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Referee #2

Evidence, reproducibility and clarity

SUMMARY OF THE PRESENTED FINDINGS

Abstract

1. LCOR (Ligand-dependent corepressor), which suppresses tumor growth by inducing the antigen presentation machinery (APM) of the tumor cells and constrains cellular plasticity.
2. poly β-(amino esters) (pBAE) nanoparticles (NPs).. Our results show optimal endosomal escape, which results in high transfection efficiency in vitro and in vivo
3. the combination of Lcor mRNA-loaded NPs with anti-PDL1 or anti-CTLA4 immunotherapies eradicated most of the tumors in our preclinical TNBC model.

Introduction

a. These structures facilitate endosomal escape due to protonation of tertiary amines at lower pH7.

Results

b. In human models MDAMB-231 and MCF7 cells, the NPs also showed high eGFP mRNA transfection efficiency

c. The efficiency of eGFP mRNA-loaded pBAE-NPs to transfect mRNA into different mouse breast cancer cells (AT3, 4T07, EO771, EMT6, 66cl4, EpRAS, and 4T1) was tested using NPs encapsulating eGFP mRNA,

d. Synthetic Lcor mRNA contained a Cap1, 5' and 3' untranslated regions (UTR) and a standard polyA tail (Fig. S2A), and all uracil were replaced for 5-methoxyuracil (5-moU) to avoid immunogenic reactions27,28. First, we measured and detected high levels of Lcor mRNA by qRT-PCR

e. NPs were stable at 25ºC for 24 h (Fig. S2C). In contrast, under conditions simulating the physiological environment (37ºC), a decrease in FRET signaling was detected ... indicating disassembly of the NPs after 2 h (Fig. S2C).

f. Lcor mRNA NPs, induces the expression of APM genes in AT3 and 4T07 cell lines

g. AT3 cells that constitutively overexpress ovalbumin (OVA). In these cells, OVA is cleaved, generating the SIINFEKL antigen peptide presented in the H-2Kb context. This can be used to measure APM activity using the anti-SIINFEKL antibody via flow cytometry.

h. We also observed a time- and dose-dependent effect regarding APM induction.

i. When tumors reached 0.5 x 0.5 cm2, we treated them intratumorally with pBAE-NPs loaded with 5 ug of synthetic FLuc or eGFP mRNA. We detected BLI at 3 h, meaning that tumor cells had taken up the mRNA-loaded NPs and translated a luciferase active protein within 3 h. In both models, expression peaked around 6 to 10 hours after administration

j. After local administration of 5 μg of Lcor mRNA-loaded NPs, we observed a rapid increase in Lcor mRNA in the tumor tissue, followed by a decrease, reaching baseline levels after 24 h (Fig. 3C). ..To unravel the protein dynamics, we used ... LCOR-HA protein and uniquely detect the ectopic protein using anti-HA by IF. As expected, LCOR-HA protein expression was delayed, peaking 3 h after administration (Fig. 3D). Linked to protein expression, at 3 h and 6 h after administration, we detected an increase in APM genes by RT-qPCR (Fig. 3E and S3D).

k. the combination of Lcor mRNA-loaded NPs with anti-PDL1 therapy not only reduced tumor growth but also led to tumor eradication in 5 out of 7 mice.

l. The combination of Lcor mRNA-loaded NPs with different ICIs showed high efficiency in preclinical models, thus supporting the feasibility of starting clinical studies and thus bringing the treatment closer to patients.

Major points

L. 277: "NPs were stable at 25ºC for 24 h (Fig. S2C). In contrast, under conditions simulating the physiological environment (37ºC), a decrease in FRET signaling was detected ... indicating disassembly of the NPs after 2 h (Fig. S2C)." - The disassembly of the NPs after 2 h is key to the performance of the chosen approach.

L. 296: "The results showed an increased number of cells with higher OVA-SIINFEKL presentation, indicating the enhanced activity of the APM induced by the Lcor mRNA-loaded pBAE-NPs... demonstrate the efficiency of this mRNA nanotechnology to rescue the function of the LCOR TF in inducing tumor cell immunogenicity and thus modulating tumor phenotypes." - There is a key difference between activating antigen-presenting machinary and inducing immunogenicity, i.e. recognition by the immune system and activation of effector cells. There is no indication on how effective endogenous immune responses (e.g. antibody titers, TIL infiltration, cytokine release) are to the administration of Lcor mRNA-loaded NPs.

L. 325: "Based on these results, we estimated an optimal therapeutic regimen of Lcor-mRNA-loaded pBAE-NPs administration in our preclinical experimental models would be every 3 days." - It is highly unclear how the authors came to this conclusion, as it should be based on the time frame of optimal immune responses.

L. 332: "Lcor mRNA-loaded NPs were administered at a dose of 250 μg/kg by intratumoral (i.t.) injection twice a week" - This possibly is the strongest limitation of this study. Intratumor injections of largely unfeasible/unrealistic in clinical setting. Even more, the management of metastatic disease appears out of question.

L. 337: "the results revealed that Lcor mRNA monotherapy was enough to reduce 4T07 tumor 338 growth." - These effects appear rather limited (Fig. 4A,B) and are not statistically significant in Fig. S4B and Fig. S5A.

L. 338: "the combination of Lcor mRNA-loaded NPs with anti-PDL1 therapy not only reduced tumor growth but also led to tumor eradication in 5 out of 7 mice" - Fig. 4A bottom left panel. Three of the tumor growth curves abruptly stop at below 200 mm3. Typically, this is mouse death. This reduces the tumor pool to four xenografts. Among these, we notice two complete responses and two tumor progressions. Two tumor progressions are seen also in the combination Lcor mRNA+ α-PD-L1 group. We are unsure about the statistics of this experiment.

L. 350: "The combination of Lcor mRNA-loaded NPs with different ICIs showed high efficiency in preclinical models, thus supporting the feasibility of starting clinical studies and thus bringing the treatment closer to patients."

• Please see comment on L. 332. It appears unrealistic to consider clinical studies in patients unless a systemic administration of Lcor mRNA-loaded NPs is tackled and corresponding therapeutic efficacy is shown.

Significance

General assessment:strengths and limitations.

The identification of a candidate therapeutic means, by supplying Lcor mRNA for induction of antigen-presenting molecules is of potential interest. As this is not a basic science study, but aims at developing feasible therapeutics, it falls short in this respect, as most likely unfeasible in patients. The combined effect with anti-immune blockade agents is of interest. However, if one assumes that effective immunostimulation was indeed induced by Lcor mRNA, its overall impact on tumor growth is per se weak, if any. Maybe only antigen presentation is induced, but this is in the absence of costimulatory signals? This needs to be investigated.

Advance

This article is based on good papers that were published years ago. The science novelty is limited. As the idea is to develop a novel therapeutic approach, the lack of realistic feasibility severely limits merits.

Audience

Scientists involved in preclinical studies.

Reviewer expertise

This reviewer and his research group have cloned the genes and biochemically characterized novel tumor drivers. He identified their function as stimulators of tumor cell growth and of metastatic spreading, together with roles in cell-cell adhesion, signal transduction and local cancer invasion. This led to the discovery of their prognostic / predictive relevance in human cancer. Two murine models of rare genetic diseases were generated by ablating the corresponding murine genes. He then pioneered the development of software for the identification of fusion oncogenes and of transcription factor-DNA binding sites. This reviewer fostered novel anti-cancer immunotherapies. He generated anti-cancer cytotoxic T lymphocytes, by the use of in vitro engineered antigen presenting cells. Using proprietary discovery platforms, this reviewer developed novel anti-cancer monoclonal antibodies, that selectively target cancer cells. This led to the engineering of humanized antibody-drug conjugates, bispecific anti-CD3/activated Trop-2 antibodies and innovative CAR-T designs. ADCs are now being tested in clinical trials in cancer patients.

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Referee #1

Evidence, reproducibility and clarity

In this manuscript, Serra-Mir et al investigate the therapeutic potential of delivering the mRNA of LCOR transcription factor via nanoparticles to enhance the efficacy of immune checkpoint inhibitors. The authors show that the mRNA delivery mediated by H and R-nanoparticles was efficient in multiple breast cancer cell lines in vitro. Moreover, using mouse models, they show that LCOR mRNA delivery may improve the efficacy of the treatment with anti-PDL1 or anti-CTLA4 checkpoint inhibitors against tumors. Although this proof-of-concept study has promising aspects, there are significant weaknesses that should be addressed. Details below.

Major points:

1. In vitro delivery of LCOR appears to be effective in both AT3 and 4T07 cell lines when continuously exposed to the mRNA loaded nanoparticles. However, the impact of LCOR on antigen presentation machinery (APM) is rather mixed and not very convincing. The expression pattern and kinetics of several APM genes are inconsistent with LCOR kinetics and at several timepoints the expression in LCOR samples is essentially the same as in mutant LCOR negative controls (Figure 2D). Moreover, the APM reporter assay experiments show that APM in LCOR transduced 4T07 cells is induced rather modestly at best (Figure 2E). The APM effect needs to be demonstrated more rigorously to be convincing.
2. Considering that previous studies by the authors suggest a role for LCOR in regulating stem cell properties in normal and malignant mammary cells (Celia-Terrassa et al Nat Cell Bio 2017; Perez-Nunez et al Nat Can 2022), it is important to address whether transduced LCOR mRNA impacts these properties. Moreover, other autocrine cell functions such as proliferation and apoptosis are also relevant and should be analyzed.
3. The impact of LCOR delivery on immune responses in mouse models could be more rigorous. Analysis of APM genes shows rather modest difference in these gene after LCOR transduction (Figure 3E). Is this sufficient to induce effective anti-tumor immune response? What is the status of T cell activity or exhaustion? Furthermore, LCOR may regulate cytokines and chemokines that are critical for modulation of the immune environment. Did the authors measure any immune-modulating cytokines in the tumor microenvironment, following LCOR expression? Finally, whereas the study focuses on APM and its function, LCOR may directly modulate expression of checkpoint activators on cancer cells. The impact of LCOR transduction on PD-L1, PD-L2 and CTLA-4 expression in cancer cells should be determined.
4. In line with point nr 2, it would be important to analyze the impact of delivered LCOR mRNA on cell functions such as proliferation and apoptosis in the mouse tumors. Even if LCOR delivery sensitizes tumors to checkpoint inhibitors, it cannot be assumed that the impact of LCOR is primarily due to induction of the APM.
5. The experiments analyzing treatment efficacy in the 4T07 model in mice show lack of consistency and a substantial variation between mice that are treated in the same manner. Even the group treated with PBS and Ctr-mRNA contains mice with tumors that regress (Figure 5A). This inconsistency suggests that more mice are required to generate a convincing pattern. Furthermore, the inclusion of a second model would provide a stronger case for a broad applicability of the LCOR treatment with checkpoint inhibitors. Indeed, it is surprising that the authors did not use the AT3 model in vivo considering that mRNA delivery and LCOR expression is substantially more efficient in AT3 compared to 4T07.
6. Following the injection of LCOR nanoparticles to the tumor, the proportion and spatial distribution of LCOR expressing cells should be determined. This is particularly relevant in light of the almost complete elimination of the tumors treated with combination therapy (Figures 4 and 5). Is this striking impact on tumors in spite of mRNA being delivered only to a small portion of cells within the tumor?
7. The in vivo results indicate that expression levels of Fluc mRNA decline rapidly post-treatment, returning to baseline within 24 hours after peaking at 10 hours (Supplementary Figure 3). Although the investigators treat mice every 3rd day with LCOR nanoparticles in their therapeutic experiments, the analysis of durability of immune responses after single injection should be done and can provide important practical insights to guide therapeutic design.

Minor points:

1. The authors mention that LCOR mRNA delivery synergizes with checkpoint inhibitor treatment. However, synergy has a specific meaning when drug interaction is analyzed. This was not really addressed or calculated.
2. There seems to be a mistake in the text (lines 261-263). Based on Figure 1C the mRNA delivery efficiency is higher in AT3 cells compared to 4T07 cells (very difficult to determine anything from Figure 3D, since the cell density is not visible).
3. It is surprising how little expression of luciferase is observed in the 4T07 model (Figure S3), even if almost 60% of cancer cells and 40% of stromal cells are positive (Figure 3A). What could explain this discrepancy?
4. Representative FACS plots from Figure 3 should be shown.
5. There are issues with the figure legends of Figure 3 (from 3C onwards) and Figure S2 (from 2D onwards) that need to be fixed.

Significance

The study is a proof-of-concept investigation addressing whether LCOR mRNA can be delivered by nanoparticles to sensitize tumors to immunotherapy. This approach aims to overcome the limitations and difficulties of targeting transcription factors for therapeutic purposes. However, although the delivery of LCOR mRNA appears to be sufficient, further characterization of the resulting impact needs to be done. This includes both impact on immune responses as well as cell-autonomous impact on cancer cell proliferation and apoptosis.

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Reply to the reviewers

Manuscript number: RC-2025-02946

Corresponding author(s): Margaret, Frame

Roza, Masalmeh

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Reviewer #1

Evidence, reproducibility and clarity

Review of Masalmeh et al. Title: "FAK modulates glioblastoma stem cell energetics..."

Previous studies have implicated FAK and the related tyrosine kinase PYK2 in glioblastoma growth, cell migration, and invasion. Herein, using a murine stem cell model of glioblastoma, the authors used CRISPR to inactivate FAK, FAK-null cells selected and cloned, and lentiviral re-expression of murine FAK in the FAK-null cells (termed FAK Rx) was accomplished. FAK-/- cells were shown to possess epithelial characteristics whereas FAK Rx cells expressed mesenchymal markers and increased cell migration/invasion in vitro. Comparisons between FAK-/- and FAK Rx cells showed that FAK re-expressed increased mitochondrial respiration and amino acid uptake. This was associated with FAK Rx cells exhibiting filamentous mitochondrial morphology (potentially an OXPHOS phenotype) and decreased levels of MTFR1L S235 phosphorylation (implicated in mito morphology fragmentation). Mito and epithelial cell morphology of FAK-/- cells was reversed by treatment with Rho-kinase inhibitors that also increased mito metabolism and cell viability. Last, FAK-dependent glioblastoma tumor growth was shown by comparisons of FAK-/- and FAK Rx implantation studies.

The studies by Masalmeh provide interesting findings associating FAK expression with changes in mitochondrial morphology, energy metabolism, and glutamate uptake. According to the authors model, FAK expression is supporting a glioblastoma stem cell like phenotype in vitro and tumor growth in vivo. What remains unclear is the mechanistic connection to cell changes and whether or not these are be dependent on intrinsic FAK activity or as the Frame group has previously published, potentially FAK nuclear localization. The associations with MTFR1L phosphorylation and effects by Rho kinase inhibition are likely indirect and remind this reviewer of long-ago studies with FAK-null fibroblasts that exhibit epithelial characteristics, still express PYK2, exhibited elevated RhoA GTPase activity. Some of these phenotypes were linked to changes in RhoGEF and RhoGAP signaling with FAK and/or Pyk2. At a minimum, it would be informative to know whether Pyk2 signaling is relevant for observed phenotypes and whether the authors can further support their associations with FAK-targeted or FAK-Pyk2-targeted inhibitors or PROTACs.

Some questions that would enhance potential impact. 1. Cell generation. Please describe the analysis of FAK-/- clones in more detail. The "low viability" phenotype needs further explanation with regard to clonal expansion and growth characteristics?

Response:

• We included a better description and a supplementary figure in our revised manuscript to indicate that we have examined several FAK -/- clones and confirmed that our observations were not due to clonal variation; multiple clones displayed similar morphological changes (Figure S1D). We also show that the elongated mesenchymal-like morphology was observed at 48 h after nucleofecting the cells with the FAK‑expressing vector, before beginning G418 selection to enrich for cells expressing FAK (Figure S1C). We also included experiments to acutely modulate FAK signalling (detaching and seeding cells on fibronectin) (Figure S2D, E, F and Figure S3) to exclude the possibility that the profound effects are due to protocols/selection we used for generating FAK-deleted cells.
• Regarding the term “low viability”, we have clarified in the text that there is no significant difference in cell number (Figure S1A) or ‘cell viability’ when it is assessed by trypan blue exclusion (a non-mitochondria-dependent read-out) (Figure S1B) between FAK-expressing FAK Rx and FAK-/- cells cultured for three days under normal conditions. Therefore, we agree the term ‘cell viability’ in this context could be confusing and have replace "cell viability” with “metabolic activity as measured by Alamar Blue.” in Figure 1D and Figure 5B, and the corresponding text in the original manuscript. This wording more accurately reflects the data.

Figure 1F: need further support of MET change upon FAK KO and EMT reversion.

Response: We have added a heatmap (Figure S1E) illustrating the changes in protein expression of core-enriched EMT/MET genes products (by proteomics) after FAK gene deletion (EMT genes as defined in Howe et al., 2018) ; this strengthens the conclusion that the MET reversion morphological phenotype is accompanied by recognised MET protein changes.

Fig. 2: Need further support if FAK effects impact glycolysis or oxidative phosphorylation in particular as implicated by the stem cell model.

Response: We show that FAK impacts both glycolysis (Figure 2A, 2E, and 2F) and mitochondrial oxidative phosphorylation on the basis of the oxygen consumption rate (OCR) (Figure 2B, and 2D), showing both are contributing pathways to FAK-dependent energy production. We have clarified this in the text.

Is there a combinatorial potential between FAKi and chemotherapies used for glioblastoma. Need to build upon past studies.

Response: Yes, previous studies suggest that inhibiting FAK can sensitize GBM cells to chemotherapy (Golubovskaya et al., 2012; Ortiz-Rivera et al., 2023). We have included a paragraph in the discussion section to make sure this is clearer. Although it is not the subject of this study, we appreciate it is useful context.

The notation of changes in glucose transporter expression should be followed up with regard to the potential that FAK-expressing cells may have different uptake of carbon sources and other amino acids. Altered uptake could be one potential explanation for increase glycolysis and glutamine flux.

Response: We agree with the reviewer that glucose uptake could be contributing and we include data that 2 glucose transporters are indeed FAK-regulated namely Glucose transporter 1 (GLUT1, encoded by Slc2a1 gene) and Glucose transporter 3 (GLUT 3, encoded by Slc2a3 gene) (shown in Figure S2B and C).

It would be helpful to support the confocal microscopy of mitos with EM.

Response:

We are concerned (and in our experience) that Electron microscopy (EM) may introduce artefacts during sample preparation. In contrast, immunofluorescence sample preparation is less susceptible to artefacts. The SORA system we used is not a conventional point-scanning confocal microscope, but is a super-resolution module based on a spinning disk confocal platform (CSU-W1; Yokogawa) using optical pixel reassignment with confocal detection. This method enhances resolution in all dimensions with resolution in our samples measured at 120nm. This has been instructive in defining a new level of changes in mitochondrial morphology upon FAK gene deletion.

Lack of FAK expression with increased MTFR1 phosphorylation is difficult to interpret.

Response: We do not directly show that this phosphorylation event is causal in our experiments; however, we think it important to document this change since it has been published that phosphorylation of MTFR1 has been causally linked to the mitochondrial morphology we observed in other systems (Tilokani et al., 2022).

Need to have better support between loss of FAK and the increase in Rho signaling. Use of Rho kinase inhibitors is very limited and the context to FAK (and or Pyk2) remains unclear. Past studies have linked integrin adhesion to ECM as a linkage between FAK activation and the transient inhibition of RhoA GTP binding. Is integrin signaling and FAK involved in the cell and metabolism phenotypes in this new model?

Response: To better support the antagonistic effect of FAK on Rho-kinase (ROCK) signalling, we included a new experiment in which the integrin-FAK signalling pathway has been disrupted by treating FAK WT cells with an agent that causes detachment from the substratum, Accutase, and growing the cells in suspension in laminin-free medium. We present ROCK activity data, as judged by phosphorylated MLC2 at serine 19 (pMLC2 S19), relating this to induced FAK phosphorylation at Y397 (a surrogate for FAK activity) that is supressed after integrin disengagement. These measurements have been compared with conditions whereby integrin-FAK signalling is activated by growing the cells on laminin coated surfaces. We observed a time-dependent decrease in pFAK(Y397) levels (normalised to total FAK) in suspended cells compared to those spread on laminin, while pMLC2(S19) levels increased in a reciprocal manner over time in detached cells relative to spread cells (S4A and B). There is therefore an inverse relationship between integrin-FAK signalling and ROCK-MLC2 activity, consistent with findings from FAK gene deletion experiments. In the former case, we do not rely on gene deletion cell clones.

Significance

The studies by Masalmeh provide interesting findings associating FAK expression with changes in mitochondrial morphology, energy metabolism, and glutamate uptake. According to the authors model, FAK expression is supporting a glioblastoma stem cell like phenotype in vitro and tumor growth in vivo. What remains unclear is the mechanistic connection to cell changes and whether or not these are be dependent on intrinsic FAK activity or as the Frame group has previously published, potentially FAK nuclear localization. The associations with MTFR1L phosphorylation and effects by Rho kinase inhibition are likely indirect and remind this reviewer of long-ago studies with FAK-null fibroblasts that exhibit epithelial characteristics, still express PYK2, exhibited elevated RhoA GTPase activity. Some of these phenotypes were linked to changes in RhoGEF and RhoGAP signaling with FAK and/or Pyk2. At a minimum, it would be informative to know whether Pyk2 signaling is relevant for observed phenotypes and whether the authors can further support their associations with FAK-targeted or FAK-Pyk2-targeted inhibitors or PROTACs.

__Response: __

Deleting the gene encoding FAK in mouse embryonic fibroblasts leads to elevated Pyk2 expression (Sieg, 2000). However, in the GBM stem cell model we used here, Pyk2 was not expressed (determined by both transcriptomics and proteomics). We have included Figure S1E to show that PYK2 expression was undetectable in FAK -/- and FAK Rx cells at the RNA level (Figure S1F). We conclude that there is no compensatory increase in Pyk2 upon FAK loss in these cells. In the transformed neural stem cell model of GBM, we do not consistently or robustly detect nuclear FAK.

Review #2

Masalmeh and colleagues employ a neural stem/progenitor cell-based glioma model (NPE cells) to investigate the role of Focal Adhesion Kinase (FAK) in GBM, with a focus on potential links between the regulation of morphological/adhesive and metabolic GBM cell properties. For this, the authors employ wt cells alongside newly generated FAK-KO and -reexpressing cells, as well as pharmacological interventions to probe the relevance of specific signaling pathways. The authors´ main claims are that FAK crucially modulates glioma cell morphology, cell-cell and cell-substrate interactions and motility, as well as their metabolism, and that these effects translate to changes to relevant in vivo properties such as invasion and tumor growth.

My main issues are with the model chosen by the authors.

As per the methods section, generation of FAK-KO and -"Rx" NPE cells entailed protracted selection/expansion processes, which may have resulted in inadvertent selection for cellular/molecular properties unrelated to the desired one (loss or gain of FAK expression) and which may have had cascading effects on NPE cells. The authors nonetheless repeatedly claim the parameters they quantify, such as mitochondrial or cytoskeletal properties or metabolic features, to have directly resulted from FAK loss or reintroduction. Examples of such causal inferences are to be found in lines 123, 134/135, 165, 181. Such causal claims are, in my view, unsupported.

Acute perturbation of FAK expression/activity, genetically or pharmacologically, followed by a rapid assessment of the processes under investigation, would be needed to begin to assess causality, even if acute genetic perturbations may be technically challenging as sufficient gene expression reduction or restoration to physiologically relevant levels may be hard to achieve.

Response:

We would like to first comment on the model we used here, which we think will clarify the validity of our approach. The model is a transformed stem cell model of GBM that was published in (Gangoso et al., Cell, 2021) and is now used regularly in the GBM field. As mentioned in the response to Reviewer 1, we have added text (page 4 and 5 in the revised manuscript) and a new supplementary figure (Figure S1D) clarifying that the morphological changes we observed were consistent across multiple FAK -/- clones, showing this was not due to any inter-clonal variability. We also added images showing that the morphological changes were apparent at 48 h after nucleofecting FAK -/- cells with the FAK‑expressing vector specifically (not the empty vector), prior to starting G418 selection to enrich for FAK‑expressing cells (Figure S1C), addressing the worry that clonal variation and selection was the cause of the FAK-dependent phenotypes we observed. We believe that our model provides a type of well controlled, clean genetic cancer cell system of a type that is commonly used in cancer cell biology, allowing us to attribute phenotypes to individual proteins.

We have also carried out a more acute treatment by using the FAK inhibitor VS4718 to perturb FAK kinase activity and assessed the effects on glycolysis and glutamine oxidation after 48h treatment (Figure S2D, E and F). We found that treating the transformed neural stem cells (parental population) with FAK inhibitor (300nM VS4718) decreases glucose incorporation into glycolysis intermediates and glutamine incorporation into TCA cycle intermediates, consistent with a role for FAK’s kinase activity in maintaining glycolysis and glutamine oxidation.

The employed pharmacological modulation of ROCK activity is the only approach that, given the presumably acute nature of the treatment, may have allowed the authors to probe the proposed functional links. The methods section of the manuscript does not however comprise details as to the duration of these treatments, which leaves open the possibility of long-term treatment having been carried out (data shown in Figure 5B refers to 72hr treatment).

__Response: __

We have added the duration of the treatment to the Methods section and Figure Legends, to clarify that cells were treated with ROCK inhibitors for 24h, before assessing the effects on mictochondria (Figure 4C, D, S4C and D) and glutamine oxidation (Figure 5A, and S5). For metabolic activity by AlamarBlue assay, cells were treated with ROCK inhibitors for 72h (Figure 5B).

Even in the case of ROCK inhibitor experiments, it is however unclear if and how the effects on cell morphology and adhesion, mitochondrial organization and metabolic activity may be connected to each other and, if at all, to FAK expression.

Given the above uncertainties due to the nature of the model and experimental approaches, it is hard to assess the reliability and thus the relevance of the findings.

