Fig 4 (above comment).

As mentioned above, validation of FK506 targets is out of scope of this study.

Lines 313 -352

An alternative scenario for the FK506 drug data in CETSA experiments is that they bind directly to ribosomes interacting with rRNA, as many macrolides do. One should note that these are not ribosomal factors (line 334) but ribosomal proteins mentioned in Fig.4 F, mainly associated with large ribosomal subunit.

We agree with Reviewer 2 that FK506 could bind indirectly to ribosomal proteins. This scenario is already described in the initial version of the manuscript (see lines 285-287: “Of note, these ribosomal proteins were stabilized at virtually identical FK506 concentrations (Figs. 4D, and S7), indicating that the drug – directly or indirectly – interacts with ribosomal complexes.”).

We thank the Reviewer for pointing out that we are indeed talking about “ribosomal proteins” rather than “ribosomal factors”. We now corrected this.

Reviewer #3 (Recommendations For The Authors):

Please see Public review for suggestions about experimental validation of the link to ribosome homeostasis.

We would like to thank Reviewer 3 for the detailed suggestions.

References

1) Kennedy K, Cobbold SA, Hanssen E, Birnbaum J, Spillman NJ, McHugh E, et al. Delayed death in the malaria parasite Plasmodium falciparum is caused by disruption of prenylation-dependent intracellular trafficking. PLoS Biol. 2019;17(7):e3000376.

2) Kotaka M, Ye H, Alag R, Hu G, Bozdech Z, Preiser PR, et al. Crystal structure of the FK506 binding domain of Plasmodium falciparum FKBP35 in complex with FK506. Biochemistry. 2008;47(22):5951-61.

3) Kasahara K, Nakayama R, Shiwa Y, Kanesaki Y, Ishige T, Yoshikawa H, et al. Fpr1, a primary target of rapamycin, functions as a transcription factor for ribosomal protein genes cooperatively with Hmo1 in Saccharomyces cerevisiae. PLoS Genet. 2020;16(6):e1008865.

Author Response

We thank the reviewers for their comments, and their evident close reading of the manuscript. Generally, we agree with the reviewers on the strengths and weaknesses of our manuscript. We plan to submit a revised version which has a more extensive discussion of alternative explanations for initial high ribosome density as seen by ribosome profiling, and which more specifically points out the limitations of our work.

As a preface to specific responses to the reviewers, we will say that we could divide observations of slow initial translation into two categories, which we will call “encoded slow codons”, and “increased ribosome density”. With respect to the first category, Tuller et al. documented initial “encoded slow codons”, that is, there is a statistical excess of rare, slowly-translated codons at the 5’ ends of genes. Although the size of this effect is small, statistical significance is extremely high, and the existence of this enrichment is not in any doubt. At first sight, this appears to be a strong indication of a preference for slow initial translation. In our opinion, our main contribution is to show that there is an alternative explanation for this initial enrichment of rare, slow codons—that they are a spandrel, a consequence of sequence plasticity at the 5’ (and 3’) ends of genes. The reviewers seem to generally agree with this, and we are not aware that any other work has provided an explanation for the 5’ enrichment of rare codons.

The second category of observations pertaining to slow initial translation is “increased ribosome density”. Early ribosome profiling studies used cycloheximide, and these showed a much greater density of ribosomes near the 5’ end of genes than elsewhere. This high initial ribosome density helped motivate the paper of Tuller et al., though their finding of “encoded slow codons” could explain only a very small part of the increased ribosome density. More modern ribosome profiling studies do not use cycloheximide as the first step in arresting translation, and in these studies, the density of ribosomes near the 5’ end of genes is greatly reduced. And yet, there remains, even in the absence of cycloheximide at the first step, a significantly increased density of ribosomes near the 5’ end (e.g., Weinberg et al., 2016). (However, at least some of these studies do use cycloheximide at later steps in the protocol, and the possibility of a cycloheximide artefact is difficult to exclude.) It appears to us that some of the reviewer’s main concerns are that we do not explain the increased 5’ ribosome density seen by ribosome profiling. We agree; but we feel it is not the main point of our manuscript. In revision, we will more extensively discuss other work on increased ribosome density, and more explicitly point out the limitations of our manuscript in this regard. We also note, though, that increased ribosome density is not a direct measure of translation speed—it can have other causes.

Specific Responses.

Reviewer 1 was concerned that we did not more fully discuss other work on possible reasons for slow initial translation. We will discuss such work more extensively in our revision. However, as far as we know, none of this work proposes a reason for the 5’ enrichment of rare, slow codons.

Reviewer 1 was also concerned about confounding effects in our reporter gene analysis of the effects of different codons on efficiency of translation. We have two comments. First, it is important to remember that although we changed codons in our reporters, we did not change any amino acids. We changed codons only to synonymous codons. Thus at least one of the reviewer’s possible confounding effects—interactions of the nascent peptide chain with the exit channel of the ribosome—does not apply. However, of course, the mRNA nucleotide sequence is altered, and this would cause a change in mRNA structure or abundance, which could matter. We agree this is a limitation to our approach. However, to fully address it, we feel it would be necessary to examine a really large number of quite different sequences, which is beyond the scope of this work.

Reviewer 2 was concerned that the conservation scores for the 5’ 40 amino acids, and the 3’ 40 amino acids were similar, but slow translation was only statistically significant for the 5’ 40 amino acids. As we say in the manuscript, we are also puzzled by this. We note that 3’ translation is statistically slow, if one looks over the last 100 amino acids. Our best effort at an explanation is a sort of reverse-Tuller explanation: that in the last 40 amino acids, the new slow codons created by genome plasticity are fairly quickly removed by purifying selection, but that in the first 40 amino acids, for genes that need to be expressed at low levels, purifying selection against slow codons is reduced, because poor translation is actually advantageous for these genes. To expand on this a bit, we feel that the 5000 or so proteins of the proteome have to be expressed in the correct stoichiometric ratios, and that poor translation can be a useful tool to help achieve this. In this explanation, slow translation at the 5’ end is bad for translation (in agreement with our reporter experiments), but good for the organism, whereas in Tuller, slow translation at the 5’ end is good for translation.

Reviewer 2 wondered whether the N-terminal fusion peptide affects GFP fluorescence in our reporter. This specific reporter, with this N-terminus, has been characterized by Dean and Grayhack (2012), and by Gamble et al. (2016), and the idea that a super-folder GFP reporter is not greatly affected by N-terminal fusions is based on the work of Pedelacq (2006). None of these papers show whether this N-terminal fusion might have some effect, but together, they provide good reason to think that any effect would be small. We will add these citations to the revision.

Author Response

Reviewer 2 (Public Review):

1) The authors developed a novel C.elegans model for studying extracellular amyloid beta aggregation and is therefore likely to be taken up broadly by the field. However, the new model should be fully characterized. Throughout the manuscript, the only method to detect amyloid deposition was the GFP fluorescence intensity and morphology, while direct characterization of amyloid aggregates is lacking.

We thank the reviewer for the feedback and the foresight that this model might be taken up by the field. To strengthen our model, as the reviewer had suggested, we confirmed that the GFP fluorescence is indeed amyloid aggregations. Please, see point 3 above and the new Supporting Figure 1.1.

2) A targeted RNA interference (RNAi) screen was used to identify the key regulators of Aβ aggregation and clearance, which is one of the strengths of the study. There should be evidence that RNAi works to knockdown the specific genes. Similarly, there should be evidence indicating that ADM-2 is indeed expressed in the overexpression experiments.

We aimed to verify our main hits (cri-2 and adm-2) with a mutation in these genes, as RNAi can have off-target effects. The adm-2(ok3178) allele is a 989 bp deletion leading to a splice/acceptor change leading to a probably truncated and out-of-frame protein.

Author response image 1.

The cri-2(gk314) allele is a 1213 bp deletion covering the whole cri-2 locus, suggesting to be a null allele.

Author response image 2.

For the overexpression, there is no ADM-2 antibody available. We tried to generate an ADM-2 antibody, unfortunately unsuccessfully. Thus, we can only, based on the induction and higher red fluorescence of ADM-2::mScarlet (Supporting Figure 6.1.) infer the ADM-2 overexpression.

3) It remains unknown whether ADM-2 directly degrades Aβ or facilitates the clearance of Aβ by remoulding the ECM. The effect of ADM-2 on ECM remodeing should be examined.

We addressed this in point 1 above and also in our discussion section.

Author Response

Reviewer #2 (Public Review):

During meiosis, mitotic cohesin complexes are replaced by meiosis-specific cohesins to enable a stepwise loss of sister chromatid cohesion. The identity of the cohesin complex is defined by its kleisin subunit. In the early meiotic prophase, the mitotic kleisin Scc1 is replaced by a meiotic counterpart Rec8. C. elegans expresses two additional meiotic kleisins, COH-3 and COH-4; however, how meiotic cohesin complexes differ in their loading and function has been unclear. In this paper, Castellano-Pozo and colleagues unveil their differential dynamics and functions using elegant approaches that include auxin-mediated depletion and TEV-mediated removal of meiotic kleisins. The association of COH-3/4 with chromosomes is dynamic and is under the control of two cohesin regulators, WAPL-1 and SCC-2, while REC-8 remains more stably associated. The authors established that COH-3/4 is involved in maintaining the structural integrity of chromosome axes, whereas the REC-8 cohesin is solely responsible for sister chromatid cohesion throughout meiosis. They further demonstrated the role of REC-8 in the repair of meiotic DSBs.

Overall, this solid work unequivocally establishes the distinct regulation and requirements for REC-8 and COH-3/4 cohesin complexes during C. elegans meiosis.

We thank the reviewer for their overall support.

However, as the authors acknowledged, the role of REC-8 cohesins in sister chromatid cohesion has been shown previously using genetic mutants (Crawley et al., 2016 eLife). While the authors highlighted the advantages of removing cohesin subunits in establishing their distinct requirements, many of the results were recapitulated from their previous work (e.g. rec-8; spo-11 and coh-3/4; spo-11). It might be helpful for the readers to compare the results between the two studies and point out uniquely illuminating results.

Although we and others have previously suggested that REC-8 cohesin provides SCC in worms based on observations made in different meiotic mutants, a convincing demonstration of this possibility was lacking and an alternative model proposing that COH-3/4 cohesin do provide SCC had been proposed (Severson et al 2014). Using TEV-tagged versions of REC-8 and COH-3/4 we unequivocally establish that SCC is uniquely provided by REC-8 complexes in metaphase I oocytes. We have introduced modifications in the text and figures (including a model shown in Figure 5) to highlight the main results of our study.

The role of REC-8 in DNA repair has also been shown in different contexts. Chromosomes fragmentation and DNA bridges are observed in rec-8; syp-1 or rec-8; syp-2 (RNAi) animals (Colaiacovo et al., 2003 Dev Cell; Crawley et al., 2016 eLife), suggesting a role of REC-8 in inter-sister repair. Persistent RAD-51 foci are also observed on asynapsed chromosomes in rec-8 mutants, suggesting a role for REC-8 in DNA repair (Cahoon et al., 2019 Genetics). The authors must cite these papers and discuss the results in the context of prior work.

We agree with the reviewer that the studies mentioned above are consistent with the possibility that REC-8 complexes contribute to inter-sister repair. We now include citations of the manuscripts mentioned by the reviewer. The experiments presented in Figures 4A-B are different from those in the studies mentioned by the reviewer in that by introducing exogenous DSBs by IR (including in a spo-11 mutant background (Figure 4B)) we can more directly address the contribution of REC-8 and COH-3/4 complexes in pachytene nuclei under a situation in which similar numbers of DSBs are introduced. These experiments show that low abundance REC-8 complexes play a much more prominent role in DSB repair than highly-abundant COH-3/4 complexes and suggest that this activity is coupled to REC-8’s role in SCC.

Reviewer #3 (Public Review):

The study, performed in the animal model C. elegans, aims at characterizing functional differences in the meiosis-specific kleisins, REC-8 and COH-3/4.

The authors conclude that in worms the identity of the kleisin subunit of the cohesin complex determines whether cohesin promotes cohesion, or controls higher-order chromosome structure. COH-3/4 is highly abundant and dynamic and responds to SCC-2 and WAPL-1. In contrast, REC-8 complexes associate stably and in low abundance and are resistant to SCC-2 and WAPL-1 perturbations.

Main points:

This study is a continuation and partially a repeat of a study Castellano-Pozo & Martinez-Perez published in Nat. Comm. 2020, in which they depleted COH-3/4 and REC-8 by injecting TEV and cleaved artificially engineered TEV sites in these kleisins.The results were slightly different though, as the authors concluded: "Disassembly of axial elements requires simultaneous removal of REC-8 and COH-3/4."

The current study uses a degron instead of TEV and SIM to revisit the same result. This time, degradation of COH-3/4 alone, but not of Rec8 alone completely eliminates axial elements. It seems that, if the conclusion is now correct, the previous headline must be incorrect, showing that more care has to be taken in the conclusions.

The reviewer is referring to data shown in Figure 1C saying that we used a degron system to degrade COH-3/4 and REC-8 from pachytene nuclei. This is incorrect, images in this figure correspond to rec-8 and coh-3 coh-4 double mutants (as indicated in main text and figure legend) and therefore to germlines lacking REC-8 or COH-3/4 from the onset of meiosis. In contrast, in the Castellano-Pozo et al 2020 study REC-8 or COH-3/4 were removed from pachytene chromosomes using the TEV approach following normal chromosome morphogenesis at meiosis onset to specifically address how kleisin removal in nuclei at the pachytene stage impacted on meiotic progression. In addition to this, Figure 1C does not show that lack of COH-3/4 “completely eliminates axial elements”, as stated by the reviewer, but rather that “SMC-1::GFP signals appeared as discontinuous weak signals in pachytene nuclei” (see description of this result in lines 103-104 of first version). This finding is consistent with the Castellano-Pozo et al 2020 study where we reported that staining of HORMADs (used to visualise axial elements) became weaker and more discontinuous following removal of COH-3/4 than REC-8 from pachytene axial elements (this observation is also mentioned in lines 96-97 of the first version of our manuscript).

One new experiment in this study is the degradation of scc-2::AID::GFP. The authors treat the germline with auxin for 14 hours. How long scc-2::AID actually needs for degradation and thus, how long cells actually remain without SCC-2, is unknown. What is definitely needed is a serious analysis of the speed of degradation of Scc2 in the various stages.

It is currently not possible to estimate, as the authors do, how long cells have been without SCC-2. This estimation assumes an immediate depletion of SCC-2.

If this were indeed the case, then depletion intervals should be much shorter, because the important primary phenotypes occur immediately after depletion, not 14 hours later.

We now analyse REC-8::HA and COH-3/4 staining after auxin treatment for 8 and 14 hours, showing that 8 hours results in weaker effect on COH-3/4 depletion in pachytene nuclei and a smaller section of the germline lacking REC-8::HA staining in early prophase. We also include cartoons in Figure 2B to explain how nuclei progress through pachytene (35 hours in total).

Author Response

Reviewer #2 (Public Review):

This manuscript tackles the important and vexing problem of mapping alleles for TB. It is a really important problem, and this paper presents the largest genetic data set. It does so by amalgamating data from multiple cohorts. The manuscript rightly points out that many studies have not produced reproducible results, and most alleles are population specific, and rarely seen in multiple studies.

1) Authors find a strong HLA associated SNP. They do conduct HLA imputation, but there is little effective fine-mapping. Authors should report which classical alleles are consistent with this allelic association (e.g. which classical alleles are in phase with it). Authors comment on DQA1-0301, but it isn't clear in the main text how significant it is. I think the authors should dig a little deeper. Imputing amino acids and assessing association might be useful. Finding classical alleles that explain the SNP associations and are seen across populations might be useful. If the authors think that the SNP might be a regulatory allele, the authors should make a case for that based on genomic annotations, eQTL analyses etc.

We thank the reviewer for pointing out the issues with the HLA section. We also received feedback from another reviewer about the HLA section. Based on this we have completely reworked the HLA section with more rigorous analysis to make the results easier to interpret and detect potential underlying HLA alleles that could explain the significant SNP detected in the MR-MEGA meta-analysis. This includes our findings with summary statistics for the DQA1*02:01 allele with those available from studies that were not included in our genome-wide meta-analysis. The HLA section has been updated on page 7-9, as shown below and a figure has been added to the main manuscript (Figure 3B) and the supplementary data (Figure S2):

Notwithstanding inconsistency across populations the strongest signal in the combined global analyses is at DQA102:01, revealing a protective effect (OR 0.88, 95% CI 0.82-93, p-value = 1.3e-5, Figure 3B). The signal remains apparent in the six populations with the lead SNP at MAF >2.5% and individual level data available (p-value = 0.0003). However, conditioning on the significant SNP (rs28383206) in this subset, we find the signal at DQA102:01 all but disappears (Figure S2) suggesting the classical allele is tagging the rs28383206 association (p-value = 0.44). This observation is consistent with previous observations of HLA analysis in Icelandic (DQA102:01: OR 0.82, p-value = 7.39e-4) and Han Chinese populations (DQA102:01: OR 0.82, p-value = 7.39e-4), but showed opposite direction of effect in another Chinese population (DQA1*02:01: OR 1.28, p-value = 0.0193, Figure 3B)19,21,23.

The discussion was also updated (page: 14-15) to incorporate and discuss the updated results as shown below:

Based on the significant association, rs28383206, in the HLA region identified in this multi-ancestry (Figure 3A), HLA specific imputation and association testing was done to fine map the region and identify potential HLA epitopes driving this association. HLA DQA102:01 had the strongest signal in the meta-analysis across the 8 included studies (Figure 3B), but this signal disappeared when conditioning on the significant SNP (rs28383206). HLA DQA102:01 has previously been identified in an Icelandic and two Chinese population, but the direction of effect was not consistent19,21,23. Despite these inconsistencies the association between Mtb and HLA class II should be explored in more detail in future studies. A study investigating outcomes of Mtb exposure in individuals of African Ancestry identified protective effects of HLA class II alleles for individuals resistant to TB, highlighting the importance of HLA class II and susceptibility to TB62. HLA class II is a key determinant of the immune response in TB and Mtb has mechanisms to directly interfere with MHC class 2 antigen presentation63. This is supported by studies in mice, where mice in which the MHC class ll genes were deleted died quickly when exposed to Mtb and died faster than mice in which MHC class I genes were deleted63.

2) The authors comment on ancestry. Are ancestry components disease associated in any cohort? It might be interesting to demonstrate this.

We thank the reviewers for this recommendation. While ancestry components have been shown to be disease associated in the admixed (RSA) populations in previous studies, we have considered the fact that effects of genetic ancestry can be severely confounded by socioeconomic factors. Factors such as housing, employment, poverty and access to healthcare have significant impact on TB incidence rates, especially in African populations. We cannot account for these socioeconomic differences in our analysis, but we have updated the manuscript (page: 15) to highlight this issue and the potential impact of socioeconomic factors on our results.

This is supported by the fact that previous TB genetic association studies have identified significant effects of ancestry on TB susceptibility11,26. However, the effects of genetic ancestry can be confounded by other factors not accounted for in this analysis, such as differences in socioeconomic factors (including differences in housing, employment, poverty, and access to healthcare) between the included study populations59–61. For the ancestry-specific analysis, fewer studies result in there being less input heterogeneity to account for, but the reduced sample size was not sufficient to detect any ancestry-specific genome-wide associations. This is particularly evident for the African ancestry-specific meta-analysis where the large degree of heterogeneity, which could be a result of the high genetic diversity within Africa, in combination with differences in socioeconomic factors compared to other populations included in this study, resulted in no observable suggestive association peaks59,60.

Reviewer #3 (Public Review):

This paper was a significant and commendable effort, given all the challenges in TB genetics research. It was generally well written and analyses well done. Analytical methods were appropriate. The inclusion of polygenic heritability estimates is also nice to have within this large work. There is also a wealth of supplemental data provided, which will be useful to the field.

However, there are a number of important weaknesses that need to be addressed. These are listed here, and recommended revisions are addressed in the recommendations section:

1) As the authors point out, one of the challenges in this work is the varying phenotype definitions (diagnosis of TB cases, definition of controls) across all the included genetic studies. Table S1 is critical for this, however it is missing information, and some of the information is unclear. More importantly, the authors state multiple times that there is no evidence of heterogeneity due to these variable phenotype definitions, and that genetic ancestry contributes more to differences in effect sizes between GWAS than study design. However, these two things are confounded - different study designs / phenotype definitions were used in studies of different ancestry.

We thank the reviewer for pointing this out and we have updated Table S1 to define the phenotype definitions and how cases and controls were identified. All datasets should now have clear definitions. As for the impact of different phenotype definitions on the heterogeneity we do agree that these are confounding factors and we do not claim that there is no evidence of phenotype definitions influencing heterogeneity, but rather we claim that the genetic ancestry of the included populations has a larger impact on heterogeneity than other factors investigated in this study. We updated the manuscript to clarify this in the discussion (page: 15) as shown below:

The p-values of residual heterogeneity in genetic effects between the studies in the multi-ancestry meta-analysis show no significant inflation between the studies suggesting that differences in study characteristics (phenotype definition, infection pressure, Mtb strain) are not the main contributor to the lack of significant associations, but they certainly have an impact and are compounded with ancestry-correlated heterogeneity and other factors. However, the ancestry-correlated heterogeneity p-values are generally lower than the residual heterogeneity, suggesting that genetic ancestry has a stronger impact on the differences in effects sizes between the studies. This is supported by the fact that previous TB genetic association studies have identified significant effects of ancestry on TB susceptibility11,26. However, the effects of genetic ancestry can be confounded by other factors not accounted for in this analysis, such as differences in socioeconomic factors (including differences in housing, employment, poverty, and access to healthcare), phenotype definitions and differences in infection pressure between the included study populations 60–62

And we also updated the polygenic heritability in the results section (page: 4) as shown below:

Furthermore, variations in phenotype definition can have an impact on heritability estimates (Table S1).

2) The polygenic heritability analysis table is not explained very well.

We thank the reviewer for pointing out this issue. The polygenic heritability table (Table S2) has been updated and some columns were removed (as they contained results from a discarded analysis). We have added footnotes to the table to define the variables and make the table more understandable and we have also updated the results section to clarify the analysis (page: 19) as shown below:

The genetic relationship matrix was calculated for each autosomal chromosome (un-imputed data) which were pruned for SNPs in linkage disequilibrium (LD) using a 50 SNP window, sliding by 10 SNPs at a time and removing all variants with LD greater than 0.5.

And page 19:

Heritability estimations were transformed onto the liability scale using the GCTA software to account for the difference in the proportion of cases in the data compared to the population prevalence74.

3) The supplemental data file is not very helpful without some sort of guide. It isn't clear whether the wealth of candidate genes that have been studied in TB were examined in these data. That would be a great benefit of this work.

We thank the reviewer for pointing this out and we agree that the supplemental data excel sheet was difficult to understand. We have included a readme file (also on sheet 1 of the excel sheet) to explain which information is in the sheets of the excel document. This includes a list of candidate SNPs and genes that we investigated along with the meta-analysis results of these candidate SNPs and genes. We also updated the “Prior associations” section of the manuscript in which we cover the results of candidate SNPs and genes (page: 13-14).