Response:

FAK suppresses ROCK activity (as judged by pMLC2 S19, Figure 4A and B). Treating FAK -/- cells with two different ROCK inhibitors restored mesenchymal-like cell morphology, mitochondrial morphology and glutamine oxidation. As mentioned above, to strengthen our evidence for the antagonistic role of FAK in ROCK-MLC2 signalling, we have now introduced an experiment whereby integrin-FAK signalling was disrupted through treatment with a detachment agent (Accutase), and subsequently maintaining the cells in suspension in laminin-free medium. We assessed pMLC2 S19 levels (a measure of ROCK activity) relating this to FAK phosphorylation that is supressed after integrin disengagement. These results were evaluated relative to spread wild type cells growing on laminin where Integrin-FAK signalling was active (Figure S4A and B). We observed an inverse relationship between Integrin-FAK signalling and ROCK-MLC2 activity in keeping with our conclusions (Figure 4A and B).

Experimental support for the ability of cell-substrate interaction modulation to concomitantly impact cellular metabolism and motility/invasion would be significant both in terms of advancing our understanding of glioma cell biology and of its translational potential, but the evidence being provided is at best compatible with the proposed model.

Response: We carried out a new experiment to support the ability of cell-substrate interaction modulation to impact metabolism; specifically, we inhibited cell-substrate interactions by plating the cells on Poly-2-hydroxyethyl methacrylate (Poly 2-HEMA)-coated dishes. This suppressed FAK phosphorylation at Y397, as expected, with concomitant reduction in glutamine utilisation in the TCA cycle (Figure S3A, B and C).

My background/expertise is in developmental and adult neurogenesis, in vivo modelling of gliomagenesis and cell fate control/reprogramming, with a focus on molecular mechanisms of differentiation and quantitative aspects of lineage dynamics; molecular details of the control of cellular metabolism, cell-cell adhesion and cytoskeletal dynamics are not core expertise of mine.

We appreciate this reviewer’s expertise are not necessarily in the cancer cell biology and genetic intervention aspects of our study. We hope that the explanations we have provided satisfy the reviewer that our conclusions are valid.

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Referee #2

Evidence, reproducibility and clarity

Masalmeh and colleagues employ a neural stem/progenitor cell-based glioma model (NPE cells) to investigate the role of Focal Adhesion Kinase (FAK) in GBM, with a focus on potential links between the regulation of morphological/adhesive and metabolic GBM cell properties. For this, the authors employ wt cells alongside newly generated FAK-KO and -reexpressing cells, as well as pharmacological interventions to probe the relevance of specific signaling pathways. The authors´ main claims are that FAK crucially modulates glioma cell morphology, cell-cell and cell-substrate interactions and motility, as well as their metabolism, and that these effects translate to changes to relevant in vivo properties such as invasion and tumor growth. My main issues are with the model chosen by the authors.

As per the methods section, generation of FAK-KO and -"Rx" NPE cells entailed protracted selection/expansion processes, which may have resulted in inadvertent selection for cellular/molecular properties unrelated to the desired one (loss or gain of FAK expression) and which may have had cascading effects on NPE cells. The authors nonetheless repeatedly claim the parameters they quantify, such as mitochondrial or cytoskeletal properties or metabolic features, to have directly resulted from FAK loss or reintroduction. Examples of such causal inferences are to be found in lines 123, 134/135, 165, 181. Such causal claims are, in my view, unsupported. Acute perturbation of FAK expression/activity, genetically or pharmacologically, followed by a rapid assessment of the processes under investigation, would be needed to begin to assess causality, even if acute genetic perturbations may be technically challenging as sufficient gene expression reduction or restoration to physiologically relevant levels may be hard to achieve.

The employed pharmacological modulation of ROCK activity is the only approach that, given the presumably acute nature of the treatment, may have allowed the authors to probe the proposed functional links. The methods section of the manuscript does not however comprise details as to the duration of these treatments, which leaves open the possibility of long-term treatment having been carried out (data shown in Figure 5B refers to 72hr treatment). Even in the case of ROCK inhibitor experiments, it is however unclear if and how the effects on cell morphology and adhesion, mitochondrial organization and metabolic activity may be connected to each other and, if at all, to FAK expression.

Significance

Given the above uncertainties due to the nature of the model and experimental approaches, it is hard to assess the reliability and thus the relevance of the findings.

Experimental support for the ability of cell-substrate interaction modulation to concomitantly impact cellular metabolism and motility/invasion would be significant both in terms of advancing our understanding of glioma cell biology and of its translational potential, but the evidence being provided is at best compatible with the proposed model.

My background/expertise is in developmental and adult neurogenesis, in vivo modelling of gliomagenesis and cell fate control/reprogramming, with a focus on molecular mechanisms of differentiation and quantitative aspects of lineage dynamics; molecular details of the control of cellular metabolism, cell-cell adhesion and cytoskeletal dynamics are not core expertise of mine.

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Referee #1

Evidence, reproducibility and clarity

Review of Masalmeh et al.

Title: "FAK modulates glioblastoma stem cell energetics..."

Previous studies have implicated FAK and the related tyrosine kinase PYK2 in glioblastoma growth, cell migration, and invasion. Herein, using a murine stem cell model of glioblastoma, the authors used CRISPR to inactivate FAK, FAK-null cells selected and cloned, and lentiviral re-expression of murine FAK in the FAK-null cells (termed FAK Rx) was accomplished. FAK-/- cells were shown to possess epithelial characteristics whereas FAK Rx cells expressed mesenchymal markers and increased cell migration/invasion in vitro. Comparisons between FAK-/- and FAK Rx cells showed that FAK re-expressed increased mitochondrial respiration and amino acid uptake. This was associated with FAK Rx cells exhibiting filamentous mitochondrial morphology (potentially an OXPHOS phenotype) and decreased levels of MTFR1L S235 phosphorylation (implicated in mito morphology fragmentation). Mito and epithelial cell morphology of FAK-/- cells was reversed by treatment with Rho-kinase inhibitors that also increased mito metabolism and cell viability. Last, FAK-dependent glioblastoma tumor growth was shown by comparisons of FAK-/- and FAK Rx implantation studies.

The studies by Masalmeh provide interesting findings associating FAK expression with changes in mitochondrial morphology, energy metabolism, and glutamate uptake. According to the authors model, FAK expression is supporting a glioblastoma stem cell like phenotype in vitro and tumor growth in vivo. What remains unclear is the mechanistic connection to cell changes and whether or not these are be dependent on intrinsic FAK activity or as the Frame group has previously published, potentially FAK nuclear localization. The associations with MTFR1L phosphorylation and effects by Rho kinase inhibition are likely indirect and remind this reviewer of long-ago studies with FAK-null fibroblasts that exhibit epithelial characteristics, still express PYK2, exhibited elevated RhoA GTPase activity. Some of these phenotypes were linked to changes in RhoGEF and RhoGAP signaling with FAK and/or Pyk2. At a minimum, it would be informative to know whether Pyk2 signaling is relevant for observed phenotypes and whether the authors can further support their associations with FAK-targeted or FAK-Pyk2-targeted inhibitors or PROTACs.

Some questions that would enhance potential impact.

1. Cell generation. Please describe the analysis of FAK-/- clones in more detail. The "low viability" phenotype needs further explanation with regard to clonal expansion and growth characteristics?
2. Figure 1F: need further support of MET change upon FAK KO and EMT reversion.
3. Fig. 2: Need further support if FAK effects impact glycolysis or oxidative phosphorylation in particular as implicated by the stem cell model.
4. Is there a combinatorial potential between FAKi and chemotherapies used for glioblastoma. Need to build upon past studies.
5. The notation of changes in glucose transporter expression should be followed up with regard to the potential that FAK-expressing cells may have different uptake of carbon sources and other amino acids. Altered uptake could be one potential explanation for increase glycolysis and glutamine flux.
6. It would be helpful to support the confocal microscopy of mitos with EM.
7. Lack of FAK expression with increased MTFR1 phosphorylation is difficult to interpret.
8. Need to have better support between loss of FAK and the increase in Rho signaling. Use of Rho kinase inhibitors is very limited and the context to FAK (and or Pyk2) remains unclear. Past studies have linked integrin adhesion to ECM as a linkage between FAK activation and the transient inhibition of RhoA GTP binding. Is integrin signaling and FAK involved in the cell and metabolism phenotypes in this new model?

Significance

The studies by Masalmeh provide interesting findings associating FAK expression with changes in mitochondrial morphology, energy metabolism, and glutamate uptake. According to the authors model, FAK expression is supporting a glioblastoma stem cell like phenotype in vitro and tumor growth in vivo. What remains unclear is the mechanistic connection to cell changes and whether or not these are be dependent on intrinsic FAK activity or as the Frame group has previously published, potentially FAK nuclear localization. The associations with MTFR1L phosphorylation and effects by Rho kinase inhibition are likely indirect and remind this reviewer of long-ago studies with FAK-null fibroblasts that exhibit epithelial characteristics, still express PYK2, exhibited elevated RhoA GTPase activity. Some of these phenotypes were linked to changes in RhoGEF and RhoGAP signaling with FAK and/or Pyk2. At a minimum, it would be informative to know whether Pyk2 signaling is relevant for observed phenotypes and whether the authors can further support their associations with FAK-targeted or FAK-Pyk2-targeted inhibitors or PROTACs.

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Referee #3

Evidence, reproducibility and clarity

In this work, the authors investigate the cytoplasmatic roles of Mei2, an RNA-binding protein in fission yeast, in particular its interactions with processing bodies (PBs) in the cytoplasm. The manuscript rests heavily on microscopy data, using a combination of time-resolved microscopy and molecular mutation and tagging techniques.

Mei2 is known for its role in the nucleus of zygotic cells. Here, it is shown that Mei2 co-localizes with the PB markers Dcp2 and Edc3. This happens in zygotes but not in gametes (e.g. when fusion is blocked in fus1 mutants) (Fig 4E). <br /> This co-localization in PBs is counteracted by Pat1-driven phosphorylation of Mei2. Phosphorylation by Pat1 is known to suppress Mei2 activity. Mei3 inhibits Pat1; in a mei3 mutant Mei2 cannot accumulate in PBs, the same happens with a non-phosphorylatable mei2 allele (Fig. 5). In a pat1Δ mutant, constitutively active Mei2 is compatible with growth if it stays in the nucleus (mei2-NLS), but not if Mei2 is forced to the cytoplasm (mei2-NES) (Fig. 3G). This indicates that it is the cytoplasmic function of Mei2 that is critical.

Forcing Pat1 to be cytoplasmic (Pat1-NES) allowed normal vegetative growth and mating (Fig. 3A-C), whereas nuclear Pat1 (Pat1-NLS) produced premature mating (Fig. 3A,B). Thus, cytoplasmic Pat1 phosphorylation of Mei2 is critical for controlling the transition from mitotic growth to fusion and zygote formation.

Mei2 shuttles between the nucleus and cytoplasm, and one of its RNA-binding domains (RRM1) drives nuclear import, while both RRM1 and RRM3 are required for export to the cytoplasm (Fig. 2 and S2). Little was known previously of the role of RRM1.

They present evidence that this localization to PBs is required for development. Knocking out the RNA helicase Ste13 (ortholog of S. cerevisiae Dhh1 which is a PB component) reduces PB formation (Fig. 6A). Even a non-phosphorylatable mei2 allele (i.e. it cannot be inactivated by Pat1) is incapable of driving sporulation in a ste13Δ background (Fig. 6B-D). This demonstrates that Mei2 activity is dependent on PBs.

The study is well conceived and performed, and the conclusions mostly well backed by data. Experimental and statistical procedures are well described, and the number of replicates is sufficient.

There are some minor questions however:

In the literature, Mei2 is described as appearing as a nuclear dot in zygotic cells, but invisible in mitotic cells. Here, the authors demonstrate a Mei2 dot already 30 minutes before fertilization (Fig. 2A). Is the reason for this a more sensitive microscopic technique, or something else?

The authors claim that the RRM1 RNA-binding region of Mei2 is essential for cytoplasmic Mei2 function and recruitment to PBs. This contrasts with previous publications (Watanabe 1994, Watanabe 1997, Otsubo 2014), as pointed out by the authors, where RRM1 appears to be dispensable for development. How do the authors argue about this discrepancy?

Significance

Overall, this paper presents major advances in our understanding of the cytoplasmic functions of this intensely studied RNA-binding protein, Mei2, in the transitions between the mitotic and meiotic cell cycles.

It builds on the original observations of Mei2 as an essential protein for fusion and meiosis (Watanabe EMBO J 1988), being RNA-binding (Watanabe Cell 1994), and forming a nuclear dot in meiotic cells (Yamashita Cell 1998). These were followed by e.g. reports how Pat1 phosphorylation regulates Mei2 degradation (Matsuo J Cell Sci 2007) and its binding to RNA (Shen J Mol Cell Biol 2022). The present manuscript gives a broader view of the functions of Mei2 beyond its previously described role in the nucleus, and characterizes its interactions with the other players in fusion and meiosis.

These findings will be of great interest not only to the fission yeast community, but to a wide range of scientists specializing in meiosis and fertilization, and to the RNA biologists at large. Since Mei2 is conserved across many branches of the eukaryotic tree as an RNA-binding protein, albeit with somewhat different functions in e.g. plants, the work has general relevance.

I have read this manuscript with a background in general yeast cell and molecular biology, including post-transcriptional regulation. I am no microscopy expert, however I find the experimental setup with fluorescent tagging, combinations of mutations in key components in the pathway, and high resolution microscopy data from time series, convincing.

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Referee #2

Evidence, reproducibility and clarity

In this manuscript, Araoyinbo et al. present a wealth of detailed data analyzing the cellular behavior of mainly three proteins, the RNA-binding protein Mei2, the kinase Pat1 and its inhibitor the protein Mei3 during mating and subsequent initiation of meiosis in fission yeast. This analysis involve also the detailed testing of potential models about how these protein act on each other to fulfil their different functions, such as to block remating on zygotes, the initiation of zygotic S-phase and the initiation of meiosis and sporulation. These data converge to a model whereby Pat1 inhibition by Mei3 expression upon cell fusion unleashes Mei2 function in the cytoplasm. This is due to the subsequent dephosphorylation of Mei2, and its RNA-recognition motif RRM1 interacting with and recruiting Mei2-bound RNAs to P-bodies, where their translation is most likely repressed (at least the translation of a synthetic mRNA - Mei2 pair is repressed when the pair is targeted to P-bodies). Together, this study provides detailed insights into how the meiotic cycle is induced upon mating of fission yeast cells but not in gametes).

Overall, this is a very carefully controlled study and the data are very convincing and very interesting. It makes a compelling case for the model proposed and makes many original observations and far reaching observations, such as the role of nucleo-cytoplasmic compartmentalization and P-bodies in implementing developmental decisions. Since the notion that P-bodies have a function at all has been strongly questioned in recent years, this study will be very useful for the field.

The only limitations that I have concerns the readability of the manuscript. It is extremely dense and that makes it a laborious read. Furthermore, the manuscript is not particularly well motivated, such that it is not very obvious what questions the authors are after. This becomes more or less clear only slowly as the reader progresses, or in the second read. Therefore, this very nice piece of work may escape people who are not working on fission yeast mating and meiosis, which would be a pity. I therefore recommend working on better motivating the study and its different parts for a general audience, streamlining the fission yeast intricacies and explaining more precisely what is conceptually learnt from these studies, on a broad sense and possibly in a way that would be relevant beyond the model used. This paper is opening a reach area of research and it would be unfortunate to not make that point more clearly.

Significance

Overall, this is a very carefully controlled study and the data are very convincing and very interesting. It makes a compelling case for the model proposed and makes many original observations and far reaching observations, such as the role of nucleo-cytoplasmic compartmentalization and P-bodies in implementing developmental decisions. Since the notion that P-bodies have a function at all has been strongly questioned in recent years, this study will be very useful for the field.

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Referee #1

Evidence, reproducibility and clarity

Summary

The study by Araoyinbo et al. explores the role of the RNA-binding protein Mei2 in fission yeast zygotic development. It highlights Mei2's cytosolic functions, its interaction with P-bodies, and nucleocytoplasmic shuttling. Mei2's regulation by Mei3 and Pat1, and the importance of its RNA recognition motifs (RRM1 and RRM3) are also discussed.

The main conclusion of the manuscript is somewhat unexpected from previous studies about Mei2. Particularly, the cytoplasmic function of Mei2 is a novel point in this field.

Lots of experiments have been done to make the scenario of the manuscript. The experiments and results are technically sound, and I potentially agree with the interpretation by the authors. It would require some more explanation as well as additional experiments to conclude in the way the authors wish to do.

Major points

1. Page 4. "Taken together, these results show that fertilization, and Mei3 expression in particular, promote Mei2 nuclear export." It is also possible that Mei2-NLS-GFP was degraded somewhere in the cell (as Mei2 may be still shuttling even if NLS was fused) upon mating (120 min onwards in Fig2D) rather than exported to the cytoplasm. In mei3∆ (Fig 2E) Mei2-NLS-GFP might be somehow escaped from the degradation. Also, nuclear signal of Mei2 is very bright but cytosolic signal seems vague. I wonder the entire results in the manuscript could be interpreted from the viewpoint of degradation/protein stability/protein amount, rather than regulation of localization such as nuclear import and export.
2. Page 4. "We conclude that RRM1 promotes nuclear import of Mei2." This may be true, but is it also possible that RRM1 inhibits nuclear export of Mei2? This type of possible dual explanation can be applied to the entire manuscript. This is expected to be neutralized or clarified at each point.
3. Page 5. "Thus, diminishing nuclear Pat1 levels does not compromise its roles during growth and mating." It is interesting for me to find that Pat1-NLS induced ectopic meiosis. This is a fine finding. I wonder just addition of NLS (basic residues) at the C-terminus of Pat1 might deteriorate the activity of Pat1, apart from localization shift. Is it possible to exclude this possibility by making NES-Pat1-NLS-3GFP fusion, in which NLS and NES are fused doubly and distally, because proximal double fusion such as Pat1-NLS-NES-3GFP might just mutually cancel the NLS NES activities.
4. In general in the Results section. What confused me is when each event occurred. Nutritional conditions, -N but not yet conjugated, after conjugation, premeiotic S or meiotic prophase (or even later). It is particularly hard to catch the story when the timing issue and the location issue (nuclear and cytosolic localization, NLS and NES...) are discussed at the same time. Explanation in chronological order, hopefully at the earlier stages such as explanation for Figures 2 and 3, would be appreciated. The model shown in Figure 8 is quite helpful for my understanding.

Minor points

1. "Fertilization" in the title, and "Mei2 is expressed in gametes" in the main text on pare 2. Authors try to generalize fission yeast mating as fertilization of higher organisms as both are events in which two haploids conjugate. I personally do not agree with this type of explanation. This is mainly because S. pombe conjugation (mating) is a part of sexual differentiation and therefore is biologically distinct from fertilization of higher organisms. S. pombe grows and divides in the haploid state, which is distinct from general gametes. To avoid such confusion, I would propose authors to neutralize expression throughout the manuscript.
2. I found quite a few "surprising(ly)", which are hopefully neutralized, as it is somewhat emotional.

Significance

General assessment: strengths and limitations:

Strengths: It provides novel understanding of molecular mechanisms of meiotic initiation of fission yeast. Technically sound. Lots of experiments. Limitations: The story is very confusing and difficult to catch. Explanation can be simplified.

Advance: compare the study to existing published knowledge: does it fill a gap? What kind of advance does it make (conceptual, clinical, fundamental, methodological, incremental,,,,)? It is a big advancement. It is conceptually novel regarding how meiosis is initiated in fission yeast.

Audience: which communities will be interested/influenced, what kind of audience (broad, specialized, clinical, basic research, applied science, fields and subfields,,,) It is mainly for audience of basic research, biology, molecular mechanism of gene explanation, meiosis or yeast cellular events. For non-yeast researchers, this manuscript is probably very hard to read/understand, although the authors tried to generalize yeast-specific events with general words.

Describe your expertise:

Yeast genetics, Meiosis, Cell biology, Gene expression regulation

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Referee #3

Evidence, reproducibility and clarity

Summary

This manuscript presents a large-scale comparative genomics analysis of Salmonella genomes to identify and characterize the repertoire of Type VI Secretion System (T6SS) effectors. The authors combine bioinformatic predictions with experimental validation of one novel toxin domain (Tox-Act1), revealing a unique catalytic activity not previously reported in bacterial toxins. While the study is comprehensive and offers valuable insights into T6SS diversity, the insufficient description of computational methods and limited accessibility of underlying data reduce reproducibility and impact.

Major comments

1. The computational methods are inadequately described in the Materials and Methods section, and the authors did not provide the underlying datasets. These omissions make it impossible to reproduce the analysis or to apply the approach to other organisms.
2. The criteria used to distinguish between T6SS effectors and non-effectors are unclear. The reliance on proximity to structural genes ("guilt-by-association") is insufficient and may have led to the omission of cargo effectors not proximal to these structural genes.
3. No information is provided in the Materials and Methods section about the graph-based clustering strategy mentioned in the main text (Rows 109-111), including the Jaccard index and Louvain algorithm.
4. The definition and identification of T6SS subtypes, including the use of the term "orphan," are not explained (Rows 111-112).
5. The phylogenetic analysis of the newly identified domain Tox-Act1 lacks consistency and detail. For example, Rows 324-326 state: "To predict the function of Tox-Act1, we sought to understand its evolutionary relationship by constructing a phylogenetic tree using the sequences of Tox-Act1, TseH and additional permuted members, such as LRAT and YiiX." However, this contradicts Rows 342-344 and Figure 4A, which describe the phylogenetic tree as being built from permuted NlpC/P60 members, and indicate that a single query was used for PSI-BLAST, marked with a red star. It is unclear whether Tox-Act1, TseH, or another sequence was used as the initial PSI-BLAST query.
6. The Tox-Act1 domain investigated is labeled as an acyltransferase, but the evidence presented supports only phospholipid-degrading activity. In my opinion, the naming should better reflect the activity demonstrated by the data.
7. Table S1 should include representative protein accessions for each T6SS toxin domain. This is essential for evaluating the novelty of the identified domains and for enabling their use in future analyses. The repeated use of "This study" (96 times) as a reference, without further detail, is confusing and unhelpful. In my view, referencing the current study is appropriate only when the manuscript provides sufficient information on the corresponding domain.
8. In general, the authors should place greater emphasis on ensuring that the proteins and genomes analyzed in this study can be reliably identified. Genomic accessions and locus tags should be traceable in public databases such as NCBI, and the supplemental information must correspond accurately to the main text. For example, I was unable to find information on FD01543424_00914, which was used as the query for the alignment of STox_15 (the name used in the supplemental information, while in the main text it is referred to as Tox-Act1; see related comment below).
9. A supplementary table listing all Salmonella effectors and their domain annotations is missing. This is essential for transparency, reproducibility, and future use of the data.
10. The GitHub repository contains a large volume of data and code but lacks detailed documentation and clear instructions, including example files. This greatly limits reproducibility and usability. The current organization of the repository makes it difficult to locate specific results; for example, Tox-Act1 is referred to as STox_15 in the GitHub files, but this is not mentioned in the manuscript. The authors should improve data organization and provide a README file for clarity.

Minor comments

1. The introduction should discuss previous work on Salmonella T6SS effectors, including Blondel et al. (2023) (ref 71 in the manuscript), Amaya et al. (2022), and Amaya et al. (2024).
2. In Figure 1C, genomic examples should include strain names and locus tags.
3. In Figure 1F, 'ND' should be replaced with 'Unknown' or 'Not Determined'.
4. Figure 1E is overly complex and, in my opinion, does not add value, especially since the accompanying text is sufficient on its own. Moreover, the authors acknowledge that their initial analysis missed the similarity between Tox-Act1 and both DUF4105 and the TseH effector, which raises concerns about the accuracy and usefulness of this graph.
5. Figure 3D lacks information about the number of replicates (n=?).
6. Discrepancies in domain annotations:
   • Row 232: STox_47 is missing from Table S1.
   • Row 233: STox_18 is pore-forming and STox_53 is a nuclease (per Table S1), which contradicts the main text.
7. Multiple grammatical and typographical errors exist throughout the text, including:
   • Row 41: "provide" should be "provides"
   • Rows 131, 222: "immunities" should be "immunity proteins"
   • Rows 170, 253, 288: "thee" should be "three"
   • Row 388: "corresponds" should be "correspond"
   • Row 389: "chomatogram" should be "chromatogram"
8. Rows 257-259: The claim that PAAR and RHS domains assist in translocation across the bacterial inner membrane is presented as fact, but this is only a hypothesis and should be stated more cautiously.
9. Figure 3A: The selection of representative genomic loci is unclear. For example, FD01843896 is shown in the figure, but cloning was performed using FD01848827, and the HHPred analysis was based on FD01543424. The rationale for using different sequences at each step should be clarified.
10. Rows 296-299: The absence of a secretion assay in the study is notable. If this is due to the inability to activate the SPI-6 T6SS of Salmonella enterica serovar Typhimurium, as discussed in these lines, it should be explicitly mentioned in the text.
11. Figure 4C (sequence logo) is not described in the Materials and Methods section.
12. Row 467: The retrieval date of the gff files from the 10KSG database is missing.
13. Rows 474-476: The domain models used for T6SS cluster prediction are not described.

Significance

This is a comprehensive study involving a large number of Salmonella genomes, potentially identifying many new T6SS effectors and toxic activities. One new domain analyzed in this work is experimentally investigated and shown to have a unique catalytic activity not previously observed in toxins. However, the bioinformatic methods are not described in sufficient detail, making it difficult to assess or reproduce the work. Protein accession numbers are missing, even for representative toxins, and locus tags are not traceable, making the identified effectors not readily accessible. There are many inaccuracies throughout the text and supplemental data. The Tox-Act1 domain investigated is labeled as an acyltransferase, but the evidence only supports phospholipid-degrading activity. While the study includes many graphs and histograms, they often obscure the main findings. Consequently, the audience is likely to be limited.

Nevertheless, despite these concerns, I believe this is an important work that could be valuable to the broad community once a more thorough revision is undertaken, not only by addressing the specific comments raised, but also by rechecking the analyses, reorganizing the presentation, and ensuring that all data and annotations are clearly accessible and traceable.

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Referee #2

Evidence, reproducibility and clarity

Summary:

The manuscript titled "Genome-directed study reveals the diversity of Salmonella T6SS effectors and identifies a novel family of lipid-targeting antibacterial toxins" presents a comprehensive in silico analysis of T6SS-associated effector and immunity genes across approximately 10,000 Salmonella genomes. In addition, the authors selected one of the newly identified effectors, Tox-Act1, for detailed biochemical characterization. To my knowledge, this study represents the most extensive genome-wide mining effort to date for T6SS-associated effectors and immunity proteins in Salmonella, employing a range of state-of-the-art computational prediction tools. The in vitro enzymatic characterization of Tox-Act1 further validates the in silico approach and adds a novel functional perspective to the dataset. Overall, the study provides a rich and comprehensive dataset. However, for readers without a strong bioinformatics background, the logic and workflow of the in silico prediction pipeline may be challenging to follow. Consequently, my comments focus primarily on the biochemical analysis of Tox-Act1, rather than the computational aspects of the study.

Major comments:

1. In Figure 3, the authors first demonstrated that Tox-Act1 and Imm-Act1 constitute a functional antibacterial toxin-immunity pair using a heterologous E. coli expression system. They then proceeded to an in vivo mouse colonization model, showing that prey cells lacking the tox-act1/imm-act1 locus exhibited reduced competitiveness when co-infected with a Salmonella strain carrying the endogenous tox-act1, compared to a ∆tssL mutant. As this is the first report identifying and characterizing Tox-Act1 function in Salmonella, the authors should provide additional experimental evidence addressing the following key points: (i) Whether Tox-Act1 is secreted by Salmonella in a T6SS-dependent manner; (ii) Whether target cells lacking imm-act1 (in either Salmonella or E. coli) can be intoxicated by Salmonella secreting Tox-Act1; (iii) Whether the observed competitive advantage in vitro conferred by Tox-Act1 is dependent on its phospholipase activity. Given that Salmonella T6SS can be activated by hns deletion, such experiments should be feasible and are crucial for the functional validation of any newly identified T6SS effector. Addressing these points would substantially strengthen the mechanistic basis of the study and reinforce the biological importance and relevance of Tox-Act1.
2. In Figure 4, the authors present the evolutionary relationship between Tox-Act1 and the previously identified T6SS effector TseH from Vibrio, and they propose that these two effectors may share similar enzymatic activities and overlapping cellular targets. Given the ongoing debate and unresolved questions regarding the biochemical function of TseH, the authors should leverage their established in vitro phospholipase assay to test whether TseH exhibits phospholipase activity similar to that of Tox-Act1. Demonstrating such activity would not only substantiate the proposed functional conservation but also provide critical biochemical insight into a long-standing question in the T6SS field.
3. In Figures 5C and 5D, the authors performed lipidomic analyses on E. coli cells heterologously expressing Tox-Act1 and reported that specific phospholipid species are altered in a manner dependent on Tox-Act1's phospholipase activity. However, the data presented in Figure 5D only include changes in the abundance of PG, FFA, LPG, and LPE. To provide a comprehensive overview of the lipidomic alterations, the authors should present the full dataset of all identified phospholipid species. This is essential to evaluate the extent and specificity of lipid remodeling induced by Tox-Act1. It is currently unclear whether the observed reduction in PG is the only statistically significant change or if additional lipid species were similarly affected but not shown. Furthermore, the authors claim that Tox-Act1 functions as a phospholipase A1. However, in Figures 5A and 5B, the signal corresponding to intact phospholipids remains relatively high, raising concerns about the apparent weak enzymatic activity in this assay. This observation contrasts with previously characterized phospholipase toxins in the antibacterial toxin field, such as Tle1 from Burkholderia, which exhibit robust activity under in vitro conditions. To substantiate the enzymatic potency of Tox-Act1 and clarify this discrepancy, the authors should include a side-by-side comparison using the same in vitro assay with a well-established phospholipase toxin (e.g., Tle1) as a positive control. This would allow for a direct evaluation of the relative enzymatic strength of Tox-Act1 and support the interpretation of its lipid-targeting function.

Minor Comments:

1. Line 32: Please specify "Type VI Secretion System (T6SS)" when first introducing the term in the abstract, to ensure clarity for a broad readership.
2. There are inconsistencies between the numerical values reported in the main text and those shown in the figures. For instance, the manuscript repeatedly states that approximately 10,000 Salmonella genomes were analyzed in the in silico search, whereas Figure 1 indicates a total of 10,419 genomes. Similarly, Line 108 mentions 42,560 genomic sites, yet Figure 1 displays a count of 49,080. Please ensure that all numerical data are consistent across the manuscript and figures to avoid confusion or misinterpretation.
3. The definition of "Orphan clusters" is not provided. Please specify the criteria used to define these clusters and clarify the rationale for grouping them separately from the other clusters (i1-i4) shown in Figure 1A. It would be helpful to explicitly state how they differ from the canonical clusters.
4. Lines 114-119: The sentence structure in this section is overly long and difficult to follow. Please revise this portion for clarity and conciseness to ensure that the intended message is clearly conveyed.
5. The color coding in Figure 1C is incomplete; only a few categories are indicated in the legend. Please revise the legend to include all color codes used in the figure for accurate interpretation.
6. Lines 278-280: The authors state that "cells lysed without losing their rod shape, which suggests that the peptidoglycan was not affected... indicating that this is not the target of Tox-Act1." Please provide appropriate references or supporting evidence for this interpretation. Clarification is needed to explain the morphological criteria being used to infer peptidoglycan integrity.
7. Please define "competitive index" in the legend of Figure 3D to ensure the metric is clearly understood by readers unfamiliar with the term.
8. It is unclear to me why the author use (data not shown) in Line 315. Please provide evidence to support the claim in the paragraph.
9. In Figure 4D, the authors compare the activity of wild-type and catalytic mutant Tox-Act1, but protein expression levels are not shown. Please include immunoblot or other relevant data to confirm equivalent expression of both constructs, to rule out differential expression as a confounding factor.

Referee cross-commenting

I agree with Reviewer #3 that the authors should provide more details on their search for better reproducibility.

Significance

This manuscript presents a large-scale in silico analysis of Salmonella T6SS effectors and immunity proteins, accompanied by the biochemical characterization of a novel phospholipase effector, Tox-Act1. The genome-wide dataset is comprehensive, representing the most extensive mining effort of its kind to date. The study is strengthened by in vitro validation of Tox-Act1 activity and its role in interbacterial competition. However, the manuscript would benefit from additional experimental data to confirm key mechanistic aspects, including T6SS-dependent secretion of Tox-Act1, its toxicity toward target cells lacking immunity, and the contribution of phospholipase activity to its antibacterial function. Comparative assays with established T6SS phospholipases (e.g., Tle1) are recommended to clarify enzymatic potency. Further, the authors should apply their phospholipase assay to test TseH activity and resolve long-standing questions in the field. Several areas also require clarification or correction, including inconsistencies in reported genome counts, incomplete figure legends, unclear terminology (e.g., "Orphan clusters"), and missing experimental controls (e.g., protein expression levels, full lipidomic dataset). Minor edits to improve clarity and consistency are also suggested. Overall, the study is significant and of high potential impact but requires additional experimental validation and revisions to improve clarity and completeness.

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Referee #1

Evidence, reproducibility and clarity

Summary: In this study, authors used in silico approaches to analyse 10,000 bacterial genomes and identified 128 candidate effectors secreted via the T6SS of Salmonella. Among these, Tox-Act1 was selected for detailed characterisation. The authors demonstrated that Tox-Act1 harbours a permuted NlpC/P60 catalytic domain with phospholipase activity, targeting key membrane lipids. Furthermore, they confirmed that Tox-Act1 is secreted in a T6SS-dependent manner and enhances bacterial competitiveness during gut colonisation in mice, providing new insights into lipid-targeting toxin domains in interbacterial interactions. My concerns raised are all minor and should be readily addressable by the authors.

Minor Concerns:

Line 279-280: The statement that the peptidoglycan is not a target of Tox-Act1 is somewhat strong at this stage of the manuscript. The preservation of cell shape does not necessarily imply that the peptidoglycan remains unaltered at a subcellular level. Given that Tox-Act1 belongs to the NlpC/P60 family, members of which include known peptidases, the authors should moderate this assertion. Replacing "is not" with "is likely not" or using conditional phrasing would be more appropriate here.

Lines 328-331: The conclusion that the Tox-Act1 clade is deployed in biological conflicts is not fully explained or substantiated. The authors are encouraged to provide a brief rationale to support this conclusion.

Figure 4D: There appears to be a labelling inconsistency. The immunity protein is referred to as "Slmm15," which may relate to the original name of Tox-Act1 (i.e., STox_15), but the correct label should likely be "Imm-Act1."

Line 401 and elsewhere: The correct spelling is "L-arabinose" with a capital "L". The manuscript should be checked for consistency in this regard.

Throughout the text and figures: Bacterial species names are often incorrectly formatted, e.g., "S. Panama" (Line 226) should be written in scientific style as S. panama, with italics and the species name in lowercase. A systematic revision of species names is recommended to enhance rigour.

Figure 3D: The X-axis labelling is somewhat confusing. The use of terms such as "attackers" and "prey" is misleading in this context, as the experiment tests the in vivo survival capacity of different Salmonella strains (WT or T6SS mutants mixed with toxin/immunity double mutants) in a mouse model, rather than a direct bacterial killing assay. Clarifying this would greatly improve readability.

Significance

Overall, this study is well-executed. The approach used to identify a previously uncharacterised diversity of T6SS effectors in Salmonella is robust and provides a valuable framework that could be extended to other systems involved in interbacterial competition. This renders the work relevant and of interest for publication. While the manuscript occasionally lacks clarity in explaining the rationale behind certain experimental choices, the narrative remains generally accessible.

Field of expertise: Secretion systems, interbacterial competition, bacterial predation, live-cell imaging, protein network

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

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Reply to the reviewers

Manuscript number: RC-2023-02191

Corresponding author: Jan Rehwinkel

1. General Statements

The authors wish to thank all three reviewers and the Review Commons team for carefully evaluating our study. We have addressed all points raised as detailed below.

We have thoroughly revised our bulk RNAseq analysis, which is now performed at the transcript level using the latest GENCODE release. We have updated Figure 3 and associated supplementary figures and tables. This change from gene to transcript level was important for accurate motif analysis as requested by reviewer 2: matching promoters to individual IFN-regulated transcripts – rather than aggregating all promoters per gene – avoids significant signal dilution. This strategy yields higher-resolution expression data and is biologically preferable. Indeed, several well characterised IFN-regulated RNAs (e.g., the ADAR1-202 transcript encoding the p150 isoform) originate from promoters located far from the constitutive promoters of their host genes. In our revised manuscript, we now provide in the new supplementary figure 13 the requested promoter motif analysis. Using two computational approaches – de novo motif search and analysis of a curated motif database – we find strong enrichment of interferon-stimulated response elements (ISREs) in promoters of type I IFN regulated transcripts. No other motifs reached similarly high levels of enrichment, and our analysis did not reveal differences between different type I IFNs. These new data show that all type I IFNs engage a common regulatory pathway, supporting our overall conclusion that different type I IFNs do not induce qualitatively different responses in PBMCs.

Regrettably, in the process of analysing the bulk RNAseq data at transcript level, we noticed that our original lncRNA analysis contained numerous false positives. Closer inspection showed that many “differentially expressed” LNCipedia models were likely not full-length transcripts and commonly shared a single IFN-induced set of exons that artificially inflated expression estimates for every overlapping model. To correct this issue, we replaced LNCipedia with the latest high-quality non-coding RNA catalogue from GENCODE, most entries of which were defined by full-length RNA sequencing [1]. We also tightened our filtering criteria and now report only transcripts that are robustly expressed in our dataset and are either classified as high-confidence by GENCODE or robustly supported at every splice junction by our RNAseq.

We hope our manuscript is sufficiently improved and suitable for publication in PLoS Biology. New or revised text is highlighted in green in our revised manuscript.

2. Point-by-point description of the revisions

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Reviewer #1

Evidence, reproducibility and clarity:

The study can be directly connected to a landmark paper in the field (Mostafavi et al. , Cell 2016). By comparison with this study, the authors use improved technologies to address the question if and how responses to type I IFN differ between human peripheral blood-derived cells types. In line with Mostafavi et al. the authors conclude that only a comparably low number of interferon-stimulated genes (ISG) is induced in all cell types and that considerable differences exist between cell types in the IFN-induced transcriptome. The authors address a second relevant aspect, whether and how the many different subtypes of type I IFN differ in the way they engage IFN signals to produce transcriptome changes. The data lead the authors to conclude that any differences are of quantitative rather than qualitative nature.

The authors' conclusions are based on a mass cytometry approach to phenotype STAT activation in different cell types, bulk RNA sequencing to study ISG expression in PBMC, and single cell sequencing to study ISG responses in individual cell types. The data are solid, clear and reproducible in biological replicates (eg different blood donors).

Significance: While some of the data can be considered confirmatory, the comprehensive analysis of cell-type specificity and IFN-I subtype specificity advances the field and provides a reference for future analyses. The study is complete and there is no obvious lack of a critical experiment. The number of scientists interested in the multitude of open questions around type I IFN is large, thus the study is likely to attract a broad readership.

We thank the reviewer for her/his positive assessment of our study.

The biggest limitation is to my opinion the low sequencing depth of scRNAseq which is clearly the downside of this technology. Using 11 hematopoietic cell types and bulk RNA sequencing the total number of ISG was determined to be 975 by Mostafavi et al. and the core ISG numbered 166. This is in stark contrast to this studies' 10 core ISG. The authors limitations paragraph should discuss the fact that scRNAseq reduces the overall ISG number that can be analyzed.

Thank you for this valid comment. We amended the limitations paragraph as requested. We agree that the Mostafavi et al. 2016 Cell paper [2] is important but note that there are many differences to our study: Mostafavi et al. use mice, a seemingly very high IFN dose (10,000 Units) and microarrays (not RNAseq).

A minor point concerns the 25 supplementary figures of the study. There must be a better way to support the conclusions with the necessary data.

We agree that our supplementary materials are extensive. However, this is not unusual for studies reporting multiple large datasets. We would be delighted to organise our supplementary information differently in due course according to journal guidelines.

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Reviewer #2

Evidence, reproducibility and clarity:

The manuscript entitled “Single-cell analysis of signalling and transcriptional responses to type I interferon" by Rigby et al. examines the response to type I IFN subtypes in PBMCs using an integrative proteomics and transcriptomics approach. Some of the analysis could be deepened to provide better insights into what governs the magnitude of change in gene expression as well as the cell type-specific response to expression and generate more excitement for the study.

We thank the reviewer for evaluating our study and the suggestions made.

*Major Comments: *

• Although the authors appropriately conclude that type I IFNs induce qualitatively similar, the response is not quantitatively similar. What elements in the promoters of ISGs make them more responsive to IFN subtypes? (PMID: 32847859) We thank the reviewer for the suggestion to study the promoters of genes regulated by type I IFNs. The analyses outlined below were performed by A. Fedorov, who is now a new co-author of our study. To investigate promoter features that might underlie the observed transcriptional responses across type I IFNs, we first performed a de novo*motif search using STREME [3] on our bulk RNAseq dataset (Figure 3). Specifically, we compared the promoters of transcripts that were up- or down-regulated by each IFN subtype (e.g., IFN-β-induced) either with one another or with promoters of robustly expressed RNAs that remained unresponsive to any treatment. No significant motifs emerged from these comparisons, except when we compared promoters of IFN-induced transcripts to the background set of unresponsive RNAs. This comparison consistently yielded strong enrichment of interferon-stimulated response element (ISRE)-like motifs in the promoters of up-regulated RNAs (new Figure S13a).

Next, we conducted a complementary analysis using known transcription factor (TF) motifs from the JASPAR database [4]. We screened all promoters of annotated RNAs using clustered JASPAR motifs and Z-standardised motif scores relative to all high-confidence GENCODE RNAs, including those not expressed in PBMCs. We reasoned that TFs actively mediating IFN responses would likely bind promoters with high motif scores (Z ≥ 2), while promoters with low scores (Z ≤ -1) would represent an unregulated background. This approach produced two sets of RNAs per TF cluster: putatively regulated and unregulated. We then restricted each set to RNAs expressed in our dataset and associated each transcript with its estimated fold change in response to each type I IFN, regardless of statistical significance. Next, we compared median fold changes between the likely regulated and unregulated sets across all TF clusters and IFN subtypes (Figure S13b). Among all tested TF motifs, only the ISRE-like cluster showed strong and consistent associations with transcriptional changes across all IFN subtypes. We also observed statistically significant but much weaker associations for other TFs, including a known negative regulator of innate antiviral signaling, NRF1 [5]. However, effect sizes for these motifs were dwarfed by those of ISRE-like motifs, suggesting that no JASPAR TFs other than those within the ISRE-like cluster play a major role in PBMCs under our conditions. Overall, these findings support the idea that all type I IFNs engage a common regulatory pathway, differing primarily in the magnitude rather than the nature of their transcriptional effects.

How do they relate to the activation of kinases by IFN subtypes?

We did not analyse the activation of the canonical kinases (i.e., TYK2 and JAK1) downstream of IFNAR. This would be interesting and may be possible using phospho-specific antibodies to these kinases in our CyTOF setup. However, this would require a very large investment of time and resources to identify specific antibodies, optimise a new CyTOF staining panel and to acquire and analyse new datasets. We therefore believe this should be pursued as a separate future study.

*Are there distinct features that dictate differential responses in monocytes and lymphocytes? *

Following the computational approach described above, we applied STREME to identify DNA motifs that could distinguish promoters associated with monocyte- and lymphocyte-specific ISGs. Regrettably, this analysis did not yield any significant motifs, likely due in part to the limited number of genes in each category.

• Figure 2a, d-h - Consider using the same scale for all heatmaps. This will allow for comparison of pSTATs median expression. Consider increasing the range in the color scale as some of the subtle changes in STAT phosphorylation across subtypes are not well appreciated. This also applies to Supplementary figures related to Figure 2.*

Thank you for this suggestion. We tried using the same scale for all heatmaps. However, given that the values for pSTAT1 are higher than those for other pSTATs, the resulting heatmaps did not show differences for the other pSTATs well. We therefore decided to leave these panels unchanged. Please also note that Figures 2b and S3b provide comparison between pSTATs (and other markers) using the same scale.

Minor Comments:

• The title of subsections are a bit generic (e.g "Analysis of the signalling response to type I IFNs using mass cytometry". Consider updating them to reflect some of the findings from each analysis.* Thank you for this suggestion. We have amended sub-headers accordingly.

• Figure 3 and S3 - Increase the heatmap scale to better appreciate changes in gene expression.*

The scales have been enlarged for better visibility as requested.

• Consider combining panel a and b in figure S7 for better contrasts of the response to IFNa1 or IFNb. *

Thank you for the suggestion. We combined these panels.

• Figure 4 - The authors could visualize ISGs that are unique across IFN types or cell types. *

Figure 5 and several accompanying supplementary figures already depict ISGs unique to IFN subtypes or cell types. Whilst we appreciate the suggestion, we prefer not to add additional figures to avoid redundancies.

• The gene ontology analysis should be performed with higher statistical stringency to capture the most significant IFN responsive processes. *

Thank you for this comment. We changed the presentation of the GO analysis in Fig S11 by sorting on p-value (instead of % of hits in category). We hope this shows more clearly that GO category enrichment amongst genes encoding IFN-induced transcripts had high statistical significance (log10 p-values of about -5 or lower for many categories).

Significance:* ** The authors provide an extensive compendium of cell type specific changes in response to type I IFN stimulation. They have created a public repository which extends the value of this dataset. *

Audience: *** This is a valuable resource for immunologists, virologists, and bioinformaticians.*

Thank you for these encouraging comments.

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Reviewer #3

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Evidence, reproducibility and clarity:

*Summary *

Rigby and collaborators analyzed the signaling responses and changes in gene expression of human PBMCs stimulated with different IFN type I subtypes, using mass cytometry, bulk and single-cell RNA sequencing. Their study represents the first single-cell atlas of human PBMCs stimulated with five type I IFN subtypes. The generated datasets are useful resources for anyone interested in innate immunity. The data and the methods are well presented. We thus recommend publication.

Thank you for your positive assessment of our work and for recommending publication.

*Major comments: *

• *

*Two of the key conclusions are not very convincing. *

• *

First, the authors claim that the magnitude of the responses varied between the 5 types of IFNs, however, as they point out in the 'limitation' paragraph, doses of the different IFNs were normalized using bioactivity. Knowing that this bioactivity is based on assays performed on A549 lung cells, this normalization likely induces a bias. How do the authors explain similar antiviral bioactivity but differing magnitudes of modulation of ISG expression? Would the authors expect the same differences of expression between the several IFNs tested in A549 cells? We thus recommend being very cautious when comparing magnitude of the response between the 5 types of IFNs.

We thank the reviewer for this important point and included the following reasoning in our discussion:

“An important technical consideration for our study was the normalisation of type I IFN doses used to treat cells (see also ‘Limitations of the study’ below). We relied on bioactivity (U/ml) that is measured by the manufacturer of recombinant type I IFNs using a cytopathic effect (CPE) inhibition assay. In brief, the lung cancer cell line A549 is treated with type I IFN and is infected with the cytopathic encephalomyocarditis virus (EMCV). Control cells not treated with IFN are killed by EMCV, whereas cells treated with sufficient IFN survive. How, then, is it possible that different type I IFNs induce differing magnitudes of STAT phosphorylation and ISG expression despite being used at the same bioactivity? Cell survival in the CPE inhibition assay may be due to one or a few ISGs. Indeed, single ISGs can mediate powerful antiviral defence. For example, MX1 is crucial for host defence against influenza A virus [6]. Thus, similar bioactivity of different IFNs in A549 cells against EMCV-triggered cell death may not reflect the breadth of effects on many ISGs. Moreover, IFN-induced survival of A549 cells following EMCV infection is a binary readout. Induction of the relevant ISG(s) mediating protection beyond a threshold required for cell survival is unlikely to register in this assay. Thus, similar antiviral bioactivity (in the CPE inhibition assay) and differing magnitudes of modulation of ISG expression (at transcriptome level) are compatible.”

We believe inclusion of this paragraph demonstrates an appropriate level of caution in our data interpretation. Further, we would expect to make similar observations if we were to apply transcriptomic analysis to A549 cells treated with different type I IFNs. However, given our focus in this study on primary, normal cells, we decided not to pursue work with the transformed and lab adapted A549 cell line.

Second, the qualitatively different responses to type I IFN subtypes claimed by the authors were not apparent. This seems true at the level of the bulk population (Fig. S10) but not at cell-type level (Fig. S15/S16).

We believe there may be a misunderstanding here. In relation to Figure S10, we do not claim “qualitatively different responses to type I IFN subtypes”. Instead, we conclude that “differences in expression between the different type I IFNs were quantitative” (page 8; lines 229-230, now: 238-239). Moreover, Figures S15/S16 (now: S16/S17) do not refer to analyses of responses to different type I IFN subtypes.

The authors state (line 311-312) that 'Consistent with our bulk RNAseq data, differences were again quantitative rather than qualitative' at the cell-type level. The response between cell types seems very different to us since a core set of only 10 ISGs are shared by all cell types and all 5 type I IFNs. Knowing that the expression of hundreds, sometimes thousands of genes, are induced by IFN, this seems like a rather small overlap (and thus qualitatively different responses). Fig S15 and S16 nicely illustrate that the responses are qualitatively different between cell-type. Please modify this conclusion accordingly.

Thank you for highlighting this. The statement in lines 311-312 does not refer to differences between cell types but to differences between type I IFN subtypes. We are sorry this was not clear and changed this sentence (now lines 357-358). Furthermore, we have made it clearer in the revised text that qualitative differences were observed between cell types (e.g. lines 329 and 350-352).

*No additional experiments are needed to support the claims. However, we believe that two additional analyses could provide useful information. *

• *

The levels of IFNAR1 and IFNAR2 expressed at the plasma membrane probably vary between cell types and may thus influence the magnitude of the IFN response. While it would be difficult to measure these levels by flow cytometric analysis on the different cell types, could the authors extract information from their scRNAseq analysis on the expression level of IFNAR1/2 in all cell types? This would give a hint about potential differences in expression (and thus in magnitude).

We analysed IFNAR1/2 transcript levels in our scRNAseq dataset (Figure R1 below). Unfortunately, for many cells, IFNAR1 and IFNAR2 transcripts were not detected (see width of violin plots at zero), probably due to low sequencing depth inherent to scRNAseq analysis. We therefore prefer not to draw conclusions from these data.

Could the authors investigate further the expression of lncRNAs at the single-cell levels? It would be useful to also define a core set of lncRNAs that are shared between cell types and IFN subtypes. If such a core set does not exist (since lncRNAs are less conserved than coding genes), it would be nice to mention it.

Thank you for this suggestion. The expression of lncRNAs is generally lower than protein-coding genes, resulting in high drop-out rates in 10X datasets. Indeed, Zhao et al. comment that “current development of single-cell technologies may not yet be optimized for lncRNA detection and quantification” [7]. We only detected a small number of lncRNAs in our scRNAseq analysis, and only four lncRNAs were significantly differentially expressed between cell types. We thus could not perform a meaningful analysis of lncRNAs in our scRNAseq dataset. This is now mentioned in the limitations paragraph at the end of the manuscript.

Minor comments:

There is a typo in line 355 Fig.4C =>6C.

Thank you for spotting this.

***Referees cross-commenting** *

We agree with Reviewer 1 that the low sequencing depth of scRNAseq restricts the analysis and must be discussed in the 'limitation' paragraph. This would explain why the authors identified only 10 ISGs that are common to all cell types and all 5 IFN subtypes. Of note, as a comparison, Shaw et al (10.1371/journal.pbio.2004086) identified a core set of 90 ISGs that are upregulated upon IFN treatment in cells isolated mainly from kidney and skin of nine mammalian species ("core mammalian ISGs"). It is thus expected that stimulated blood cells isolated from a single mammalian species share more than 10 ISGs.

We amended the limitations section as requested. Shaw et al. [8] used a single type I IFN (universal or IFNα, depending on species) at a very high dose (1000 U/ml). Taken together with the use of bulk RNAseq in this study, it is unsurprising that our work identified fewer core ISGs. We believe our small list of core ISGs is nonetheless both a high confidence and a high utility set of ISGs: these genes are induced by multiple type I IFNs, in all major cell types in blood and their regulation can be measured even when sequencing depth is low.