4) There needs to be clarity on how unpublished works were sought. In non-genetic meta-analyses, there is usually some detail about a process of contacting authors, etc. There needs to be some assurance that every attempt was made to collect all the relevant data. It is also not clear why family-based analyses could not be included considering that summary statistics were the basis of analysis.

I updated the manuscript to address this (page: 18):

This analysis includes 12 of the 17 published (and un-published, Table 1 and S1) GWAS studies of TB (with HIV negative cohorts) prior to 202210–17,26. For unpublished works we contacted researchers that were funded for genetic TB research and acquired data sharing agreements to obtain summary statistics (or raw data) along with any meta-data that was available. It excludes data from Iceland and Vietnam 18,31, as they declined to share data. It excludes data from China, Korea, Peru and Japan6,20,21,23,31, as data sharing agreements could not be finalized in time for this analysis. The Indonesian and Moroccan data were to sparsely genotyped and not suitable for reliable imputation and the Moroccan data was also family-based and thus also not suitable for this meta-analysis, as this would introduce confounding effects from the inclusion of related individuals24,25.

5) It is rather surprising that only one locus meets genome-wide significance. The authors do explain this well in terms of the ancestry-specific effects driving these results, but it is also surprising that no candidate genes (that had not been discovered in GWAS studies, but were rather studied separately) did not rise to some higher significance threshold.

We agree that it is surprising that we did not detect more significant associations and failed to replicate any candidate SNPs or genes at a genome wide significance level. We aim to have future iterations of this analysis with more data to increase power to detect more variants of interest, but this is beyond the scope of this manuscript.

Author Response

Reviewer #1 (Public Review):

“Liu et al present a very interesting manuscript investigating whether there are distinct mechanisms of learning in children with ASD. What they found was that children with ASD showed comparable learning to typically developing children, but that there was a difference in learning strategy, with less plasticity and more stable learning representations in children with ASD. In other words, children with ASD showed similar learning performance to typically developing children but were more likely to use different learning rules to get there. Interestingly greater fMRI-measured brain plasticity was associated with learning gains in typically developing children, whereas more stable (less plasticity) neural patterns were associated with learning gains in autistic children. This was mediated by insistence on sameness (from the RRIB) in the ASD group. This is a good paper, well reasoned and with strong methods.”

We appreciate the positive comments from the reviewer.

1.1) “The biggest issue is related to subject numbers...With n=35 it is only possible to make a generalized statement about autism.”

Thank you for this comment. Although the sample size in the current study was modest, we would like to note that acquiring high-quality behavioral and brain imaging data at multiple time points a is a challenge in children with ASD. The current training study with unique longitudinal behavioral and brain imaging data provides an unprecedented opportunity to investigate the potentially atypical training-induced learning and brain plasticity in children with ASD relative to TD peers. To our knowledge, the present longitudinal sample is largest of its kind in studies of neurocognitive function in children with ASD. We have acknowledged these points in the revised Discussion section (Page 15), including the following statement:

“First, larger sample sizes are required to further characterize heterogeneous patterns of atypical learning and whether the findings can be generalized to a broader ASD population.” (Page 15)

1.2) “[Another] issue is related to [heterogeneity of autism-related findings]. For example, take the following statement from the results: "while most TD children used the memory-based strategy most frequently following training, nearly half of the children with ASD used rule-based strategies most frequently for trained problems." Is this the heterogeneity of autism at play, or the noisiness of the task and measures?

We hypothesize that group differences in changes in strategy use following training are due to atypical learning style or high level of inter-individual differences, i.e., greater heterogeneity, in autism, rather than noisiness of the measures. This hypothesis is based on the fact that we used the same tasks before and after training and a standardized training protocol across the two groups, which (i) allowed us to systemically examine atypical learning of these tasks in children with ASD compared to TD children and (ii) provided ecologically valid measures. This design minimized potential differences in measurement error between the two groups. We have clarified these points in the revised Introduction section (Page 4), including the following statement: “Crucially, we employed identical tasks before and after training and a standardized training protocol across the two groups. This approach enabled systemic analysis of learning in children with ASD relative to TD children.” (Page 4)

1.3) “Conceptually, is it realistic to expect a unitary learning strategy in all of autism?

We agree with the sentiment expressed by the reviewer, and indeed this notion led to the hypothesis that our study was to test. We hypothesized that children with ASD would not show a unitary learning strategy at this stage of development examined. Our results reveal that a disproportionate number of children with ASD use a rule-based strategy, reflecting atypical learning styles.

1.4) “Lastly, the task itself can only be solved in a subset of autistic children and therefore presents a limited view of the condition.”

We thank the reviewer for this important point and agree that additional studies tailored to more severely affected children with ASD are required for a more comprehensive characterization of learning in children with autism.

Reviewer #2 (Public Review):

“Overall, the authors sought to determine whether children with autism spectrum disorder (ASD) or typical development (TD) would both benefit from a 5-day intervention designed to improve numerical problem-solving. They were particularly interested in how learning across training would be associated with pre-post intervention changes in brain activity, measured with functional magnetic resonance imaging (fMRI). They also examined whether brain-behavior associations driven by learning might be moderated by a classic cognitive inflexibility symptom in ASD ("insistence on sameness"). The study is reasonably well-powered, uses a 5-day evidence-based intervention, and uses a multivariate correlation-based metric for examining neuroplastic changes that may be less susceptible to random variation over time than conventional mass univariate fMRI analyses. The study did have some weaknesses that draw into question the specific claims made based on the present set of analyses, as well as limit the generalizability of the findings to the significant proportion of individuals with ASD that are outside of the normative range of general cognitive functioning. The study also found minimal evidence for transfer between trained and untrained mathematical problems, limiting enthusiasm for the intervention itself. The majority of the authors' claims were rooted in the data and the team was generally able to accomplish their aims. I am sensitive to the fact that one of the main limitations I noted would have significant ethical implications-i.e. NOT offering potentially beneficial numerical training to children randomized to a sham or control group. I think the authors' work will represent a welcome addition to a growing corpus of studies showing similar neuropsychological test performance across several cognitive domains (e.g. learning, memory, proactive cognitive control, etc.) in ASD and TD. However, these relatively preserved cognitive functions still appear to be implemented by unique neural systems and demonstrate unique correlations to clinical symptoms in youth with ASD relative to TD, which may have implications for both educational and clinical contexts.

We thank the reviewer for the positive feedback and helpful suggestions.

Reviewer #3 (Public Review):

“Liu and colleagues examined learning and brain plasticity in neurotypical children and children with autism. The main findings include autistic children relying more on rule-based versus memory-based learning strategies, altered associations between learning gains and brain plasticity in children with autism, and insistence on sameness as a moderator between brain plasticity and learning in autism. Although the sample size is limited in this study, the findings provide a significant contribution to the field. The major strengths of this paper include an extensive pre and post training protocol, a detailed methods section, rationale behind the study, investigation of a potential moderator of learning gains and neural plasticity, and investigation of "neural plasticity" in association to learning in autism. Weaknesses of the study include a small sample size, and some missing information/analyses from the study. The authors laid out four clear aims of the study. They investigated these aims and the analytic approaches were appropriate. The paper included significant findings toward better understanding the mechanisms underlying differences in learning strategies and behavior in children diagnosed with autism spectrum disorder. This holds significant value in educational and classroom settings. Further, the investigation of a potential moderator of learning gains and neural plasticity provides a potential mechanism to improve the relationship. Overall, this is a significant contribution to the field. The autism literature is limited in understanding differences in learning styles and the underlying neural mechanisms of these differences.”

We thank the reviewer for the positive comments and detailed suggestions.

Author Response

Reviewer #1 (Public Review):

As part of a special issue on COVID-19 and cancer, Fuzzell and colleagues report findings from their mixed method study on the impact of the pandemic on cervical cancer screening and colposcopies, consisting of a national (United States) survey (March-August 2021) of 1251 clinicians (675 perform colposcopy) and qualitative interviews (June-December 2021) with 55 of these clinicians. The study looked specifically at perceived pandemic-related practice changes and disruptions over one year into the pandemic after the lockdowns had been lifted.

The overall focus is on three pandemic-related questions (impact on cervical cancer screening practice, colposcopy practice, ability to provide LEEP) that were asked as part of a larger survey related to cervical cancer screening and management of abnormal results, details of which are however not fully described in terms of the survey's general aim and items, but seem to have been designed within the context of adherence to guidelines (following Cabana's Guideline Based Practice Improvement Framework).

The authors thank the reviewer for their thoughtful feedback. The surveys topics assessed are now described more fully in the Method, and measures are available upon request. The survey covered several areas related to cervical cancer screening practices and management of abnormal screening results, including presentation of vignettes focused on screening intervals, management or treatment, and screening exit or continuation in relation to 2019 ASCCP risk-based management guidelines adoption, as well as a sub-set of items for clinicians who perform colposcopy. There were also items related to HPV self-sampling, as well as the impact of the COVID-19 pandemic on screening and follow-up (which is the focus of the present manuscript).

Reviewer #2 (Public Review):

Lindsay Fuzzell and her team of researchers have performed an extremely well-executed survey study, which captures a wide spectrum of providers who perform cervical cancer screening in the US. The researchers have captured a vast amount of demographic data in this study in attempting to determine whether cervical cancer screening continued to be reduced in the year immediately after the lockdown period caused by the COVID-19 pandemic.

The authors have uncovered some important and revealing concerns regarding the current state of cancer screening during the public health crisis caused by the COVID-19 pandemic. The most notable implication from their survey was a statistically higher reported reduction in cervical cancer screening in Internal medicine and family medicine providers as well as for community health and safety net clinics. These findings are important as they represent a large portion of primary care and a vulnerable patient population that has been shown to have worse cancer-related outcomes.

This study is more sobering information about the magnitude of ramifications of the COVID-19 pandemic on the US public health system. Decreases in cancer screening may have lasting implications for cancer-related mortality for many years to come. The implications of not going back to pre-pandemic cancer screening rates are daunting, to say the least.

The scope of this survey, the amount of data attained, and the sound methodology of the data acquisition and statistical analysis are the strengths of this study. Weaknesses are inherent to the study relying on survey answers rather than data from cervical cancer screening registries. Reporting biases are complex in surveys and answers given may not reflect the true rates of screening. The authors have also reported a disproportionate and statistically significant reduction in cervical cancer screening for Black and Asian providers. I would conclude more cautiously here with confidence intervals crossing one in both for this statistical analysis.

Overall, this is a survey study with a great magnitude, which has important implications for cancer screening and public health in the US.

The authors thank the reviewer for their kind assessment. The discussion now includes an acknowledgement of the weaknesses inherent with using self-report surveys, namely that self-report surveys have inherent biases and may not be actual representations of screening and colposcopy practices that could be ascertained via medical record or claims databases. Additionally, regarding confidence intervals that cross one, given the few studies that have explored factors associated with clinician perspectives on screening and colposcopy changes due to the pandemic, we desired a more broad-based approach to identifying factors associated with our outcomes of interest, thus electing to utilize p of .10 as significance level. This strikes a balance between the commonly accepted method of using the AIC (Akaike's Information Criterion, which implicitly assumes a significance level of 0.157), and the often-used significance level of 0.05. We now describe the choice of 0.10 in the text. However, we acknowledge that by using 0.10 as a significance level, some 95% confidence intervals for factors we consider significant cross one. We have tempered language in the discussion for findings with p-values between 0.05 and 0.10. Additionally, in examination of the confidence intervals for findings related to race that the reviewer mentions, we identified an error in the labelling of Table 3. Marginally significant findings for Asian clinicians actually apply to mixed race/other clinicians. We have corrected this error in Table 3 and throughout the manuscript. We thank the reviewer for bringing the confidence intervals that cross one to our attention as this triggered an examination of our findings.

Author Response

Reviewer #2 (Public Review):

Reviewer #2 was critical of every aspect of our manuscript and we were disappointed that they failed to appreciate the significance of our findings. However, we have responded to each point as described below:

1) The experiment displayed in Figure 5 is deeply flawed for multiple reasons and should be removed from the manuscript entirely. A Michaelis-Menton plot compares the initial rate of a reaction versus substrate concentration. Instead, the authors plotted the fraction of SsrB that is phosphorylated after 10 minutes at various substrate concentrations. Such a plot must reach saturation because the enzyme is limiting, whereas it is not always possible to achieve saturation in a genuine Michaelis-Menton plot. Because no reaction rates were measured, it is not possible to derive kcat values from the data.

Mea culpa. We now plot our phosphorylation data and describe the mid-point as a k0.5 and have removed Fig. 1g. When we directly compare the H12 mutant to wt at neutral pH, its phosphorylation level is less compared to the wt (see new Fig. 4a). The wt phosphorylation is reduced at acid pH, (Fig 4b), but with His12Q, there was no difference in phosphorylation between neutral and acid pH (Fig 4c). It is important to include this data, because in RcsB, a close homolog of SsrB, an H12A mutant was not phosphorylated by acetyl phosphate and it was incapable of binding to DNA, unlike what we show here with SsrB.

(i) Increasing the concentration of the phosphoramidite substrate increased ionic strength. Response regulator active sites contain many charged moieties and autophosphorylation of at least one response regulator (CheY) is inhibited by increasing ionic strength (PMID 10471801).

The reviewer raises some interesting points and they are based on CheY phosphorylation by small molecules. We have a long history of studying OmpR and SsrB as well as other RRs and we know that they can all behave very differently from “canonical signaling”. We examined the effect of ionic strength on SsrB phosphorylation and it was relatively insensitive to changes in ionic strength (our original buffer was 267-430 mOsm and in each case, we have 90% phosphorylation). However, we repeated all of the phosphorylation experiments and kept ionic strength constant. These data are now presented in the revised manuscript.

(ii) Autophosphorylation with phosphoramidite is pH dependent because the nitrogen on the donor must be protonated to form a good leaving group (PMID 9398221). The pKa of phosphoramidite is ~8. Therefore, the fraction of phosphoramidite that is reactive (i.e., protonated) will be very different at pH 6.1 and 7.4.

We are aware of those findings, but we are comparing the H12 mutant with the wt protein in each case. There is no reason to believe that the presence of the mutant should alter the phosphoramidate substrate, so we are comparing how the wt phosphorylation compares with the mutant (Fig 4b, c).

(iii) Response regulator autophosphorylation absolutely depends on the presence of a divalent metal ion (usually Mg2+) in the active site (PMID 2201404). There is no guarantee that the 20 mM Mg2+ included in the reaction is sufficient to saturate SsrB. Furthermore, as the authors themselves note, the amino acid at SsrB position 12 is likely to affect the affinity of Mg2+ binding. Therefore, the fraction of SsrB that is reactive (i.e. has Mg2+ bound) may differ between wildtype and the H12Q mutant, and/or between wildtype at different pHs (because the protonation state of His12 changes).

This is exactly the point that we are making. And why we varied the magnesium concentration (increasing to 50-100 mM). There was a slight increase in phosphorylation at 50 mM MgCl2 compared to 20 mM, and only a slight increase between 50 and 100 mM at pH 6.1. The revised phosphorylation experiments all contain 100 mM MgCl2.

2) The data in Figures 1abcd and 3de are clearly sigmoidal rather than hyperbolic, indicating cooperativity. However, there are insufficient data points between the upper and lower bounds to accurately calculate the Hill coefficient or KD values. This limitation of the data means that comparisons of apparent Hill coefficient or KD values under different conditions cannot be the basis of credible conclusions.

We respectfully disagree. In every curve that we provide, there is at least one data point in the transition between low and high binding. With the mutant H12Q, we did manage to get two data points in the transition and the KD was the same as the wildtype (Fig. 2). We provide an analysis of the binding curve which nicely demonstrates the range of KD values based on the lowest and highest error in the point (132-168 nM) and it doesn’t significantly change the value (this is now shown in Fig.1– figure supplement 1). The very high affinity we observed at pH 6.1 (KD ~5 nM) makes the range of possibilities between 4-8 nM (i.e. still VERY high affinity). These range in affinities at neutral and acid pH are very reminiscent of affinities we measured for OmpR and OmpR~P at the porin promoters, suggesting that acid pH puts SsrB in an activated state even in the absence of phosphorylation. A similar argument holds for the Hill coefficient (see Figure).

3) There are hundreds of receiver domain structures in PDB. There is some variation, but to a first approximation receiver domain structures, all exhibit an (alpha/beta)5 fold. The structure of SsrB predicted by i-TASSER breaks the standard beta-2 strand into two parts, which throws off the numbering for subsequent beta strands. Given the highly conserved receiver domain fold, I am skeptical that the predicted i-TASSER structure is correct or adds any value to the manuscript. If the authors wish to retain the structure of the manuscript, then they should point out the unusual feature and the consequence of strand numbering.

We now include a new model based on the RcsB/DNA crystal structure that eliminates this problem (see new Fig.2– figure supplement 2). We have replaced this model with an Alphafold prediction that was energy minimized to align with the RcsB dimer crystal structure (Fig.5– figure supplement 2). This model retains the original (beta/alpha)5 fold, so the classical numbering is retained.

4) The detailed predictions of active site structure in Supplementary Figure 5 are not physiologically relevant because Mg2+ was not included in the simulation. The presence of a divalent cation binding to Asp10 and Asp11 is likely to substantially alter interactions between Asp 10, Asp11, His12, and Lys109.

See response to 1iii, above and new Fig.5– figure supplement 2. Author response image 1 is a zoomed-in snapshot of supplementary Figure 8c that has been modelled using the RcsB dimer bound to BeF3 and Mg2+(6ZIX). Both the i-TASSER and Alphafold model receiver domains align well with this structure, and the polar contacts and pi-cation interactions made by His12 are maintained.

Author response image 1.

5) The authors present an AlphaFold model of an SsrB dimer, and note that His12 is at the dimer interface. However, the authors also believe that a higher-order oligomer of SsrB binds to DNA in a pH-dependent manner. Do the authors have any suggestions or informed speculation about how His12 might affect higher-order oligomerization than dimerization?

As mentioned to point 3, above, we now include a new model of an SsrB dimer bound to DNA based on our NMR structure of the CTD and the RcsB/DNA structure. In the RcsB paper, they also have evidence for a higher-order oligomer in the crystal structure of unphosphorylated (and BeF3-) RcsB, which showed an asymmetric unit containing 6 molecules of RcsB, which form 3 dimers arranged in a hexameric structure that resembles a cylinder. This configuration involves a crossed conformation with the REC of one molecule interacting with the DBD of another and interestingly, His12 is interacting with the DBD of another molecule. We modelled an SsrB oligomer structure using the RcsB hexamer as a template and have included it as a new figure (see Fig.5– figure supplement 3) and in the revised discussion (lines 432-448).

Author Response

Reviewer #2 (Public Review):

This paper addresses the topic of how T cells migrate in different tissues. The authors provide experimental evidence that T cell migration in the lung is more confined than in lymph nodes and gut villi. While prior studies have started to define the way T cells migrate during normal and pathological conditions, there is still a lot to learn about the factors that control this process. Thus, the topic is significant and timely. The authors use previously acquired data with two-photon microscopy from murine tissues. They compare multiple motility parameters of T cells in lymph nodes, gut villi, and inflamed lungs. Experiments demonstrate that T cells in the lung have a particular mode of migration characterized by low speeds, back-and-forth motions, and confinement.

Strengths:

Overall, this is a very well-performed study. The data presented is of excellent quality and, for the most part, supports the authors' conclusions. The imaging techniques used to track T cells in various organs and the mouse models implemented are very relevant and robust. The functional analysis of the different migration features of T cells is compelling and should be of use to the community. The conclusion that T cells use different migration modes depending on the organ appears novel. This is considered of major significance.

We appreciate these comments by the reviewer that the study is relevant, robust, and timely.

Weaknesses:

The main weakness of the manuscript is that the study remains descriptive and comparative. It is important to analyze and describe different migration modes depending on the organ. Still, it would have been desirable for the authors to provide information on the reason for such differences. One of the striking observations is the back-and-forth motion of T cells in the lung. Searching for mechanisms underlying this unique mode of displacement would strengthen the quality of the study.

We agree that the next step is to determine the underlying cells, signals, and structures that determine motility differences between tissues. However, we believe that a detailed study is beyond the scope of this manuscript, which is the first to directly compare the types of motility that should be studied in individual tissues that distinguish T cell motility in individual tissues such as villi and lung.

Reviewer #3 (Public Review):

The ability of T cells to move through a variety of complex and disparate tissue environments is fundamental to their success in surveying and responding to infectious challenges. A better understanding of the molecular cues that regulate T cell motility in tissues is needed in order to inform therapeutic targeting of T cell migration. Contributions that are intrinsic and extrinsic to the T cells themselves have been shown to shape the pattern of T cell movement. This study uses advanced quantitative image analysis tools to dissect differences in T cell motility in different tissue locations, to better define how the tissue environment shapes the pattern of motility and scope of tissue explored. The combination of different quantitative measures of motion enables the extensive characterization of CD8 T cell motility in the lymph node, lung, and villi of the small intestine. However, there are too many variables with respect to the CD8 T cell populations used for analysis to be able to gain new insight into the impact of the tissue microenvironment itself.

The use of these advanced quantitative imaging analysis tools has the potential to significantly expand our analysis capabilities of T cell movement within and across tissues. The strength of the paper is the comprehensive analysis of multiple motility parameters designed with T cell function in mind. Specifically, with respect to the need for T cells to search a tissue area to identify antigen-bearing cells for T cell activation and identify cellular targets for the delivery of anti-microbial effector functions. The inclusion of an analysis of the "patrolled volume per time" is seen as a particularly useful advance to compare T cell behaviors across tissues.

However, with the current data sets, it is difficult to draw definitive conclusions on the impact of the tissue environment on how T cell move, given the considerable variability in the CD8 T cells themselves. Extended experimentation would be needed to fully support their key claims. In particular:

1) The authors have separated out naïve and activated CD8 T cells for their analysis, but this is a marked over-simplification. There are too many variables within these groups to be able to distinguish between differences in the T cell populations versus differences in the tissue environment. Variables include:

a) T cells pre-activated in vitro before in vivo transfer (LPS-lung) versus transfer of naïve T cells for activation in vivo (Flu-lung, LCMV-villi)

b) Polyclonal CD8 T cells (naïve, LPS-lung, Flu-lung) versus monoclonal (P14) CD8 T cells (LCMV-villi)

c) Presence of cognate-antigen (Flu-lung, LCMV-villi) versus absence of antigen (LPS-lung)

d) Cell numbers, 104 polyclonal naïve for Flu-lung versus 5 x 104 monoclonal (P14 T cells) for LCMV-villi)

e) Intravital imaging (LCMV-villi) versus tissue explants (Flu-lung)

The reviewer is absolutely correct that many factors differ, and we have added details about these potential differences. However, we can conclude that there are similarities in motility despite tissue and T cell activation differences, particularly between naive T cells in LN and d8 activated CD8 T cells in the gut villi. We report that the most significant differences between T cell motility parameters are in activated CD8 T cells in the lung compared to those in other tissues, regardless of antigen specificity. These lead us to suggest that the specific motility differences we see in T cells in the lung are likely to be the result of a combination of factors which we hypothesize are likely to be due to molecular changes in both the T cells (chemokine receptors) and the tissue (cell types, chemokines, and structural components). Future work will include defining specific differences that lead to changes in motility.