Significance (Required)

*Multiple single-cell RNAseq analysis of PBMCs, stimulated or not, have been previously performed in multiple contexts (for instance with PBMCs isolated from the blood of patients infected with influenza virus or SARS-CoV-2). The technical advance is thus limited. *

• *

*However, the work represents a conceptual advance for the field since it provides the first single-cell atlas of PBMCs stimulated with five type-I IFN subtypes. The generated datasets represent a great resource for anyone interested in innate immunity (virologists, immunologists and cancerologists). *

• *

Of note, we are studying innate immunity in the context of RNA virus infection but we have no expertise on scRNA sequencing. We may thus have missed a flaw in the analyses.

We thank the reviewer for their positive assessment of the advances of our study and the value of our IFN resource.

A

B

C

D

Figure R1. IFNAR1/2 expression in scRNAseq data.

Violin plots showing expression of IFNAR1 (A,C) or IFNAR2 (B,D) in different cell types. In (A,B), data were pooled across conditions. In (C,D), data are shown separately for unstimulated control cells and cells stimulated with different type I IFNs.

References

Kaur G, Perteghella T, Carbonell-Sala S, Gonzalez-Martinez J, Hunt T, Madry T, et al. GENCODE: massively expanding the lncRNA catalog through capture long-read RNA sequencing. bioRxiv. 2024. Epub 20241031. doi: 10.1101/2024.10.29.620654. PubMed PMID: 39554180; PubMed Central PMCID: PMCPMC11565817. Mostafavi S, Yoshida H, Moodley D, LeBoite H, Rothamel K, Raj T, et al. Parsing the Interferon Transcriptional Network and Its Disease Associations. Cell. 2016;164(3):564-78. Epub 2016/01/30. doi: 10.1016/j.cell.2015.12.032. PubMed PMID: 26824662; PubMed Central PMCID: PMCPMC4743492. Bailey TL. STREME: accurate and versatile sequence motif discovery. Bioinformatics. 2021;37(18):2834-40. doi: 10.1093/bioinformatics/btab203. PubMed PMID: 33760053; PubMed Central PMCID: PMCPMC8479671. Rauluseviciute I, Riudavets-Puig R, Blanc-Mathieu R, Castro-Mondragon JA, Ferenc K, Kumar V, et al. JASPAR 2024: 20th anniversary of the open-access database of transcription factor binding profiles. Nucleic acids research. 2024;52(D1):D174-D82. doi: 10.1093/nar/gkad1059. PubMed PMID: 37962376; PubMed Central PMCID: PMCPMC10767809. Zhao T, Zhang J, Lei H, Meng Y, Cheng H, Zhao Y, et al. NRF1-mediated mitochondrial biogenesis antagonizes innate antiviral immunity. The EMBO journal. 2023;42(16):e113258. Epub 20230706. doi: 10.15252/embj.2022113258. PubMed PMID: 37409632; PubMed Central PMCID: PMCPMC10425878. Grimm D, Staeheli P, Hufbauer M, Koerner I, Martinez-Sobrido L, Solorzano A, et al. Replication fitness determines high virulence of influenza A virus in mice carrying functional Mx1 resistance gene. Proceedings of the National Academy of Sciences of the United States of America. 2007;104(16):6806-11. Epub 20070410. doi: 10.1073/pnas.0701849104. PubMed PMID: 17426143; PubMed Central PMCID: PMCPMC1871866. Zhao X, Lan Y, Chen D. Exploring long non-coding RNA networks from single cell omics data. Comput Struct Biotechnol J. 2022;20:4381-9. Epub 20220804. doi: 10.1016/j.csbj.2022.08.003. PubMed PMID: 36051880; PubMed Central PMCID: PMCPMC9403499. Shaw AE, Hughes J, Gu Q, Behdenna A, Singer JB, Dennis T, et al. Fundamental properties of the mammalian innate immune system revealed by multispecies comparison of type I interferon responses. PLoS Biol. 2017;15(12):e2004086. Epub 2017/12/19. doi: 10.1371/journal.pbio.2004086. PubMed PMID: 29253856.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

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Referee #3

Evidence, reproducibility and clarity

Summary

Rigby and collaborators analyzed the signaling responses and changes in gene expression of human PBMCs stimulated with different IFN type I subtypes, using mass cytometry, bulk and single-cell RNA sequencing. Their study represents the first single-cell atlas of human PBMCs stimulated with five type I IFN subtypes. The generated datasets are useful resources for anyone interested in innate immunity. The data and the methods are well presented. We thus recommend publication.

Major comments:

Two of the key conclusions are not very convincing.

First, the authors claim that the magnitude of the responses varied between the 5 types of IFNs, however, as they point out in the 'limitation' paragraph, doses of the different IFNs were normalized using bioactivity. Knowing that this bioactivity is based on assays performed on A549 lung cells, this normalization likely induces a bias. How do the authors explain similar antiviral bioactivity but differing magnitudes of modulation of ISG expression? Would the authors expect the same differences of expression between the several IFNs tested in A549 cells? We thus recommend being very cautious when comparing magnitude of the response between the 5 types of IFNs.

Second, the qualitatively different responses to type I IFN subtypes claimed by the authors were not apparent. This seems true at the level of the bulk population (Fig. S10) but not at cell-type level (Fig. S15/S16). The authors state (line 311-312) that 'Consistent with our bulk RNAseq data, differences were again quantitative rather than qualitative' at the cell-type level. The response between cell types seems very different to us since a core set of only 10 ISGs are shared by all cell types and all 5 type I IFNs. Knowing that the expression of hundreds, sometimes thousands of genes, are induced by IFN, this seems like a rather small overlap (and thus qualitatively different responses). Fig S15 and S16 nicely illustrate that the responses are qualitatively different between cell-type. Please modify this conclusion accordingly.

No additional experiments are needed to support the claims. However, we believe that two additional analyses could provide useful information.

The levels of IFNAR1 and IFNAR2 expressed at the plasma membrane probably vary between cell types and may thus influence the magnitude of the IFN response. While it would be difficult to measure these levels by flow cytometric analysis on the different cell types, could the authors extract information from their scRNAseq analysis on the expression level of IFNAR1/2 in all cell types? This would give a hint about potential differences in expression (and thus in magnitude).

Could the authors investigate further the expression of lncRNAs at the single-cell levels? It would be useful to also define a core set of lncRNAs that are shared between cell types and IFN subtypes. If such a core set does not exist (since lncRNAs are less conserved than coding genes), it would be nice to mention it.

Minor comments:

There is a typo in line 355 Fig.4C =>6C.

Referees cross-commenting

We agree with Reviewer 1 that the low sequencing depth of scRNAseq restricts the analysis and must be discussed in the 'limitation' paragraph. This would explain why the authors identified only 10 ISGs that are common to all cell types and all 5 IFN subtypes. Of note, as a comparison, Shaw et al (10.1371/journal.pbio.2004086) identified a core set of 90 ISGs that are upregulated upon IFN treatment in cells isolated mainly from kidney and skin of nine mammalian species ("core mammalian ISGs"). It is thus expected that stimulated blood cells isolated from a single mammalian species share more than 10 ISGs.

Significance

Multiple single-cell RNAseq analysis of PBMCs, stimulated or not, have been previously performed in multiple contexts (for instance with PBMCs isolated from the blood of patients infected with influenza virus or SARS-CoV-2). The technical advance is thus limited.

However, the work represents a conceptual advance for the field since it provides the first single-cell atlas of PBMCs stimulated with five type-I IFN subtypes. The generated datasets represent a great resource for anyone interested in innate immunity (virologists, immunologists and cancerologists).

Of note, we are studying innate immunity in the context of RNA virus infection but we have no expertise on scRNA sequencing. We may thus have missed a flaw in the analyses.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #2

Evidence, reproducibility and clarity

The manuscript entitled "Single-cell analysis of signalling and transcriptional responses to type I interferon" by Rigby et al. examines the response to type I IFN subtypes in PBMCs using an integrative proteomics and transcriptomics approach. Some of the analysis could be deepened to provide better insights into what governs the magnitude of change in gene expression as well as the cell type-specific response to expression and generate more excitement for the study.

Major Comments:

1. Although the authors appropriately conclude that type I IFNs induce qualitatively similar, the response is not quantitatively similar. What elements in the promoters of ISGs make them more responsive to IFN subtypes? (PMID: 32847859) How do they relate to the activation of kinases by IFN subtypes? Are there distinct features that dictate differential responses in monocytes and lymphocytes?
2. Figure 2a, d-h - Consider using the same scale for all heatmaps. This will allow for comparison of pSTATs median expression. Consider increasing the range in the color scale as some of the subtle changes in STAT phosphorylation across subtypes are not well appreciated. This also applies to Supplementary figures related to Figure 2.

Minor Comments:

1. The title of subsections are a bit generic (e.g "Analysis of the signalling response to type I IFNs using mass cytometry". Consider updating them to reflect some of the findings from each analysis.
2. Figure 3 and S3 - Increase the heatmap scale to better appreciate changes in gene expression.
3. Consider combining panel a and b in figure S7 for better contrasts of the response to IFNa1 or IFNb.
4. Figure 4 - The authors could visualize ISGs that are unique across IFN types or cell types.
5. The gene ontology analysis should be performed with higher statistical stringency to capture the most significant IFN responsive processes.

Significance

Significance:

The authors provide an extensive compendium of cell type specific changes in response to type I IFN stimulation. They have created a public repository which extends the value of this dataset.

Audience:

This is a valuable resource for immunologists, virologists, and bioinformaticians.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

The study can be directly connected to a landmark paper in the field (Mostafavi et al. , Cell 2016). By comparison with this study, the authors use improved technologies to address the question if and how responses to type I IFN differ between human peripheral blood-derived cells types. In line with Mostafavi et al. the authors conclude that only a comparably low number of interferon-stimulated genes (ISG) is induced in all cell types and that considerable differences exist between cell types in the IFN-induced transcriptome. The authors address a second relevant aspect, whether and how the many different subtypes of type I IFN differ in the way they engage IFN signals to produce transcriptome changes. The data lead the authors to conclude that any differences are of quantitative rather than qualitative nature. The authors' conclusions are based on a mass cytometry approach to phenotype STAT activation in different cell types, bulk RNA sequencing to study ISG expression in PBMC, and single cell sequencing to study ISG responses in individual cell types. The data are solid, clear and reproducible in biological replicates (eg different blood donors).

Significance

While some of the data can be considered confirmatory, the comprehensive analysis of cell-type specificity and IFN-I subtype specificity advances the field and provides a reference for future analyses. The study is complete and there is no obvious lack of a critical experiment. The number of scientists interested in the multitude of open questions around type I IFN is large, thus the study is likely to attract a broad readership.

The biggest limitation is to my opinion the low sequencing depth of scRNAseq which is clearly the downside of this technology. Using 11 hematopoietic cell types and bulk RNA sequencing the total number of ISG was determined to be 975 by Mostafavi et al. and the core ISG numbered 166. This is in stark contrast to this studies' 10 core ISG. The authors limitations paragraph should discuss the fact that scRNAseq reduces the overall ISG number that can be analyzed.

A minor point concerns the 25 supplementary figures of the study. There must be a better way to support the conclusions with the necessary data.

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

Learn more at Review Commons

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Reply to the reviewers

1. General Statements

We would like to thank all reviewers assigned by Review Commons for their thoughtful and constructive feedback, which helped us to further improve the quality and clarity of our manuscript. In this study, we developed a novel fluorescence-based live-cell imaging platform for detecting mitochondria-endoplasmic reticulum contact sites (MERCS), which we named MERCdRED. This system enables quantitative analysis of MERCS dynamics in living cells by combining stable gene expression of dimerization-dependent fluorescent proteins with single-cell cloning. Using this tool, we uncovered a nutrient-dependent regulatory mechanism of MERCS formation mediated by the ER-localized tethering protein PDZD8. We appreciate that all the reviewers acknowledged the methodological robustness of this work. In response to reviewers' comments, we will significantly improve the manuscript by adding the live-cell imaging to assess the reversible propertyof MERCdRED, and investigating the physiological impacts of MERCS remodeling in regulating metabolism in response to nutrient starvation. We believe that both the methodological advance and the biological findings presented in this study will be of broad interest to the cell biology community.

1. Description of the planned revisions

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

Summary: In this study, the authors successfully established a stable cell line expressing MERCdRED, a dimerization-dependent fluorescent protein (ddFP)-based sensor for monitoring mitochondrial-ER contact sites (MERCS). Through light and electron microscopy analyses, they demonstrated that MERCS formation is regulated by nutrient availability and requires PDZD8. While the work is technically sound and well-presented, the biological implications of nutrient-dependent MERCS regulation remain underexplored.

Major Concerns: Although the manuscript is methodologically robust and suitable for a Methods-type article, its biological significance is limited. The findings primarily serve as proof-of-concept for the MERCdRED tool, without substantially advancing our understanding of MERCS regulation.

We appreciate the reviewer for acknowledging the methodological robustness of our study. We would like to respectfully emphasize that, using the MERCdRED cell system, we uncovered the distinct features of MERCS dynamics by comparing structures of various sizes (Figure 4A-D). Furthermore, we discovered an unexpected biological finding: nutrient starvation leads to a reduction in MERCS formation, which contrasts with previous reports using cell lines (former Figure 4E-H). Additionally, we revealed that PDZD8 mediates nutrient-dependent MERCS regulation (former Figure 4E-H).

To clarify these findings, we have now separated the former Figure 4 into two distinct figures (now Figure 4 and 5). Furthermore, to assess the functional relevance of PDZD8-mediated MERCS regulation upon nutritional change, we will perform rescue experiments by overexpressing PDZD8 in starved cells, along with a metabolomic analysis in these conditions. We will add these new data in Figure 6.

Taken together, we believe that our data provide novel mechanistic insights into how MERCS are modulated and utilized for the regulation of metabolism under physiological stress, thereby contributing to a deeper understanding of the roles and regulation of MERCS beyond the scope of a mere proof-of-concept study.

Reviewer #1 (Significance (Required)):

To enhance the impact of the study, the authors could use this sensor to investigate novel biological questions-such as the molecular pathways linking nutrient sensing to MERCS dynamics-or explore downstream activities of nutrient-dependent MERCS formation. Deeper mechanistic insights would significantly strengthen the work's contribution to the field.

We thank the reviewer for their constructive suggestions. We fully agree that the MERCdRED cell system has great potential for investigating upstream signaling pathways regulating MERCS dynamics, as well as the downstream consequences of nutrient-dependent MERCS modulation. As mentioned above, this study already presents important findings, including the discovery of PDZD8 as a key protein linking the nutrient starvation and MERCS remodeling, and a relationship between MERCS dynamics and contact site size.

To further assess the biological consequence of the MERCS remodeling, we will perform metabolomics analysis in PDZD8-overexpressing cells under starved conditions.

Additionally, to further reinforce the utility of MERCdRED and extend the findings presented in this study, we performed live-cell imaging experiments using MERCdRED. The preliminary results demonstrated dynamic and reversible changes in MERCS in response to nutrient starvation and subsequent recovery (Please see the response to Reviewer 3 below, Reviewer-only Figure 1).

These new data will significantly strengthen the contribution of this study to the field.

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

This manuscript entitled "Live-cell imaging reveals nutrient-dependent dynamics of ER-mitochondria contact formation via PDZD8" by Saeko Aoyama-Ishiwatari et al., describes a novel methodology for visualizing contacts between mitochondria and the endoplasmic reticulum (MERCs) by fluorescence microscopy. Inter-organelle contacts, defined as membrane proximities below ~30 nm, fall below the diffraction limit of conventional light microscopy. The method developed by Hirabayashi's laboratory leverages dimerization-dependent fluorescence complementation to create a reporter capable of both visualizing and quantifying ER-mitochondria contacts (MERCs).

Reviewer #2 (Significance (Required)):

This timely study provides a valuable and innovative approach to overcoming a longstanding technical limitation in the field, enabling dynamic analysis of ER-mitochondria contacts.

We appreciate the reviewer for recognizing the timeliness and innovation of our work.

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

In this manuscript, the authors develop a new system to study mitochondrial-ER contact sites in living mouse embryonic fibroblast cells and explore the impact that nutritent starvation has on these contact sites in real time. By stably expressing a bicistroic reporter construct of a dimerization-dependent fluorescent protein that will generate a signal once the two moities, one anchored in the ER by Sec61b, and the other anchored in the outer membrane of mitochondria, via TOM20, comme in close apposition. This cell model is validated using sofisticated CLEM experiments and via the ablation of known regulators of MERCs, such as PDZD8 and FKBP8.

Major comments

The authors claim to have developed a new for the study of MERCs. They indeed have benchmarked this system using very sophisticated CLEM approaches and through the ablation of known regulators of MERCs, all of which is very carefully performed and convincing.

We appreciate the reviewer for acknowledging our efforts in the development and validation of the MERCdRED system presented in this study.

They argue that the generation of a stable cell line via lentiviral delivery is an improvement over the transient transfection approaches that have been applied in the past (see cited references), which I would generally agree. However, they have not contrasted or compared their system to the widly-used SLPICs system from the Tito Cali group (Vallese, F. et al. An expanded palette of improved SPLICS reporters detects multiple organelle contacts in vitro and in vivo. Nat. Commun. 11, 6069 (2020)) which measures bi and tri-partite interactions with other membrane contacts, including mitochondria and ER at two specific distances, which in my opinion has been more extensivley used to study cell and tissue physiology. They accurately point out that the reversability of this and other systems is challenging and it would be important to define highlight whether the current system allows the study of reversible MERCs. It does not appear as though the reversability of MERCs has been explored in this study.

We thank the reviewer for these thoughtful suggestions and agree that further investigation into the reversibility of MERCS using the MERCdRED system would be valuable. Following the reviewer's suggestion, we performed a live-cell imaging experiment using MERCdRED to monitor dynamic changes in MERCS in response to nutrient starvation and subsequent recovery. The preliminary results were obtained as shown in Reviewer-only Figure 1, which strongly suggests the utility of MERCdRED for detecting reversible MERCS formation. The data will be added in Figure 5 if the reproducibility is confirmed. This new data set highlights the distinct utility of the MERCdRED system in studying MERCS dynamics.

We acknowledge that the SPLICS system has been widely adopted for studying membrane contact sites. In the revised manuscript, we will include a comparative discussion of MERCdRED, SPLICS, and other existing MERCS reporters, particularly with respect to their capabilities in capturing the reversible nature of these contacts.

The genetic (PDZD8, FKBP8) and nutritional (starvation) interventions are very helpful to benchmark the system. The description of the methods and data appear to be reproducible and the stastical analyses are acceptable.

We thank the reviewer for their positive evaluation of our data and analyses.

Minor comments

As mentioned above, it would be helpful to reference and compare the current study in the context of reversability, which the current MERCdRED system has the potential to provide beyond the state-of-the-art.

We thank the reviewer for this helpful suggestion. We will include additional discussion comparing the reversibility of the MERCdRED system with that of existing tools, highlighting the potential advantages of MERCdRED in capturing dynamic and reversible MERCS.

Reviewer #3 (Significance (Required)):

Significance

The major strength of this study is the development of a stable cell line that allows for the study of MERCs, which has the potential to study the reversible nature of these membrane contact sites. It is debatable as a stable cell line rather than a transient transfection offers a major advancement, even if it does make the study of the system more straightforward, especially if the phenomenon of reversibilty is to be explored.I believe that the CLEM study offers a very informative and precise way to benchmark the ddFP system. Defining how MERC formation and separation (once again the reversibility discovery) have impacts in cell physiology beyond the distances altered by starvation would improve the study. Examining the impact on calcium homeostasis, lipid metabolism, and other aspects of biology that are known to be influenced by MERCs would be interesting. As such, there are no new conceptual, mechanistic, or functional advances, simply minor technical advances in the creation of a stable cell line followed by very solid benchmarking experiments. More complex tri-partite interactions, studied elsewhere, which are conceptually very important for cell and organelle biology, have not been attempted here. Similarly, the notion of studied different types of MERCs, which have been proposed to be important for cell biology, has not been explored using this single reporter. The target audience for this study is one that is interested in membrane contact sites and quantitative biology. My expertise is in mitochondrial fluorescence imaging and biology. I am not an expert in CLEM.

We thank the reviewer for their thoughtful and detailed comments. We would like to respectfully emphasize that the establishment of a clonal cell line has enabled us to uncover a striking and unexpected biological finding-namely, that nutrient starvation leads to a reduction, rather than an increase, in MERCS formation, and that this change is regulated by PDZD8. This observation directly contradicts previous reports and highlights the value of our robust and quantitative system for re-evaluating previously held assumptions.

We agree that demonstrating the reversibility of MERCS formation using our system would further strengthen the utility and reliability of the MERCdRED platform. To address this, as mentioned above, we performed a live-cell imaging to assess the dynamic reversibility of MERCS formation (Reviewer-only Figure 1) and will add the results in the revised manuscript.

We agree that investigation of tri-partite interactions is conceptually important for understanding the broader landscape of organelle communication. However, assessing tri-partite organelle contacts is beyond the scope of this study. We recognize that this is one of the key directions for future studies and believe that the MERCdRED platform is a promising tool for exploring such complex interactions.

Regarding different types of MERCS, we would like to clarify that our study does address this point to some extent. We identified distinct features of MERCS behavior by comparing structures of different sizes-an aspect that, to our knowledge, has not been previously examined. These findings contribute conceptually to our understanding of the dynamic and heterogeneous nature of ER-mitochondria contacts.

We believe that our methodological development provides important mechanistic insights into MERCS dynamics, as described above. In line with the reviewer's suggestion, we will investigate the physiological impacts of MERCS remodeling in regulating metabolism in response to nutrient starvation. We hope these forthcoming data will further enhance the biological relevance of our findings.

Taken together, we believe our study provides both a solid technical advance and novel mechanistic insights into MERCS biology, which will be of interest to researchers working on membrane contact sites, organelle dynamics, and cell physiology.

We will revise the manuscript to more clearly convey the significance and implications of this study.

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

Reviewer #2

Major points:

In Figure 1E (and the rest of the manuscript), the meaning of the label "MERCdRED on Mito" is unclear. A portion of the MERCdRED signal does not co-localize with mitochondria. The authors should clearly define what "MERCdRED on Mito" represents which appears to be the intensity of the MERCdRED signal within the mitochondrial mask. How about the global MERCdRED signal intensity? When the authors knocked-out PDZD8, did the global fluorescence intensity of the MERCdRED signal decrease?

As the reviewer pointed out, some red signals appear outside of mitochondria in MERCdRED cells, which are presumably due to autofluorescence. While the global red channel fluorescence intensity also decreased upon PDZD8 conditional knockout (cKO), as shown in Reviewer-only Figure 2A, the reduction was less pronounced than the decrease observed when only the red signals on mitochondria were measured (Reviewer-only Figure 2B). We consider the mitochondrial red signals to represent MERCdRED signals, and we agree that the label "MERCdRED on Mito" may be misleading. To improve clarity, we revised the figure labels as follows: "MERCdRED" was changed to "Red channel," and "MERCdRED on Mito" was changed to "MERCdRED (Red signals on Mito)."

1. While the authors demonstrate that MERCdRED can quantify a reduction in MERCs (e.g., in PDZD8 knockout conditions), it would be valuable to assess its sensitivity to increases in MERCs as well. For example, previous work from the authors (Nakamura et al., 2025) showed that FKBP8 overexpression leads to an increase in MERCs.

We thank the reviewer for suggesting this valuable experiment. To assess whether the dynamic range of MERCdRED covers increased MERCS formation, we overexpressed PDZD8 in MERCdRED cells. Notably, PDZD8 overexpression resulted in a significant increase in MERCdRED signal intensity, demonstrating that the system is indeed capable of detecting enhanced MERCS formation. These new data were added in the revised manuscript as new Figure 3D-E.

Minor points: 1. Please revise the sentence "First, signals from MERCdRED fluorescence overlapped with the mitochondrial marker Tomm20-iRFP were detected by confocal microscopy in living cells."

We revised this sentence to "First, fluorescence from MERCdRED and the mitochondrial marker Tomm20-iRFP wasdetected by confocal microscopy in living cells."

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

Reviewer #2

Major points: 1. The authors claim that their construct enables balanced expression of the RA and GB moieties of the reporter. This should be substantiated by showing protein expression levels via Western blot analysis.

We thank the reviewer for pointing this out. In our system, Tomm20-GB and RA-Sec61β are expressed from a single plasmid using a self-cleaving P2A peptide sequence, which ensures that the two proteins are produced in equimolar amounts upon translation. Therefore, their expression levels are expected to be approximately equal. Given that comparing the expression levels of these two proteins by Western blotting would require extensive work, including obtaining reconstituted proteins to normalize band intensities, but remains inconclusive due to the semi-quantitative nature of the method, we have decided not to pursue this approach.

Minor points:

1. In Figure 2, the ER structures are not segmented in the EM images. It would enhance the manuscript to show the three-dimensional spatial relationship between mitochondria and the ER, rather than only highlighting the regions identified as contacts.

We agree that visualizing the entire ER structure would enhance the reader's understanding of the three-dimensional spatial relationship between mitochondria and the ER. However, complete segmentation of the ER in EM images is extremely labor-intensive. Given the scope and focus of this study, we have decided not to include full ER segmentation in this manuscript.

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Referee #3

Evidence, reproducibility and clarity

In this manuscript, the authors develop a new system to study mitochondrial-ER contact sites in living mouse embryonic fibroblast cells and explore the impact that nutritent starvation has on these contact sites in real time. By stably expressing a bicistroic reporter construct of a dimerization-dependent fluorescent protein that will generate a signal once the two moities, one anchored in the ER by Sec61b, and the other anchored in the outer membrane of mitochondria, via TOM20, comme in close apposition. This cell model is validated using sofisticated CLEM experiments and via the ablation of known regulators of MERCs, such as PDZD8 and FKBP8.

Major comments

The authors claim to have developed a new for the study of MERCs. They indeed have benchmarked this system using very sophisticated CLEM approaches and through the ablation of known regulators of MERCs, all of which is very carefully performed and convincing. They argue that the generation of a stable cell line via lentiviral delivery is an improvement over the transient transfection approaches that have been applied in the past (see cited references), which I would generally agree. However, they have not contrasted or compared their system to the widly-used SLPICs system from the Tito Cali group (Vallese, F. et al. An expanded palette of improved SPLICS reporters detects multiple organelle contacts in vitro and in vivo. Nat. Commun. 11, 6069 (2020)) which measures bi and tri-partite interactions with other membrane contacts, including mitochondria and ER at two specific distances, which in my opinion has been more extensivley used to study cell and tissue physiology. They accurately point out that the reversability of this and other systems is challenging and it would be important to define highlight whether the current system allows the study of reversible MERCs. It does not appear as though the reversability of MERCs has been explored in this study. The genetic (PDZD8, FKBP8) and nutritional (starvation) interventions are very helpful to benchmark the system. The description of the methods and data appear to be reproducible and the stastical analyses are acceptable.

Minor comments

As mentioned above, it would be helpful to reference and compare the current study in the context of reversability, which the current MERCdRED system has the potential to provide beyond the state-of-the-art.

Significance

The major strength of this study is the development of a stable cell line that allows for the study of MERCs, which has the potential to study the reversible nature of these membrane contact sites. It is debatable as a stable cell line rather than a transient transfection offers a major advancement, even if it does make the study of the system more straightforward, especially if the phenomenon of reversibilty is to be explored. I believe that the CLEM study offers a very informative and precise way to benchmark the ddFP system. Defining how MERC formation and separation (once again the reversibility discovery) have impacts in cell physiology beyond the distances altered by starvation would improve the study. Examining the impact on calcium homeostasis, lipid metabolism, and other aspects of biology that are known to be influenced by MERCs would be interesting. As such, there are no new conceptual, mechanistic, or functional advances, simply minor technical advances in the creation of a stable cell line followed by very solid benchmarking experiments. More complex tri-partite interactions, studied elsewhere, which are conceptually very important for cell and organelle biology, have not been attempted here. Similarly, the notion of studied different types of MERCs, which have been proposed to be important for cell biology, has not been explored using this single reporter. The target audience for this study is one that is interested in membrane contact sites and quantitative biology.

My expertise is in mitochondrial fluorescence imaging and biology. I am not an expert in CLEM.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

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Referee #2

Evidence, reproducibility and clarity

This manuscript entitled "Live-cell imaging reveals nutrient-dependent dynamics of ER-mitochondria contact formation via PDZD8" by Saeko Aoyama-Ishiwatari et al., describes a novel methodology for visualizing contacts between mitochondria and the endoplasmic reticulum (MERCs) by fluorescence microscopy. Inter-organelle contacts, defined as membrane proximities below ~30 nm, fall below the diffraction limit of conventional light microscopy. The method developed by Hirabayashi's laboratory leverages dimerization-dependent fluorescence complementation to create a reporter capable of both visualizing and quantifying ER-mitochondria contacts (MERCs).

Major points:

1. The authors claim that their construct enables balanced expression of the RA and GB moieties of the reporter. This should be substantiated by showing protein expression levels via Western blot analysis.
2. In Figure 1E (and the rest of the manuscript), the meaning of the label "MERCdRED on Mito" is unclear. A portion of the MERCdRED signal does not co-localize with mitochondria. The authors should clearly define what "MERCdRED on Mito" represents which appears to be the intensity of the MERCdRED signal within the mitochondrial mask. How about the global MERCdRED signal intensity? When the authors knocked-out PDZD8, did the global fluorescence intensity of the MERCdRED signal decrease?
3. While the authors demonstrate that MERCdRED can quantify a reduction in MERCs (e.g., in PDZD8 knockout conditions), it would be valuable to assess its sensitivity to increases in MERCs as well. For example, previous work from the authors (Nakamura et al., 2025) showed that FKBP8 overexpression leads to an increase in MERCs.

Minor points:

1. Please revise the sentence "First, signals from MERCdRED fluorescence overlapped with the mitochondrial marker Tomm20-iRFP were detected by confocal microscopy in living cells."
2. In Figure 2, the ER structures are not segmented in the EM images. It would enhance the manuscript to show the three-dimensional spatial relationship between mitochondria and the ER, rather than only highlighting the regions identified as contacts.

Significance

This timely study provides a valuable and innovative approach to overcoming a longstanding technical limitation in the field, enabling dynamic analysis of ER-mitochondria contacts.

Expertise: cell biology, membrane contact sites, lipid transfer proteins

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

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Referee #1

Evidence, reproducibility and clarity

Summary:

In this study, the authors successfully established a stable cell line expressing MERCdRED, a dimerization-dependent fluorescent protein (ddFP)-based sensor for monitoring mitochondrial-ER contact sites (MERCS). Through light and electron microscopy analyses, they demonstrated that MERCS formation is regulated by nutrient availability and requires PDZD8. While the work is technically sound and well-presented, the biological implications of nutrient-dependent MERCS regulation remain underexplored.

Major Concerns:

Although the manuscript is methodologically robust and suitable for a Methods-type article, its biological significance is limited. The findings primarily serve as proof-of-concept for the MERCdRED tool, without substantially advancing our understanding of MERCS regulation.

Significance

To enhance the impact of the study, the authors could use this sensor to investigate novel biological questions-such as the molecular pathways linking nutrient sensing to MERCS dynamics-or explore downstream activities of nutrient-dependent MERCS formation. Deeper mechanistic insights would significantly strengthen the work's contribution to the field.

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

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Reply to the reviewers

Reviewer #1

Major points

• *

• • The introduction describes the effects of different environmental cues and aging on fibroblast phenotype, but it would be good to note the developmental origins of dermal fibroblasts, which specifies their fate and function (Driskell et al, Nature 2013).* Our response:

In accordance with the reviewers' suggestions, we have incorporated a summary of prior research regarding the developmental origins of dermal fibroblasts into lines 53–56 of the Introduction.

• In Fig 2, how do TEWL measurements compare to constructs without an epidermal layer or human skin? It may seem obvious that barrier function would be negligible in these models, but it would be a helpful negative control for interpreting the relative effects of vasculature on barrier function.*

We appreciate your valuable comments regarding the accurate interpretation of TEWL measurements. Estimated TEWL values for human skin have been reported in a systematic review and meta-analysis by Kottner et al. Specifically, the estimated TEWL (95% CI) for individuals aged 18–64 years varies by anatomical site: 15.4 (13.9–17.0) g/m²h for the right cheek, 6.5 (6.2–6.8) g/m²h for the midvolar right forearm, and 36.3 (29.5–43.1) g/m²h for the right palm. In comparison, the TEWL of our EDV model was 9.68 g/m²h, a value relatively close to that of human skin.

We also considered measuring TEWL in artificial skin models lacking epidermis. However, we found that such models remain moist due to culture medium, and pressing the measurement probe against them risks water droplets adhering to the sensor and causing damage. Although we recognize the significance of this measurement as a negative control, we refrained from conducting it due to the limitations of the equipment.

This information has been added to the Results section, lines 178–182.

• *

• The mechanical measurements in Fig 2 are a nice idea, but it is a bit difficult to interpret without comparison to other conditions (e.g. human skin) or by reporting more universal mechanical parameters (e.g. Young's modulus).*

We greatly appreciate your insightful comments regarding the interpretation of skin viscoelasticity measurements using the Cutometer. The Cutometer is a device that applies negative pressure to the skin to elevate its surface, allowing for the calculation of biomechanical properties based on the temporal changes in skin displacement. Notably, the R7 parameter—defined as the ratio of immediate retraction after pressure release to the maximum deformation during suction—has been shown to correlate significantly with age.

In this study, we evaluated HSEs under the same measurement conditions as those used in previous human clinical studies. Accordingly, we have cited past Cutometer data for human skin and discussed the relationship between those findings and our HSE measurements. These revisions have been made to lines 205–215.

We determined that performing Cutometer measurements on human skin would be impractical due to the ethical committee procedures and associated costs. Although evaluating Young’s modulus using techniques such as AFM to assess the mechanical properties of collagen fibers is a fascinating and informative approach, we have opted not to pursue this analysis due to the substantial time and cost required for sample preparation.

• The induction of region-specific fibroblast markers is interesting and a bit unexpected since all the fibroblasts came from the same source before seeding into HSEs. The conclusions require additional support from quantification of the IF staining in Fig 3.*

Our response:

Thank you for your valuable advice on strengthening the conclusion of our manuscript. We are currently conducting quantitative analysis through manual counting across multiple fields for all mesenchymal cell markers and Vimentin immunostaining data presented in Fig. 3.

• *

• Likewise, could the authors clarify whether the cells were passaged before seeding into the HSE, and if so, what passage number. Could passaging affect the responses observed? Please add a discussion point about this.*

Our response:

For all cell types, passage 4 or 5 cells were utilized for the reconstitution of human skin equivalents (HSE). Indeed, Philippeos et al. demonstrated that while CD39, CD90, and CD36 are detectable in primary CD31⁻CD45⁻Ecad⁻ dermal cells, the expression of CD39 is lost after a single passage. In contrast, CD90 and CD36 remain detectable for up to four passages. These findings underscore the impact of in vitro culture on the depletion of fibroblast marker expression. Since we employed NHDFs that had undergone four to five passages for HSE reconstruction, it is reasonable to assume that these cells had already lost specific fibroblast subpopulations, including CD39⁺ cells. Consistent with this, our scRNA-seq analysis revealed that most fibroblasts cultured in 2D formed an artificial population comprising cells in the S and G2M phases, along with secretory-reticular fibroblasts. Additionally, immunohistochemical analysis confirmed a near-complete absence of CD39⁺, CD90⁺, FAP⁺, NG2⁺, and αSMA⁺ cells in the dermis of both D and DV models, further indicating that serial passaging significantly reduces the expression of markers associated with papillary fibroblasts, reticular fibroblasts, and pericytes. Interestingly, the introduction of vascular endothelial cells into the HSE appears to facilitate a partial restoration of fibroblast heterogeneity in cells passaged four to five times. However, whether this effect can be replicated in more extensively passaged fibroblasts remains to be verified. It is well established that excessive passaging induces cellular senescence, leading to reduced proliferative and differentiation capacities in mesenchymal stem cells. Therefore, it is conceivable that fibroblasts beyond a certain passage number may fail to recapitulate dermal mesenchymal cell heterogeneity, even in the presence of endothelial cells.

We have added this discussion to the revised manuscript on lines 372-385, 391–397, and 470-471. However, due to the prolonged culture period required, we regret that we are unable to perform the additional validation experiments at this time.

• The scRNA-seq suggests that the in vitro populations do not discriminate between secretory papillary and pro-inflammatory fibroblasts. Could the authors add some further analysis or discussion regarding this point?*

Our response:

We are currently conducting an additional enrichment analysis on fibroblast subpopulations #0, 1, 2, 6, 8, and 11, identified through UMAP analysis integrating HSE and human skin datasets. We believe that this analysis will elucidate the functional characteristics of each in vitro subpopulation and enable us to speculate on the underlying factors contributing to the observed differences from the human skin analysis results.

• In Fig 6, it will be important to add quantification of epidermal thickness and differentiation marker expression to support the conclusions.*

Our response:

Thank you for your valuable advice regarding quantitative analysis. We are currently measuring the thickness of the entire epidermal layer, the CK5-positive cell layer, and the CK10-positive cell layer based on HE-stained and IHC-stained images.

• A key question is how NP and AA conditions affect the fibroblast populations as this seems to be a key factor in HSE maturation and would then link back to the previous sections. It would be good to stain for fibroblast markers in these samples.*

Our response:

We are grateful for your insightful comments, which are crucial for a more precise understanding of the physiological relevance of the NP culture model. In response, we are currently undertaking additional analyses to investigate the expression patterns of dermal mesenchymal markers under both NP and AA conditions.

• As noted above, the ability of the vasculature to direct differentiation of a common fibroblast population into different phenotypes is one of the key findings of the study. To strengthen these observations, could additional analysis of the transcriptional data be possible. For example, would trajectory analysis potentially show how the different populations are evolving or related? In addition, could the CellChat analysis be performed between the vasculature and the different populations in Fig 5, which are mapped to in vivo populations? This might be a more relevant analysis than the populations in Fig 4.*

Our response:

As pointed out by reviewers, we acknowledge that elucidating the process and underlying mechanisms by which fibroblasts, whose heterogeneity is compromised in 2D culture, re-differentiate into distinct dermal mesenchymal subtypes constitutes a critical additional analysis to strengthen our findings. Accordingly, we are currently conducting trajectory analysis using Monocle3. This includes identifying branch points that regulate the differentiation of dermal mesenchymal clusters shown in Fig. 4b, as well as predicting transcription factors and cell signaling pathways playing pivotal roles at those branch points. Furthermore, we are planning a CellChat analysis between vascular endothelial cells and dermal mesenchymal cells. We anticipate that integrating the results of these two analyses will provide valuable insights into the differentiation processes of dermal mesenchymal cells, particularly the induction of perivascular cell differentiation.

• *

• *

Reviewer #1

Minor points

• *

• • The abstract states that enabling in vitro evaluation of drug efficacy using methodologies that are identical to those used in human clinical studies. This seems to be an over interpretation of the study and not well supported by the data. Please consider revising or removing.*

Our Response:

Upon thorough consideration, we have deleted the statements that may be regarded as exaggerated (line 26-28 and 346-348).

• Check referencing formatting in lines 118-121*

Our Response:

We appreciate your attention to the reference format error. The necessary revisions have been completed.

Reviewer #2 Major comments:

1. • Despite its strengths, the study has several limitations that warrant further investigation. The authors describe a "senescent-like" phenotype under nutrient-poor (NP) conditions, yet do not provide direct evidence of cellular senescence using canonical markers such as SA-β-gal staining, p16^INK4a or p21 expression, or SASP profiling-weakening their aging-related conclusions.*

Our Response

Thank you for your valuable advice, which has helped clarify the physiological phenomena modeled by the NP condition. We are planning additional experiments involving histological analysis, including SA-β-gal staining and the detection of p16^INK4a and/or p21.

• The 500 μM dose of ascorbic acid (AA), while within the reported range for skin models, is at the higher end compared to commonly used concentrations (100-300 μM) and lacks justification via dose/response data. Normal physiological levels and changes in aging dermis should be referenced in discussion. AA is also an additive in their standard HSE media, but this was not sufficiently emphasized to draw attention. Would its removal from the baseline media make a difference?*

Our Response

We sincerely appreciate the important comment regarding the rationale behind the ascorbic acid concentration used in the culture medium. As Reviewer 3 rightly pointed out, concentrations around 100–300 μM are commonly employed in general in vitro assays. In our artificial skin model, we opted for a concentration of 500 μM AA in the growth medium based on two considerations: (1) the model contains a high cell density of approximately 4 × 10⁶ cells immediately after reconstruction, which is expected to result in substantial AA consumption, and (2) AA is not sufficiently stable in culture medium. Given the relatively long medium exchange interval of 48–72 hours, we deemed it necessary to maintain a certain AA level throughout this period. While no rigorous dose–response validation has been conducted, we have confirmed that this concentration does not induce toxicity or abnormalities in skin morphogenesis.

As part of the revision, we considered revisiting the basal medium formulation; however, due to the significant time and resource demands, we have decided to forgo further optimization at this stage.

As described on lines 307–311, the NP medium was formulated to evaluate the potential impact of age-related declines in plasma component transport. We apologize for any confusion regarding the relationship between the HSE growth medium and the NP medium. In response to the reviewer’s suggestion, we have added clarifying explanations and cautionary notes regarding the composition and rationale of these two media in both the Results and Methods sections (line 307-311 and 634-636).

• Mechanistically, fibroblast heterogeneity is attributed to keratinocyte and vascular signals, but the signaling pathways involved (e.g., Wnt, TGF-β, VEGF) are not directly examined. Validating which paracrine factors (VEGF, PDGF, LAMA5, KGF) are mediating fibroblast transitions using inhibitors or RNA profiling could shed more light.*

Our response:

As pointed out by reviewers, we acknowledge that elucidating the process and underlying mechanisms by which fibroblasts, whose heterogeneity is compromised in 2D culture, re-differentiate into distinct dermal mesenchymal subtypes constitutes a critical additional analysis to strengthen our findings. Accordingly, we are currently conducting trajectory analysis using Monocle3. This includes identifying branch points that regulate the differentiation of dermal mesenchymal clusters shown in Fig. 4b, as well as predicting transcription factors and cell signaling pathways playing pivotal roles at those branch points. Furthermore, we are planning a CellChat analysis between vascular endothelial cells and dermal mesenchymal cells. We anticipate that integrating the results of these two analyses will provide valuable insights into the differentiation processes of dermal mesenchymal cells, particularly the induction of perivascular cell differentiation. We fully recognize that validation using specific inhibitors is crucial to substantiate the mechanisms suggested by the scRNA-seq analysis. However, given that the reconstruction and reanalysis of the artificial skin model requires more than three months, we have decided not to include these experiments in the current revision and instead consider them as important subjects for future investigation.

Minor comments: 1. The role of pericytes is also underexplored; while their presence is confirmed, functional assays or transcriptomic analyses to elucidate their contribution to ECM remodeling or vascular stability are not fully explored. The origin of pericyte-like cells remains uncertain without lineage tracing or barcoding to distinguish whether they derive from fibroblasts, endothelial cells, or culture artifacts. Since they observe induced differentiation of fibroblast-like cells in 3D culture, it would be compelling to reconstruct differentiation trajectories (pseudotime analysis) from progenitor states to papillary/reticular/pericyte-like states from their scRNAseq data.

Our respnse:

This point will be addressed and validated through our response to Major Comment 3 from Reviewer #2.

• Although AA enhanced collagen production and elasticity in the vascularized EDV model, the lack of response in the ED model is not addressed mechanistically.*

Our response

We have planned additional experiments to examine two hypotheses regarding the mechanism underlying the improved responsiveness of the EDV model to AA. The first hypothesis posits that the behavior of ascorbic acid uptake in the cells constituting the EDV model differs from that in the ED model. To investigate this, we plan to analyze the expression patterns of transporter genes potentially involved in the uptake and efflux of ascorbic acid, such as SVCT1 (SLC23A1), SVCT2 (SLC23A2), GLUT1 (SLC2A1), GLUT3 (SLC2A3), GLUT4 (SLC2A4), and MRP4, using scRNA-seq data. The second hypothesis suggests that the absence of bFGF signaling and low FBS treatment under NP conditions may affect subpopulations of dermal mesenchymal cells in the HSEs. To test this, we plan to analyze the expression patterns of dermal mesenchymal cell markers by IHC under NP and AA conditions, following the same approach as shown in Fig. 3.

• The omission of immune cells which are key players in skin aging and homeostasis could increase physiological relevance of the model.*

Our response:

As rightly noted by Reviewer 2, immune cells are integral to skin aging and the maintenance of tissue homeostasis, underscoring the necessity of incorporating them into future research models. Nonetheless, the primary aim of the present study is to elucidate the influence of vascular endothelial cells on dermal mesenchymal cell heterogeneity and to establish an in vitro research model specifically addressing this heterogeneity, with particular emphasis on perivascular cells. Accordingly, we would prefer to consider the analysis of immune cells as a subject for future investigation.

• The exclusive use of standard HUVECs may not fully capture the behavior of tissue-specific microvascular endothelial cells, potentially limiting the fidelity of the vascular niche.*

In this study, we opted to use HUVECs as vascular endothelial cells due to their relative ease of expansion in culture. Consequently, we acknowledge the potential limitation in fully recapitulating the functions of tissue-specific endothelial cells. To address this concern, we have revised and expanded the Discussion section on lines 352–356.

Reviewer #3 Major comments:

1. • Are the key conclusions convincing? The core claim-that tricellular interactions recapitulate dermal mesenchymal heterogeneity and enhance skin functionality-is well-supported by histology, immunohistochemistry, functional assays (TEWL, elasticity), and scRNA-seq.
2. Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether? The assertion that HSEs enable "identical" methodology to clinical studies (p. 2, line 29) is exaggerated. While elasticity was measured via Cutometer (used clinically), the model lacks immune/neural components and long-term stability for full translational equivalence.* Our Response:

Upon thorough consideration, we have deleted the statements that may be regarded as exaggerated (line 26-28 and 346-348).

• Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation. Adequacy of Experimental Evidence & Need for Additional Experiments: No essential control appears to be missing: the authors include conditions {plus minus}ascorbic acid and {plus minus}vascular cells to isolate those effects. One could suggest a few additional experiments to further bolster the conclusions, but they are not strictly required for the main message. For example, to pinpoint the contribution of each mesenchymal subset, the authors could engineer HSE variants lacking one component at a time (omit pericytes or use only papillary vs. only reticular fibroblasts) to see how each omission affects barrier or elasticity. This would directly confirm each cell type's role. However, such experiments may be technically involved (especially isolating pure papillary vs. reticular fibroblast populations and ensuring viability in 3D culture) and might be beyond the scope of a single study. Another possible extension could be mechanistic assays, such as examining specific molecular signals: e.g., testing if blocking known paracrine factors from pericytes or fibroblast subsets diminishes the observed improvements. Given that pericytes can secrete laminin-511 and other factors that promote keratinocyte growth, the authors might, in future work, explore whether such factors mediate the enhanced epidermal proliferation seen with the vascularized HSE. Overall, the current data are sufficiently convincing that additional experiments are not absolutely necessary for publication.
• Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments-*

Our response

We are deeply grateful for the reviewer’s constructive feedback. As rightly pointed out, cell ablation and mechanistic assays utilizing signaling inhibitors to assess the contribution of individual mesenchymal subsets are indispensable for reinforcing our findings and claims. However, as the reviewer has also indicated, these experiments would require no less than four months to complete. Consequently, we have opted to forgo high-cost additional experiments such as the optimization of HSE construction protocols and inhibitor-based assays. Instead, we are proactively conducting mechanism-oriented analyses using our existing scRNA-seq and histological datasets. Specifically, we are currently implementing an integrated approach combining Monocle3 and CellChat to pinpoint critical branch points in dermal mesenchymal cell differentiation and to elucidate the signaling pathways orchestrating these bifurcations.

• Are the experiments adequately replicated and statistical analysis adequate? The manuscript's data are presented in a manner that generally supports reproducibility. The authors state that all data are presented as "mean {plus minus} SD" (Methods, p.36). This is acceptable and clearly reported. However, I suggest that the authors consider using mean {plus minus} SEM for specific datasets where the primary goal is to assess statistical significance between groups - for example, for the Ki67-positive cell proliferation data (Fig. 6c) - as SEM better reflects the precision of the group mean for inferential comparisons. In contrast, for functional measures that inherently exhibit biological variation across samples (e.g., TEWL, skin elasticity), using mean {plus minus} SD remains fully appropriate, as SD reflects true inter-sample variability. To improve clarity and reproducibility, I encourage the authors to briefly state in the Methods or figure legends why SD or SEM is used in each case, in line with best practice guidelines.*

Our Response:

We appreciate your guidance regarding appropriate statistical analysis and data presentation. We planned to revise the depiction of error margins in accordance with best practice guidelines.

Reviewer #3 Minor comments: 1. For Figure 4e, it would be helpful if the authors could clarify in the figure legend or Methods whether the heatmap shows log-normalized expression values (as derived from the Seurat object) or z-scored expression across cells or samples. This distinction affects the interpretation of relative versus absolute expression levels of the collagen and elastic fiber-related genes, which are central to the study's conclusions about ECM remodeling.

Our response:

Thank you for pointing out the inconsistency in data representation. We have revised the manuscript to clearly indicate that Fig. 4e presents the Z-score normalized average expression levels.

• Typos: "factr" → "factor" (p. 16, line 244); "severl" → "several" (p. 22, line 367).

*

Our response

Thanks for pointing out the typo, we have corrected it.

Reviewer #4

Minor Points:

1. • The human skin control in Fig. 1c seems thinner than normal and would suggest that the ED and EDV models are hyperproliferative. Replacing the control with one that shows normal thickness would prevent incorrect conclusions of the data.* Our response:

In accordance with the reviewer’s suggestion, the display area of the human skin image in Fig. 1c has been modified.

KI67 and TEWL readings for human skin as controls for Fig. 2b-c would help gauge how the organoids perform and whether they are abnormal. What is the elasticity index for facial sagging?

Thank you for your valuable advice, which has deepened our understanding of the evaluation results of HSEs. We are currently planning and conducting an additional analysis by including the quantification of Ki67-positive cells in human skin samples. Regarding the assessment of skin barrier and viscoelasticity using TEWL and Cutometer measurements, we have reffered data from previous clinical studies and added an explanation of the functional differences between HSEs and human skin.

• Ascorbic acid utilizes SLC23A1 and SLC23A2 to transport across cell membranes. Are their expression more pronounced in cluster 14 fibroblasts? This would help connect the scRNA-seq data to the ascorbic acid experiments.

*

Our response:

We appreciate the valuable suggestions provided to investigate the mechanisms underlying the altered VC responsiveness observed in the EDV model. We plan to analyze the expression patterns of transporter genes potentially involved in the uptake and efflux of ascorbic acid, such as SVCT1 (SLC23A1), SVCT2 (SLC23A2), GLUT1 (SLC2A1), GLUT3 (SLC2A3), GLUT4 (SLC2A4), and MRP4, using scRNA-seq data.

There seems to be quite a bit of variability between replicant immunostains, in particular, vimentin in Fig. 3. Can the authors discuss this variability and whether any of the HSE organoid combinations reduced this variability?

Our response:

Thank you for your comments regarding the immunostaining. A reanalysis of the data, including newly acquired immunostaining images during the revision process, is planned.

• Please provide number of replicates throughout figure legends.*

Our response:

Thank you for your valuable advice. We have added the number of replicates to all figure legends.

• Line 148 states "E and EV models were transparent and extremely soft", should read "E and ED models".*

Our response:

The photographic data for the EV and ED models in Fig. 1b was incorrect and has therefore been corrected. We sincerely apologize for our oversight. As it was actually the E and EV models that appeared transparent, the description in the text remains unchanged.

• Line 150-151 states "In the E and EV models, an abnormal epidermis lacking a basal cell layer formed". The Krt5 staining in Figure 2 clearly shows a basal cell layer in these models, albeit abnormal. Stating that this the abnormal epidermis displayed a disrupted basal cell layer or columnar shape of basal cells were disrupted is more appropriate. In addition, these results do not show "crosstalk between NHEKs and NHDFs is essential for epithelialization" as the E and EV organoid models show epithelial stratification.*

Our response:

We sincerely appreciate your insightful guidance regarding the accurate presentation of the histological analysis results. Accordingly, we have revised lines 154–156 in the Results section in line with your recommendations.