The authors do present data that suggest similarities of motility patterns within the same tissue occur despite variabilities in the CD8 T cell source, for example, the MSD is not significantly different in the two lung groups despite differences in the way the CD8 T cells were activated. However, these similarities are lost when other parameters are analyzed suggesting additional variability independent of the tissue itself.

In addition to the MSD (Fig 3), we also include parameters commonly analyzed including cell- based speed (Fig 2A). Regardless of the type of T cell, the median cell-based speeds range from 4.3 um/min to 6.5 um/min. Meandering ratio is also commonly used to analyze motility dynamics and naive T cells (0.70) and activated T cells in villi (0.63) also show similar meandering ratios (Fig 5).

2) Controlled experiments are needed, where the input CD8 T cell population is kept constant and the target tissue differs, to substantiate any of the current conclusions. This could be done by using a single source and/or specificity of CD8 T cells (e.g., P14 or OT-I TCR transgenics, or polyclonal in vitro activated CD8 T cells) transferred into mice where the tissue providing the antigen or inflammation source is varied (lung with pOVA-flu versus small intestine with pOVA-LCMV for example).

Alternatively, activated polyclonal CD8 T cells could be analyzed in the LPS-lung draining LN as well as in the LPS-lung to make a direct comparison between the tissues (LN versus lung) using CD8 T cells of the same activation status.

The experimental systems cannot be directly compared except in some circumstances. For example, we included LPS-induced lung injury because we wanted to directly compare non-antigen specific with antigen specific activated T cells in the lung. We have compared motility of OTI Tg T cells responses in the lung with non-OTI Tg T cells and found similar motility and effector characteristics [15]. We have not repeated the additional controls requested here as OVA is a model antigen and commonly used as a tag to simply track CD8 T cell effector responses. There is vast literature showing similar responses between OVA-specific versus antigen specific CD8 T cell responses in multiple tissues, with OTI Tg T cells analyzed as “normal CD8 T cells”. Thus, while it is possible that imaging OTIs in multiple tissues could confirm that the type of T cells is “more similar” in each tissue, we do not believe adding this analysis would add to the overall conclusions of the manuscript as there is no data to suggest that OTIs would behave differently in different tissues. Adding in vitro activated CD8 T cells imaged in activated lymph nodes would add more variables (activated lymph node versus naive lymph node) which we do not believe would shed new light on our primary finding which is that the lung appears to induce specific types of T cell behavior compared to the naive lymph node and the gut.

3) Differences in the micro-anatomical regions of the tissues studied may also contribute to tissue differences in movement patterns between the lung and the small intestine. The region of the small intestine imaged was specifically focused on the villi, close to the gut epithelium. Details of the location within the lung where images were taken are missing, therefore the motility differences between the lung and small intestine could reflect differences in the micro-anatomical position of the CD8 T cells within the tissue (proximal to epithelium versus parenchymal), rather than differences between the tissues themselves.

The reviewer is absolutely correct and we have added greater discussion of this in both the Introduction and Discussion.

Overall, the authors have developed a quantitative multi-parameter approach to the study of T-cell motility in different tissues. Application of these analytical tools to the study of T-cell behavior in different tissue locations has the potential to reveal tissue and/or T-cell-specific patterns of movement that may help to identify molecular requirements for context-specific dynamic T-cell behavior. Their quantitative approach reveals small but statistically significant differences in particular motility parameters, the functional significance of which will require further study. The careful design of experiments to reduce as many variables as possible will be needed to increase the impact of the work and ensure new insights into this important aspect of T-cell function.

Author Response

Reviewer #1 (Public Review):

The manuscript by Curtis et al. reports the interaction between CaMKII and alpha-actinin-2. The authors found that the interaction was elevated after NMDA receptor activation in dendritic spines. In addition, this study reveals NMDA receptor binding to CaMKII facilitates alpha-actinin-2 access to the CaMKII regulatory segment, indicating that the NMDA receptor is involved in this interaction. The authors identified the EF1-4 motifs mediated this interaction, and overexpression of this motif inhibited structural LTP. Moreover, biochemical measurements of affinities from various combination of protein fragments including autoinhibited CaMKII 1-315, regulatory segments of CaMKII, and the EFhand motif reveals that autoinhibited CaMKII has limited access to alpha-actinin-2. The authors also solved the structure of the interaction, supporting their finding in neurons at the molecular level. The authors claim that the interaction between CaMKII and alpha-actinin-2 is essential for structural LTP through cooperative action by the NMDA receptor and actin cytoskeleton.

Overall, the experiments are well-designed and the results are largely convincing and well-interpreted. But some aspects of the experiments need to be clarified.

1) Time resolution of the interaction analysis appears to be poor, as calcium elevation in a dendritic spine would be at milli-second order. What is the time window to interact alpha-actinin-2 with CaMKII during NMDA receptor activation or LTP?

We have performed additional time-course experiments to determine how quickly interactions between alpha-actinin-2 and CaMKII are elevated following NMDAR activation. The results of these experiments are shown in Figure 2A and Figure 2-Figure Supplement 1. We found that the change in association was established rapidly after NMDAR activation (t50% = 22±1 s, Figure 2A), which is consistent with proposed time-courses for CaMKII interactions following the induction of LTP (see Yasuda, Hayashi & Hell, Nat Rev Neuroscience, 2022, PMID 36056211). We have included additional text in the results (lines 138-147), methods (lines 609-611 & 650-652), and discussion (lines 426-427) sections explaining these experiments, and figure legends are provided for the new figures on lines 10061009 and lines 1096-1101.

2) The authors analyzed the binding of CaMKII and alpha-actinin-2 with partial fragments. It remains to be unknown whether CaMKII can form a protein complex with GluN2B and alpha-actinin-2 in a single CaMKII protomer.

The reviewer is referring to experiments shown in figure 5, in which we found that a fragment of GluN2B (1260-1492) increases pull-down of full-length CaMKIIa with a fusion of GST to the EF3-4 region of a-actinin-2. This region of GluN2B contains a CaMKII phosphorylation sequence (positions 1290-1309) that occupies the substrate binding groove of the kinase domain (Stratton et al., Cell Reports, 2023, PMID 35830796). Therefore, the most logical explanation for the results of the pulldown experiment is that GluN2B increases a-actinin-2 access to the regulatory segment by binding to the substrate binding groove of the same CaMKII protomer. Nevertheless, we discuss the difficulty of conceptualising and investigating interactions between oligomeric proteins within the PSD on lines 451461.

3) Besides synaptic localization, the effect of the interaction on the enzymatic activity of CaMKII is not known.

The Colbran laboratory has previously examined the effect of a-actinin-2 on CaMKII activity. Jalan-Sakrikar and colleagues (JBC, 2012, PMID 22427672) showed that a fragment of aactinin-2 corresponding to EF hands 3 and 4 is able to weakly activate CaMKII (~ 10 % compared to Ca2+/CaM) towards peptide substrates autocamtide-2 and GluN2B but not syntide-2 (see Figure 1B&C of this paper). An earlier study by Robison and colleagues (JBC, 2005, PMID 16172120) found that aactinin-2 antagonises Ca2+/CaM-dependent activation of unphosphorylated CaMKII towards autocamtide2, but does not affect the activity of pT286 auto-activated CaMKII (see Figure 4A of this paper). This work is referred to on lines 63-65 of the introduction.

4) Although the authors quantify the effect of the EF-hand disruptor by measuring numbers of the dendritic spine by its shape, the specificity of the EF-hand disruptor needs to be clarified.

There are two known interaction partners for the EF hand region of a-actinin-2: CaMKII and Titin (Young et al., EMBO J, 1998, PMID 9501083; Atkinson et al., Nat Struct Biol, 2001, PMID 11573089). Titin is an extremely long sarcomeric protein that is expressed in striated muscle cells but not neurons. Therefore, the effects of the disruptor are highly likely to reflect disruption of interactions to CaMKII. We also performed control experiments with EF34 L854R that does not bind CaMKII effectively (Figure 3-figure supplement 1C). We have added a sentence to clarify the specificity of the EF-hand disruptor on lines 182-184, as follows: ” Furthermore, the only known interaction partner for the EF14 region of a-actinin-2 besides CaMKII is the muscle-specific protein titin (Young et al., 1998), so any effects of EF14 in neurons are likely to reflect destabilisation of native interactions between CaMKII and a-actinin-2”.

Author Response

Reviewer #1 (Public Review):

This study uses electrophysiological techniques in vitro to address the role of the Na+ leak channel NALCN in various physiological functions in cartwheel interneurons of the dorsal cochlear nucleus. Comparing wild type and glycinergic neuron-specific knockout mice for NALCN, the authors show that these channels 1) are required for spontaneous firing, 2) are modulated by noradrenaline (NA, via alpha2 receptors) and GABA (through GABAB receptors), 3) how the modulation by NA enhances IPSCs in these neurons.

This work builds on previous results from the Trussell's lab in terms of the physiology of cartwheel cells, and from other labs in terms of the role of NALCN channels, that have been characterized in more and more brain areas somewhat recently; for this reason, this study could be of interest for researchers that work in other preparations as well. The general conclusions are strongly supported by results that are clearly and elegantly presented.

I have a few comments that, in my opinion, might help clarify some aspects of the manuscript.

1) It is mentioned throughout the manuscript, including the abstract, that the results suggest a closed apposition of NALCN channels and alpha2 and GABAB receptors. From what I understand, this conclusion comes from the fact that GABAB receptors activate GIRK channels through a membrane-delimited mechanism. Is it possible that these receptors converge on other effectors, for example adenylate cyclase (see https://www.ncbi.nlm.nih.gov/pmc/articles/PMC6374141/).

It will be of interest to test the roles of adenylyl cyclase modulation in the control of NALCN, as a complement to the studies we have presented here.

2) In Figure 2G, the neurons from NALCN KO mice appear to reach a significantly higher frequency than those from WT (figure 2E, 110 vs. 70 spikes/s). Was this higher frequency a feature of all experiments? The results mention a rundown of peak firing rate due to whole-cell dialysis, but, from what I understand, the control conditions should be similar for all experiments.

The peak firing rates in control solutions for WT and KO CWC are not statistically different.

3) Also in Figure 2, the firing patterns for neurons from WT and NALCN KO mice appear to be quite different, with spikes appearing to be generated during the hyperpolarization of the bursts in the second half of the current step for WT neurons but always during the depolarization in KO neurons. Was this always the case? If so, could NALCN channels be involved in this type of firing? Along these lines, it would be interesting to show an example of a firing pattern of neurons from WT mice in the presence of NA, which inhibits NALCN channels.

The specific pattern of spikes in CWC is quite variable from trial-to-trial or cell-to-cell, as it is dependent on multiple CaV and calcium dependent K channels subtypes, and is not dependent on the genotypes used here. The primary effects observed in the KO are in background firing and sensitivity to NA, both reflected alterations in rheobase. The firing pattern example requested was shown in the raster plot of fig 2B2.

4) It might be interesting to discuss how the hyperpolarization induced by the activation of GIRK channels and inhibition of NALCN channels could have different consequences due to their opposite effect on the input resistance.

We considered this as a point of discussion, but decided that making sense of it would depend on assumptions about the location of the channels (dendritic vs somatic, distance to AIS) that we do not have data for. For example, a dendritic increase in resistance through NALCN block, leading to a hyperpolarization of the soma, might have actions similar to a somatic hyperpolarizing conductance increase by GIRK, as far as the voltage at the AIS is concerned.

Reviewer #3 (Public Review):

The study by Ngodup and colleagues describes the contribution of sodium leak NALCN conductance on the effects of noradrenaline on cartwheel interneurons of the DCN. The manuscript is very well-written and the experiments are well-controlled. The scope of the study is of high biological relevance and recapitulates a primary finding of the Khaliq lab (Philippart et al., eLife, 2018) in ventral midbrain dopamine neurons, that Gi/o-coupled receptors inhibit NALCN current to reduce neuronal excitability. Together these studies provide unequivocable evidence for NALCN as a downstream target of these receptors. There are no major concerns. I have only minor suggestions:

Minor

1) As introduced in the introduction, NALCN is inhibited by extracellular calcium which has led to some discourse of the relevance of NALCN when recorded in 0.1 mM calcium. A strength of this study is the effect of NA on NALCN is recorded in physiological levels of calcium (1.2 mM). I suggest including the concentration of extracellular calcium in the aCSF in the Results section instead of relying on the reader to look to the Methods.

Will do.

2) It would be interesting to include the basal membrane properties of the KO compared to wildtype, including membrane resistance and resting membrane potential. From the example recording in Figure 2, one might think that the KOs have lower membrane resistance, so it is interesting that the 2 mV hyperpolarization produced similar effects on rheobase. In addition, from the example in Figure 2G, it appears that NA has an effect on firing frequency with large current injection in the KO. Is this true in grouped data and if so, is there any speculation into how this occurs?

Will do.

3) Please expand on the rationale for why GABAB and alpha2 must be physically close to NALCN. To my knowledge, the mechanism by which these receptors inhibit NALCN is not known. Must it be membrane-delimited?

Given the known membrane delimited modulation of GIRK by GABAB, and that alpha2 and GABAB receptors appear to share the same population of NALCN channels, and that alpha2 receptors do not appear to target GIRK channels, we felt the simplest explanation would be coupling through G-proteins, with spatial segregation of different receptor/channel pools providing the means for separating GIRK and NALCN effects. However, the involvement of an additional second messenger is testable.

Author Response

We wish to thank the Reviewers for the appreciation they have expressed for our work, and the constructive feedback that they offered. We agree that clarifying the interpretation of synergy and information decomposition in the context of macroscale BOLD signals and loss of consciousness will be a valuable addition to the manuscript, and so will be improving the quality of our figures, and we will endeavour to do so. Briefly, at this stage we just wish to clarify that it is not our intention to claim that Phi-R and synergy, as measured at the level of regional BOLD signals, represent a direct cause of consciousness, or are identical to it. Rather, our work is intended to use these measures similarly to the use of sample entropy and LZC for BOLD signals: as theoretically grounded macroscale indicators, whose empirical relationship to consciousness may reveal the relevant underlying phenomena. We will ensure that our updated manuscript reflects this additional nuance.

Author Response

We thank the reviewers for their very thorough and detailed comments as well as the overall positive reception of the work. Additionally, the reviewers provided excellent detailed suggestions for future work.

Specific response to Reviewer 1:

“Indeed, the major disappointment of this work is the clinical relevance that was highlighted in the Introduction but was never really studied in the end. iPSC from patients could be added to the study.”

We completely agree that it would be very exciting to use patient-derived iPSC in the platform that we describe in this manuscript. We recognize that extensive work to characterize and validate BMECS differentiated from patient-derived iPSCs would be required, including validating BBB-like properties, before retinol transport data could be collected and interpreted. This work is beyond the scope of the current manuscript. We hope that in the future the in vitro model we describe in this manuscript will be used for exactly this type of clinically relevant application.

Specific response to Reviewer 2:

“1) The authors assume that there is a significant fraction of free ROL, 20% for ROH/RBP and 7% for RBP/TTR complexes (summarized in Table 1). This implies that at the physiological concentration of ROH/RBP in the plasma of 2 uM, free ROL represents 0.4 uM. However, the concentration of free ROL is limited by its poor solubility in the aqueous phase, which is around 0.06 uM (Szuts EZ, 1991, Arch Biochem Biophys). Moreover, taking into account the large concentration of other potential nonspecific carriers for lipids, it is safe to assume that there is virtually no free ROH in the plasma. There is also an important physiological reason for the limited amount of free ROL. Its rapid and nonspecific partition into cells (also observed in this study) would work against the highly specific RBP/STRA6-dependent ROH uptake pathway, undermining its physiological function.”

The reviewer raises an important point that we considered carefully during the design of the research. As the reviewer says, Szuts (1991) reported retinol (ROH) solubility of ~0.06 µM (range of 0.03 – 0.11 µM). Szuts defined ROH solubility as ‘the amount of dissolved solute in equilibrium with its solid state…includ[ing] all its dissolved forms (monomers, multimers, and micelles)’. We are using a definition of ‘free’ ROH as ‘ROH not bound to protein’; in our work ‘free’ ROH could include retinol multimers and micelles, which likely do exist under our experimental conditions. (We did not see any evidence of solid ROH.) That said, we calculate that the concentration of free ROH (ROH not bound to protein) is ~0.14 µM when both RBP and TTR are present. In more complex biological mixtures containing other ROH carriers, the concentration of unbound ROH is expected to be lower, in agreement with the reviewer.

One key point is that the free ROH concentration depends on the experimental setup, and must be correctly accounted for. For example, in some of the literature investigating STRA6-mediated uptake and signaling in vitro, purified ROH-RBP is used as the retinol source and samples do not include TTR. In such a case, the unbound ROH concentration in an equilibrated sample is anticipated to be significantly higher than the physiological concentration. Our investigation demonstrates that unbound ROH can accumulate intracellularly; thus, failure to include TTR and/or to account for the action of unbound ROH could lead to errors in mechanistic interpretation of experimental studies on retinol transport into cells or across barriers such as the BBB.

2) “However, a question remains: would the outcome of the experiment be different if the basolateral chamber contained an ROH acceptor (retinol-binding proteins) rather than Hank's balanced salt solution, to which the partition of ROL is limited by its water solubility?”

We agree with the reviewer that it would be very interesting to determine whether retinol permeability changes in the presence of RBP and/or TTR on the basolateral side. This is a logical next step and can readily be performed in the Transwell setup. We chose not to do this for this project because we wanted to compare our setup with other in vitro models (e.g., with porcine BMECs) where no retinol-binding proteins were present basolaterally.

3) “The authors claim that transthyretin (TTR) increases BMECs permeability when compared to ROH/RBP. However, the mechanistic explanation for this phenomenon remains unclear. Do the authors imply the presence of a putative TTR receptor whose signaling could affect the efflux of ROL at the basolateral side of BMECs? TTR is an ubiquitous plasma protein. The concentration of TTR is tightly regulated and maintained between 300 - 330 mg/L. Therefore, it is questionable how TTR can serve as a signaling molecule modulating retinoid homeostasis in the brain.”

We disagree with the reviewer about the TTR concentration. Per Johnson et al (Clin Chem Lab Med 2007, 45:419-426), TTR concentration varies with age, gender, inflammation and nutritional status, with typical concentrations for adults ranging from 150-450 mg/L. We were surprised at our observations that TTR enhanced ROH permeability across BMECs and that LRAT expression increased in the presence of TTR. We do not currently have a mechanistic interpretation and agree with the reviewer that further exploration of these tantalizing observations is warranted.

“Additional technical issues that could affect the experimental outcomes: The formation of the ROH/RBP-TTR complex should be confirmed and purified using gel filtration to separate free TTR and ROH/RBP. Only fractions containing the complex should be used in the experiments. Assuming that the complex is formed with 100% efficiency is overly optimistic.”

We respectfully disagree with the reviewer regarding using gel filtration to isolate TTR/ROH/RBP complexes. Any such isolated complexes will fairly rapidly re-equilibrate so that some protein and some ROH is unbound. It is important to note that we do not assume that the complex is formed with 100% efficiency. In fact, on the contrary, we explicitly take into account the distribution of materials (free TTR, free RBP, free ROH, RBP-ROH, TTR-RBP-ROH) in any sample; values are reported in the manuscript. This issue is also relevant to the first point raised by the reviewer. We routinely validated binding of ROH to RBP by FRET and ROH-RBP to TTR by fluorescence anisotropy.

“Reloading RBP with isotopically labeled ROH requires an additional purification step. Stripping ROL from the ROH/RBP complex with organic solvent (diethyl ether) is appropriate but relatively harsh, causing partial unfolding of a fraction of RBP. Therefore, assuming that 100% of stripped RBP remains functional and can be reloaded with ROH is inaccurate. Reloading apo-RBP with a stoichiometric amount of ROH without an additional purification step (e.g., ion exchanger) leads to an excess of free ROL and/or its nonspecific association with nonfunctional RBP fractions. Measuring absorbance at 330 nm is not sufficient proof of binding since free ROH also absorbs at the same wavelength.”

We produced RBP by refolding of guanidine-denatured RBP in an excess of ROH to ensure near 100% ROH loading. High quality refolded RBP can qualitatively be determined by examination of the A330/280 absorbance ratio, which should be ~1.0. We then extract ROH to completion by diethyl ether to produce pure apo-RBP (ROH-free). We utilized this diethyl-ether stripped apo-RBP stock for all future characterizations, including binding to ROH and TTR. We found our stripped apo-RBP was a suitable replacement for serum sources in every biophysical assay performed. Reloaded ROH-RBP elutes as a single peak on ion exchange chromatography, indicating the vast majority of stripped RBP is available for ROH binding. We provide detailed information about RBP characterization in Est and Murphy, Prot. Exp. Purif. (2020), to which the interested reader is referred.

Author Response

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

Comment 1: The descriptions about body weights should be matched.

Regrettably, we did not monitor the body weights throughout the study. We have now revised the description clarifying the confusions. Importantly we evaluated the weights of the muscle (EDL and soleus) and heart tissues in 8-month-old mice (Fig. 1A).

Comment 2: Quantitative data for figures.

As stated in the manuscript, the presented images are representatives of at least three mice per genotype. However, assessing specific measurements such as cell sizes, diameters, or mitochondria sizes in histological tissue sections and electron microscopical fields is not feasible due to practical limitations. Unfortunately, we do not have access to specialized software for such analyses. While semi-quantification of Western blot bands is possible, implementing this for all Western blots in the manuscript would result in a substantial increase in the number of bar graphics. Below are Western blots from additional two pairs of mice used in all figures.

Comment 3: Confusions about “total mitochondrial content”.

The mitochondria content in cells was assessed by quantitatively comparing the DNA level of the mitochondrial gene cytochrome B to that of the nuclear gene 18S using quantitative PCR. This method is commonly used to determine the relative number of mitochondria in cells. However, we have revised and provided a clearer description in the figure legend to avoid any potential confusion.

Comment 4: Suggestions on further analyses of PGC1-alpha and TFAM. LC3-I and -II.

We evaluated LC3-I/II levels in PTPMT1 knockout muscles, and our findings did not indicate any signs of increased autophagic activity (Supplementary Figure S3). We will examine PGC1-alph and TFAM levels in our future studies. It is worth noting that in our previous RNA-seq analyses of PTPMT1 knockout hematopoietic cells, we did not observe any significant alterations in the expression levels of these two genes.

Comment 5: Description on fibrotic lesions.

Quantifying fibrotic areas poses a significant challenge. Therefore, we were only able to describe this finding.

Comment 6: Fig 6 is not well organized and aligned.

In response to your suggestion, we have reorganized this figure accordingly. Panels C, D, and E display mitochondrial OCR data derived from three biological replicates/genotype. We feel that these changes are sufficient to demonstrate the differences in substrate utilization between PTPMT1 knockout and control mitochondria.

Comment 7: Descriptions on glucose oxidation and glycolysis in different types of muscle fibers are confusing

We have followed the suggestions and revised the descriptions accordingly.

Comment 8: A discussion about lactate utilization in cardiomyocytes would be helpful.

Following this suggestion, we have now added a brief discussion.

Comment 9: “Cropped” images were used in Fig 10.

The images shown in Fig. 10 were not cropped images. In order to efficiently use the tissue and mitochondrial lysates, the Western blot membranes were intentionally cut into smaller fragments based on the molecular weights of the proteins to be detected. These smaller membrane sections were then employed for individual Western blotting purposes.

Minor comment 1: The order of Fig 1 panels should be reorganized.

Following this suggestion, we have now reorganized this figure.

Minor comment 2: Suggestion for an Echocardiograph result table.

These analyses were carried out by trained personnel at the Emory Animal Physiology Core. The data presented in our manuscript was provided by them. It is important to note that no additional parameters were measured beyond the data provided by the Core.

Minor comment 3: Is ROS production increased in PTPMT1 knockout muscle cells?

Yes, PTPMT1 knockout tissues showed elevated overall cellular ROS levels even at 3 months (Figure 6I).

Minor comment 4: Typo in S10 legend.

The typo has been corrected.

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

Comment 1: The effects of PTPMT1 on the skeletal muscle and heart might be an embryonic defect. They might be mediated by significantly reduced mTOR signaling

We acknowledge the valid point made by this reviewer. While both CKMM-Cre and Myh6Cre express Cre during the embryonic stage, we did not observe any developmental defects in skeletal muscle-specific (PTPMT1fl/fl/CKMM-Cre) or heart-specific (PTPMT1fl/fl/Myh6-Cre) knockout mice. These knockout mice appeared indistinguishable from their WT littermates until the age of 3-4 months.

Morphologically, the skeletal muscle and heart dissected from these mice showed no abnormalities. Additionally, mitochondria isolated from these tissues did not exhibit any morphological/structural defects. Undoubtedly, the late-onset phenotypes observed in the knockout mice over time was attributed to the metabolic defects arising from the loss of PTPMT1 in the embryos. Although PTPMT1 knockout muscle cells and cardiomyocytes initially maintained energy homeostasis through enhanced fatty acid and glutamate oxidation, along with metabolic adaptations or activation of alternative energy-producing pathways in the first few months, they eventually encountered substantial energy deficits. This was attributed to the subsequent occurrence of oxidative stress and mitochondrial damage. In response to this valuable feedback, we have included a brief discussion in the manuscript's discussion section to address this point.

As mentioned in the manuscript, the late-onset phenotypes observed in our study were likely a result of subsequent damages induced by prolonged metabolic substrate shift and lipid accumulation within the cells. We agree with the reviewer that decreased mTOR activities may also contribute to these late effects, and have included a brief discussion in the discussion section.

Comment 2: Why are the effects of the loss of PTPMT1 similar in the skeletal muscle and heart.

The depletion of PTPMT1 yields similar effects in both tissue types; however, the manifestations occur earlier in the skeletal muscle. Although mitochondria in the skeletal muscle and heart have distinct preferences for energy sources, prolonged forced utilization of fatty acids caused by PTPMT1 depletion eventually leads to lipid accumulation and cellular damage (lipotoxicity) in both tissue types. This phenomenon underscores the importance of maintaining a balance in substrate utilization to prevent adverse effects on cellular health in the skeletal muscle and heart.

Comment 3: AMPK is activated in PTPMT1 knockout cardiomyocytes; this should have cardioprotective effects.

AMPK can be activated through various mechanisms. In our study, AMPK activation occurs in response to energetic stress in late-stage PTPMT1 knockout tissues that displayed significantly reduced ATP levels, aligning with its role as a bioenergetic stress sensor. It is possible that AMPK activation alone was insufficient to overcome the secondary damages induced by the prolonged metabolic switch from carbohydrate metabolism to fatty acid metabolism.

Comment 4: Knockout skeletal muscles and hearts had lipid accumulation; why were knockout mice smaller than controls? Are there any changes in white fat, core temperature or browning of fat? Rescue experiments should be considered to prove that lipid accumulation is the cause of death in the knockout mice.

We believe that the lipid accumulation observed in muscle cells and cardiomyocytes of the knockout mice does not necessarily imply that these tissue-specific knockout mice would be heavier or have increased body fat. We appreciate the suggestions regarding energy expenditure tests and rescue experiments. We will certainly consider incorporating these experiments into our future study.

As stated in the manuscript, we did not observe any morphological changes in white or brown fat tissues in the adipocyte-specific PTPMT1 knockout mice. Furthermore, we assessed body temperature and its response to a cold environment (4°C), and no differences were detected between the knockout mice and the control mice.

Comment 5: Are there sex differences in muscle and heart phenotypes in the tissue specific knockout mice?

We did not observe significant differences in phenotypes between male and female knockout mice.

Comment 6: What happens to UCP2 activity in PTPMT1 deleted cells and what is its function in mediating AMPK and/mTOR regulation.

Currently, there is a lack of direct methods available to measure UCP2 activity. The relationship between UCP2 and the regulation of AMPK and mTOR has not been extensively investigated.

Comment 7: What is the effect of PTPMT1 deletion on cardiolipin synthesis?

PTPMT1 has been implicated in both facilitating mitochondrial utilization of pyruvate and participating in the synthesis of cardiolipin. To investigate the impact of PTPMT1 knockout on cardiolipin levels, we plan to establish a mass spectrometry assay for the quantitative analysis of cardiolipin in knockout mitochondria. Completing these experiments might require a considerable amount of time. Nonetheless, we extensively addressed this point in the discussion section.

Minor concerns:

Comment 8: The title needs more specificity.

As suggested, we have revised the title to "Loss of PTPMT1 restricts mitochondrial utilization of carbohydrates and induces muscle atrophy and heart failure in tissue-specific knockout mice".

Comment 9: Heart and skeletal muscle weights in Fig 1A should be normalized against tibia length.

Unfortunately, we did not perform normalization in this study. However, we appreciate the suggestion and will incorporate it into our future studies. It is important to note that the lengths of tibias in the knockout mice were only marginally shorter.

Comment 10: Low magnification and longitudinal section of the muscle should be shown in Fig 1B and 2A.

The histological images provide supporting evidence for the conclusion, despite not being optimal in quality. We acknowledge the suggested improvements and assure you that we will integrate them into our future studies. It is crucial to emphasize that each conclusion in this study was derived from multiple experimental designs, rather than solely relying on morphological changes.

Comment 11: Fig 1F is mislabeled as 1G.

We have conducted a thorough review and can confidently confirm that the labeling is correct.

Comment 12: Fig 2F and 6B should be quantified.

As indicated in the manuscript, the images presented are representatives of at least three mice per genotype. While semi-quantification of Western blot bands is possible, implementing this for all Western blots in the manuscript would result in a substantial increase in the number of bar graphics. Below are Western blot images from additional two pairs of mice included in Fig. 2F and Fig. 6B. Furthermore, Western blot images from two additional pairs of mice in other figures are also provided below.

Author response image 1

Western blotting data from additional two pairs of mice in Fig. 2F.

Author response image 2

Western blotting data from additional two pairs of mice in Fig. 6B.

Author response image 3

Western blotting data from additional two pairs of mice in Supplementary Fig. 2G.

Author response image 4

Western blotting data from additional two pairs of mice in Supplementary Fig. 3A.

Author response image 5

Western blotting data from additional two pairs of mice in Supplementary Fig. 3C.

Author response image 6

Western blotting data from additional two pairs of mice in Supplementary Fig. 3D.

Author response image 7

Western blotting data from additional two pairs of mice in Supplementary Fig. 4F.

Author response image 8

Western blotting data from additional two pairs of mice in

Author response image 9

Western blotting data from additional two pairs of mice in Supplementary Fig. 7C.

Comment 13: Knockout mice should be placed on HFD or keto diet to test for the effects of PTPMT1 depletion.

We appreciate this thoughtful suggestion. We will certainly incorporate this suggestion into our future studies, expanding beyond the scope of the current initial report.

Comment 14: Suggestions on Fig 4A.

Please see our response to Comment 10.

Comment 15: Suggestions for improving echocardiographs.

These analyses were conducted by trained personnel at the Emory Animal Physiology Core. The data presented in our manuscript was provided by them. We appreciate bringing the issues to our attention, and we will inform them accordingly.

Comment 16: Comment on Fig 5B.

The tissues were sectioned at comparable, if not identical, levels. WT and PTPMT1 knockout heart sections look dramatically different because of the dilated myopathy observed in the knockout hearts.

Comment 17: Comment on Fig 5C.

We believe the cell death occurred predominantly in cardiomyocytes.

Author Response

We thank the reviewers for their careful reading of our manuscript and for their constructive and positive comments. We will revise the manuscript to address their key points. Here, we address the reviewer’s scepticism of sleep-learning being mediated by the episodic memory system. We agree that the reported unconscious learning of novel verbal associations during sleep may not match textbook definitions of episodic memory. However, the traditional definitions of episodic memory have long been criticized (e.g, Henke, 2010; Hannula, Minor, Slabbekoorn, 2023; Shohamy & Turk-Browne, 2013; Dew & Cabeza, 2011; Reder et al, 2009). We stand by our claim that sleep-learning was of episodic nature. Here, we provide arguments for this claim:

In the introduction and the discussion, we are reporting that we use a computational definition of episodic memory (Cohen & Eichenbaum, 1993; Henke, 2010; O’Reilly et al., 2014; O’Reilly & Rudy, 2000), and not the traditional definition of episodic memory that ties episodic memory to wakefulness and conscious awareness (Gabrieli, 1998; Moscovitch, 2008; Schacter, 1998; Squire & Dede, 2015; Tulving, 2002). Consciousness and wakefulness are no properties of episodic memory according to the computational definition of episodic memory. Instead, the core computational features of episodic memory according to the computational definition are 1) rapid learning, 2) association formation, and 3) a compositional and flexible representation of the associations in long-term memory. We designed the retrieval task in the current study to assess only the retention of sleep-formed flexibly and compositionally stored word-word associations. Reviewer 3 suggests that sound-sound associations may have been formed during sleep and may have been reactivated at test resulting in the translation of the sound pattern of the translation word to the meaning of the translation word and further to the correct superordinate semantic category of the translation word. Although these processing steps during sleep and during the wake retrieval are possible, the rapid sound-sound associative encoding, long-term storage, and the flexible sound retrieval would still require hippocampal processing and hence computations in the episodic memory system. The interpretation in terms of associative auditory learning with a double semantic translation at wake testing is laborious and inefficient and hence a less parsimonious interpretation of sleep-learning than conceptual associative encoding during sleep. Our view resonates the findings by Andrillon et al. (2017) that mere auditory perceptual learning during slow-wave sleep was not possible at all or led to suppressive memory traces that could not be retrieved following awakening.

Importantly, Züst et al. (Current Biology, 2019) had also presented pseudowords and translation words for paired-associative word encoding during slow-wave sleep. Retrieval testing was performed in the waking state following sleep by use of a cued-recall task, as in the current study. During retrieval testing, Züst et al. recorded brain blood oxygenation using functional magnetic resonance imaging. Importantly, the hippocampus was activated during correctly, but not during incorrectly retrieved memories that had been formed during sleep. Crucially, activation resulting from this contrast within the posterior and anterior hippocampus and within lexical-semantic storage sites in the left temporal pole correlated between participants with retrieval performance (Züst et al., 2019). These correlation results demonstrate that those participants, who learned the vocabulary best during slow-wave sleep activated the hippocampus and lexical-semantic storage sites the most during wake retrieval testing. Because the learning and retrieval tasks in the current study were similar to Züst et al. (2019), the hippocampus was likely mediating the retrieval of the sleep-formed associations in the current study. We have also measured the brain oxygenation using functional magnetic resonance imaging in five persons while they learned pairs of pseudowords and translation words during slow-wave sleep and found the hippocampus activated (besides language areas) in all persons (unpublished).

For these reasons, we believe that vocabulary presentations during sleep had triggered a hippocampus-mediated rapid conceptual-associative encoding process that provided for flexible representations of combinations of pseudowords and translation words in episodic memory.

Author Response

We thank the reviewers for their insightful reviews of our work, including both its strengths and limitations. Below we present minor corrections to the preprint and responses to the main points brought up by each reviewer.

Erratum:

• Line 330 refers to Fig. 7F (instead of 7D).

• Line 331 refers to Fig. 7G (instead of 7E).

Reviewer #1 (Public Review):

The experimental design presented cannot clearly show that the effect of passive exposure was due to the specific exposure to task-relevant stimuli since there is no control group exposed to irrelevant stimuli.

We acknowledge the possibility that exposure to task-irrelevant stimuli could result in improvements in learning. Testing this possibility would be a worthwhile goal of future experiments, but it is outside the scope of our current study. We have been careful in our paper to only draw conclusions about the effects of exposure to task-relevant stimuli compared to no exposure. We will also add a discussion of this point and references to the literature pointed out by the reviewer to the final version of our manuscript.

The conclusion that "passive exposure influences responses to sounds not used during training" (line 147) does not seem fully supported by the authors' analysis. The authors show that there is an increase in accuracy for intermediate sweep speeds despite the fact that this is the first time the animals encounter them in the active session. However, it seems impossible to exclude that this effect is not simply due to the increased accuracy of the extreme sounds that the animals had been trained on.

The conclusion that the reviewer quotes from our paper is drawn from Figure 3, in which we show that mice exhibit an improvement on non-extreme stimuli after training on extreme stimuli. Panel 3D illustrates that the observed improvements are not just changes in psychometric performance driven by the extreme sounds. In the context of this result, the conclusion relates to generalization in performance on task-relevant stimuli that are closely related to the training stimuli. In our view, it was not entirely obvious a priori that this result would have to occur, since it is possible that performance could improve at the extremes without improving at the intermediate stimuli.

In the modelling section, the authors adjusted the hyper-parameters to maximize the difference between pure active and passive/active learning. This makes a comparison of learning rates between models somewhat confusing.

We apologize for the confusion. None of our conclusions are based on comparisons of learning speed between models, but perhaps this was not pointed out sufficiently clearly. The relevant comparisons between conditions for each specific model are made using the same hyperparameters. We will clarify this in the updated version of our manuscript.

The description of the sound does not state whether when reducing the slope of the sweeps the center or the onset frequency of the sounds is preserved.

Frequency modulated sounds of different FM slopes were generated such that the center frequency was always the same. This will be clarified in the updated version of our manuscript.

Reviewer #2 (Public Review):

One limitation here is that the presented analysis is somewhat simplistic, does not include any detailed psychometric analysis (bias, lapse rates etc), and primarily focuses on learning speed.

In our analyses of trials that included extreme and intermediate stimuli, we investigated some metrics of the type that the reviewer suggests here. However, since such additional psychometric analyses generally led to null results and would in any case be somewhat tangential to our main results, which are about learning speed and responses to sounds not included during training, we did not include these in our manuscript. A limitation of our study is that the available data does not allow for an analysis of psychometrics during the initial learning stages, since only the extreme stimuli were presented during the task.

Reviewer #3 (Public Review):

The first [major weakness] is that even Model 5 differs from their data. For example, the A+P (passive interleaved condition) learning curve in Figure 7 seems to be non-monotonic, and has some sort of complex eigenvalue in its decay to the steady state performance as trials increase. This wasn't present in their experimental data (Figure 2D), and implies a subtle but important difference. There also appear to be differences in how quickly the initial learning (during early trials) occurs for the A+P and A:P conditions. While both A+P and A:P conditions learn faster than A only in M5, A+P and A:P seem to learn in different ways, which isn't supported in their data.

The reviewer is correct that there are subtle differences between the two learning curves produced by Model 5. Due to noise in the experimental data, however, it is possible that such subtle distinctions also appear in the learning curves of the mice. Further, the slight overshoot of the learning curve that the reviewer mentions is not constrained by the experimental data due to the fact that different mice reach asymptotic performance at different times, and many of them have not even reached asymptotic performance by the end of the training period.

However, even if there are minor discrepancies between the learning curves produced by the final version of the model and by the mice, we do not see this as being especially surprising or problematic. As in any model, there are a large number of potentially important features that are not included in any of our models–for example, realistic spectrotemporal neural responses, nonlinearity in neural activations, heterogeneity across mice, and many others. The aim of our modeling was to choose a space of possible models (which is inevitably restricted) and show which model version within that space best captures our experimental observations. Expanding the space of possible models that we considered to capture further nuances in the data will be a task for future work.

The second major weakness is that the authors also don't generate any predictions with M5. Can they test this model of learning somehow in follow-up behavioural experiments in mice? ... Without follow-up experiments to test their mechanism of why passive exposure helps in a schedule-independent way, the impact of this paper will be limited.

Although testing behavioral predictions from our models was beyond the scope of the current study, we do generate specific predictions with M5 (specifically, about neural representations). Our model produces predictions about neural representations and the ways in which they evolve through learning, and we hope to test these predictions in future work.

I believe the authors need to place this work in the context of a large amount of existing literature on passive (unsupervised) and active (supervised) learning interactions. This field is broad both experimentally and computationally. For example, there is an entire sub-field of machine learning, called semi-supervised learning that is not mentioned at all in this work.

We thank the reviewer for pointing this out. The updated version of our manuscript will include a discussion on how our results fit in with this literature.

Author Response

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

First, the authors would like to thank the reviewers and editors for their thoughtful comments. The comments were used to guide our revision, which is substantially improved over our initial submission. We have addressed all comments in our responses below, through a combination of clarification, new analyses and new experimental data.

Reviewer #1 (Public Review):

In this manuscript, the authors identified and characterized the five C-terminus repeats and a 14aa acidic tail of the mouse Dux protein. They found that repeat 3&5, but not other repeats, contribute to transcriptional activation when combined with the 14aa tail. Importantly, they were able to narrow done to a 6 aa region that can distinguish "active" repeats from "inactive" repeats. Using proximal labeling proteomics, the authors identified candidate proteins that are implicated in Dux-mediated gene activation. They were able to showcase that the C-terminal repeat 3 binds to some proteins, including Smarcc1, a component of SWI/SNF (BAF) complex. In addition, by overexpressing different Dux variants, the authors characterized how repeats in different combinations, with or without the 14aa tail, contribute to Dux binding, H3K9ac, chromatin accessibility, and transcription. In general, the data is of high quality and convincing. The identification of the functionally important two C-terminal repeats and the 6 aa tail is enlightening. The work shined light on the mechanism of DUX function.

A few major comments that the authors may want to address to further improve the work:

We thank the reviewer for their efforts and constructive comments, which have guided our revisions.

1) The summary table for the Dux domain construct characteristics in Fig. 6a could be more accurate. For example, C3+14 clearly showed moderate weaker Dux binding and H3K9ac enrichment in Fig 3c and 3e. However, this is not illustrated in Fig. 6a. The authors may consider applying statistical tests to more precisely determine how the different Dux constructs contribute to DNA binding (Fig. 3c), H3K9ac enrichment (Fig. 3e), Smarcc1 binding (Fig. 5e), and ATAC-seq signal (Fig. 5f).

We thank the reviewer for this comment, and agree that there were some modest differences in construct characteristics that were not captured in the Summary Table (6a). To better reflect the differences between constructs, we added additional dynamic range to our depiction/scoring, and believe that the new scoring system provides sufficient qualitative range to capture the difference without imposing a statistical approach.

2) Another concern is that exogenous overexpressed Dux was used throughout the experiments. The authors may consider validating some of the protein-protein interactions using spontaneous or induced 2CLCs (where Dux is expressed).

We agree that it would be helpful to determine endogenous DUX interaction with our BioID candidates. Here, we attempted co-IPs for endogenous DUX protein with the DUX antibody and were unsuccessful, which indicated that the DUX antibody is useful for detection but not efficient in the primary IP. This is why we utilized the mCherry tag for DUX IP experiments, which worked exceptionally well.

3) It could be technically challenging, but the authors may consider to validate Dux and Smarcc1 interaction in a biologically more relevant context such as mouse 2-cell embryos where both proteins are expressed. Whether Smarcc1 binding will be dramatically reduced at 4-cell embryos due to loss of Dux expression?

While we agree that it would be interesting to validate the in vivo interaction of DUX and SMARCC1 in the early embryo, it is not technically feasible for us to conduct the experiment, as the IP would require thousands of two-cell embryos, and we have the issue of poor co-IP quality with the DUX antibody.

Reviewer #2 (Public Review):

In this manuscript, Smith et al. delineated novel mechanistic insights into the structure-function relationships of the C-terminal repeat domains within the mouse DUX protein. Specifically, they identified and characterised the transcriptionally active repeat domains, and narrowed down to a critical 6aa region that is required for interacting with key transcription and chromatin regulators. The authors further showed how the DUX active repeats collaborate with the C-terminal acidic tail to facilitate chromatin opening and transcriptional activation at DUX genomic targets.

Although this study attempts to provide mechanistic insights into how DUX4 works, the authors will need to perform a number of additional experiments and controls to bolster their claims, as well as provide detailed analyses and clarifications.

We thank this reviewer for their constructive comments, and have conducted several new analyses, additional experiments and clarifications – which have strengthened the manuscript in several locations. Highlights include a statistical approach to the similarity of mouse repeats to themselves and to orthologs (Figure S1d) and clarified interpretations, a wider dynamic range to better reflect changes in DUX construct behaviors (Figure 6a), and additional data on construct behavior, including ‘inactive’ constructs (e.g C1+14aa in Figure 1a,d, new ATAC-seq in Figure S1g), and active constructs such as C3+C5+14aa and C3+C514aa (in Figure S1b).

Reviewer #3 (Public Review):

Dux (or DUX4 in human) is a master transcription factor regulating early embryonic gene activation and has garnered much attention also for its involvement in reprogramming pluripotent embryonic stem cells to totipotent "2C-like" cells. The presented work starts with the recognition that DUX contains five conserved c. 100-amino acid carboxy-terminal repeats (called C1-C5) in the murine protein but not in that of other mammals (e.g. human DUX4). Using state-of-the-art techniques and cell models (BioID, Cut&Tag; rescue experiments and functional reporter assays in ESCs), the authors dissect the activity of each repeat, concluding that repeats C3 and C5 possess the strongest transactivation potential in synergy with a short C-terminal 14 AA acidic motif. In agreement with these findings, the authors find that full-length and active (C3) repeat containing Dux leads to increased chromatin accessibility and active histone mark (H3K9Ac) signals at genomic Dux binding sites. A further significant conclusion of this mutational analysis is the proposal that the weakly activating repeats C2 and C4 may function as attenuators of C3+C5-driven activity.

By next pulling down and identifying proteins bound to Dux (or its repeat-deleted derivatives) using BioID-LC/MS/MS, the authors find a significant number of interactors, notably chromatin remodellers (SMARCC1), a histone chaperone (CHAF1A/p150) and transcription factors previously (ZSCAN4D) implicated in embryonic gene activation.