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Referee #4

Evidence, reproducibility and clarity

The manuscript by Kimura et al. define how epidermal morphogenesis in human skin equivalents (HSE) differ by combining vascular endothelial cells, epidermal keratinocytes, and dermal fibroblasts using staining and single-cell RNA-sequencing (scRNA-seq). The three cell system (EDV) displayed higher levels of Ki67+ cells, decreased levels of TEWL, and higher elasticity in comparison to the keratinocyte and fibroblast HSE system (ED). The overall structural morphology between the two systems is quite similar, though the expression of cytokeratin markers varies. EDV organoids specifically express COL1 and COL4 collagen markers surrounding the blood vessels. VEGF-VEGFR1 signaling between endothelia-fibroblasts seems to be pronounced in the EDV organoids according to scRNA-seq, suggesting active signaling between these two cell types. And ascorbic acid appeared to help nutrient poor ED and EDV organoids proliferate compared to controls. This work is well detailed and interesting, helping to define how endothelial cells function to make HSE organoids more faithfully mimic in vivo human skin. Only minor clarifications detailed below are needed.

1. The human skin control in Fig. 1c seems thinner than normal and would suggest that the ED and EDV models are hyperproliferative. Replacing the control with one that shows normal thickness would prevent incorrect conclusions of the data.
2. KI67 and TEWL readings for human skin as controls for Fig. 2b-c would help gauge how the organoids perform and whether they are abnormal. What is the elasticity index for facial sagging?
3. Ascorbic acid utilizes SLC23A1 and SLC23A2 to transport across cell membranes. Are their expression more pronounced in cluster 14 fibroblasts? This would help connect the scRNA-seq data to the ascorbic acid experiments.
4. There seems to be quite a bit of variability between replicant immunostains, in particular, vimentin in Fig. 3. Can the authors discuss this variability and whether any of the HSE organoid combinations reduced this variability?
5. Please provide number of replicates throughout figure legends.
6. Line 148 states "E and EV models were transparent and extremely soft", should read "E and ED models".
7. Line 150-151 states "In the E and EV models, an abnormal epidermis lacking a basal cell layer formed". The Krt5 staining in Figure 2 clearly shows a basal cell layer in these models, albeit abnormal. Stating that this the abnormal epidermis displayed a disrupted basal cell layer or columnar shape of basal cells were disrupted is more appropriate. In addition, these results do not show "crosstalk between NHEKs and NHDFs is essential for epithelialization" as the E and EV organoid models show epithelial stratification.

Significance

This work is well detailed and interesting, helping to define how endothelial cells function to make HSE organoids more faithfully mimic in vivo human skin. Only minor clarifications detailed below are needed.

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Referee #3

Evidence, reproducibility and clarity

The study develops a tricellular human skin equivalent (HSE) model incorporating epidermal keratinocytes (NHEKs), dermal fibroblasts (NHDFs), and vascular endothelial cells (HUVECs). This model autonomously organizes pericytes, papillary fibroblasts, and reticular fibroblasts, mimicking in vivo dermal mesenchymal heterogeneity. The EDV model (all three cell types) demonstrates enhanced epidermal barrier function (reduced TEWL), dermal elasticity, collagen deposition, and vascular organization compared to simpler models. Single-cell RNA-seq confirms the emergence of pericyte-like and fibroblast subpopulations resembling in vivo counterparts. Nutrient-poor (NP) culture replicates aging phenotypes (reduced proliferation, barrier dysfunction, disordered collagen), rescued by ascorbic acid (AA), highlighting vascular cells' role in skin homeostasis. However, several key methodological clarifications (e.g., heatmap normalization, statistical reporting), more precise qualification of certain claims, and enhanced contextualization within the literature are needed before the work can be considered suitable for publication; I therefore recommend major revision.

Major comments:

1. Are the key conclusions convincing?<br /> The core claim-that tricellular interactions recapitulate dermal mesenchymal heterogeneity and enhance skin functionality-is well-supported by histology, immunohistochemistry, functional assays (TEWL, elasticity), and scRNA-seq.
2. Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether? The assertion that HSEs enable "identical" methodology to clinical studies (p. 2, line 29) is exaggerated. While elasticity was measured via Cutometer (used clinically), the model lacks immune/neural components and long-term stability for full translational equivalence.
3. Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation. Adequacy of Experimental Evidence & Need for Additional Experiments: No essential control appears to be missing: the authors include conditions {plus minus}ascorbic acid and {plus minus}vascular cells to isolate those effects. One could suggest a few additional experiments to further bolster the conclusions, but they are not strictly required for the main message. For example, to pinpoint the contribution of each mesenchymal subset, the authors could engineer HSE variants lacking one component at a time (omit pericytes or use only papillary vs. only reticular fibroblasts) to see how each omission affects barrier or elasticity. This would directly confirm each cell type's role. However, such experiments may be technically involved (especially isolating pure papillary vs. reticular fibroblast populations and ensuring viability in 3D culture) and might be beyond the scope of a single study. Another possible extension could be mechanistic assays, such as examining specific molecular signals: e.g., testing if blocking known paracrine factors from pericytes or fibroblast subsets diminishes the observed improvements. Given that pericytes can secrete laminin-511 and other factors that promote keratinocyte growth, the authors might, in future work, explore whether such factors mediate the enhanced epidermal proliferation seen with the vascularized HSE. Overall, the current data are sufficiently convincing that additional experiments are not absolutely necessary for publication.

4. Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments

5. Are the data and the methods presented in such a way that they can be reproduced? Yes
6. Are the experiments adequately replicated and statistical analysis adequate? The manuscript's data are presented in a manner that generally supports reproducibility. The authors state that all data are presented as "mean {plus minus} SD" (Methods, p.36). This is acceptable and clearly reported. However, I suggest that the authors consider using mean {plus minus} SEM for specific datasets where the primary goal is to assess statistical significance between groups - for example, for the Ki67-positive cell proliferation data (Fig. 6c) - as SEM better reflects the precision of the group mean for inferential comparisons. In contrast, for functional measures that inherently exhibit biological variation across samples (e.g., TEWL, skin elasticity), using mean {plus minus} SD remains fully appropriate, as SD reflects true inter-sample variability. To improve clarity and reproducibility, I encourage the authors to briefly state in the Methods or figure legends why SD or SEM is used in each case, in line with best practice guidelines.

Minor comments:

1. For Figure 4e, it would be helpful if the authors could clarify in the figure legend or Methods whether the heatmap shows log-normalized expression values (as derived from the Seurat object) or z-scored expression across cells or samples. This distinction affects the interpretation of relative versus absolute expression levels of the collagen and elastic fiber-related genes, which are central to the study's conclusions about ECM remodeling.
2. Typos: "factr" → "factor" (p. 16, line 244); "severl" → "several" (p. 22, line 367).

Significance

The study innovatively reconstructs dermal mesenchymal heterogeneity using commercially available cells and autonomous tricellular interactions, bypassing costly cell-sorting approaches. This democratizes complex HSE models for broader labs. This study demonstrates that vascularization is critical not only for nutrient supply but for instructing fibroblast/pericyte differentiation and ECM organization. The NP+AA paradigm (Fig. 6) offers a facile in vitro model for skin aging interventions, highlighting AA's efficacy via perivascular mechanisms.

Audience: Tissue engineers, dermatologists, cosmetic/pharma researchers (anti-aging screening), and developmental biologists studying mesenchymal niche regulation.

Placement in existing literature: Recent advances in skin tissue engineering have highlighted the importance of dermal fibroblast heterogeneity in skin homeostasis and regeneration. Single-cell transcriptomic studies (Tabib et al., J Invest Dermatol 2018; Solé-Boldo et al., Commun Biol 2020) have established that papillary and reticular fibroblasts exhibit distinct gene expression and functional roles. Prior engineered skin models incorporating fibroblast subtypes (Moreira et al., Biomater Sci 2023) or pericytes (Paquet-Fifield et al., J Clin Invest 2009) demonstrated improvements in vascularization or epidermal differentiation. However, a unified 3D human skin equivalent integrating vascular cells, pericytes, and spatially organized fibroblast subpopulations has not been systematically achieved. The present work by Kimura et al. advances the field by demonstrating that autonomous interaction among keratinocytes, endothelial cells, pericytes, and heterogeneous fibroblasts significantly enhances both barrier function and dermal elasticity, thus bringing engineered skin models closer to physiological skin. This addresses a key gap between prior single-cell descriptive studies and functional tissue engineering.

Define your field of expertise with a few keywords: experimental dermatology, skin cancer, tissue engineering and 3D skin models, cell biology, tumor microenvironment, and the skin microbiome and barrier function.

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Referee #2

Evidence, reproducibility and clarity

In this study, the authors present a novel and well-executed approach to reconstructing human skin equivalents (HSEs) that more faithfully replicate the functional complexity of native skin by incorporating the natural heterogeneity of dermal mesenchymal cells, including spatially organized pericytes, papillary fibroblasts, and reticular fibroblasts. Through autonomous interactions among keratinocytes, fibroblasts, and vascular endothelial cells, the fully tricellular EDV model emerged as the most functionally complete among seven engineered HSE variants, demonstrating enhanced epithelialization, barrier integrity, dermal elasticity, and angiogenic architecture. The study's strengths lie in its realistic aging induction via nutrient deprivation by mimicking aspects of vascular insufficiency in the papillary dermis, and its integration of diverse and rigorous evaluation methods, including histological and molecular analyses (Ki67, ECM markers), barrier function (TEWL), and mechanical testing. Notably, ascorbic acid treatment improved epidermal turnover and extracellular matrix organization, particularly through effects on perivascular niche cells, highlighting its translational relevance for anti-aging interventions. Although the EDV model showed superior elasticity via suction testing, more comprehensive mechanical characterization and longitudinal ECM analysis could further elucidate how mesenchymal heterogeneity supports biomechanical resilience. Overall, this work underscores the importance of multicellular crosstalk in skin physiology and positions the EDV model as a robust in vitro platform with high relevance for regenerative medicine, aging research, and therapeutic screening, offering the potential to eliminate animal models in skin biology.

Major comments:

Despite its strengths, the study has several limitations that warrant further investigation. The authors describe a "senescent-like" phenotype under nutrient-poor (NP) conditions, yet do not provide direct evidence of cellular senescence using canonical markers such as SA-β-gal staining, p16^INK4a or p21 expression, or SASP profiling-weakening their aging-related conclusions.

The 500 μM dose of ascorbic acid (AA), while within the reported range for skin models, is at the higher end compared to commonly used concentrations (100-300 μM) and lacks justification via dose/response data. Normal physiological levels and changes in aging dermis should be referenced in discussion. AA is also an additive in their standard HSE media, but this was not sufficiently emphasized to draw attention. Would its removal from the baseline media make a difference? Mechanistically, fibroblast heterogeneity is attributed to keratinocyte and vascular signals, but the signaling pathways involved (e.g., Wnt, TGF-β, VEGF) are not directly examined. Validating which paracrine factors (VEGF, PDGF, LAMA5, KGF) are mediating fibroblast transitions using inhibitors or RNA profiling could shed more light.

Minor comments:

The role of pericytes is also underexplored; while their presence is confirmed, functional assays or transcriptomic analyses to elucidate their contribution to ECM remodeling or vascular stability are not fully explored. The origin of pericyte-like cells remains uncertain without lineage tracing or barcoding to distinguish whether they derive from fibroblasts, endothelial cells, or culture artifacts. Since they observe induced differentiation of fibroblast-like cells in 3D culture, it would be compelling to reconstruct differentiation trajectories (pseudotime analysis) from progenitor states to papillary/reticular/pericyte-like states from their scRNAseq data. Although AA enhanced collagen production and elasticity in the vascularized EDV model, the lack of response in the ED model is not addressed mechanistically. The omission of immune cells which are key players in skin aging and homeostasis could increase physiological relevance of the model. The exclusive use of standard HUVECs may not fully capture the behavior of tissue-specific microvascular endothelial cells, potentially limiting the fidelity of the vascular niche.

Significance

This study presents a robust and innovative approach to human skin equivalent (HSE) reconstruction by integrating pericyte-like and endothelial cells with dermal fibroblast subtypes, using only commercially available cell types. A key strength lies in its ability to recapitulate aspects of in vivo fibroblast heterogeneity, including papillary, reticular, and perivascular populations, and to demonstrate functional consequences on tissue architecture, barrier integrity, ECM dynamics, and mechanical properties under aging-like, nutrient-poor conditions. The spontaneous emergence of a pericyte-like population without relying on freshly isolated primary pericytes or complex sorting protocols represents a methodological advance that increases the model's accessibility and scalability. Furthermore, the use of ascorbic acid to reverse aging-associated features in a vascular cell-dependent manner adds a compelling functional dimension, linking cell composition with therapeutic response.

Compared to existing models that either lack vascular cell compartments or do not account for dermal fibroblast heterogeneity, this study fills an important gap at the intersection of skin aging, vascular biology, and mesenchymal-epithelial interactions. The advance is both conceptual by elucidating the role of vascular and perivascular cells in shaping fibroblast identity and function and methodological, through the generation of a human skin model that approximates in vivo complexity without requiring animal models or ethically limited human tissue. The work will be of strong interest to basic science researchers in dermatology, tissue engineering, and aging, and has potential influence in regenerative medicine, cosmetic science, and drug screening, especially in the context of skin repair and anti-aging therapies. The audience is broad but most relevant to specialized communities in skin biology, mesenchymal cell biology, vascular biology, and organoid modeling, and may also attract attention from those developing non-animal testing platforms in applied and translational settings.

As a reviewer with expertise in inflammatory skin disease modeling using both animal systems and 3D organoid cultures, I bring a critical understanding of how cellular composition, microenvironmental cues, and co-culture conditions influence skin physiology and pathology. My interest in developing advanced co-culture systems to recapitulate human skin complexity positions me well to evaluate the relevance, innovation, and translational potential of this vascularized HSE model. I am especially qualified to assess the biological fidelity of the reconstructed skin architecture, the functional outcomes of introducing pericyte-like populations, and the implications of nutrient deprivation and ascorbic acid supplementation as aging-relevant perturbations.

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Referee #1

Evidence, reproducibility and clarity

The manuscript by Kimura et al investigates the role of different cell populations in the development of human skin equivalents (HSEs). The observe that the addition of vascular endothelial cells to HSEs improves epidermal differentiation and barrier function, alongside differentiation of fibroblasts into papillary, reticular, and pericyte like mesenchymal cells. The authors also use single-cell transcriptomics to characterise the gene signatures and putative signalling pathway in the fibroblasts. Finally, the authors use nutrient poor medium and ascorbic acid to modulate HSE develop.

One of the most significant questions arising from the findings is how the presence of vasculature can induce differentiation of fibroblasts from a common population, especially given that previous studies have shown that fibroblast identity is programmed during development. Some specific comments and suggestions for improving the manuscript are listed below.

Major points:

1. The introduction describes the effects of different environmental cues and aging on fibroblast phenotype, but it would be good to note the developmental origins of dermal fibroblasts, which specifies their fate and function (Driskell et al, Nature 2013).
2. In Fig 2, how do TEWL measurements compare to constructs without an epidermal layer or human skin? It may seem obvious that barrier function would be negligible in these models, but it would be a helpful negative control for interpreting the relative effects of vasculature on barrier function.
3. The mechanical measurements in Fig 2 are a nice idea, but it is a bit difficult to interpret without comparison to other conditions (e.g. human skin) or by reporting more universal mechanical parameters (e.g. Young's modulus).
4. The induction of region-specific fibroblast markers is interesting and a bit unexpected since all the fibroblasts came from the same source before seeding into HSEs. The conclusions require additional support from quantification of the IF staining in Fig 3.
5. Likewise, could the authors clarify whether the cells were passaged before seeding into the HSE, and if so, what passage number. Could passaging affect the responses observed? Please add a discussion point about this.
6. The scRNA-seq suggests that the in vitro populations do not discriminate between secretory papillary and pro-inflammatory fibroblasts. Could the authors add some further analysis or discussion regarding this point?
7. In Fig 6, it will be important to add quantification of epidermal thickness and differentiation marker expression to support the conclusions.
8. A key question is how NP and AA conditions affect the fibroblast populations as this seems to be a key factor in HSE maturation and would then link back to the previous sections. It would be good to stain for fibroblast markers in these samples.
9. As noted above, the ability of the vasculature to direct differentiation of a common fibroblast population into different phenotypes is one of the key findings of the study. To strengthen these observations, could additional analysis of the transcriptional data be possible. For example, would trajectory analysis potentially show how the different populations are evolving or related? In addition, could the CellChat analysis be performed between the vasculature and the different populations in Fig 5, which are mapped to in vivo populations? This might be a more relevant analysis than the populations in Fig 4.

Minor points:

1. The abstract states that enabling in vitro evaluation of drug efficacy using methodologies that are identical to those used in human clinical studies. This seems to be an over interpretation of the study and not well supported by the data. Please consider revising or removing.
2. Check referencing formatting in lines 118-121

Significance

Overall, the study represents a systematic analysis of how vasculature contributes to skin model development, and the impact on fibroblast differentiation is an interesting observation. It would have been more impactful if some of the pathways and genes were followed up with mechanistic studies, but the findings are still useful to the field. Likewise, further insight into exactly how the vasculature regulates fibroblast phenotype would add to the impact as this is an unexpected but important finding.

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Reply to the reviewers

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

As stated by the authors in the introduction, the RNA-binding protein Sxl is foundational to understanding sex determination in Drosophila. Sxl has been extensively studied as the master regulator of female sex determination in the soma, where it is known to initiate an alternative splicing cascade leading to the expression of DsxF. Additionally, Sxl has been shown to be responsible for keeping X chromosome dosage compensation off in females, while males hyperactivate their X chromosome. While these roles have been well defined, the authors explore an aspect of Sxl that is quite separate from its role as master regulator of female fate. They describe Sxl-RAC, a Sxl isoform that is expressed in the male and female nervous system. Using several genomic techniques, the authors conclude that the Sxl-RAC isoform associates with chromatin in a similar pattern to the RNA polymerase II/III subunit, Polr3E, and Sxl depends on Polr3E for chromatin-association. Further, neuronal loss of Sxl causes changes in lifetime and geotaxis in a similar manner as loss of Polr3E. The work is thorough and significant and should be appropriate for publication if a few issues can be addressed.

Major Concerns:*

* 1) How physiological is the Sxl chromatin-association assay? As binding interactions are concentration-dependent, how similar is Sxl-DAM expression to wt Sxl expression in neurons? In addition, does the Sxl-DAM protein function as a wt Sxl protein? Does UAS-Sxl-DAM rescue any Sxl loss phenotypes?*

Author response:

As Reviewer 3 correctly notes, Targeted DamID relies on ribosomal re-initiation (codon slippage) to produce only trace amounts of the Dam-fusion protein. By design, this results in expression levels that are significantly lower than those of the endogenous protein. As such, the experiment can be interpreted within a near–wild-type context, rather than as an overexpression model. The primary aim of this experiment was to determine whether Sxl associates with chromatin, and our dataset provides clear evidence supporting such binding.

2) Is Polr3E chromatin-association also dependent on Sxl? They should do the reciprocal experiment to their examination of Sxl chromatin-association in Polr3E knockdown. This might also help address point 1-if wt Sxl is normally required for aspects of Polr3E chromatin binding, then concerns about whether the Sxl-DAM chromatin-association is real or artifactual would be assuaged.

Author response:

This is an interesting thought, however, if Sxl were required for Polr3E recruitment to RNA Pol III, then, in most male Drosophila melanogaster cells, Polr3E would not be incorporated, and males would not be viable (as it is essential for Pol III activity). While it is possible that there could be a subtle effect on Polr3E recruitment, such an experiment, would not alter the central conclusion of our study - that Sxl is recruited to chromatin (accessory to the Pol III complex) via Polr3E.

Minor concerns:

* The observed Sxl loss of function phenotypes are somewhat subtle (although perhaps any behavior phenotype at all is a plus). Did they try any other behaviour assays-courtship, learning/memory, anything else at all to test nervous system function?*

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Author response:

Given the exploratory nature of this study, we focused on broader behavioural and transcriptional assays.

While well written, it is sometimes difficult to understand how the experiment was performed or what genotypes were used without looking into the methods sections. One example is they should describe the nature of the Sxl-DAM fusion protein clearly in the results.

Author response:

We will revise these sections to improve clarity and ensure there is no confusion.

* Reviewer #1 (Significance (Required)):

This manuscript represents a dramatic change in our thinking about the action of the Sex-lethal protein. Previously, Sxl was known as the master regulator of both sex determination and dosage compensation, and performed these roles as an RNA-binding protein affecting RNA splicing and translational regulation. Here, the authors describe a sex-non-specific role of Sxl in the male and female nervous system. Further, this activity appears independent of Sxl's RNA binding activity and instead Sxl functions as a chromatin-associating protein working with the RNA pol2/3 factor Polr3E to regulate gene expression. Thus, this represents a highly significant finding. *

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

Summary: In this paper, the authors report on an unexpected activity for Sex lethal (Sxl) (a known splicing regulator that functions in sex determination and dosage compensation) in binding to chromatin. They show, using DamID, that Sxl binds to approximately the same chromatin regions as Polr3E (a subunit of RNA Pol III). They show that this binding to chromatin is unaffected by mutations in the RNA binding domains or by deletions of either N or C terminal regions of the Sxl protein. This leads the authors to conclude that Sxl must bind to chromatin through some interacting protein working through the central region of the Sxl protein. They show that Sxl binding is dependent on Polr3E function. They show that male-specific neuronal knockdown of Sxl gives similar phenotypes to knockdown of Polr3E in terms of lethality and improved negative geotaxis. They show gene expression changes with knockdown of Sxl in male adult neurons - mainly that metabolic and pigmentation genes go down in expression. They also show that expression of a previously discovered male adult specific form of Sxl (that does not have splicing activity) in the same neurons also leads to changes in gene expression, including more upregulated than downregulated tRNAs. But they don't see (or don't show) that the same tRNA genes are down with knockdown of Sxl. Nonetheless, based on these findings, they suggest that Sxl plays an important role in regulating Pol III activity through the Polr3E subunit.

Major comments:

*

*To be honest, I'm not convinced that the conclusions drawn from this study are correct. The fact that every mutant form of Sxl shows the same result from the DamID labelling is a little concerning. I would like to see independent evidence of the SxlRac protein binding chromatin. *

Do antibodies against this form (or any form) of Sxl bind chromatin in salivary gland polytene chromosomes, for example? Does Sxl from other insects where Sxl has no role in sex determination bind chromatin?

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__Author Response: __

Regarding the reviewer’s overall concerns about the legitimacy of the Sxl binding data:

1. i) The fold differences between Dam-Sxl-mutants and the Dam-only control are very robust (up to 9 log2 fold change (500-fold change)), which is higher than what we observe with most transcription factors using Targeted DamID.

2. ii) We observed that Sxl binding was significantly reduced upon knockdown of Polr3E, confirming that the signal we observe is biologically specific and not due to technical noise or background. iii) If the concern relates to potential Sxl binding in non-neuronal tissues such as salivary glands, we would like to clarify that all DamID constructs were expressed under elav-GAL4, a pan-neuronal driver. Furthermore, dissections were performed to isolate larval brains, with salivary glands carefully removed. This ensures that chromatin profiles were derived from neuronal tissue exclusively.

3. iv) Salivary gland polytene chromosome staining with a Sxl antibody in a closely related species (Drosophila virilis) show __binding of Sxl to chromatin __in both sexes (Bopp et al., 1996). We will include more text in the revised manuscript to emphasise these points.

Do antibodies against this form (or any form) of Sxl bind chromatin in salivary gland polytene chromosomes, for example? Does Sxl from other insects where Sxl has no role in sex determination bind chromatin?

Author Response:

Prior work in Drosophila virilis (where Sxl is also required for sex determination and Sxl-RAC is conserved) has already demonstrated Sxl-chromatin association (using a full-length Sxl antibody) in salivary glands using polytene chromosome spreads (Bopp et al., 1996). Binding is observed in both sexes and across the genome, reflecting our observations. We will incorporate this into the revised discussion to support the chromatin-binding role of Sxl across species.

There is a clear and long-overlooked precedent for Sxl's alternative, sex-independent roles, findings that have been largely overshadowed by the gene’s canonical function. Our study not only validates and extends these observations but also brings much-needed attention to this understudied aspect of fundamental biology.

Bopp D, Calhoun G, Horabin JI, Samuels M, Schedl P. Sex-specific control of Sex-lethal is a conserved mechanism for sex determination in the genus Drosophila. Development. 1996 Mar;122(3):971-82. doi: 10.1242/dev.122.3.971. PMID: 8631274.

I would like to see independent evidence of the SxlRac protein binding chromatin.

* *__Author Response: __

We do not believe this is necessary:

1. i) Our data demonstrated that a large N-terminal truncation of Sxl (removing far more of the N-terminal region than is absent in Sxl-RAC) does not impair chromatin binding.
2. ii) Our deletion experiments show that it is the central domain __of Sxl that is required for chromatin association (as removal of the N-or C-terminal domain has no effect). This central domain is __unaffected in Sxl-RAC. iii) Independent Y2H experiments have shown that it is exclusively the__ RBD-1 __(RNA binding domain 1) of the central domain of Sxl that interacts with Polr3E (Dong et al., 1999). Sxl-RAC contains this region, therefore will be recruited by Polr3E.

iv) Review 3 also believes that this is not necessary (see cross-review below) and highlights the robustness of the Y2H experiments performed by Dong et al., 1999.

• *

Also, given that their DamID experiments reveal that Sxl binds half of the genes encoded in the Drosophila genome, finding that it binds around half of the tRNA genes is perhaps not surprising.

---

__Author Response: __

Our data show that Sxl binds to a range of Pol III-transcribed loci, and this binding pattern supports the proposed model that Sxl plays a broader regulatory role in Pol III activity. Within these Pol III targets, tRNA genes represent a specific and biologically relevant subset. The emphasis on tRNAs is not to suggest they are the exclusive or primary targets of Sxl, but rather to__ highlight a functionally important class of Pol III-transcribed elements__ that align with the model we are proposing. We will revise the text to better reflect this framing and avoid any confusion regarding the scope of Sxl’s binding profile.