The experiments are of high quality, with appropriate controls, thus providing a rich compendium of Dux interactors for future study. Indeed, a number of these (SMARCC1, SMCHD1, ZSCAN4) make biological sense, both for embryonic genome activation and for FSHD (SMCHD1).

A critical question raised by this study, however, concerns the function of the Dux repeats, apparently unique to mice. While it is possible, as the authors propose, that the weak activating C1, C2 C4 repeats may exert an attenuating function on activation (and thus may have been selected for under an "adaptationist" paradigm), it is also possible that they are simply the result of Jacobian evolutionary bricolage (tinkering) that happens to work in mice. The finding that Dux itself is not essential, in fact appears to be redundant (or cooperates with) the OBOX4 factor, in addition to the absence of these repeats in the DUX protein of all other mammals (as pointed out by the authors), might indeed argue for the second, perhaps less attractive possibility.

In summary, while the present work provides a valuable resource for future study of Dux and its interactors, it fails, however, to tell a compelling story that could link the obtained data together.

We appreciated the reviewer’s views regarding the high quality of the work and our generation of an important dataset of DUX interactors. We also appreciate the comments provided to improve the work, and have performed and included in the revised version a set of clarifications, additional analyses and additional experiments that have served to reinforce our main points and provide additional mechanistic links. We also agree that more remains to be done to understand the function and evolution of repeats C1, C2 and C4.

Reviewer #1 (Recommendations For The Authors):

1) For immuno-blots, authors may indicate the expected bands to help readers better understand the results.

Agreed, and we have included the predicted molecular weight of proteins in the Figure Legends. We note that our work shows that the C-terminal domains confer anomalous migration in SDS-PAGE.

2) Fig. 5b, a blot missing for the mCherry group?

Figure 5b is a volcano blot, so we believe the reviewer is referring to Figure 5d, which is a coimmunoprecipitation experiment between SMARCC1 and mCherry-tagged DUX constructs. However, we are unsure of the comment as an anti mCherry sample is present in that panel.

3) Line 99-100, Fig. S1d, it seems that repeat2, but not repeat3, is more similar to human DUX4 C-terminal region.

This comment and one by another reviewer have prompted us to re-examine the similarities of the DUX repeats, and we have new analyses (Figure S1d) and an alternative framing in the manuscript as a result. We have expanded on this in our response to Reviewer #2, point #1 – and direct the reviewer there for our expanded treatment.

4) There are a few references are misplaced. For example, line 48, the studies that reported the role of Dux in inducing 2CLCs should be from Hendrickson et al., 2017, De Iaco et al., 2017, and Whiddon et al., 2017. The authors may want to double check all references.

Thanks for pointing these out. These issues have been corrected in the manuscript.

5) In the materials & methods section, a few potential errors are noticed. For example, concentrations of PD0325901 and CHIR99021 in mESC medium appear ~1000-fold higher than standards.

Thanks – corrected.

Reviewer #2 (Recommendations For The Authors):

Major Points

1) Line 99 - The authors claimed that the "human DUX4 C-terminal region is most similar to the 3rd repeat of mouse DUX", but based on Supp. Fig. 1d, the human DUX4 C-term should be most similar to the 2nd repeat of mouse DUX. If this is indeed the case, it will undermine the rest of this study, since the authors claim that the 3rd repeat is transcriptionally active, whereas the 2nd repeat is transcriptionally inactive, and the bulk of this study largely focused on how the active repeats, not the inactive repeats, are critical in recruiting key transcriptional and chromatin regulators to induce the embryonic gene expression program.

We thank the reviewer for their comments here. Since submission,and as mentioned above for reviewer #1 we have revisited the issue of similarity of the DUX4 C-terminal region to the mouse C-terminal repeats, with a BLAST-based approach that is more rigorous and informed by statistics – which is in Author response table 1 and now in the manuscript as Figure S1d, and has affected our interpretation. Our prior work involved a simple % identity comparison table and we now appreciate that some of the similarity analyses did not meet statistical significance, and therefore we are unable to draw certain conclusions. We make the appropriate modifications in the text. For example, we no longer state that the DUX4 C-terminus appears to be most similar to mouse repeats 3 and 5. This does not affect the main conclusions of the paper regarding interactions of the C-terminus with chromatin-related proteins, only our speculation on which repeat might have represented the original single repeat in the mouse – an issue we think of some interest, but did not rise to the level of mentioning in the original or current abstract.

Author response table 1.

Parameters: PAM250 matrix. Gap costs of existence: 15 and extension: 3. Numbers represent e-value of each pairwise comparison

*No significant similarities found (>0.05).

2) In Supp Fig 1d, it seems that the rat DUX4 C-terminal region is most similar to the 4th repeat of mouse DUX, which according to the author is supposedly transcriptionally inactive. This weakens the authors justification that the 3rd or 5th repeat is likely the "parental repeat for the other four", and further echoes my concern in point 1 where the human DUX4 C-term is most similar to the 2nd (inactive) repeat of mouse DUX.

The reviewer’s point is well taken and is addressed in point #1 above.

3) In Fig. 1d, the authors showed that DUX4-containing C3 and C5, but lacking acidic tail, can promote MERVL::GFP expression, albeit to a slightly lower extent compared to FL. However, in Fig. 2b, C3 or C5 alone (lacking acidic tail) completely failed to promote MERVL::GFP expression. However, in the presence of the acidic tail, both versions were able to promote MERVL::GFP expression, similar to that of FL. The latter would suggest that it is the acidic tail that is crucial for MERVL::GFP expression, and this does not quite agree with Fig 1b, where C12345 (lacking acidic tail) was able to promote MERVL::GFP expression. Although C12345 did not activate MERVL to a similar level as FL, it is clearly proficient, compared to C3 or C5 alone (lacking acidic tail) where there is no increase in MERVL at all. Additional constructs will be helpful to clarify these points. For example, 'C3+C5 minus acidic tail' and 'HD1+HD2+acidic tail only' constructs.

We agree that constructs such as those mentioned would add to the work. First, we have done the additional construct HD1+HD2+14aa tail, which is presented as ΔC12345+14aa in Figure 2a and in S2a. Additionally, we performed experiments on the requested C3+C5+14aa and C3+C5Δ14aa (see samples 6 and 7 in Author response image 1, which are now included in Supplemental Figure 2b). The results reinforce our hypothesis of an additive effect toward DUX target gene activation by increasing C-terminal repeats and including the 14aa tail.

Author response image1.

4) Related to the above, the flow cytometry data for the MERVL::GFP reporter as presented in Figures 1 and 2, as well as in Supp. Fig. 2, show a considerably large difference in the %GFP|mCherry for the FL construct, ranging from ~6-26%. This makes it difficult to convince the reader which of the different DUX domain constructs cannot or can partially induce GFP|mCherry signal when compared to FL, and hence it is tough to definitively ascertain the exact contribution of each of the 5 C-terminal repeats with high confidence, as it appears that there exists a significant amount of variability in this MERVL::GFP reporter system. The authors need to address this issue since this is their primary method to elucidate the transcriptional activity of each of the mouse DUX repeat domains.

We note that with the Dux-/- cell lines we used throughout the timeline of the study, the percent of %GFP|mCherry expression progressively and slowly decreased – possibly due to slow/modest epigenetic silencing of the reporter. However, we always used the full-length DUX construct to establish the dynamic range. We emphasize that the relative differences between constructs over multiple cell line replicates remained relatively consistent. However, we elected to show absolute values in each experiment, rather than simply normalizing the full-length to 100% and showing relative.

5) Lines 140-142 - The authors claimed that the functional difference between the transcriptionally active and inactive repeats could be narrowed down to a "6aa region which is conserved between repeats C3 and C5, but not conserved in C1, C2 and C4". Assuming the 6aa sequence is DPLELF, why does C1C3a elicit almost twice the intensity of GFP|mCherry signal compared to C3C1c, despite both constructs having the exact same 6aa sequence?

Indeed, C1C3a and C3C1c both containing the ‘active’ DPL sequence but having different relative levels of %GFP|mCherry. This is consistent with these sequences having a positive role in DUX target gene regulation – but likely in combination with other other regions which potentiate its affect, possibly through interacting proteins or post-translational modifications.

Why does DPLEPL (the intermediate C3C1b construct) induce a similar extent of GFP|mCherry signal as the FL construct, even though the former includes 3aa from a transcriptionally inactive repeat? In contrast, GSLELF (the other intermediate C1C3b construct) that also includes 3aa from a transcriptionally inactive repeat is almost completely deficient in inducing any GFP|mCherry signal. Why is that so? Is DPL the most crucial sequence? It will be important to mutate these 3 (or the above 6) residues on FL DUX4 to examine if its transcriptional activity is abolished.

These are interesting points. DPL does appear to be the most important region in the mouse DUX repeats. However, DPL is not shared in the C-terminus of human DUX4. Notably, the DUX4 C-terminus is sufficient to activate the mouse MERVL::GFP reporter when cloned to mouse homeodomains (see Author response image 2, second sample) and other DUX target genes (initially published in Whiddon et al. 2017). One clear possibility is that the DPL region is helping to coordinate the additive effects of multiple DUX repeats, which only exist in the mouse protein.

Author response image 2.

6) Line 154 - The intermediate DUX domain construct C1C3b occupied a different position on the PCA plot from the C1C3c construct that does not contain any of the critical 6aa sequence, as shown in Fig. 2e. However, both these constructs appear to be similarly deficient in inducing any GFP|mCherry signal, as seen in Fig. 2c. Why is that so?

The PCA plot assesses the impact on the whole transcriptome and not just the MERVL::GFP reporter, suggesting the 3aa region has transcriptional effects on the genome beyond what is detected in the MERVL::GFP reporter.

7) To strengthen the claim that "Chromatin alterations at DUX bindings sites require a transcriptionally active DUX repeat", the authors should also perform CUT&Tag for constructs containing transcriptionally inactive DUX repeats (e.g. C1+14aa), and show that such constructs fail to occupy DUX binding sites, as well as are deficient in H3K9ac accumulation.

This is a good comment. We elected to control this with constructs containing or lacking an active repeat. Although we have not pursued this by CUT&TAG, we have examined the impact of DUX constructs with inactive repeats (including the requested C1+14aa, new Figure S1g) by ATAC-seq (see #12, ATAC-seq section, below), and observe no chromatin opening, suggesting that the lack of transcriptional activity is rooted in the inability to open chromatin.

8) It would be good if the authors could also include CUT&Tag data for some of the C1C3 chimeric constructs that were used in Fig. 2, since the authors argued that the minimal 6aa region is sufficient to activate many of the DUX target genes. This would also strengthen the authors’ case that the transcriptionally active, not inactive, repeats are critical for binding at DUX binding sites and ensuring H3K9ac occupancy.

We agree that these would be helpful, and have examined the inactive repeats in transcription and ATAC-seq formats during revision (new data in Figures 1d and S1g), but not yet the CUT&TAG format.

9) Line 213 - "SMARCA4" should have been "SMARCA5"? Based on Fig. 4d, SMARCA5 is picked up in the BirA*-DUX interactome, not SMARCA4.

Thanks – corrected.

10) Lines 250-252 - The authors compared the active BirA-C3 against the inactive BirA-C1 to elucidate the interactome of the transcriptionally active C3 repeat, as illustrated in Fig. 5c. They found 12 proteins more enriched in C1 and 154 proteins in C3. This information should be presented clearly as a separate tab in Supp Table 2. What are the proteins common to both constructs, i.e. enriched to a similar extent? Do they include chromatin remodellers too? Although the authors sought to identify differential interactors between the 2 constructs, it is also meaningful to perform 2 separate comparisons - active BirA-C3 against BirA alone control, and inactive BirA-C1 against BirA alone control - like in Fig. 4d, so as to more accurately define whether the active C3 repeat, and not the inactive C1 repeat, interacts with proteins involved in chromatin remodeling.

We thank the reviewer for this comment, and we have modified the manuscript by adding a second sheet in Supplementary Table 2 including the results for enriched proteins in BirA-C1 vs. C3. Additionally, due to limitations of annotation between BirA alone and BirA*-C3 being sequenced in different mass spectrometry experiments, it is difficult to quantitatively compare the two datasets with pairwise comparisons.

11) Fig 5d: The authors mentioned in the legend that endogenous IP was performed for SMARCC1. However, in line 266, they stated Flag-tagged SMARCC1. Is SMARCC1 overexpressed? The reciprocal IP should also be presented. More importantly, C1 constructs (e.g. C1+14aa and C1Δ14aa) should also be included.

To clarify, Figure 4e used exogenously overexpressed FLAG-SMARCC1 in HEK-293T cells to confirm the results of the full-length DUX BioID experiment. Figure 5d was performed with overexpressed DUX construct, but involved endogenous SMARCC1 in mESCs. This has now been made clearer in the revised manuscript.

12) For both the SMARCC1 CUT&Tag and ATAC-seq experiments shown in Figures 5e and 5f respectively, the authors need to include DUX derivatives that contain transcriptionally inactive repeats with and without the 14aa acidic tail, i.e. C1+14aa and C1Δ14aa, and show that these constructs prevent the binding/recruitment of SMARCC1 to DUX genomic targets, and correspondingly display a decrease in chromatin accessibility. Only then can they assert the requirement of the transcriptionally active repeat domains for proper DUX protein interaction, occupancy and target activation.

We agree that examination of an inactive repeat in certain approaches would improve the manuscript. Importantly, we have now included C1+14 in our ATAC-seq experiments, and in Author response image 3 two individual replicates, which constitute a new Figure S1g. Compared to the transcriptionally active DUX constructs, which see opening at DUX binding sites, we do not see chromatin opening at DUX binding sites with transcriptionally inactive C1+14.

Author response image 3.

13) To prove that DUX-interactors are important for embryonic gene expression, it will be important to perform loss of function studies. For instance, will the knockdown/knockout of SMARCC1 in cells expressing the active DUX repeat(s) lead to a loss of DUX target gene occupancy and activation?

We agree that it would be interesting to better understand SMARCC1 cooperation with DUX function in the embryo, but we believe this is beyond the scope of this paper.

Minor Points

1) Lines 124-126 - What is the reason/rationale for why the authors used one linker (GGGGS2) for constructs with a single internal deletion, but 2 different linkers (GGGGS2 and GAGAS2) for constructs with 2 internal deletions?

With Gibson cloning, there are homology overhang arms for each PCR amplicon that are required to be specific for each overlap. Additionally, each PCR amplicon needs to be specific enough from one another so that all inserts (up to 5 in this manuscript) are included and oriented in the right order. The linker sequences were included in the homology arm overlaps, so the nucleotide sequences for each linker needed to be specific enough to include all inserts. This is a general rule to Gibson cloning. Additionally, both GGGGS2 and GAGAS2 are common linker sequences used in molecular biology and the amino acids structures are similar to one another, suggesting there is no functional difference between linkers.

2) Line 704 - 705: In the figure legend, the authors stated that 'Constructs with a single black line have the linker GGGGS2 and constructs with two black lines have linkers with GGGGS2 and GAGAS2, respectively.'. This was not obvious in the figures.

Constructs used for flow and genomics experiments that are depicted in Figure 2, Supplementary Figure 2, Figure 3, Figure 4, and Figure 5 have depicted black lines where deletions are present. Where these deletions are present, there are linkers in order to preserve spacing and mobility for the protein.

3) Line 160 - Clusters #1 and #2 are likely written in the wrong order. It should have been "activating the majority of DUX targets in cluster #2, not cluster #1" and "failed to activate those in cluster #1, not cluster #2", based on the RNA-seq heatmap in Fig. 2f.

We thank the reviewer for this comment, and the error has been corrected in the manuscript.

4) Line 188 - Delete the word "of" in the following sentence fragment: "DUX binding sites correlating with the of transcriptional".

Thanks – corrected.

5) Line 191 - Delete the word "aids" in the following sentence fragment: "important for conferring H3K9ac aids at bound".

Thanks – corrected.

6) Line 711 - "C1-C3 a,b,d" should be "C1-C3 a,b,c".

Thanks – corrected.

7) Lines 711-712 - The colors "pink to blue" and "blue to pink" are likely written in the wrong order. Based on Fig. 2c, the blue to pink bar graphs should represent C1-C3 a,b,c in that order, and likewise the pink to blue bar graphs should represent C3-C1 a,b,c in that order.

Thanks – corrected.

8) There is an overload of data presented in Fig. 2c, such that it is difficult to follow which part of the figure represents each data segment as written in the figure legend. It is recommended that the data presented here is split into 2 sub-figures.

Figure 2c has a supporting figure in Supplementary Figure 2b. While there is both a graphical depiction of the constructions and the data both in the main panel of Figure 2C, we have depicted it as so to be as clear as possible for the reader to interpret the complexity and presentence of amino acids in each of the constructs.

9) Line 717 - "following" is misspelt.

Thanks – corrected.

10) Lines 720-721 - "(Top)" and "(Bottom)" should be replaced with "(Left)" and "(Right)", as the 2 bar graphs presented in Fig. 2d are placed side by side to each other, not on the top and bottom.

Thanks – corrected.

11) Lines 725 and 839 - "Principle" is misspelt. It should be "Principal".

Thanks – corrected.

12) In Figures 3d and 3e, the sample labeled "C3+14_1" should be re-labeled to "C3+14", in accordance with the other sub-figures. Additionally, for the sake of consistency, "aa" should be appended to the relevant constructs, e.g. "C3+14aa" and "C3Δ14aa".

Thanks – corrected.

13) Line 773 - Were the DUX domain constructs over-expressed for 12hr (as written in the figure legend) or 18hr (as labeled in Fig. 5d)?

Thanks – corrected.

14) Related to minor point 19 above, is there a reason/rationale for why some of the experiments used 12hr over-expression of DUX domain constructs (e.g. for CUT&TAG in Fig. 3), whereas in other experiments 18hr over-expression was chosen instead (e.g. flow cytometry for MERVL::GFP reporter in Figures 1 and 2, and co-IP validations of BirA*-DUX interactions in Fig. 4)?

Thanks for the opportunity to explain. In this work, experiments that reported on proteins that are translated following DUX gene activation (e.g. MERVL:GFP via flow) were done at 18hr to allow for enough time for transcription and translation of GFP (or other DUX target genes). For experiments that report on the impact of DUX on chromatin and transcription, such as RNA-seq, CUT&Tag, and ATAC-seq, we induced DUX domain constructs for 12 hours.

15) Line 804 - "ΔHDs" is missing between "C2345+14aa" and "ΔHD1".

Thanks – corrected.

16) In Fig. 5c, "Chromatin remodelers" is misspelt.

Thanks – corrected.

17) There is no reference in the manuscript to the proposed model that is presented in Fig. 6b.

Thanks – corrected.

Reviewer #3 (Recommendations For The Authors):

Given the uncertainty of the function of the Dux peptide repeats in mice, could it not also be possible that the underlying repeated nature of the (coding) DNA? That is, could these DNA repeats exert a regulatory function on Dux transcription itself (also given the dire consequences of misregulated DUX4 expression as seen in FSHD, for example).

Yes, it remains possible that the internal coding repeats within Dux are playing a role in locus regulation, and might be interesting to examine. However, we consider this question as being outside the scope of the current paper.

Finally, it would be interesting to know whether these repeats are, in fact, present in all mouse species. Already no longer present in rat, do they exist, or not, in more "distant" mice, e.g. M. caroli?

Determining whether all mouse strains contain C-terminal repeats in DUX is a question we also considered. However, Dux and its orthologs are present in long and very complex repeat arrays that are not present in the sequencing data or annotation in other mouse strains. Therefore, we are not unable to answer this question from existing sequencing data. Answering would require a considerable genome sequencing and bioinformatics effort, or alternatively a considerable effort aimed at cloning ortholog cDNAs from 2-cell embryos.

Minor points:

line 169: here it seems, in fact, that the 'inactive' C2, C4 repeats are more similar to each other (my calculation: 91 and 96% identity at the protein and DNA level, respectively) than the active C3 and C5 repeats (82 and 89% identity, resp.), the outlier being C1.

Thanks for this comment, which was mentioned by other reviewers as well and has been addressed through new statistical analyses and interpretation (see new Figure S1d).

line 191: I'm not sure this sentence parses correctly ("...14AA tail is important for conferring H3K9Ac aids at bound sites...")

We thank the reviewer for this comment, and we have corrected the sentence in the manuscript.

Author Response

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

Reviewer #1 (Public Review):

This study presents an important finding on human m6A methyltransferase complex (including METTL3, METTL14 and WTAP). The evidence supporting the claims of the authors is convincing, although the model and assays need to be further modified. The work will be of interest to biologists working on RNA epigenetics and cancer biology.

In mammals, a large methyltransferase complex (including METTL3, METTL14 and WTAP) deposits m6A across the transcriptome, and METTL3 serves as its catalytic core component. In this manuscript, the authors identified two cleaved forms of METTL3 and described the function of METTL3a (residues 239-580) in breast tumorigenesis. METTL3a mediates the assembly of METTL3-METTL14-WTAP complex, the global m6A deposition and breast cancer progression. Furthermore, the METTL3a-mTOR axis was uncovered to mediate the METTL3 cleavage, providing potential therapeutic target for breast cancer. This study is properly performed and the findings are very interesting; however, some problems with the model and assays need to be modified. It is widely known that METTL3 and METTL14 form a stable heterodimer with the stoichiometric ratio of 1:1 (Wang X et al. Nature 534, 575-578 (2016), Su S et al. Cell Res 32(11), 982994 (2022), Yan X et al. Cell Res 32(12), 1124-1127 (2022)), the numbers of METTL3 and METTL14 in the model of Fig 7P are not equivalent and need to be modified.

We thank for reviewer’s good suggestion. We have modified the model in Fig. 7P.

Reviewer #2 (Public Review):

In this study, Yan et al. report that a cleaved form of METTL3 (termed METTL3a) plays an essential role in regulating the assembly of the METTL3-METTL14-WTAP complex. Depletion of METTL3a leads to reduced m6A level on TMEM127, an mTOR repressor, and subsequently decreased breast cancer cell proliferation. Mechanistically, METTL3a is generated via 26S proteasome in an mTOR-dependent manner.

The manuscript follows a smooth, logical flow from one result to the next, and most of the results are clearly presented. Specifically, the molecular interaction assays are welldesigned. If true, this model represents a significant addition to the current understanding of m6A-methyltransferase complex formation.

A few minor issues detailed below should be addressed to make the paper even more robust. The specific comments are contained below.

1) The existence of METTL3a and METTL3b.<br /> In this study, the author found the cleaved form of METTL3 in breast cancer patient tissues and breast cancer cell lines. Is it a specific event that only occurs in breast cancer? The author may examine the METTL3a in other cell lines if it is a common rule.

We thank reviewer for point this out. We discovered the cleaved form of METTL3 in breast cancer, and we further examined this cleaved METTL3 in other cell lines such as lung cancer cell lines, renal cancer cell lines, HCT116 and MEF (new Supplementary Figures 1A-1C), these data suggest that it is a common rule. Therefore, we speculate that METTL3a may be ubiquitiously expressed. We have added this part in the revised manuscript, please see Line 118-120.

2) Generation of METTL3a and METTL3b.

1) Figure 1 shows that METTL3a and METTL3b were generated from the C-terminal of full-length METTL3. Because the sequence of METTL3a is involved in the sequences of METTL3b, can METTL3b be further cleaved to produce METTL3a?

Although the sequence of METTL3a is involved in the sequences of METTL3b, overexpression of METTL3b in T47D, MDA-MB-231 and 293T cells did not show METTL3a expression in these cells (please see Figures 3A, 3C, 3G), suggesting that METTL3b can not be further cleaved to produce METTL3a, and the METTL3 cleavage may require its N-terminal region. We have added this in the discussion, please see Line 358 to 360.

2) Based on current data, the generation of METTL3a and METTL3b are separated. Are there any factors that affect the cleavage ratio between METTL3a and METTL3b?

We thank for reviewer’s excellent question. In this study, we show that both METTL3a and METTLb are produced through proteasomal cleavage, and both of them are positively regulated by the mTOR pathway. On the other hand, we indeed observed the differential cleavage ratios between METTL3a and METTL3b across different cell lines. For example, METTL3a/METTLb ratio was greater than 1 in MDA-MB-231 cells (see Figure 7C), less than 1 in T47D and 293T cell lines (see Figure 7A and 7B), and equal to 1 in MEF cells (see Figure 7O). Based on these results, we speculate that there may be some factors that control the cleavage ratio between METTL3a and METTL3b, which warrants further investigation. We have added this in the discussion, please see Line 374 to 379.

3) In Figure 2G, the author shows the result that incubation of the Δ198+Δ238 METTL3 protein with T47D cell lysates cannot produce the METTL3a and METTL3b variants. The author may also show the results that Δ198 METTL3 protein or Δ238 METTL3 protein incubates with T47D cell lysates, respectively.

Following the reviewer’s suggestion, we had performed in vitro cleavage assays by incubation of METTL3-Δ238 or METTL3-Δ198 with T47D cell lysates, and had incorporated this result in the revised manuscript. Please see our new Supplementary Figure 3A.

4) As well as many results published in previous studies, the in vitro methylation assay shows that WT METTL3 is capable of methylating RNA probe (figure 2H). The main point of this study is that METTL3a is required for the METTL3-METTL14 assembly. However, the absence of METTL3a in the in vitro system did not inhibit METTL3METTL14 methylation activity. Moreover, the presence of METTL3a even resulted in a weak m6A level.

The main point of this study is that METTL3a is required for the METTL3WTAP interaction, but dispensable for the METTL3-METTL14 assembly (see Figure 4A-4B). In this in vitro methylation assays, METTL3 and METTL14 is capable of methylating RNA probe in the absent of WTAP. In this condition, we found that METTL3 WT as well as its different variants (METTL3-Δ238, METTL3-Δ198, METTL3b and METTL3a) except the catalytically dead mutant METTL3 APPA showed methylation activity in vitro.

5) In Figure 4A, the author suggests that WTAP cannot be immunoprecipitated with METTL3a and 3b because WTAP interacted with the N-terminal of METTL3. If this assay is performed in WT cells, the endogenous full-length METTL3 may help to form the complex. In this case, WTAP is supposed to be co-immunoprecipitated.

We thank reviewer for point this out. METTL3 interacts with WTAP through its N-terminal (1-33aa) (1). Consistently, we find that the two cleaved forms METTL3a and METTL3b which lack the N-terminal region are not able to bind with WTAP. In Figure 4A, we overexpressed METTL3 WT as well as its different variants METTL3-Δ238, METTL3-Δ198, METTL3b and METTL3a respectively in WT cells, and compared the binding ability with WTAP or METTL14 across these overexpressed METTL3 variants. We acknowledge that the exogenous METTL3a and METTL3b interact with endogenous full-length METTL3, and the endogenous full-length METTL3 may help them to form the complex with WTAP. But in fact, the exogenous expression levels of METTL3a and METTL3b are much higher than that of endogenous full-length METTL3 (see Figure 3A and 3C). In this case, METTL3a or METTL3b predominantly interacts with itself, METTL3, METTL14 or other potential interacting proteins through its C-terminal region, this may greatly dilute the condition for the interaction between WTAP and endogenous full-length METTL3. Moreover, in Figure 4A, the comparison is among overexpressed METTL3 variants, the week indirect interactions through much lower expression levels of endogenous protein are probably not comparable to those direct interactions between overexpressed METTL3 variants and WTAP.

Reference:

1) Schöller, E., Weichmann, F., Treiber, T., Ringle, S., Treiber, N., Flatley, A., Feederle, R., Bruckmann, A., and Meister, G. (2018). Interactions, localization, and phosphorylation of the m6A generating METTL3–METTL14–WTAP complex. Rna 24, 499-512

Reviewer #1 (Recommendations For The Authors):

Major points:

1) It is widely known that METTL3 and METTL14 form a stable heterodimer with the stoichiometric ratio of 1:1 (Wang X et al. Nature 534, 575-578 (2016), Su S et al. Cell Res 32(11), 982-994 (2022), Yan X et al. Cell Res 32(12), 1124-1127 (2022)), the numbers of METTL3 and METTL14 in the model of Fig 7P are not equivalent and need to be modified.

We thank for reviewer’s good suggestion. We have modified the model in Fig. 7P.

2) The in vitro methylation activity was detected by the m6A antibody, which has limited linear range. The MTase-Glo{trade mark, serif} Methyltransferase Assay is a SAMdependent enzyme assay with wide applications (Please refer to the references below).

Could this assay be performed by authors?

Wilkinson AW et al. Nature 565(7739), 372-376 (2019).

Yu D et al. Nucleic Acids Res 49(20),11629-11642 (2021).

Yan X et al. Cell Res 32(12), 1124-1127 (2022).

Chen J et al. Nat Commun 13(1), 3257 (2022).

Thanks for reviewer’s good suggestion. We had performed the in vitro methylation assay by using MTase-Glo kit, and the data is consistent with the dot blot results. Please see the new Figure 2H-J.

3) When expressed alone in mammalian cell lines, METTL14 is unstable and is easily contaminated with endogenous METTL3 during purification (Yang W et al. Nat Cell Biol 16(2), p.191-8 (2014), Fig 1e). In Fig 2I, Co-expressing METTL3 and METTL14 maybe a good choice.

We thank for reviewer’s good suggestion. In fact, we co-expressed METTL3 and METTL14 in this in vitro methylation assay in Fig 2I (new Figure 2J in the revised version), METTL3-Flag or its mutant with Flag tag and METTL14-Flag were co-transfected into 293T cells, and co-purified by using Flag M2 magnetic beads from the cell lysates. We have added these details in the indicated method section, please see Line 574-585.

Other minor points:

1) In Fig 5D, the protein domain information of METTL3 and relevant references need to be added (Su S et al. Cell Res 32(11), 982-994 (2022), Fig 6g; Yan X et al. Cell Res 32(12), 1124-1127 (2022), Fig 1a).

We have added these references in the revised manuscript.

2) In Fig 5, would METTL3b contribute to the METTL3-METTL3 interaction?

Our data showed that METTL3a but not METTL3b is responsible for the METTL3-WTAP interaction, breast cancer cell proliferation and the m6A modification. Then, we investigated the mechanism of how METTL3a regulates the METTL3-WTAP interaction, and found that METTL3a is essential for METTL3-METTL3 interaction, which is a prerequisite step for WTAP recruitment in MTC complex. In this case, we speculate that METTL3b is not required for the METTL3-METTL3 interaction. Indeed, through Co-IP assays,we found that METTL3b has no effect on the METTL3-METTL3 interaction (new supplementary Figure 4D), which is consistent with our above data showing that METTL3b is dispensable for the METTL3-WTAP interaction. We have added this comment in Page 6, Line 226 to 228.

3) In Fig 3F, the color in the legend and figure is inconsistent.

We have corrected the inconsistent color in the revised manuscript.

Reviewer #2 (Recommendations For The Authors):

1) In Figure 5D, the construction details of METTL3-HA and Flag should have been included in the method section. Are these tag sequences in the N-terminal of METTL3 protein?

These tags are all in the C-terminal of METTL3. We have added the construction details of these plasmids in the method section. Please see Line 434.

2) In Figure 7A, the labels of the inhibitors are overlapped with the figures.

We have corrected the labels of the inhibitors in Figure 7A in the revised manuscript.

Author Response

We thank the reviewers and editors for their thoughtful evaluation of our preprint. We felt that the reviews were fair and that addressing them will improve the rigor and clarity of our presentation. We are working to address all of the comments, with intent to submit a revised manuscript in the near future.

Author Response

Reviewer #1 (Public Review):

This cross-sectional study examined the results of a survey about cancer treatment disruption during June-August 2020 in 82 counties located in Missouri and Illinois in the U.S. The main outcome was disruption in cancer care. Authors reported that higher education, being a female, experiencing more discrimination in healthcare settings, and having scheduled a telehealth appointment were associated with higher odds of care disruption. Lack of a research focus, lack of following any conceptual framework, the cross-sectional nature of the study, and the small sample size were the noted shortcomings of the manuscript.

We thank Reviewer 1 for their comments. We agree that it is important to understand COVID-related care disruptions using causal methods. However, this manuscript aimed to examine the local impact of COVID care disruptions. We focused on the Siteman Cancer Center’s (SCC) catchment area because the co-author team includes the SCC’s Associate Director of Community Outreach and Engagement (COE) program, the SCC Associate Director for Diversity, Equity, and Inclusion, multiple members of the SCC COE leadership team. Thus, we are uniquely positioned to mobilize and identify outreach opportunities and/or programs that address any gaps we discover. Moreover, this focus on our catchment area and the motivation for this survey aligns with the National Cancer Institute’s priorities of population health assessments to characterize cancer-relevant knowledge, attitudes, beliefs, and behaviors across cancer center catchment areas. While this is a crosssectional study, this snapshot of care disruption will be helpful in planning local outreach strategies. Lastly, our catchment area is challenged with multiple cancer disparities patterned by social identities. Therefore, our analysis was guided by the theory that social identities related to race, ethnicity, class, and gender shape access to healthcare and disease processes and are the fundamental drivers of health. Thus, we included variables that impact health and are patterned by these social factors.

Reviewer #2 (Public Review):

Dr. Kia Davis and colleagues present a thoughtful analysis of disruptions to cancer care during COVID-19 in the article, "Understanding disruptions in cancer care to reduce increased cancer burden: a cross-sectional study." The article is based on an online survey of 680 residents in the Siteman Cancer Center catchment area in Summer 2020. The authors aim to characterize demographic differences in cancer care disruptions. Information about the causes and distribution of care disruption can help reduce the impacts of COVID-19 and guide the recovery of programs and services. The article provides a clear and detailed assessment of factors associated with care disruption and return to care during the first six months of the pandemic.

A strength of the study is the focus on the catchment area of the cancer center during a period of dramatic change. The results would provide timely and actionable data to address emerging barriers to care and associated social or contextual factors. This information helps the Community Outreach and Engagement efforts to be responsive to community priorities despite rapidly evolving circumstances.

The analysis would benefit from greater detail in three areas. First, it would be helpful to have more information about how the outcome measures were originally developed or tested. Second, for the regression analysis, it would be helpful to show the demographic characteristics of the two strata to better understand the sample composition. Third, the authors should demonstrate that the data do not violate the assumptions for conducting logistic regression to improve confidence in the findings.

COVID-19 affected all aspects of the cancer continuum. The study reports factors associated with postponing or canceling cancer-related appointments during the pandemic. It will be of great interest to researchers and practitioners in cancer prevention and control.

We thank Reviewer 2 for their thoughtful critique of our work. Their suggestions have strengthened our manuscript. Since our article was submitted, the questionnaire where we derived our outcome measure has been published. The questions were drawn from validated measures assessing the impact of pandemics such as H1N1, and major life disruptions such as natural disasters. This language was updated in the manuscript as were the references. Moreover, we added a supplemental Table 2 to show the demographic characteristics by race strata. Finally, we tested and can confirm that the analysis does not validate the assumptions of logistic regression. We believe that our results will aid in the understanding of how COVID impacted cancer care in our catchment area so that we can better mobilize resources. While we understand this is a cross-sectional study with the potential for unmeasured confounding, we believe this snapshot of cancer care during the pandemic will also be of interest to researchers, clinicians, and other practitioners in cancer prevention and control in locations like ours.

Author Response

Reviewer #3 (Public Review):

In this manuscript, Castano et al generate and test a small molecule inhibitor of CDKL5, an Xlinked kinase whose loss-of-function is the cause of a severe neurodevelopmental disorder. Since the current knowledge of CDKL5 functions mainly rely on genetic models it is still unclear which effects are caused directly by CDKL5 loss and which can be ascribed to indirect effects. A specific inhibitor would therefore be an important tool for the field.

Castano and colleagues therefore tested a panel of twenty kinase inhibitors for their capacity to block phosphorylation of a EB2, a bona fide CDKL5 substrate, in rat neurons. Among the three that could inhibit EB2 phosphorylation at low concentrations, one was found to inhibit CDKL5 while not affecting GSK3 kinases, which share significant homology to CDKL5. Considering that genetic studies have previously linked CDKL5 to excitatory synaptic transmission, acute hippocampal slices were exploited to test the consequences of CDKL5 inhibition. While CDKL5 loss in the past was found to affect both AMPA- and NMDA-Rs, the small molecule-based inhibition affected only AMPA-R responses at the post-synaptic level. Since pharmacokinetic analyses showed that the inhibitor has a low capacity for brain penetration the molecule remains limited for testing the acute inhibition of CDKL5 in vitro and ex vivo. Such a tool represents an important aspect in the CDKL5 field and the findings suggesting a direct role of CDKL5 in regulating AMPA-R functions are interesting. However, the manuscript could be improved to render it more readable.

Thank you for this positive feedback and we hope that our adjustments improve the readability.

The description of the binding and orthogonal assays, which are the basis for the selection of the small molecule inhibitor, is not straightforward to understand for non-expert readers and could be improved.

We have added additional text to the Methods and Results to better explain the assays.

While the in vitro and ex vivo assays are well presented, it is not clear why the myelin basic protein is used as a substrate for CDKL5 in the in vitro kinase assays. Does this protein contain a CDKL5 consensus site?

To execute the in vitro kinase assays, myelin basic protein (Active Motif, 31314) was employed as a substrate for recombinant CDKL5. Myelin basic protein is used as a substrate for multiple kinases, both serine/threonine and tyrosine kinases, to enable in vitro kinase assays due to the presence of multiple sites for phosphorylation. As such, we and others have used this protein as a kinase substrate for evaluating kinase activity[2, 4]. MBP does not contain a CDKL5 consensus site of RPXS/T*, and as such could be considered a less than ideal substrate to study CDKL5 activity, however for in vitro kinase assays MBP is still suitable as it can be phosphorylated by CDKL5. In addition, CDKL5 is known to phosphorylate substrates that do not contain a consensus motif[3].

Author Response

Reviewer #1 (Public Review):

This study demonstrates that a hybrid measurement method increases 3 fold the resolution of mouse USV localization. This increased resolution enables to revise previous occurrence frequency measures for female vocalizations and establishes the existence of vocal dominance in triadic interactions. The method is well described and its efficiency is carefully quantified. A limitation of the study is the absence of ground truth data, which may have been generated eventually with miniaturized loudspeakers in mouse puppets. However, a careful error estimation partially compensates for the absence of these likely challenging calibrations. In addition, the conclusions take into account this uncertainty. The gain in accuracy with respect to previous methods is clear and the impact of localisation accuracy on biological conclusions about vocalisation behavior is clearly exemplified. This study demonstrates the impact of the new method for understanding vocal interactions in the mouse model, which should be of tremendous interest for the growing community studying social interactions in mice.

We have performed the requested, additional ground estimate using a movable miniature speaker, for more details see point 2 of Reviewer 2, and the new supplementary figure.

Reviewer #2 (Public Review):

Past systems for identifying and tracking rodent vocalizations have relied on triangulating positions using only a few high-quality ultrasonic microphones. There are also large arrays of less sensitive microphones, called acoustic cameras that don't capture the detail of the sounds, but do more accurately locate the sound in 3D space. Therefore the key innovation here is that the authors combine these two technologies by primarily using the acoustic camera to accurately find the emitter of each vocalization, and matching it to the highresolution audio and video recordings. They show that this strategy (HyVL) is more accurate than other methods for identifying vocalizing mice and also has greater spatial precision. They go on to use this setup to make some novel and interesting observations. The technology and the study are timely, important, and have the potential to be very useful. As machine learning approaches to behavior become more widespread in use, it is easy to imagine this being incorporated and lowering entry costs for more investigators to begin looking at rodent vocalizations. I have a few comments.

1) What is the relationship of the current manuscript to this: https://www.biorxiv.org/content/10.1101/2021.10.22.464496v1 which has a number of very similar figures and presents a SLIM-only method that reportedly has lower precision than the current HyVL approach. Is this superseded by the submitted paper?

The referred manuscript (now published in Scientific Reports) is indeed related to the current work: The currently presented system is based on the integration between SLIM (based on 4 high quality microphones) and Beamforming (based on the 64-channel microphone array). The accuracy of SLIM is generally lower than that of HyVL, but it makes essential contributions to the overall accuracy of HyVL through the integration of the complementary strengths of the two methods/microphone arrays (see Fig. 3A, L-shape of errors). To our knowledge, SLIM was the previously most accurate technique (based on 4 microphones, see comparison in the Discussion), but HyVL exceeds this by a substantial margin. Some figures appear similar mostly due to related code in the underlying analysis pipeline and visualization scripts (e.g. the half-disc densities). However, the set of dyadic and triadic recordings was collected specifically for the present study, and all top-level analyses were performed separately. The single mouse (C57Bl/6 WT) ground truth dataset is shared between the two studies, where in the SLIM paper only the USM4/SLIM part was evaluated (leading to a correspondingly lower, single animal accuracy).

We felt that the level of detail above would probably impede the reading of the manuscript, and we have therefore added a subset of the above clarifications to the methods and the first time the other study is mentioned.

2) Can the authors provide any data showing the accuracy of their system in localizing sounds emitted from speakers as a function of position and amplitude? I am imagining that it would be relatively easy to place multiple speakers around the arena as ground truth emitting devices to quantify the capabilities of the system.

Ground truth data is critical for any meaningful comparison. First, we would like to highlight that we already provided ground truth data in the previous version of the manuscript: In Fig. 3C. we analyzed vocalization data from trials with (1) just a single mouse as well as (2) vocalization at times when all mice were far apart in relation to the accuracy of HyVL (>100 mm, i.e. >25x the accuracy of HyVL) where the chances of erroneous assignment are negligible. We think that these tests are the most relevant, as they are conducted with the relevant sounds, at their actual intensity, spectral profile and emitter acoustics.

In addition, we have now conducted a series of tests with sounds produced by a miniature speaker placed in 25 different locations to demonstrate the lower-bound of accuracy achievable with the system. The tests indicate an accuracy of MAE < 1mm under these ideal conditions, i.e. without the absorption of the mouse bodies, varying direction of emission of the mouse snout, varying intensity, varying spectral content, duration, etc. Exploring the dependence on all these parameters is in itself interesting, but requires a detailed study in itself. The detailed experimental conditions and results are now provided in Supplementary Fig. 4, including a quantification of the dependence on amplitude.

3) How is the system's performance affected by overlapping vocalizations? It might be useful to compare the accuracy of caller identification for periods where only one animal is calling at a time vs. periods where multiple animals are simultaneously calling.

This is an excellent question. Our current code for detecting vocalizations cannot automatically determine if one or multiple vocalizations are concurrently present. We have therefore manually checked all vocalizations for overlapping instances, including those in triadic recordings with two males, where this would be expected to occur most frequently.

We considered vocalizations to be overlapping if the overlapping constituent timefrequency traces did not form a harmonic stack. Overall, overlaps were surprisingly rare. We did find a couple of cases (<0.1%) where our detection algorithm produced a longer vocalization interval that contained multiple, differently shaped vocalization traces that, when re-analyzed in shortened time-frequency bins with beamforming, belonged to two different males. Note here that beamforming is separately performed from the onset to the end of each vocalization, so the cumulative heatmap can change depending on these onset and end times, which are normally determined by our detection algorithm.

However, although the identity of the assigned vocalizer could shift in these very rare cases depending on which time bin was re-analyzed, the system’s localization performance remained in principle unaffected: as mentioned above, shorter time bins on non-overlapping parts correctly show the origin of the vocalizations in this case, and therefore a solution to this issue could be a USV detection algorithm that is able to detect the overlap based on the spectral shapes and parses them apart. During the beamforming each vocalization can then be separately localized, by restricting the beamforming to the corresponding time and frequency range. Further, the analysis could be refined so that multiple salient peaks can be detected in the soundfield estimate. This would, however, substantially change the analysis approach, i.e. rather than a single estimate per USV, a sequence of soundfield estimates should be computed and later fused again. Since such a procedure uses less data per single estimate, it also increases the possibility of false positives, which in the current situation with very few overlaps in time, would likely reduce the overall accuracy of the system, we decided to not modify the algorithm in this direction, but we agree that ideally a joint approach - combining separation on the spectrogram and soundfield level - should be pursued. For the present data, if a time window was analyzed such that the intensity map of the sound field contains multiple hotspots of an approximately equal magnitude, the USV would likely remain unassigned, because the within soundfield uncertainty would be higher than for a single peak, and this would reduce the MPI. However, given the rarity of these cases in our dataset, we do not think that their exclusion would change the results appreciably. This information was added as a paragraph to the Discussion.

It is worth noting that HyVL is very robust: There were a number of cases (<5%) where environmental dampening in combination with harmonic stacking produced interesting timefrequency traces in some of the USM4 microphones, but our system did not have any issue spatially localizing this - what seems like a - smeared vocalization trace. We provide a few examples of this kind in a short video (see Rebuttal Video 2 and the legend at the bottom of this document), where the overlap is also reflected in the intensity map of the sound field, overlaid onto the platform.

4) Can the authors comment on how sound shadows cast by animals standing between the caller and a USM4 affect either the accuracy of identification or the fidelity of the vocal recording?

An important point to raise. Sound scattering and dampening caused by the conspecifics of the vocalizing animal can impede the accuracy of any sound localization system, but can unfortunately not be avoided in a social setting. To address this issue, we raised all USM4 microphones by ~12 cm above the interaction platform to minimize the instances of sound blocked by the mice. Further, the Cam64 device should largely be unaffected by sound shadows as it is centrally located above the platform. We have added a modified version of the above comment to the discussion under the heading "Current limitations and future improvements of the presented system".

5) I'm a bit confused about how the algorithm uses the information from the video camera. Reading through the methods, it seems like they primarily calculate competing location estimates by the two types of microphone data and then make sure that a mouse is in close proximity to one location, discarding the call if there isn't. Why did the authors choose this procedure rather than use the tracked position of the snouts as constrained candidate locations and use the microphone data to arbitrate between them? Do they think that their tracking data are not reliable or accurate enough?