*I would like to see evidence beyond citing a 1999 yeast two-hybrid study that Sxl and Polr3E directly interact with one another. *

---

Author response:

We do not believe this is necessary (these points were also mentioned above):

1. i) The Dong et al., 1999 study was highly comprehensive in its characterisation of Sxl binding to Polr3E.
2. ii) Our DamID data provide strong complementary evidence for this interaction: knockdown of Polr3E robustly reduces Sxl’s recruitment to chromatin, strongly supporting the relevance of the interaction in vivo. iii) Review 3 highlights the robustness of the Y2H experiments performed by Dong et al., 1999.

In my opinion, the differences in lethality observed with loss of Sxl versus control are unlikely to be meaningful given the different genetic backgrounds. The similar defects in negative geotaxis could be meaningful, but I'm unsure how often this phenotype is observed. What other class of genes affect negative geotaxis? It's a little unclear why having reduced expression of metabolic and pigment genes or of tRNAs would improve neuronal function.

---

Author response:

While the differences in survival were indeed subtle, they were statistically significant and thus warranted inclusion. Our primary aim in this section was to demonstrate that knockdown of Sxl or Polr3E results in comparable behavioural and transcriptional phenotypes, suggesting overlapping functional roles. In this context, we believe the data were presented transparently and effectively support our interpretation.

Regarding the negative geotaxis phenotype, we appreciate the reviewer’s interest and agree that it is both intriguing and atypical. For this reason, we performed the assay multiple times, particularly in Polr3e knockdowns, to confirm the robustness of the result. To address potential confounding variables, we carefully selected control lines that account for genetic background and transgene insertion site, including KK controls and attP40-matched lines. We also employed multiple independent RNAi lines targeting Sxl to validate the phenotype across different genetic backgrounds.

Although the observed improvement in climbing is unexpected, it is not without precedent in the RNA polymerase III field. Notably, Malik et al. (2024) demonstrated that heterozygous Polr3DEY/+ mutants exhibit a significantly delayed decline in climbing ability with age. We allude to this in the discussion and will revise the text to emphasise this connection more explicitly.

Finally, while we recognise that negative geotaxis is a relatively broad assay and thus does not pinpoint the precise cellular mechanisms involved, we interpret the phenotype as suggesting a neural basis and a functional role for Sxl in the nervous system.

One would expect that not just the same classes of genes would be affected by loss and overexpression of Sxl, but the same genes would be affected - are the same genes changing in opposite directions in the two experiments or just the same classes of genes. Likewise, are the same genes changing expression in the same direction with both Sxl and the Polr3E loss? Also, why are tRNA genes not also affected with Sxl loss. Finally, they describe the changes in gene expression as being in male adult neurons, but the sequencing was done of entire heads - so no way of knowing which cell type is showing differential gene expression.

Author response:

While we do examine gene classes, our approach also includes pairwise correlation analyses of gene expression changes between specific genotypes. Notably, we observed a significant positive correlation between Polr3e knockdowns and Sxl knockdowns, and a significant negative correlation between Sxl-RAC–expressing flies and Sxl knockdowns. Furthermore, we examined Sxl-DamID target genes within our RNA-seq datasets and found a consistent relationship between Sxl targets and genes differentially expressed in Polr3e knockdowns.

Regarding the Pol III qPCR results, we note that tRNA expression changes may require a longer duration of RNAi induction (e.g., beyond 4 days) to become apparent, especially given that phenotypic effects such as changes in lifespan and negative geotaxis only emerge after 20 days or more. It is also plausible that Sxl knockdown leads to a partial reduction in Pol III efficiency, which may not be readily detectable through bulk Pol III qPCRs. We are willing to repeat Pol III qPCRs at later timepoints to further investigate this trend.

Finally, we infer that gene expression changes observed in our RNA-seq data are of neuronal origin, as all knockdown and overexpression constructs used in this study were driven pan-neuronally using elav-/nSyb-GAL4. While we acknowledge that bulk RNA-seq does not provide cell-type resolution, tissue-specific assumptions are widely used in the field when driven by a relevant promoter.

I'm also not sure what I'm supposed to be seeing in panel 5F (or in the related supplemental figure) and if it has any meaning - If they are using the Sxl-T2A-Gal4 to drive mCherry, I think one would expect to see expression since Sxl transcripts are made in both males and in females. Also, one would expect to see active protein expression (OPP staining) in most cells of the adult male brain and I think that is what is observed, but again, I'm not sure what I'm supposed to be looking at given the absence of any arrows or brackets in the figures.

Author Response:

Due to the presence of the T2A tag and the premature stop codon in exon 3 of early male Sxl transcripts, GAL4 expression is not expected in males unless the head-specific SxlRAC isoform is produced. The aim of panel 5F is to demonstrate the spatial overlap between SxlRAC expression (as we are examining male brains) and regions of elevated protein synthesis, as detected by OPP staining.

To quantitatively assess this relationship, we performed colocalisation analysis using ImageJ, which showed a positive correlation between Sxl and OPP signal intensity, supporting this interpretation. It is also evident from our images that regions with lower levels of protein synthesis (such as the neuropil - as shown in independent studies Villalobos-Cantor et al., 2023) concurrently lack Sxl-related signal. We have highlighted regions in Fig. 5 exhibiting higher/lower levels of Sxl/OPP signal to better illustrate this relationship. We can also test the effects of knockdown/overexpression on general protein synthesis if required.

Villalobos-Cantor S, Barrett RM, Condon AF, Arreola-Bustos A, Rodriguez KM, Cohen MS, Martin I. Rapid cell type-specific nascent proteome labeling in Drosophila. Elife. 2023 Apr 24;12:e83545. doi: 10.7554/eLife.83545. PMID: 37092974; PMCID: PMC10125018.

Minor comments:

* Line 223 - 225 - I believe that it is expected that Sxl transcripts would be broadly expressed in the male and female adult, given that it is only the spliced form of the transcript that is female specific in expression. *

As explained above, the only isoform that will be ‘trapped’ by the T2A-GAL4 in males is the Sxl-RAC isoform (as the other isoforms contain premature stop codons). Our immunohistochemistry data indicate that Sxl-RAC is expressed in the male brain, specifically in neurons. Therefore, knockdown experiments in males will reduce all mRNA isoforms, of which, Sxl-RAC is the only one producing a protein.

Line 236 - 238 - Sentence doesn't make sense.

We have addressed and clarified this.

Reviewer #2 (Significance (Required)):

It would be significant to discover that a gene previously thought to function in only sex determination and dosage compensation also moonlights as a regulator of RNA polymerase III activity. Unfortunately, I am not convinced by the work presented in this study that this is the case.

My expertise is in Drosophila biology, including development, transcription, sex determination, morphogenesis, genomics, transcriptomics, DNA binding

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

Storer, McClure and colleagues use genome-wide DNA-protein binding assays, transcriptomics, and genetics to work out that Drosophila Sxl, widely known as an RNA-binding protein which functions as a splicing factor to determine sex identity in Drosophila and related species, is also a chromatin factor that can stimulate transcription by Pol III and Pol II of genes involved with metabolism and protein homeostasis, specifically some encoding tRNAs.

The evidence for the tenet of the paper -- that Sxl acts as a chromatin regulator with Polr3E, activating at least some of its targets with either Pol III or Pol II -- is logical and compelling, the paper is well written and the figures well presented. Of course, more experiments could always be wished for and proposed, but I think this manuscript could be published in many journals with just a minor revision not involving additional experiments. I have a few specific comments below, all minor.*

Scientific points: - The approach taken for the evaluation of Sxl DNA-binding activity in Fig2 is not entirely clear. I assume these are crosses of elav-Gal4 x different UAS- lines, then using males or females for UAS-Sxl-Full-Length. But what about the others? Were the experiments done in males only? This is hinted at in the main text but not explicitly indicated in the figure or the methods (at least, that I could easily find). And is this approach extended to all other experiments? Longevity? Climbing assays? Considering the role of Sxl, it may be helpful to be fastidiously systematic with this.

---

Author Response:

We have revised the wording to ensure greater clarity. Males were used for all survival and behavioural experiments (as only males can be leveraged for knocking down Sxl-RAC without affecting the canonical Sxl-F isoform).

- In the discussion, lines 360-61, the authors say: Indeed, knockdown of Polr3E leads to a loss of Sxl binding to chromatin, suggesting a cooperative mechanism. Maybe I am misunderstanding the authors, but when I read "cooperation" in this context I think of biochemical cooperative binding. This is possible, but I do not think a simple 'requirement' test can suggest specifically that this mechanistic feature of biochemical binding is at play. I would expect, for starters, a reciprocal requirement for binding (which is not tested), and some quantitative features that would be difficult to evaluate in vivo. I do not think cooperative binding needs to be invoked anyway, as the authors do not make any specific point or prediction about it. But if they do think this is going on, I think it would need to be referred to as a speculation.

---

Author Response:

We appreciate that the original wording may have been unclear and will revise the text to more accurately reflect a functional relationship, rather than implying direct cooperation.

- In lines 428-432, the authors discuss the ancestral role of Sxl and make a comparison with ELAV, in the context of an RNA-binding protein that has molecular functions beyond those of a splicing factor, considering the functions of ELAV in RNA stability and translation, and finishing with "suggesting that similar regulatory mechanisms may be at play". I do not understand this latter sentence. Which mechanisms are these? Are the authors referring to the molecular activities of ELAV and SXL? But what would be the similarity? SXL seems to have a dual capacity to bind RNA and protein interactors, which allows it to work both in chromatin-level regulation as well as post-transcriptionally in splicing; but ELAV seems rather to take advantage of its RNA binding function to make it work in multiple RNA-related contexts, all post-transcriptional. I do not see an obvious parallel beyond the fact that RNA binding proteins can function at different levels of gene expression regulation -- but I would not say this parallel are "similar regulatory mechanisms", so I find the whole comparison a bit confusing.

---

Author Response:

We have reduced this section, as it is largely speculative and intended to highlight potential, though indirect, links in higher organisms. Our goal was primarily to illustrate the possibility that Sxl may have an ancestral role distinct from its well-characterised function, and to suggest a potential avenue for future research into ELAV2’s involvement in chromatin or Pol III regulation.

- One aspect of the work that I find is missing in the discussion is the possibility that the simultaneous capacity of Sxl for RNA binding and Polr3E binding: are these mutually exclusive? if so, are they competitive or hierarchical? how would they be coordinated anyway?

---

Author Response:

This is an interesting point, and we have expanded on it further in the Discussion section.

- The only aspect of the paper where I found that one could make an experimental improvement is the claim that Sxl induces the expression of genes that have the overall effect of stimulating protein synthesis. The OPP experiment shows a correlation between the expression of Sxl and the rate of protein synthesis initiation. However, a more powerful experiment would be, rather obviously, to introduce Sxl knock-down in the same experiment, and observe whether in Sxl-expressing neurons the incorporation of OPP is reduced. I put this forth as a minor point because the tenet of the paper would not be affected by the results (though the perception of importance of the newly described function could be reinforced).

• *

Author Response:

This could be a valid experiment and we are prepared to perform it if required.

- In a similar way, it would be interesting to know whether the recruitment of Polr3E and Sxl to chromatin is co-dependent or Sxl follows Polr3E. This is also a minor point because this would possibly refine the mechanism of recruitment but does not alter the main discovery.

Author Response:

We have addressed a similar point for Reviewer 2 (see below) and will include a Discussion point for this:

If Sxl were required for Polr3E recruitment to RNA Pol III, then, in most male Drosophila melanogaster cells, Polr3E would not be incorporated, and males would not be viable (as it is essential for Pol III activity). While it is possible that there could be a subtle effect on Polr3E recruitment, such an experiment, would not alter the central conclusion of our study - that Sxl is recruited to chromatin (accessory to the Pol III complex) via Polr3E.

* Figures and reporting:

• In Figure 2, it would be helpful to see the truncation coordinate for the N and C truncations.

• In Figure 3D, genomic coordinates are missing.

• In Figure 3E, the magnitude in the Y axis is not entirely clear (at least not to me). How is the amount of binding across the genome quantified? Is this the average amplitude of normalised TaDa signal across the genome? Or only within binding intervals?

• Figure S3E-F: it would be interesting to show the degree of overlap between the downregulated genes that are also binding targets (regardless of the outcome).

• Figure 5C-E: similarly to Figure S3, it would be interesting to know how the transcriptional effects compare with the binding targets.

• Authors use Gehan-Breslow-Wilcoxon to test survival, which is a bit unusual, as it gives more weight to the early deaths (which are rare in most Drosophila longevity experiments). Is there any rationale behind this? It may be even favour their null hypothesis.*

---

Author response:

Thank you for the detailed feedback on our figures. We have__ incorporated__ the suggested changes.

We agree that examining the overlap between Sxl binding sites and transcriptional changes is valuable, and we aimed to highlight this in the pie charts shown in Figures S3 and S5. If the reviewer is suggesting a more explicit quantification of the proportion of Sxl-Dam targets with significant transcriptomic changes, we are happy to include this analysis in the final version of the manuscript.

As noted in the Methods, both Gehan–Breslow–Wilcoxon (GBW) and Kaplan–Meier tests were used. The significance in Figure 4a is specific to the GBW test, which we indicated by describing the effect as mild. Our focus here is not on the magnitude of survival differences, but on the consistent trends observed in both Polr3e and Sxl knockdowns.

Writing and language:*

• Introduction finishes without providing an outline of the findings (which is fine by me if that is what the authors wanted).

• In lines 361-5, the authors say "We speculate that this interaction not only facilitates Pol III transcription but may also influence chromatin architecture and RNA Pol II-driven transcription as observed with Pol III regulation in other organisms". "This interaction" refers to Polr3E-Sxl-DNA interaction and with "Pol III transcription" I presume the authors refer to transcription executed by Pol III. I am not clear about the meaning of the end of the sentence "as observed with Pol III regulation in other organisms". What is the observation, exactly? That Pol III modifies chromatin in Pol II regulated loci, or that Pol III interactors change chromatin architecture?

• DPE abbreviation is not introduced (and only used once).

• A few typos: Line 41 ...splicing of the Sxl[late] transcripts, which is [ARE?] constitutively transcribed (Keyes et al.,... Line 76 ...sexes but appears restricted to the nervous system [OF] male pupae and adults (Cline et Line 289 ...and S41). To assess any effect [ON]translational output, O-propargyl-puromycin (OPP)o Line 323 ...illustrating that the majority (72%) changes in tRNA levels [ARE] due to upregulation...hi Line 402 ...it was discovered [WE DISCOVERED] Line 792 ...Sxl across chromosomes X, 2 L/R, 3 L/R and 4. The y-axis represents the log[SYMBOL] ratio... This happens in other figure legends as well.*

---

Author response:

Thank you for the detailed feedback, we have clarified and incorporated the suggested changes.

**Referee Cross-commenting***

Reviewer 1 asks how physiological is the Sxl chromatin-association assay. I think the loss of association in Polr3E knock-down and the lack of association of other splicing factors goes a long way into answering this question. It is true that having positive binding data specifically for Sxl-RAC and negative binding data for a deletion mutant of the RMM domain would provide more robust conclusions (see below), but I am not sure it is completely necessary -- though this will depend on which journal the authors want to send the paper to.

I think that the comment of reviewer 1 about the levels of expression of Sxl-DAM does not apply here because of the way TaDa works - it relies on codon slippage to produce minimal amounts of the DAM fusion protein, so by construction it will be expressed at much lower levels than the endogenous protein.

Reviewer 1 also asks whether Polr3E chromatin-association is also dependent on Sxl, to round up the model and also as a way to address whether Sxl association to chromatin is real. While I agree with this on the former aim (this would be a nice-to-have), I think I disagree on the latter; there is no need for Polr3E recruitment to depend on Sxl for Sxl association to chromatin to be physiologically relevant. Polr3E is a peripheral component of Pol III and unlikely to depend on a factor of restricted expression like Sxl to interact with chromatin. The recruitment of Sxl could well be entirely 'hierarchical' and subject to Polr3E.

Revewer 2 is concerned with the fact that every mutant form of Sxl shows the same result from the DamID labelling. I have to agree with this to a point. A deletion mutant of RMM domains would address this. Microscopy evidence in salivary glands would be nice, certainly, but the system may not lend itself to this particular interaction, which might be short-lived and/or weak. I do not immediately see the relevance of the chromatin binding capacity of non-Drosophilidae Sxl -- though it might indicate that the impact of the discovery is less likely to go beyond this group.

Reviewer 2 does not find surprising that some tRNA genes (less than half) are regulated by Sxl. I think the value of that observation is just qualitative, as tRNAs are Pol III-produced transcripts, but their point is correct. A hypergeometric test could settle this.

Reviewer 2 is concerned that the evidence of direct interaction between Sxl and Polr3E is a single 1999 two-hybrid study. But that paper contains also GST pull-downs that narrow down the specific domains that mediate binding, and perform the binding in competitive salt conditions. I think it is enough. The author team, I think, are not biochemists, so finding the right collaborators and performing these experiments would take time that I am not sure is warranted.

Reviewer 2 is also concerned that the longevity assays may not be meaningful due to the difference in genetic backgrounds. This is a very reasonable concern (which I would extend to the climbing assays - any quantitative phenotype is sensitive to genetic background). However, I think the authors here may have already designed the experiment with this in mind - the controls express untargeted RNAi constructs, but I lose track of which one is control of which. This should be clarified in Methods.

Other comments are in line, I think, with what I have pointed out and I generally agree with everything else that has been said.

Reviewer #3 (Significance (Required)):

Drosophila Sxl is widely known as an RNA-binding protein which functions as a splicing factor to determine sex identity in Drosophila and related species. It is a favourite example of how splicing factors and alternative can have profound influence in biology and used cleverly in the molecular circuitry of the cell to enact elegant regulatory decisions.

In this work, Storer, McClure and colleagues use genome-wide DNA-protein binding assays, transcriptomics, and genetics to work out that Sxl is also a chromatin factor with an sex-independent, neuron-specific role in stimulating transcription by Pol III and Pol II, of genes involved with metabolism and protein homeostasis, including some encoding tRNAs.

This opens a large number of interesting biological questions that range from biochemistry, gene regulation or neurobiology to evolution. How is the simultaneous capacity of binding RNA and chromatin (with the same protein domain, RRM) regulated/coordinated? How did this dual activity evolve and which one is the ancestral one? How many other RRM-containin RNA-binding proteins can also bind chromatin? How is Sxl recruited to chromatin to both Pol II and Pol III targets and are they functionally related? If so, how is the coordination of cellular functions activated through different RNA polymerases taking place and what is the role of Sxl in this? What are the functional consequences to neuronal biology? Does this affect similarly all Sxl-expressing neurons?

The evidence for the central tenet of the paper -- that Sxl acts as a chromatin regulator with Polr3E, activating at least some of its targets with either Pol III or Pol II -- is logical and compelling, the paper is well written and the figures well presented. Of course, more experiments could always be wished for and proposed, but I think this manuscript could be published in many journals with just a minor revision not involving additional experiments.*

Reviewer #4 (Evidence, reproducibility and clarity (Required)):

*The convincing analysis demonstrates a role for the Drosophila Sex determining gene sex lethal in controlling aspects of transcription in the nervous system independent of its role in splicing. Interaction with an RNA Pol III subunit mediating Sxl association with chromatin and similar knockdown phenotypes strongly support the role of Sxl in the regulation of neuronal metabolism. Given that Sxl is an evolutionary recent acquisition for sex determination, the study may reveal an ancestral role for Sxl.

The conclusions are well justified by the datasets presented and I have no issues with the study or the interpretation. Throughout the work is well referenced, though perhaps the authors might take a look at Zhang et al (2014) (PMID: 24271947) for an interesting evolutionary perspective for the discussion.*

Author Response:

Thank you for the thoughtful suggestion. We will be sure to incorporate the findings from Zhang et al. regarding the evolution of the sex determination pathway.

*I have some minor comments for clarification:

There is no Figure 2b, should be labelled 2 or label TaDa plots as 2b

Clarify if Fig 2 data are larval or adult *

*Larval

Fig 3d - are these replicates or female and male?

Please elaborate on tub-GAL80[ts] developmental defects

Fig 4e, are transcriptomics done with the VDRC RNAi line? The VDRC and BDSC RNAi lines exhibit different behaviours - former has "better" survival and Better negative geotaxis, the latter seems to have poorer survival but little geotaxis effect?*

*Fig S3 - volcano plot for Polr3E?

Fig S4a - legend says downregulated genes?

The discussion should at least touch on the fact that Sxl amorphs (i.e. Sxl[fP7B0] are male viable and fertile, emphasising that the newly uncovered role is not essential.*

Author Response:

We agree with the suggestions outlined in the comments and have made the appropriate revisions.

Reviewer #4 (Significance (Required)):*

A nonessential role for Sxl in the nervous system independent of sex-determination contributes to better understanding a) the evolution of sex determining mechanisms, b) the role of RNA PolIII in neuronal homeostasis and c) more widely to the neuronal aging field. I think this well-focused study reveals a hitherto unsuspected role for Sxl.*

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

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Referee #4

Evidence, reproducibility and clarity

The convincing analysis demonstrates a role for the Drosophila Sex determining gene sex lethal in controlling aspects of transcription in the nervous system independent of its role in splicing. Interaction with an RNA Pol III subunit mediating Sxl association with chromatin and similar knockdown phenotypes strongly support the role of Sxl in the regulation of neuronal metabolism. Given that Sxl is an evolutionary recent acquisition for sex determination, the study may reveal an ancestral role for Sxl.

The conclusions are well justified by the datasets presented and I have no issues with the study or the interpretation. Throughout the work is well referenced, though perhaps the authors might take a look at Zhang et al (2014) (PMID: 24271947) for an interesting evolutionary perspective for the discussion. I have some minor comments for clarification:

There is no Figure 2b, should be labelled 2 or label TaDa plots as 2b

Clarify if Fig 2 data are larval or adult

Fig 3d - are these replicates or female and male?

Please elaborate on tub-GAL80[ts] developmental defects

Fig 4e, are transcriptomics done with the VDRC RNAi line? The VDRC and BDSC RNAi lines exhibit different behaviours - former has "better" survival and Better negative geotaxis, the latter seems to have poorer survival but little geotaxis effect?

Fig S3 - volcano plot for Polr3E?

Fig S4a - legend says downregulated genes?

The discussion should at least touch on the fact that Sxl amorphs (i.e. Sxl[fP7B0] are male viable and fertile, emphasising that the newly uncovered role is not essential

Significance

A nonessential role for Sxl in the nervous system independent of sex-determination contributes to better understanding a) the evolution of sex determining mechanisms, b) the role of RNA PolIII in neuronal homeostasis and c) more widely to the neuronal aging field. I think this well-focused study reveals a hitherto unsuspected role for Sxl.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #3

Evidence, reproducibility and clarity

Storer, McClure and colleagues use genome-wide DNA-protein binding assays, transcriptomics, and genetics to work out that Drosophila Sxl, widely known as an RNA-binding protein which functions as a splicing factor to determine sex identity in Drosophila and related species, is also a chromatin factor that can stimulate transcription by Pol III and Pol II of genes involved with metabolism and protein homeostasis, specifically some encoding tRNAs.

The evidence for the tenet of the paper -- that Sxl acts as a chromatin regulator with Polr3E, activating at least some of its targets with either Pol III or Pol II -- is logical and compelling, the paper is well written and the figures well presented. Of course, more experiments could always be wished for and proposed, but I think this manuscript could be published in many journals with just a minor revision not involving additional experiments. I have a few specific comments below, all minor.

Scientific points:

• The approach taken for the evaluation of Sxl DNA-binding activity in Fig2 is not entirely clear. I assume these are crosses of elav-Gal4 x different UAS- lines, then using males or females for UAS-Sxl-Full-Length. But what about the others? Were the experiments done in males only? This is hinted at in the main text but not explicitly indicated in the figure or the methods (at least, that I could easily find). And is this approach extended to all other experiments? Longevity? Climbing assays? Considering the role of Sxl, it may be helpful to be fastidiously systematic with this.
• In the discussion, lines 360-61, the authors say: Indeed, knockdown of Polr3E leads to a loss of Sxl binding to chromatin, suggesting a cooperative mechanism. Maybe I am misunderstanding the authors, but when I read "cooperation" in this context I think of biochemical cooperative binding. This is possible, but I do not think a simple 'requirement' test can suggest specifically that this mechanistic feature of biochemical binding is at play. I would expect, for starters, a reciprocal requirement for binding (which is not tested), and some quantitative features that would be difficult to evaluate in vivo. I do not think cooperative binding needs to be invoked anyway, as the authors do not make any specific point or prediction about it. But if they do think this is going on, I think it would need to be referred to as a speculation.
• In lines 428-432, the authors discuss the ancestral role of Sxl and make a comparison with ELAV, in the context of an RNA-binding protein that has molecular functions beyond those of a splicing factor, considering the functions of ELAV in RNA stability and translation, and finishing with "suggesting that similar regulatory mechanisms may be at play". I do not understand this latter sentence. Which mechanisms are these? Are the authors referring to the molecular activities of ELAV and SXL? But what would be the similarity? SXL seems to have a dual capacity to bind RNA and protein interactors, which allows it to work both in chromatin-level regulation as well as post-transcriptionally in splicing; but ELAV seems rather to take advantage of its RNA binding function to make it work in multiple RNA-related contexts, all post-transcriptional. I do not see an obvious parallel beyond the fact that RNA binding proteins can function at different levels of gene expression regulation -- but I would not say this parallel are "similar regulatory mechanisms", so I find the whole comparison a bit confusing.
• One aspect of the work that I find is missing in the discussion is the possibility that the simultaneous capacity of Sxl for RNA binding and Polr3E binding: are these mutually exclusive? if so, are they competitive or hierarchical? how would they be coordinated anyway?
• The only aspect of the paper where I found that one could make an experimental improvement is the claim that Sxl induces the expression of genes that have the overall effect of stimulating protein synthesis. The OPP experiment shows a correlation between the expression of Sxl and the rate of protein synthesis initiation. However, a more powerful experiment would be, rather obviously, to introduce Sxl knock-down in the same experiment, and observe whether in Sxl-expressing neurons the incorporation of OPP is reduced. I put this forth as a minor point because the tenet of the paper would not be affected by the results (though the perception of importance of the newly described function could be reinforced).
• In a similar way, it would be interesting to know whether the recruitment of Polr3E and Sxl to chromatin is co-dependent or Sxl follows Polr3E. This is also a minor point because this would possibly refine the mechanism of recruitment but does not alter the main discovery.