Thanks for this important suggestion, which we have actually grappled with a lot during the analysis. First of all, the visual tracking data, in particular the manual data, is in our opinion (based on human visual identification) near perfect (within the limits of the video resolution, pixel resolution = 0.8 mm), i.e. on the order of 1-2 mm, and is therefore not the source of any unattributable vocalizations. If we understand the reviewer correctly, then we indeed perform the attribution as he indicates based on the tracked snouts of all mice, specifically by measuring the MPI's of both acoustic location estimates for all mice and then choosing the most reliable one. Specifically, the attributions can be grouped into 3 cases: (i) Estimated origin close to one snout, and snouts rather far apart, (ii) Estimated origin close to one snout and snouts close, and (iii) estimated origin not close to either snout. (i) is easy to address, (ii) is appropriately handled by the mouse probability index, but (iii) is tricky. Since the vocalization has to come from one of the mice, this already indicates that the localization is not working well in this case. Therefore we found it prudent (similar to Neunuebel et al. 2015) to not assign in these cases. Interestingly the MPI is not useful in these cases, as due to the exponential dependence of the normal density on distance, for example a case with a distance of 50 mm to one snout and 60 mm to another snout could lead to an MPI close to 1, which is likely not trustable. We have described this in the Methods as follows:

"This distance threshold mainly serves to compensate for a deficiency of the 𝑀𝑃𝐼: if all mice are far from the estimate, all 𝑃𝑘 are extremely small, however, the 𝑀𝑃𝐼𝑘 will often exceed 0.95."<br /> Due to the inherent limit for localizing very quiet, short USVs by any system, we think this kind of selection (introduced originally by Neunuebel et al 2015) is a valuable and necessary step in the processing to avoid confusions (which are of course already substantially reduced through HyVL here).

6) I guess the authors have code that we can run, but I couldn't access it. The manuscript describes the algorithms and equations that are used to calculate the location, but this doesn't really give me a feel for how it works. If you want to have the broadest impact possible, I think you would do well to make the code user-friendly (maybe it is, I don't know). In pursuit of that goal, I would suggest that the authors devote some of the paper to a guided example of how to use it.

While the code was made available to the reviewers via the link at the beginning of the manuscript (p2, before abstract), we completely agree that this method of distribution is not very accessible. We have therefore created a publicly available GitHub repository (https://github.com/benglitz/HyVL) which hosts the code and details its use on the basis of a sample data set (which is available to the reviewers in the repository link, and later to the public under https://doi.org/10.34973/7kgc-ta72). While we do provide a sample video and analysis workflow there, our data analysis pipeline is quite integrated and other labs will likely use different pipelines. We have therefore tried to make the core functions independent of our pipeline and thus easy to integrate by others into their analysis pipelines.

Reviewer #3 (Public Review):

The present manuscript describes a new method to identify the emitter of ultrasonic vocalisations during social interactions between 2 or 3 mice. The method combines two technologies (an "acoustic camera" and a set of four microphones) and succeeds in increasing the spatial precision and the attribution of USV emission to one of the mice. The manuscript describes the characteristics and advantages of each method and the advantages of using both to optimize the identification of USV emitter. The authors used the method to confirm that females are also vocalising during male-female interactions and that females emit USV mostly during nose-nose contact while this was not the case for males. Interestingly, the authors identified that the vocal behaviour of two competing males was strongly asymmetric when facing a female. This was not the case for two females facing one male.

The method is really promising since the identification of the emitter of USVs during mouse social interactions is a necessary step to speed up our understanding of this communication modality. The increase in spatial precision and in the proportion of attributed vocalisations is non-negligible and will be of great utility in the future.

We would like to thank the reviewer for this positive perspective on the future utility of our system.

Generally, the statistical analyses should be adjusted. Indeed, the statistical analyses do not consider the fact that the same individuals were recorded several times (if we understood well the methods). Each point was considered independent (in non-parametric Wilcoxon tests), while this is not the case given the repetitions with the same individuals (the number of repeated encounters per individual should be given in the methods section, by the way). We strongly recommend revising the statistical analyses of the results in Figures 4 and 5. In addition, it could be interesting to check whether the vocal behaviour is stable within each individual (i.e., a male that is vocalising frequently in one situation vocalises always frequently in other situations).

We generally agree with this suggestion: In order to properly conduct the analysis for individuals as you suggest, a balanced dataset should be used. We had initially collected such a balanced dataset, which was previously not detailed in the manuscript, as the focus was on USV localization/attribution and hence only the recordings containing USVs were analyzed (detailed now in the beginning of Results and Methods). However, overall, the probability of a recording containing vocalizations at all is low: in our balanced set only 23/112 recordings contained vocalizations. We therefore had collected additional recordings with the best vocalizers which created the previously analyzed set of 83 recordings containing USVs recorded with all microphones. This dataset is therefore dominated by recordings from mice that are active vocalizers. While this does not raise any issue for the estimation of the accuracy of the method (Figure 3) or the female vocalizations (Figure 4, because recordings were always randomized across female mice), it precludes an encompassing analysis of individual differences in Figure 5, i.e. the dyadic-triadic comparison. In the new Figure 5, we address the reviewer's question for the dyadic recordings, finding that the current set of recordings does not provide sufficient evidence that individual male mice had significantly different vocalization rates. We would, however, like to point out that this is likely a consequence of the n=4 recordings that are compared here. For the female mice, we also did not find differences in vocalization rates, which is based on n=14 recordings and thus a more reliable result (p=0.16, 1-way ANOVA with factor individual).

For the triadic recordings, however, due to a limitation in the experiment execution, we unfortunately do not have the complete information available on an experiment level for the triadic recordings, i.e. the video stream was accidentally started after all mice were placed in the platform, and since the same sex animals are visually not separable (while the female mice are separable from the males, based on a slightly shaved region on their head), we cannot completely assess this question in triadic recordings based on the available data. When including the triadic recordings in addition and assuming a single vocalizer (combining all male USVs, see below for why the males could not be assigned in the triadic condition) the male individual comparison can be approximately performed with n=8 recordings, and then the dependence on individual becomes borderline significant (p=0.028, 2-way ANOVA with factors individual and condition).

For the comparison of vocalization rates in the previous Figure 5 that the reviewer was referring to, we cannot perform a rigorous analysis on the individual level, due to the lack of balance. While we thus agree that differences between individual mice can contribute to the differences observed, we do not think that this would change the conclusion that one of the mice dominates the vocal emissions. If the reviewers agree, we would thus leave Figures 6 (old Fig. 5) and new Figure 7 (behavioral confirmation of dominant/subordinate division) as part of the manuscript, with a clear cautioning about the possible contribution of individual differences to the observed differences. If the reviewers find it inappropriate to leave the results based on the unbalanced dataset in, all results after figure 5 could also be excluded (although we would find this unfortunate, given the additional time and effort we have invested in these).

It is not easy to understand the rationale behind testing animals in pairs and in triads from the beginning of the manuscript. The authors should better introduce this aspect in the manuscript, especially given the fact that biological results deal with this aspect in Figure 5. The authors might strengthen the parts of the biological results extracted from their new method.

Thank you for pointing out the need for clarification regarding the rationale behind testing animals in pairs and in triads. It is because courtship interactions are particularly vocal and social, that they are of interest to many fields, e.g. neurodevelopmental disorders.3,4 Due to the natural competitiveness between mice during courtship interactions, high accuracy is particularly beneficial in this regard because it allows disentangling USVs at close distances. We adapted the introduction to better reflect this reasoning and included an extra paragraph in the introduction and also where the biological results from old Fig. 5 / new Fig. 6 are summarized.

More specifically, the fact that one male takes over the vocal behaviour within a triad is of high interest. Nevertheless, some behavioural data would be needed to strengthen these findings.

We agree that this is an interesting finding and also agree that some additional behavioral analysis is useful to complement it. In order to arrive at this analysis, we performed all-frame, 3-animal tracking on the 14 triadic recordings with two males. This required switching to skeleton tracking with SLEAP5 in addition to manual post-processing to ensure that no identity switches occur. In each recording the dominant male was then defined as the one that emitted more vocalizations, and then the vocalization-independent spatial interaction histogram was computed, similar to the ones in Fig.4, but now separating between the dominant and the subordinate males (see new Figure 7). The results are consistent with the most typical location of vocalization of the male, in proximity to the female abdomen: The dominant male's spatial interaction histogram (Fig. 7A) was more clearly peaked in the location of the female abdomen very close to the male's snout, in comparison with the subordinate male's histogram (Fig. 7B), which shows up very clearly in the difference between the normalized histograms (Fig. 7C). Significance analysis was performed using 100x bootstrapping on the relative spatial positions to estimate p=0.99 confidence bounds around the histograms of the dominant and subordinate respectively. Significance at a level of p<0.01 highlights multiple relative spatial positions (Fig. 7D), including the one proximal to the snout which has the largest absolute difference (Fig. 7C). Note, that these analyses were conducted on the basis of the non-balanced dataset which contained enough vocalizations to assess the dominant male based on the vocalization rates and thus individual traits of certain animals remain as a possible confound.

A small proportion of USVs was not assigned. The authors did not discuss the potential reason for this failure (Were the USVs too soft? Did they include specific acoustic characteristics that render them difficult to localise?). These points could be of interest when testing other mouse strains or other species.

Good point, we agree that it is interesting to know the reasons for failure. As so often, there is not a single property that makes localization hard, but multiple factors contribute. In the SLIM paper, we already identified duration and intensity as important contributors (Fig. 3E/F), and in the speaker test (see new Supplementary Fig. 4) we again demonstrated the influence of intensity. In addition, frequency bandwidth and acoustic occlusion are two other main contributors that each influence the availability of the information/signal-to-noise ratio at the microphones:

• Frequency bandwidth: In signals that are very narrowband, there are more opportunities for phase ambiguity, in particular for very high-frequency signals. These are avoided/reduced for more wideband signals.

• Acoustic occlusion: As ultrasonic sounds can be quite directional, if an animal is vocalizing away from a microphone, which in addition would put its body in the way of the sounds to the microphone, then this can reduce the intensity at the microphone to a level where the information is insufficient to utilize information from this microphone. This mostly influences the 4 microphones surrounding the platform, while the Cam64 overhead will likely not be affected by acoustic occlusion in the plain.

We have added a brief version of this explanation to the discussion under the heading: "Current limitations and future improvements of the presented system"

Author Response

Reviewer #1 (Public Review):

In this manuscript, Marmor and colleagues reanalyze a previously published dataset of chronic widefield Ca2+ imaging from the dorsal cortex of mice as they learn a go/no-go somatosensory discrimination task. Comparing hit trials that have a distinct history (i.e. are preceded by distinct trial types), the authors find that hit trials preceded by correct rejections of the nontarget stimulus are associated with larger subsequent neural responses than trials precede by other hits, across the cortex. The authors analyze the time course over which this effect emerges in the barrel cortex (BC) and the rostrolateral visual area (RL), and find that its magnitude increases as the animals become expert task performers. Although the findings are potentially interesting, I, unfortunately, believe that there are important methodological concerns that could put them into question. I also disagree with the rationale that singles out BC and RL as being especially important for the emergence of trial history effects on neural responses during decision-making. I detail these points below .

1) The authors did not perform correction for hemodynamic contamination of GCaMP fluorescence. In widefield imaging, blood vessels divisively decrease neural signals because they absorb green-wavelength photons, which could lead to crucial confounds in the interpretation of the main results because of neurovascular coupling, which lags neural activity by seconds. For example, if a reward response from the previous trial is associated with a lagged hemodynamic contamination that artificially decreases the signal in the following trial, one could get artificially higher activity in trials that were not preceded by a reward (i.e. CR), which is what the authors observed. Ideally, the experiments would be repeated with proper hemodynamic correction, but at the very least the authors should try to address this with control analyses.

Done. We basically redone the experiment with proper hemodynamic correction and maintained trial history results. Please see point 1 above for more details (Figures S4 and S5). In addition to hemodynamic controls, we also present novel two-photon single cell data with similar results in Figure S6. We also added a dedicated section for this in the Methods section (pg. 12).

For example, what is the time course of reward-related responses in BC and elsewhere?

In general, and specifically in BC, reward related responses return to baseline up to 5 seconds after the start of the reward period and at least 5 seconds before the stimulus presentation of the next trial. In the novel experiments we even extended the baseline period by an additional 2 seconds just in case. Trial history information was still present with an extended inter-trial interval.

The text now reads (pg. 4): "We further report that responses during the reward period in cortex and specifically in BC went back to baseline 4-5 seconds after the start of the reward period and 6-8 seconds before the presentation of the next stimulus (total inter-trial interval ranged between 10-12 seconds)."

Do hemodynamics artifacts have a trial-by-trial correlation with the subsequent trial history effect?

We have now done the proper hemodynamic control (Figure 2) and we did not find a strong effect of hemodynamic responses on trial history information.

What is the learning time course of reward responses?

Responses during the reward period as a function of learning were not significantly modulated. We further show the whole learning profile for BC response during the reward period in Author response image 1.

Author response image 1.

Response in BC averaged during the reward period (2-4 sec after texture stop) as a function of learning for each mouse separately.

The text now reads (pg. 4): "In addition, responses in BC during the reward period were not consistently modulated as a function of learning (p>0.05; Wilcoxon signed-rank test between naïve and expert, BC response averaged during the reward period, 2-4 seconds after stimulus onset; n=7 mice). Taken together, we find that direct responses from the reward period do not effect history-related responses during the next trial."

Note that I don't believe the FA-Hit condition analysis that the authors have already presented provides adequate control, as punishment responses are also pervasive in the cortex and therefore suffer from the same interpretational caveat. Unfortunately, I believe this is a serious methodological issue given the above. However, I will proceed to take the reported results at face value .

We hope that our additional control analysis regarding the hemodynamic controls are satisfactory.

2) The statistics used to assess the effect of trial history over learning are inadequate (e.g., Fig 2b). The existence of a significant effect in one condition (e.g., CR-Hit vs. Hit-Hit in expert) but not in another (e.g., same comparison in naive) does not imply that these two conditions are different. This needs to be tested directly. Moreover, the present analysis does not account for the fact that measures across learning stages are taken from the same animals. Thus, the appropriate analysis for these cases would be to first use a two-way ANOVA with repeated measures with factors of trial history and learning stage (or equivalent non-parametric test) and then derive conclusions based on post hoc pairwise tests, corrected for multiple comparisons .

Done. We performed 2 way ANOVA as suggested and found significant history and learning effects along with a significant interaction effect for BC.

The text now reads (pg. 4): "This difference was significant during the stim period in learning and expert phases across mice (Fig. 2b; 2-way ANOVA with repeated measures; DF (1-6) F=51 p<0.001, DF (2-12) F=18 p<0.001, DF(2-12) F=5 p<0.05 for trial history, learning and the interaction between trial history and learning; Post hoc Tukey analysis p<0.05 for trial history in learning and expert phases; p>0.05 in the naïve phase)."

3) I am not convinced that BC and RL are especially important for trial-history-dependent effects. Figures 4 and 5 suggest that this modulation is present across the cortex, and in fact, the difference between CR-Hit and Hit-Hit in some learning stages appears stronger in other areas. BC and RL do have the highest absolute activity during the epochs in Figs 4 and 5, but I would argue that this is likely due to other aspects of the task (e.g., touch) and therefore is not necessarily relevant to the issue of trial history .

Done. First, we would like to point out that RL during the pre period displays the largest difference between the CR-Hit and Hit-Hit conditions (Fig. 5c bottom). Second, we now show difference maps (i.e., activity in CR-Hit minus Hit-Hit) which clearly show a positive activity patch in BC during the stim period for 5 out of the 7 mice (Fig. S10a). Example maps also highlight RL during the pre period (Fig. S10b). We note that activity patches somewhat spread over to other areas and also slightly vary across mice. This is why the grand average may slightly average out trial history information. Taken together, we strongly feel that during the pre period, trial history information emerges in RL (and adjacent posterior association areas) which shift towards BC during the stim period

Nevertheless, we agree with the reviewer that other areas (that do not necessarily display high activity) may encode trial history information and we now clearly report this in the text (pg. 5): "We note that other areas, e.g., different association areas, also encoded historydependent information especially during learning and expert phases. In addition, we present activity difference maps between CR-Hit and Hit-Hit conditions during the stim period (Fig. S10a). These maps clearly show the highest trial history information (i.e., difference in activity) in BC. Taken together, these results indicate that BC encodes history-dependent information that emerges during the stim period and just after learning. "

And also in (pg. 6): " In addition, we present activity difference maps between CR-Hit and HitHit conditions during the pre period (Fig. S10b). These maps localize trial history information to RL which also spreads to other adjacent association areas. Moreover, activity patches slightly vary across the different mice which may affect the grand average (averaged across mice) of each area."

4) Because of similar arguments to the above, and because this was not directly assessed, I do not believe the conclusion that history information emerges in RL and is transferred to BC is warranted. For instance, there is no direct comparison between areas, but inspection of the ROC plots in Fig 6b suggests that history information emerges concomitantly across cortical areas. I suggest directly comparing the time course between these and other areas

Done. We now add example history AUC maps and quantify history AUC for all 25 areas during the pre and stim periods. During the pre period (Fig. 6), AUC values are concentrated around the RL (and other PPC areas), whereas during the stim periods AUC values shift to BC. Again, due to the inter-mouse variability, these differences are slightly averaged out which also makes it tough to have strong statistical test (with only 7 mice).

The text now reads (pg. 7): "We next calculated the history AUC for each pixel during either the pre or stim period. The history AUC maps during the pre period display AUC values around the RL areas (Fig. 6f). In contrast, the history AUC maps during the stim period display AUC values mostly in BC (Fig. 6g). Quantified across 25 areas and averaged across mice, RL displays the highest history AUC during the pre period, whereas BC displays the highest history AUC values during the stim period (Fig. 6h). We note that other cortical areas such as other association areas also display high history AUC values. Taken together, we find that trial history emerges in RL before the texture arrives and then shifts to BC during stimulus presentation. "

5) How much is task performance itself modulated by trial history? How does this change over the course of learning? These behavioral analyses would greatly help interpret the neural findings and how this trial history might be used behaviorally .

Done, we have now calculated the dprime for Hit-Hit and CR-Hit trials separately. We find no significant differences between conditions both within and across mice (see Fig. S2 below).

The text now reads pg. 3): "We note that learning curves that are calculated separately for each pair (i.e., either a preceding Hit or CR trial) were not significantly different (Fig. S2)."

Reviewer #2 (Public Review):

Marmor et al. mine a previously published dataset to examine whether recent reward/stimulus history influences responses in sensory (and other) cortices. Bulk L2/3 calcium activity is imaged across all of the dorsal cortex in transgenic mice trained to discriminate between two textures in a go/no-go behavior. The authors primarily focus on comparing responses to a specific stimulus given that the preceding trial was or was not rewarded. There are clear differences in activity during stimulus presentation in the barrel cortex along with other areas, as well as differences even before the second stimulus is presented. These differences only emerge after task learning. The data are of high quality and the paper is clear and easy to follow. My only major criticism is that I am not completely convinced that the observed difference in response is not due to differences in movement by the animal on the two trial types. That said, the demonstration of differences in sensory cortices is relatively novel, as most of the existing literature on trial history effect demonstrates such differences only in higher-order areas .

Major :

1a) The claim that body movements do not account for the results is in my view the greatest weakness of the paper - if the difference in response simply reflects a difference in movement, perhaps due to "excitement" in anticipation of reward after not receiving one on CR-H vs. HH trials, then this should show up in movement analysis. The authors do a little bit of this, but to me, more is needed .  

Done. We have now extensively and carefully analyzed body and whisker movements for CRHit and Hit-Hit conditions. First, In the figure below we decomposed body movements into 22 different body parts using DeepLabCut. In short, we find no significant difference between CRHit and Hit-Hit conditions in each body part separately (Fig. S7 below). This was true for the naïve, learning and expert phases. Please see additional analyses in the points below.

This is now reported in the text (pg. 4): “In addition, we performed a more detailed body and whisker analysis, e.g., decomposing the movement to different body parts and obtaining single whisker dynamics. These analyses did not find significant differences in movement parameters between CR-Hit and Hit-Hit conditions (Fig. s7 and s8).”

First, given the small sample size and use of non-parametric tests, you will only get p<.05 if at least 6 of the 7 mice perform in the same way. So getting p>.05 is not surprising even if there is an underlying effect. This makes it especially important to do analyses that are likely to reveal any differences; using whisker angle and overall body movement, which is poorly explained, is in my opinion insufficient. An alternative approach would be to compare movements within animals; small as the dataset is, it is feasible to do an animal-by-animal analysis, and then one could leverage the large trial count to get much greater statistical power, foregoing summary analyses that pool over only n=7 .

We agree with this point and are have now dramatically improved our statistical analysis.

1) We now perform within mouse statistics for responses in BC during naïve, learning and expert (see Fig. S4 below). In short, we find statistical significance for 7 out of 7 mice during the expert phase, 6 out of 7 mice in the learning phase and 0 out of 7 in the naive phase. For RL during the pre period we find significant difference in 5 out of 7 expert mice.

This is now reported in the text (pg. 4): "In addition, a statistical comparison between CR-Hit and Hit-Hit responses within each mouse separately maintained significance for expert (7/7 mice Mann-Whitney U-test p<0.05) and learning (6/7 mice) but not for naïve (0/7 mice. Fig. S3)."

And also in (pg. 5): "In addition, a statistical comparison between CR-Hit and Hit-Hit responses in RL within each mouse separately maintained significance for expert (5/7 mice; MannWhitney U-test p<0.05)."

2) We would like to point out that we have now added 3 additional mice (with hemodynamics control) and performed within mouse statistics in BC and RL (Fig. S5), adding to our initial observations.

3) In terms of body movements, we now performed within mice statistics and compared body movements between CR-Hit and Hit-Hit conditions. In general, most mice did not show a significant difference in body movements or whisker envelope.

This is now reported in the text (pg. 4): "A within mouse statistical comparison between body or whisker parameters in CR-Hit and Hit-Hit maintained a non-significant difference in expert (1/7 mice displayed a significant difference; Mann-Whitney U-test p>0.05), learning (2/7 mice) and naïve (0/7 mice)."

And also in (pg. 4): "Body movements and whisker parameters did not significantly differ between CR-Hit and Hit-Hit conditions during the pre-period (Similar to the stim period. Across and within mice. P>0.05; Mann-Whitney U-test)."

In summary, we have now substantially improved our statistical analysis and further decomposed the body movements, maintaining the trial history results.

The authors only consider a simple parametrization of movement (correlation across successive frames), and given the high variability in movement across animals, it is likely that different mice adopt different movements during the task, perhaps altering movement in specific ways. Aggregating movement across different body parts after an analysis where body parts are treated separately seems like an odd choice - perhaps it is fine, but again, supporting evidence for this is needed. As it stands, it is not clear if real differences were averaged out by combining all body parts, or what averaging actually entails .

Please see the above point where we decomposed body movements (Fig. S7 and Methods section in Pg. 14).

If at all possible, I would recommend examining curvature and not just the whisker angle, since the angle being the same is not too surprising given that the stimulus is in the same place. If the animal is pressing more vigorously on CR-H trials, this should result in larger curvature changes .

Done. We now decompose whisker dynamics (i.e., curvature) using DeepLabCut (Fig. S8 see below). In general, we find no significant differences in whisker parameters between Hit-Hit and CR-Hit conditions.

This is now reported in the text (pg. 4): "In addition, we performed a more detailed body and whisker analysis, e.g., decomposing the movement to different body parts. This analysis did not find significant differences between CR-Hit and Hit-Hit conditions (Fig. S7 and S8)."

Finally, the authors presumably have access to lick data. Are reaction times shorter on CR-H trials? Is lick count or lick frequency shorter?

Done. We now calculated lick reaction time and lick rate and find a significant difference for the lick reaction time but not in lick rate. We show a figure below for the reviewer and report this in the text

The text now reads (pg. 3): "In addition, the lick reaction time (but not the lick rate) between Hit-Hit and CR-Hit were significantly different (p<0.05; Wilcoxon signed-rank test) ,maybe indicating a more considered response after a previous stop signal."

If movement differs across trial types, it is entirely plausible that at least barrel cortex activity differences reflect differences in sensory input due to differences in whisker position/posture/etc. This would mitigate the novelty of the present results .

As detailed above, have now meticulously analyzed the whisker parameter differences between both conditions and did not find any significant differences.

1b) Given the importance of this control to the story, both whisker and body movement tracking frames should be explicitly shown either in the primary paper or as a supplement. Moreover, in the methods, please elaborate on how both whisker and body tracking were performed .

Done. Please see Figs. S7 and S8 for tracking frames. This is now detailed in the above points and also the revised relevant methods section

2) .Did streak length impact the response? For instance, in Fig. 1f "Learning", there is a 6-trial "no-go" streak; if the data are there, it would be useful to plot CR-H responses as a function of preceding unrewarded trials.

Done. We have now calculated response in CR-Hit as a function of the number of preceding CRs. In general, we obtain inconsistent results across mice that may be due to the small number of trials that have more than one preceding CR. Nevertheless, some mice have a trend, sometimes significant, in which CR-Hit responses are higher for longer CR preceding streaks. This is especially true during the learning phase. We have decided not to include this in the manuscript and present this figure only to the reviewer.

Author Response

Reviewer #1 (Public Review):

The central claim that the R400Q mutation causes cardiomyopathy in humans require(s) additional support.

We regret that the reviewer interpreted our conclusions as described. Because of the extreme rarity of the MFN2 R400Q mutation our clinical data are unavoidably limited and therefore insufficient to support a conclusion that it causes cardiomyopathy “in humans”. Importantly, this is a claim that we did not make and do not believe to be the case. Our data establish that the MFN2 R400Q mutation is sufficient to cause lethal cardiomyopathy in some mice (Q/Q400a; Figure 4) and predisposes to doxorubicin-induced cardiomyopathy in the survivors (Q/Q400n; new data, Figure 7). Based on the clinical association we propose that R400Q may act as a genetic risk modifier in human cardiomyopathy.

To avoid further confusion we modified the manuscript title to “A human mitofusin 2 mutation can cause mitophagic cardiomyopathy” and provide a more detailed discussion of the implications and limitations of our study on page 11).

First, the claim of an association between the R400Q variant (identified in three individuals) and cardiomyopathy has some limitations based on the data presented. The initial association is suggested by comparing the frequency of the mutation in three small cohorts to that in a large database gnomAD, which aggregates whole exome and whole genome data from many other studies including those from specific disease populations. Having a matched control population is critical in these association studies.

We have added genotyping data from the matched non-affected control population (n=861) of the Cincinnati Heart study to our analyses (page 4). The conclusions did not change.

For instance, according to gnomAD the MFN2 Q400P variant, while not observed in those of European ancestry, has a 10-fold higher frequency in the African/African American and South Asian populations (0.0004004 and 0.0003266, respectively). If the authors data in table one is compared to the gnomAD African/African American population the p-value drops to 0.029262, which would not likely survive correction for multiple comparison (e.g., Bonferroni).

Thank you for raising the important issue of racial differences in mutant allele prevalence and its association with cardiomyopathy. Sample size for this type of sub-group analysis is limited, but we are able to provide African-derived population allele frequency comparisons for both the gnomAD population and our own non-affected control group.

As now described on page 4, and just as with the gnomAD population we did not observe MFN2 R400Q in any Caucasian individuals, either cardiomyopathy or control. Its (heterozygous only) prevalence in African American cardiomyopathy is 3/674. Thus, the R400Q minor allele frequency of 3/1,345 in AA cardiomyopathy compares to 10/24,962 in African gnomAD, reflecting a statistically significant increase in this specific population group (p=0.003308; Chi2 statistic 8.6293). Moreover, all African American non-affected controls in the case-control cohort were wild-type for MFN2 (0/452 minor alleles).

(The source and characteristics of the subjects used by the authors in Table 1 is not clear from the methods.)

The details of our study cohorts were inadvertently omitted during manuscript preparation. As now reported on pages 3 and 4, the Cincinnati Heart Study is a case-control study consisting of 1,745 cardiomyopathy (1,117 Caucasian and 628 African American) subjects and 861 non-affected controls (625 Caucasian and 236 African American) (Liggett et al Nat Med 2008; Matkovich et al JCI 2010; Cappola et al PNAS 2011). The Houston hypertrophic cardiomyopathy cohort [which has been screened by linkage analysis, candidate gene sequencing or clinical genetic testing) included 286 subjects (240 Caucasians and 46 African Americans) (Osio A et al Circ Res 2007; Li L et al Circ Res 2017).

Relatedly, evaluation in a knock-in mouse model is offered as a way of bolstering the claim for an association with cardiomyopathy. Some caution should be offered here. Certain mutations have caused a cardiomyopathy in mice when knocked in have not been observed in humans with the same mutation. A recent example is the p.S59L variant in the mitochondrial protein CHCHD10, which causes cardiomyopathy in mice but not in humans (PMID: 30874923). While phenocopy is suggestive there are differences in humans and mice, which makes the correlation imperfect.

We understand that a mouse is not a man, and as noted above we view the in vitro data in multiple cell systems and the in vivo data in knock-in mice as supportive for, not proof of, the concept that MFN2 R400Q can be a genetic cardiomyopathy risk modifier. As indicated in the following responses, we have further strengthened the case by including results from 2 additional, previously undescribed human MFN2 mutation knock-in mice.

Additionally, the argument that the Mfn2 R400Q variant causes a dominant cardiomyopathy in humans would be better supported by observing of a cardiomyopathy in the heterozygous Mfn2 R400Q mice and not just in the homozygous Mfn2 R400Q mice.

We are intrigued that in the previous comment the reviewer warns that murine phenocopies are not 100% predictive of human disease, and in the next sentence he/she requests that we show that the gene dose-phenotype response is the same in mice and humans. And, we again wish to note that we never argued that MFN2 R400Q “causes a dominant cardiomyopathy in humans.” Nevertheless, we understand the underlying concerns and in the revised manuscript we present data from new doxorubicin challenge experiments comparing cardiomyopathy development and myocardial mitophagy in WT, heterozygous, and surviving (Q/Q400n) homozygous Mfn2 R400Q KI mice (new Figure 7, panels E-G). Homozygous, but not heterozygous, R400Q mice exhibited an amplified cardiomyopathic response (greater LV dilatation, reduced LV ejection performance, exaggerated LV hypertrophy) and an impaired myocardial mitophagic response to doxorubicin. These in vivo data recapitulate new in vitro results in H9c2 rat cardiomyoblasts expressing MFN2 R400Q, which exhibited enhanced cytotoxicity (cell death and TUNEL labelling) to doxorubicin associated with reduced reactive mitophagy (Parkin aggregation and mitolysosome formation) (new Figure 7, panels A-D). Thus, under the limited conditions we have explored to date we do not observe cardiomyopathy development in heterozygous Mfn2 R400Q KI mice. However, we have expanded the association between R400Q, mitophagy and cardiomyopathy thereby providing the desired additional support for our argument that it can be a cardiomyopathy risk modifier.

Relatedly, it is not clear what the studies in the KI mouse prove over what was already known. Mfn2 function is known to be essential during the neonatal period and the authors have previously shown that the Mfn2 R400Q disrupts the ability of Mfn2 to mediate mitochondrial fusion, which is its core function. The results in the KI mouse seem consistent with those two observations, but it's not clear how they allow further conclusions to be drawn.

We strenuously disagree with the underlying proposition of this comment, which is that “mitochondrial fusion (is the) core function” of mitofusins. We also believe that our previous work, alluded to but not specified, is mischaracterized.

Our seminal study defining an essential role for Mfn2 for perinatal cardiac development (Gong et al Science 2015) reported that an engineered MFN2 mutation that was fully functional for mitochondrial fusion, but incapable of binding Parkin (MFN2 AA), caused perinatal cardiomyopathy when expressed as a transgene. By contrast, another engineered MFN2 mutant transgene that potently suppressed mitochondrial fusion, but constitutively bound Parkin (MFN2 EE) had no adverse effects on the heart.

Our initial description of MFN2 R400Q and observation that it exhibited impaired fusogenicity (Eschenbacher et al PLoS One 2012) reported results of in vitro studies and transgene overexpression in Drosophila. Importantly, a role for MFN2 in mitophagy was unknown at that time and so was not explored.

A major point both of this manuscript and our work over the last decade on mitofusin proteins has been that their biological importance extends far beyond mitochondrial fusion. As introduced/discussed throughout our manuscript, MFN2 plays important roles in mitophagy and mitochondrial motility. Because this central point seems to have been overlooked, we have gone to great lengths in the revised manuscript to unambiguously show that impaired mitochondrial fusion is not the critical functional aspect that determines disease phenotypes caused by Mfn2 mutations. To accomplish this we’ve re-structured the experiments so that R400Q is compared at every level to two other natural MFN2 mutations linked to a human disease, the peripheral neuropathy CMT2A. These comparators are MFN2 T105M in the GTPase domain and MFN2 M376A/V in the same HR1 domain as MFN2 R400Q. Each of these human MFN2 mutations is fusion-impaired, but the current studies reveal that that their spectrum of dysfunction differs in other ways as summarized in Author response table 1:

Author response table 1.

We understand that it sounds counterintuitive for a mutation in a “mitofusin” protein to evoke cardiac disease independent of its appellative function, mitochondrial fusion. But the KI mouse data clearly relate the occurrence of cardiomyopathy in R400Q mice to the unique mitophagy defect provoked in vitro and in vivo by this mutation. We hope the reviewer will agree that the KI models provide fresh scientific insight.

Additionally, the authors conclude that the effect of R400Q on the transcriptome and metabolome in a subset of animals cannot be explained by its effect on OXPHOS (based on the findings in Figure 4H). However, an alternative explanation is that the R400Q is a loss of function variant but does not act in a dominant negative fashion. According to this view, mice homozygous for R400Q (and have no wildtype copies of Mfn2) lack Mfn2 function and consequently have an OXPHOS defect giving rise to the observed transcriptomic and metabolomic changes. But in the rat heart cell line with endogenous rat Mfn2, exogenous of the MFN2 R400Q has no effect as it is loss of function and is not dominant negative.

Our results in the original submission, which are retained in Figures 1D and 1E and Figure 1 Figure Supplement 1 of the revision, exclude the possibility that R400Q is a functional null mutant for, but not a dominant suppressor of, mitochondrial fusion. We have added additional data for M376A in the revision, but the original results are retained in the main figure panels and a new supplemental figure:

Figure 1D reports results of mitochondrial elongation studies (the morphological surrogate for mitochondrial fusion) performed in Mfn1/Mfn2 double knock-out (DKO) MEFs. The baseline mitochondrial aspect ratio in DKO cells infected with control (b-gal containing) virus is ~2 (white bar), and increases to ~6 (i.e. ~normal) by forced expression of WT MFN2 (black bar). By contrast, aspect ratio in DKO MEFs expressing MFN2 mutants T105M (green bar), M376A and R400Q (red bars in main figure), R94Q and K109A (green bars in the supplemental figure) is only 3-4. For these results the reviewer’s and our interpretation agree: all of the MFN2 mutants studied are non-functional as mitochondrial fusion proteins.

Importantly, Figure 1E (left panel) reports the results of parallel mitochondrial elongation studies performed in WT MEFs, i.e. in the presence of normal endogenous Mfn1 and Mfn2. Here, baseline mitochondrial aspect ratio is already normal (~6, white bar), and increases modestly to ~8 when WT MFN2 is expressed (black bar). By comparison, aspect ratio is reduced below baseline by expression of four of the five MFN2 mutants, including MFN2 R400Q (main figure and accompanying supplemental figure; green and red bars). Only MFN2 M376A failed to suppress mitochondrial fusion promoted by endogenous Mfns 1 and 2. Thus, MFN2 R400Q dominantly suppresses mitochondrial fusion. We have stressed this point in the text on page 5, first complete paragraph.

Additionally, as the authors have shown MFN2 R400Q loses its ability to promote mitochondrial fusion, and this is the central function of MFN2, it is not clear why this can't be the explanation for the mouse phenotype rather than the mitophagy mechanism the authors propose.

Please see our response #7 above beginning “We strenuously disagree...”

Finally, it is asserted that the MFN2 R400Q variant disrupts Parkin activation, by interfering with MFN2 acting a receptor for Parkin. The support for this in cell culture however is limited. Additionally, there is no assessment of mitophagy in the hearts of the KI mouse model.

The reviewer may have overlooked the studies reported in original Figure 5, in which Parkin localization to cultured cardiomyoblast mitochondria is linked both to mitochondrial autophagy (LC3-mitochondria overlay) and to formation of mito-lysosomes (MitoQC staining). These results have been retained and expanded to include MFN2 M376A in Figure 6 B-E and Figure 6 Figure Supplement 1 of the revised manuscript. Additionally, selective impairment of Parkin recruitment to mitochondria was shown in mitofusin null MEFs in current Figure 3C and Figure 3 Figure Supplement 1, panels B and C.

The in vitro and in vivo doxorubicin studies performed for the revision further strengthen the mechanistic link between cardiomyocyte toxicity, reduced parkin recruitment and impaired mitophagy in MFN2 R400Q expressing cardiac cells: MFN2 R400Q-amplified doxorubicin-induced H9c2 cell death is associated with reduced Parkin aggregation and mitolysosome formation in vitro, and the exaggerated doxorubicin-induced cardiomyopathic response in MFN2 Q/Q400 mice was associated with reduced cardiomyocyte mitophagy in vivo, measured with adenoviral Mito-QC (new Figure 7).

Reviewer #2 (Public Review):

In this manuscript, Franco et al show that the mitofusin 2 mutation MFN2 Q400 impaires mitochondrial fusion with normal GTPase activity. MFN2 Q400 fails to recruit Parkin and further disrupts Parkin-mediated mitophagy in cultured cardiac cells. They also generated MFN2 Q400 knock-in mice to show the development of lethal perinatal cardiomyopathy, which had an impairment in multiple metabolic pathways.

The major strength of this manuscript is the in vitro study that provides a thorough understanding in the characteristics of the MFN2 Q400 mutant in function of MFN2, and the effect on mitochondrial function. However, the in vivo MFN2 Q/Q400 knock-in mice are more troubling given the split phenotype of MFN2 Q/Q400a vs MFN2 Q/Q400n subtypes. Their main findings towards impaired metabolism in mutant hearts fail to distinguish between the two subtypes.

Thanks for the comments. We do not fully understand the statement that “impaired metabolism in mutant hearts fails to distinguish between the two (in vivo) subtypes.” The data in current Figure 5 and its accompanying figure supplements show that impaired metabolism measured both as metabolomic and transcriptomic changes in the subtypes (orange Q400n vs red Q400a in Figure 5 panels A and D) are reflected in the histopathological analyses. Moreover, newly presented data on ROS-modifying pathways (Figure 5C) suggest that a central difference between Mfn2 Q/Q400 hearts that can compensate for the underlying impairment in mitophagic quality control (Q400n) vs those that cannot (Q400a) is the capacity to manage downstream ROS effects of metabolic derangements and mitochondrial uncoupling. Additional support for this idea is provided in the newly performed doxorubicin challenge experiments (Figure 7), demonstrating that mitochondrial ROS levels are in fact increased at baseline in adult Q400n mice.

While the data support the conclusion that MFN2 Q400 causes cardiomyopathy, several experiments are needed to further understand mechanism.

We thank the reviewer for agreeing with our conclusion that MFN2 Q400 can cause cardiomyopathy, which was the major issue raised by R1. As detailed below we have performed a great deal of additional experimentation, including on two completely novel MFN2 mutant knock-in mouse models, to validate the underlying mechanism.

This manuscript will likely impact the field of MFN2 mutation-related diseases and show how MFN2 mutation leads to perinatal cardiomyopathy in support of previous literature.

Thank you again. We think our findings have relevance beyond the field of MFN2 mutant-related disease as they provide the first evidence (to our knowledge) that a naturally occurring primary defect in mitophagy can manifest as myocardial disease.

Author Response

Reviewer #2 (Public Review):

This manuscript reports on an important study that aims to identify symptom trajectories for the early detection of pancreatic cancer. The study's findings are based on the analysis of two complementary data sources: structured data obtained from the Danish National Patient Registry and unstructured information extracted from the free-text sections of patient notes. The researchers successfully identified various symptoms and disease trajectories that are strongly associated with pancreatic cancer, with compelling evidence from both data sources. Additionally, the study provides a detailed comparison and contrast of the results obtained from each data source, adding valuable insights into the strengths and limitations of each method.

Strengths:

The work is well motivated by the urgent need for early detection of pancreatic cancer, which is often difficult due to the lack of effective (computational) methods. The manuscript is generally well-written and includes relevant studies, providing a comprehensive overview of the current state of the field.

One of the unique contributions of this work is its use of both structured registry data and unstructured clinical notes to leverage complementary information. This approach enables a more nuanced and comprehensive understanding of the disease symptom trajectories, which is critical for improving early disease diagnosis and prognosis.

The methodology employed in this study is sound and robust, and the authors have candidly discussed its limitations. The results are significant and highlight previously unknown insights into symptom disease trajectories, which have important implications for the management of pancreatic cancer.

Overall, this is a well-designed and executed study that makes an important contribution to the field of cancer/informatics research, and it should be of great interest to both researchers and clinicians.

Weaknesses:

To complement the results in Figure 1, I'd also suggest that the authors compile a list of the most common (known) symptoms of pancreatic cancer as a reference. In other words, not only can you compare results found from the two sources but also compare them with existing knowledge. This is something you discussed partly in lines 245 but including this early as part of the results in Figure 1 would be more informative.

We agree that this would be informative to include into the Venn diagram. Hence, we have created a list of the most established and well-known symptoms of pancreatic cancer (Supplementary table S1) and converted these to the comparable ICD-10 level that we also use for the text mining and registry counts in Fig. 1. We have included the Venn diagram as Supplementary Figure S1.

In terms of the text mining evaluation results, providing information on recall errors would be beneficial to better understand the performance of the method. Additionally, line 144 mentions 53 words, but it is still not clear to me what these words refer to. Could you please clarify this point or provide more context?

We have added sensitivity/recall measures on the text mining procedure and furthermore added two references in the Discussion of the Tagcorpus program which was used for text mining the clinical notes. These references also mention similar sensitivities for the studies. The 53 words are false positives and we have clarified why these have been captured as false positives by the Tagcorpus (negations).

The disparities between Figure 2A and 2B are noteworthy, from very different initial symptoms to the proportion of short median survival dates (<=90 days), with much more pronounced differences than those observed in Figure 1 comparing two data sources. The highlighted trajectories are almost completely different. Should this be expected? I was hoping to see at least some overlap between the two results.

After updating the case population (via the cancer registry) and showing only symptoms trajectories in this revised version, we can clearly see that the trajectories are more similar. This gives an indication that the methods pick up on similar pancreatic-cancer symptoms, but there are also differences that show how each data type can complement the other, such as the text-mined trajectories being able to pick up longer symptom trajectories prior to the cancer.

All trajectories shown in Figure 2 include three symptoms. Is this by design? Could there be meaningful trajectories with different numbers of symptoms (e.g. 4 or more)?

We agree and have added the significant length 4 trajectories (for the registry data) as supplementary figure S2. No trajectories with length 5 or higher were found in the registry-based analysis. No length 4 (or higher) trajectories were found for the text-mined patients (presumably due to the data set size).

Considering those patients with both clinical notes and registry data, it may be beneficial to merge their symptoms to generate more informative trajectories.

This could be interesting but is out of scope for this paper. Here we would like to stress the proof-of-concept that the two data types can complement each other. The next steps would be to generate these multimodal trajectories to for example test if they are predictive of pancreatic cancer. Nonetheless, we acknowledge the significance of this perspective and have incorporated it into the Discussion section of the manuscript.

Given that results from two sources are being compared in Figures 1 and 2, have you considered calculating the top 20 most significant symptoms from the registry data as well?

We have done this and added them to Supplementary figure S3.

While there is a discussion related to cardiovascular diseases, I noticed no mention of cataracts or gonarthrosis, which were found to be prevalent among patients with short survival in Figure 2.

Since we now only include symptoms trajectories in the Results, we have chosen to not include these results in the Discussion for the final version of the manuscript. However, the diagnosis-wide trajectories are included in the Supplementary figure S2. Cataract and gonarthrosis have still been found significant in the results even though they are not shown in the Supplementary figure due to its visualization threshold of min. 400 patients per trajectory.

Ultimately, the goal of this research is to improve the early detection and prognosis of pancreatic cancer, thus it is important to discuss how the findings of this work could be applied in practice towards this goal (e.g. used by disease prediction algorithms?)

We agree that this is very important and have added a small section on this in the Discussion. We have also cited a recent publication using deep learning algorithms to predict pancreatic cancer based solely on registry data (Placido et al. 2023).

Author Response

Reviewer #1 (Public Review):

In general, in the discussion, I miss two of the main points that led to suspend screening programs in most countries during the pandemic:

1) protecting women from the risk of infection linked to attending a clinic during pandemic when health facilities were mostly attended by symptomatic people seeking care for Covid-19;

We agree. We have added this to the background and Discussion section (page 3, lines 76-78 & page 9, lines 296-299).

2) the of health professionals because they were mostly involved in covid related activities: lack of radiologists (addressed to the emergency department to assure diagnoses of pneumonia), lack of anesthesiologists (due to the expansion of intensive care), thus risking not having timely surgical treatment; lack of screening organization personal for invitations and phone calls (working on contact tracing).

We agree. We have added this to the background and Discussion section (page 3, lines 76-78 & page 9, lines 296-299).

Lacking the rationale for suspending screening, it is not clear to the reader how the Danish program afforded these issues and was able to maintain open the program.

We have elaborated on this in the Discussion section (page 296-299), arguing that Denmark may have partly decreased the issue of staff shortage due to e.g., a lower burden of COVID-19, use of laymen and medical student for testing and vaccinations and a high vaccine coverage.