Figures and reporting:

• In Figure 2, it would be helpful to see the truncation coordinate for the N and C truncations.
• In Figure 3D, genomic coordinates are missing.
• In Figure 3E, the magnitude in the Y axis is not entirely clear (at least not to me). How is the amount of binding across the genome quantified? Is this the average amplitude of normalised TaDa signal across the genome? Or only within binding intervals?
• Figure S3E-F: it would be interesting to show the degree of overlap between the downregulated genes that are also binding targets (regardless of the outcome).
• Figure 5C-E: similarly to Figure S3, it would be interesting to know how the transcriptional effects compare with the binding targets.
• Authors use Gehan-Breslow-Wilcoxon to test survival, which is a bit unusual, as it gives more weight to the early deaths (which are rare in most Drosophila longevity experiments). Is there any rationale behind this? It may be even favour their null hypothesis.

Writing and language:

• Introduction finishes without providing an outline of the findings (which is fine by me if that is what the authors wanted).
• In lines 361-5, the authors say "We speculate that this interaction not only facilitates Pol III transcription but may also influence chromatin architecture and RNA Pol II-driven transcription as observed with Pol III regulation in other organisms". "This interaction" refers to Polr3E-Sxl-DNA interaction and with "Pol III transcription" I presume the authors refer to transcription executed by Pol III. I am not clear about the meaning of the end of the sentence "as observed with Pol III regulation in other organisms". What is the observation, exactly? That Pol III modifies chromatin in Pol II regulated loci, or that Pol III interactors change chromatin architecture?
• DPE abbreviation is not introduced (and only used once).
• A few typos: Line 41 ...splicing of the Sxl[late] transcripts, which is [ARE?] constitutively transcribed (Keyes et al.,... Line 76 ...sexes but appears restricted to the nervous system [OF] male pupae and adults (Cline et Line 289 ...and S41). To assess any effect [ON]translational output, O-propargyl-puromycin (OPP)o Line 323 ...illustrating that the majority (72%) changes in tRNA levels [ARE] due to upregulation...hi Line 402 ...it was discovered [WE DISCOVERED] Line 792 ...Sxl across chromosomes X, 2 L/R, 3 L/R and 4. The y-axis represents the log[SYMBOL] ratio... This happens in other figure legends as well.

Referee Cross-commenting

Reviewer 1 asks how physiological is the Sxl chromatin-association assay. I think the loss of association in Polr3E knock-down and the lack of association of other splicing factors goes a long way into answering this question. It is true that having positive binding data specifically for Sxl-RAC and negative binding data for a deletion mutant of the RMM domain would provide more robust conclusions (see below), but I am not sure it is completely necessary -- though this will depend on which journal the authors want to send the paper to.

I think that the comment of reviewer 1 about the levels of expression of Sxl-DAM does not apply here because of the way TaDa works - it relies on codon slippage to produce minimal amounts of the DAM fusion protein, so by construction it will be expressed at much lower levels than the endogenous protein.

Reviewer 1 also asks whether Polr3E chromatin-association is also dependent on Sxl, to round up the model and also as a way to address whether Sxl association to chromatin is real. While I agree with this on the former aim (this would be a nice-to-have), I think I disagree on the latter; there is no need for Polr3E recruitment to depend on Sxl for Sxl association to chromatin to be physiologically relevant. Polr3E is a peripheral component of Pol III and unlikely to depend on a factor of restricted expression like Sxl to interact with chromatin. The recruitment of Sxl could well be entirely 'hierarchical' and subject to Polr3E.

Revewer 2 is concerned with the fact that every mutant form of Sxl shows the same result from the DamID labelling. I have to agree with this to a point. A deletion mutant of RMM domains would address this. Microscopy evidence in salivary glands would be nice, certainly, but the system may not lend itself to this particular interaction, which might be short-lived and/or weak. I do not immediately see the relevance of the chromatin binding capacity of non-Drosophilidae Sxl -- though it might indicate that the impact of the discovery is less likely to go beyond this group.

Reviewer 2 does not find surprising that some tRNA genes (less than half) are regulated by Sxl. I think the value of that observation is just qualitative, as tRNAs are Pol III-produced transcripts, but their point is correct. A hypergeometric test could settle this.

Reviewer 2 is concerned that the evidence of direct interaction between Sxl and Polr3E is a single 1999 two-hybrid study. But that paper contains also GST pull-downs that narrow down the specific domains that mediate binding, and perform the binding in competitive salt conditions. I think it is enough. The author team, I think, are not biochemists, so finding the right collaborators and performing these experiments would take time that I am not sure is warranted.

Reviewer 2 is also concerned that the longevity assays may not be meaningful due to the difference in genetic backgrounds. This is a very reasonable concern (which I would extend to the climbing assays - any quantitative phenotype is sensitive to genetic background). However I think the authors here may have already designed the experiment with this in mind - the controls expres untargeted RNAi constructs, but I lose track of which one is control of which. This should be clarified in Methods.

Other comments are in line, I think, with what I have pointed out and I generally agree with everything else that has been said.

Significance

Drosophila Sxl is widely known as an RNA-binding protein which functions as a splicing factor to determine sex identity in Drosophila and related species. It is a favourite example of how splicing factors and alternative can have profound influence in biology and used cleverly in the molecular circuitry of the cell to enact elegant regulatory decisions.

In this work, Storer, McClure and colleagues use genome-wide DNA-protein binding assays, transcriptomics, and genetics to work out that Sxl is also a chromatin factor with an sex-independent, neuron-specific role in stimulating transcription by Pol III and Pol II, of genes involved with metabolism and protein homeostasis, including some encoding tRNAs.

This opens a large number of interesting biological questions that range from biochemistry, gene regulation or neurobiology to evolution. How is the simultaneous capacity of binding RNA and chromatin (with the same protein domain, RRM) regulated/coordinated? How did this dual activity evolve and which one is the ancestral one? How many other RRM-containin RNA-binding proteins can also bind chromatin? How is Sxl recruited to chromatin to both Pol II and Pol III targets and are they functionally related? If so, how is the coordination of cellular functions activated through different RNA polymerases taking place and what is the role of Sxl in this? What are the functional consequences to neuronal biology? Does this affect similarly all Sxl-expressing neurons?

The evidence for the central tenet of the paper -- that Sxl acts as a chromatin regulator with Polr3E, activating at least some of its targets with either Pol III or Pol II -- is logical and compelling, the paper is well written and the figures well presented. Of course, more experiments could always be wished for and proposed, but I think this manuscript could be published in many journals with just a minor revision not involving additional experiments.

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Referee #2

Evidence, reproducibility and clarity

Summary:

In this paper, the authors report on an unexpected activity for Sex lethal (Sxl) (a known splicing regulator that functions in sex determination and dosage compensation) in binding to chromatin. They show, using DamID, that Sxl binds to approximately the same chromatin regions as Polr3E (a subunit of RNA Pol III). They show that this binding to chromatin is unaffected by mutations in the RNA binding domains or by deletions of either N or C terminal regions of the Sxl protein. This leads the authors to conclude that Sxl must bind to chromatin through some interacting protein working through the central region of the Sxl protein. They show that Sxl binding is dependent on Polr3E function. They show that male-specific neuronal knockdown of Sxl gives similar phenotypes to knockdown of Polr3E in terms of lethality and improved negative geotaxis. They show gene expression changes with knockdown of Sxl in male adult neurons - mainly that metabolic and pigmentation genes go down in expression. They also show that expression of a previously discovered male adult specific form of Sxl (that does not have splicing activity) in the same neurons also leads to changes in gene expression, including more upregulated than downregulated tRNAs. But they don't see (or don't show) that the same tRNA genes are down with knockdown of Sxl. Nonetheless, based on these findings, they suggest that Sxl plays an important role in regulating Pol III activity through the Polr3E subunit.

Major comments:

To be honest, I'm not convinced that the conclusions drawn from this study are correct. The fact that every mutant form of Sxl shows the same result from the DamID labelling is a little concerning. I would like to see independent evidence of the SxlRac protein binding chromatin. Do antibodies against this form (or any form) of Sxl bind chromatin in salivary gland polytene chromosomes, for example? Does Sxl from other insects where Sxl has no role in sex determination bind chromatin?

Also, given that their DamID experiments reveal that Sxl binds half of the genes encoded in the Drosophila genome, finding that it binds around half of the tRNA genes is perhaps not surprising.

I would like to see evidence beyond citing a 1999 yeast two-hybrid study that Sxl and Polr3E directly interact with one another. In my opinion, the differences in lethality observed with loss of Sxl versus control are unlikely to be meaningful given the different genetic backgrounds. The similar defects in negative geotaxis could be meaningful, but I'm unsure how often this phenotype is observed. What other class of genes affect negative geotaxis? It's a little unclear why having reduced expression of metabolic and pigment genes or of tRNAs would improve neuronal function.

One would expect that not just the same classes of genes would be affected by loss and overexpression of Sxl, but the same genes would be affected - are the same genes changing in opposite directions in the two experiments or just the same classes of genes. Likewise, are the same genes changing expression in the same direction with both Sxl and the Polr3E loss? Also, why are tRNA genes not also affected with Sxl loss. Finally, they describe the changes in gene expression as being in male adult neurons, but the sequencing was done of entire heads - so no way of knowing which cell type is showing differential gene expression.

I'm also not sure what I'm supposed to be seeing in panel 5F (or in the related supplemental figure) and if it has any meaning - If they are using the Sxl-T2A-Gal4 to drive mCherry, I think one would expect to see expression since Sxl transcripts are made in both males and in females. Also, one would expect to see active protein expression (OPP staining) in most cells of the adult male brain and I think that is what is observed, but again, I'm not sure what I'm supposed to be looking at given the absence of any arrows or brackets in the figures.

Minor comments:

Line 223 - 225 - I believe that it is expected that Sxl transcripts would be broadly expressed in the male and female adult, given that it is only the spliced form of the transcript that is female specific in expression.

Line 236 - 238 - Sentence doesn't make sense.

Significance

It would be significant to discover that a gene previously thought to function in only sex determination and dosage compensation also moonlights as a regulator of RNA polymerase III activity. Unfortunately, I am not convinced by the work presented in this study that this is the case.

My expertise is in Drosophila biology, including development, transcription, sex determination, morphogenesis, genomics, transcriptomics, DNA binding

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Referee #1

Evidence, reproducibility and clarity

As stated by the authors in the introduction, the RNA-binding protein Sxl is foundational to understanding sex determination in Drosophila. Sxl has been extensively studied as the master regulator of female sex determination in the soma, where it is known to initiate an alternative splicing cascade leading to the expression of DsxF. Additionally, Sxl has been shown to be responsible for keeping X chromosome dosage compensation off in females, while males hyperactivate their X chromosome. While these roles have been well defined, the authors explore an aspect of Sxl that is quite separate from its role as master regulator of female fate. They describe Sxl-RAC, a Sxl isoform that is expressed in the male and female nervous system. Using several genomic techniques, the authors conclude that the Sxl-RAC isoform associates with chromatin in a similar pattern to the RNA polymerase II/III subunit, Polr3E, and Sxl depends on Polr3E for chromatin-association. Further, neuronal loss of Sxl causes changes in lifetime and geotaxis in a similar manner as loss of Polr3E. The work is thorough and significant and should be appropriate for publication if a few issues can be addressed.

Major Concerns

1. How physiological is the Sxl chromatin-association assay? As binding interactions are concentration-dependent, how similar is Sxl-DAM expression to wt Sxl expression in neurons? In addition, does the Sxl-DAM protein function as a wt Sxl protein? Does UAS-Sxl-DAM rescue any Sxl loss phenotypes?
2. Is Polr3E chromatin-association also dependent on Sxl? They should do the reciprocal experiment to their examination of Sxl chromatin-association in Polr3E knockdown. This might also help address point 1-if wt Sxl is normally required for aspects of Polr3E chromatin binding, then concerns about whether the Sxl-DAM chromatin-association is real or artifactual would be assuaged.

Minor concerns

The observed Sxl loss of function phenotypes are somewhat subtle (although perhaps any behavior phenotype at all is a plus). Did they try any other behaviour assays-courtship, learning/memory, anything else at all to test nervous system function?

While well written, it is sometimes difficult to understand how the experiment was performed or what genotypes were used without looking into the methods sections. One example is they should describe the nature of the Sxl-DAM fusion protein clearly in the results.

Significance

This manuscript represents a dramatic change in our thinking about the action of the Sex-lethal protein. Previously, Sxl was known as the master regulator of both sex determination and dosage compensation, and performed these roles as an RNA-binding protein affecting RNA splicing and translational regulation. Here, the authors describe a sex-non-specific role of Sxl in the male and female nervous system. Further, this activity appears independent of Sxl's RNA binding activity and instead Sxl functions as a chromatin-associating protein working with the RNA pol2/3 factor Polr3E to regulate gene expression. Thus, this represents a highly significant finding.

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Reply to the reviewers

1. General Statements

• This manuscript represents a full revision incorporating all reviewer recommendations; the additional follow-up experiments and expanded analyses will be presented in dedicated subsequent manuscripts.
• Congenital dyserythropoietic anemia type I (CDA-I) is a rare hereditary disease characterized by ineffective erythropoiesis and mutations in Codanin1 and CDIN1.
• Our study reveals the structural and functional dynamics of the CDIN1-Codanin1 complex, shedding light on the molecular mechanisms of protein-protein interactions implicated in CDA-I pathology.
• The main goal of our study was to examine the interaction between CDIN1 and the C‑terminal binding domain of Codanin1 using complementary biophysical approaches.
• We quantified binding and identified interacting regions of Codanin1 and CDIN1.
• We found that CDA-I-associated mutations in interacting regions disturb CDIN1‑Codanin1 complex.
• We proposed a hypothetical molecular model of CDIN1-Codanin1 role in CDA-I hallmarks development.
• Our initial studies on BioRxiv (2023) have been cited by leading publications in the field (Jeong, Frater et al. 2025, Sedor and Shao 2025, Nature Communications) and prompted further research on this topic.

2. Point-by-point description of the revisions

*Here we provide a point-by-point reply describing the revisions already carried out and included in the transferred manuscript. *

Reply to the reviewers

Reviewer #1 – Evidence, reproducibility and clarity

This is a rigorous biophysical characterization of a protein-protein interaction relevant to CDA-1 disease. The two proteins were purified in an E. coli host but CD and DLS was performed to ensure that the purified protein is well folded. An impressive native protein EMSA was used to show a 1:1 complex. While common for protein-nucleic acid complexes, EMSAs are much more challenging with protein complexes. A higher-running complex, likely a heterotetramer was implied at higher protein concentrations. These results were supported with SEC-MALS analysis and analytic ultracentrifugation analysis. Thermophoresis and ITC were used to report a nanomolar affinity of the proteins for each other. SEC-SAXS supported the conclusions about stoichiometry and composition inferred from the earlier methods and suggested that the dimerization interface comes from CDIN1. Next HDX-MS was used to identify putative interface residues, which were then mutated in each of the proteins and assessed for binding using coimmunoprecipitation. This study uses at least 10 orthogonal biophysical and/or biochemical methodologies to characterize an important protein-protein interaction and the analysis is clear and so is the writing. I couldn't (reading it once) find any grammatical or other errors in the text or figures. This manuscript is top-quality and suitable for publication.

__Reviewer #1 – Significance __

Such detailed structural and mechanistic studies are greatly lacking in many clinical conditions for which mutations are known (unless they cause cancer, neurodegenerative disease, and so on). We need more such studies on disease topics! This study will be of interest to the hematologic diseases community.

1. Response – ____Significance

We thank Reviewer #1 for the thoughtful and encouraging evaluation of our work. We are particularly grateful for recognizing the significance of studying protein-protein interaction in the context of CDA-I disease, as well as the rigor and clarity of our biophysical and biochemical characterization.

We appreciate the reviewer's acknowledgment of the challenges associated with native protein EMSAs. We are pleased that our use of multiple orthogonal techniques was recognized as a strength of the study. We are gratified that the comprehensiveness and coherence of our data and the manuscript's clarity were well received.

We thank the reviewer for noting the broader impact of our findings on the hematologic disease community. As highlighted, there is a pressing need for a mechanistic understanding of non-oncologic, non-neurodegenerative diseases, and our studies address this gap.

We are honored by the reviewer's endorsement of our manuscript as "top-quality and suitable for publication". We value the reviewer's highly supportive and motivating feedback.

__Reviewer #2 – 1. Evidence, reproducibility and clarity __

This manuscript presents structural and biochemical characterization of the interaction between CDIN1 and the C-terminal domain of Codanin1, shedding light on a complex implicated in Congenital Dyserythropoietic Anemia Type I (CDA-I). While the authors provide valuable structural insights and identify disease-associated mutations that impair CDIN1-Codanin1 binding, I think several important concerns should be addressed to strengthen both the mechanistic claims and their functional relevance.

Contradiction Between Stoichiometry Models:

The authors propose that CDIN1 and Codanin1Cterm primarily form a heterodimer in vitro. However, this appears to contradict previous reports indicating a tetra-heteromeric arrangement. Additionally, while CDIN1 homodimerize seems confusing to me, do the authors suggest it is stable without Codanin1? This seems contrary to findings that CDIN1 is unstable in the absence of Codanin1 (Sedor, S.F., Shao, S. nature comm 2025, Swickley, G., Bloch, Y., Malka, L. et al 2020 BMC Mol and Cell Biol). These inconsistencies raise concerns about whether the observed stoichiometries are physiologically relevant or artifacts of in vitro reconstitution, especially since full-length Codanin1 was not studied.

2.1 Response ____– Consistent stoichiometry of Codanin1Cterm

We thank Reviewer #2 for raising critical points regarding the stoichiometry and physiological relevance of the CDIN1-Codanin1 interaction. The following response clarifies the rationale and interpretation in relation to previous findings.

Stoichiometry of CDIN1-Codanin1Cterm complex:

Recent Cryo-EM studies of full-length Codanin1 (Jeong, Frater et al. 2025, Sedor and Shao 2025) suggest independent internal dimerization domains (452-798 and 841-1000 amino acid residue) driving homodimer formation, with each Codanin1 monomer binding one CDIN1 via the C-terminal region (1005-1227 amino acid residue), resulting in a tetra-heteromeric complex. Therefore, the complete assembly appears as a dimer of heterodimers in the full-length context.

In our study, Codanin1 was truncated to retain only the CDIN1-binding C-terminus (1005-1227 amino acid residues), eliminating the homodimerization ability of Codanin1. Hence, in the case of truncated Codanin1Cterm, the minimal complex we observe is a 1:1 heterodimer of CDIN1-Codanin1Cterm, which is fully consistent with the equimolar stoichiometry of CDIN1-Codanin1 complex seen in the full-length structure.

Stability and oligomeric state of CDIN1 in the absence of Codanin1:

We concur with the reviewer that Sedor et al. (2025) and Swickley et al. (2020) reported decreased CDIN1 levels in cells lacking Codanin1, implying in vivo dependence of CDIN1 on Codanin1 partner for stability (Swickley, Bloch et al. 2020, Sedor and Shao 2025). The purified CDIN1 is monodisperse (Supplementary Figure 2D), exhibits thermal stability with a melting temperature of 48 °C (Supplementary Figure 2E), and displays proper folding as indicated by CD measurements (Supplementary Figure 2B). Additionally, SAXS profiles of CDIN1 correspond to AlphaFold predictions (Fig. 2B). Together, our findings indicate that the recombinant CDIN1 forms a stable conformation in vitro without Codanin1. To the best of our knowledge, no previous research has directly identified the endogenous oligomeric states of CDIN1 within cellular content.

We fully acknowledge that future analysis of the full-length Codanin1-CDIN1 assembly in a cellular context will be necessary for understanding physiological stoichiometries. As outlined in the General statements, our study focuses on the C-terminus of Codanin1 to describe the binding interface and complex biophysical properties of the CDIN-Codanin1Cterm complex.

__Reviewer #2 – ____2. Unvalidated Functional Claims: __

The manuscript identifies several CDA-I-associated mutations that disrupt CDIN1-Codanin1 interaction. However, the authors do not test how these mutations affect the biological function of the complex, particularly its role in ASF1 sequestration or histone trafficking. Given the central importance of this axis in their disease model, functional validation (e.g., ASF1 localization, histone deposition assays) is necessary to support these mechanistic conclusions.

2.2 Response – ____Hypothetical model as discussion merit

We thank the reviewer for the comment regarding the functional implications of CDA-I-associated mutations and their potential impact on ASF1 sequestration and histone trafficking hypothesized within the Discussion. We fully agree that understanding the downstream biological consequences of disrupted CDIN1-Codanin1 interaction is critical for elucidating the full molecular basis of CDA-I pathogenesis.

In the Future research directions of the Discussion, we have acknowledged and emphasized the need for follow-up studies using erythroblast cell lines to determine whether specific disease-associated mutations disrupt CDIN1-Codanin1 binding, leading to functional defects relevant to erythropoiesis and nuclear architecture typical for CDA-I disease.

However, as we respectfully note in General Statements, the main aim of the present study was to provide a rigorous biophysical characterization of the CDIN1-Codanin1Cterm interaction. Proposed cellular experiments, though relevant, are beyond the conceptual scope of the presented studies.

Reviewer #2 – ____3. Speculative and Potentially Contradictory Model:

The proposed model suggests that CDIN1 competes with ASF1 for Codanin1 binding, thereby indirectly promoting histone delivery to the nucleus. However, emerging data indicate that Codanin1, CDIN1, and ASF1 can form a stable ternary complex, calling into question this competitive binding hypothesis (Sedor, S.F., Shao, S. nature comm 2025). The authors do not acknowledge or discuss these findings, and the model in its current form may therefore be oversimplified or inaccurate.

2.3 Response – ____Hypothetical model fully aligned with current knowledge

We fully acknowledged and discussed in the current manuscript the recent findings demonstrating that Codanin1, CDIN1, and ASF1 can form a ternary complex (Sedor, S.F., Shao, S. Nature Comm. 2025; Jeong, T. K. et al. Nature Comm. 2025). Our revised model was updated accordingly to reflect the collaborative binding of Codanin1, CDIN1, and ASF1, and is presented in alignment with published data.

While earlier versions of our work published on the BioRxiv server (May 26, 2023) proposed a competitive hypothesis, the current manuscript incorporates recent literature and prior reviewer feedback to offer a refined model. We believe that the updated hypothesis suggests a plausible mechanism for how CDIN1 modulates Codanin1 function, which will be further tested in future cellular studies.

Reviewer #2 – 4. Significance:

Overall, the study adds to our structural understanding of CDIN1 and Codanin1 interactions, but the functional interpretations are currently speculative, and in some cases in conflict with existing literature. The manuscript would benefit significantly from addressing these discrepancies, incorporating relevant data on ASF1, and clarifying whether the observed assemblies reflect physiological complexes.

__2.4 Response – Significance __

We thank Reviewer #2 for the constructive feedback. As noted in General Statements, our current manuscript is primarily dedicated to defining the molecular architecture and interactions of the CDIN1–Codanin1Cterm core interface. We agree that follow-up ASF1‑dependent functional assays will be critical to fully validate observed assemblies, but these experiments lie outside the scope of the present study and are ongoing in our laboratory.

To address the reviewer's concern about possible speculative interpretation, we have:

• Used cautious language in Results and Discussion to prevent overstatement (e.g., page 31, line 754, “leads” exchanged to “may contribute” in legend of Fig. 4).
• Described in the Discussion how our results enhance and add understanding to the body of published structural data of CDIN1–Codanin1Cterm.
• Updated our hypothetical model in Fig. 4 to be fully in line with published data.
• Clearly stated that the working hypothesis is connected with a subset of CDA-I mutations (p. 31, l. 758-759, “The proposed model represents a working hypothesis relating to a subset of CDA-I mutations and is not currently substantiated by experimental evidence at the cellular level.”)
• Stated in Future research directions of Discussion that functional validation, including ASF1, will motivate future critical studies, p. 32, l. 771-773: “The ability of Codanin1 to interact with both CDIN1 and ASF1 motivates further investigation of how CDIN1 and ASF1 affect the function of full-length Codanin1, which even recent cryo-EM data has not addressed yet.”
• Highlighted the necessity of complementary in vivo studies in erythroblast cell lines to determine if CDA-I-related mutations in CDIN1-Codanin1 interaction region cause typical CDA-I phenotypes, aiming to clarify the molecular mechanisms of inherited CDA-I anemia. We state in Future research directions in Discussion, p. 32, l. 774-780: “…follow-up research utilizing erythroblast model cell lines must be conducted to determine if specific mutations that disrupt CDIN1-Codanin1 binding also affect ASF1 localization and cause a phenotype typical of CDA-I. In future work, additional Codanin1 mutations, including those outside the C-terminal region, should be evaluated to determine how the mutations affect ASF1’s nuclear concentration and subcellular localization. The proposed research directions will provide additional deeper insights into the underlying mechanisms of the molecular origin of inherited anemia CDA-I.” We believe that the revisions objectively clarify the significance and the limits of the current work and set the stage for the detailed functional studies to follow.

__Reviewer #3 – Evidence, reproducibility and clarity: __

Congenital Dyserythropoietic Anemia Type I (CDA I) is an autosomal recessive disorder characterized by ineffective erythropoiesis and distinctive nuclear morphology ("Swiss cheese" heterochromatin) in erythroblasts. CDA I is caused by mutations in CDAN1 and CDIN1. Codanin1, encoded by CDAN1, is part of the cytosolic ASF1-H3.1-H4-Importin-4 complex, which regulates histone trafficking to the nucleus. CDIN1 has been shown to bind the C-terminal domain of Codanin-1, but until now, pathogenic mutations had not been directly linked to the disruption of this interaction.

In this study, the authors used biophysical techniques to characterize the interaction between Codanin-1's C-terminal region (residues 1005-1227) and CDIN1, demonstrating high-affinity, equimolar binding. HDX-MS identified interaction hotspots, and disease-associated mutations in these regions disrupted complex formation. The authors propose that such disruption prevents ASF1 sequestration in the cytoplasm, thereby reducing nuclear histone levels and contributing to the chromatin abnormalities seen in CDA I.

Major Comments:

1. Use of Codanin-1 Fragment:

Most experiments were conducted using only the C-terminal 223 amino acids of Codanin-1. While this region is known to bind CDIN1, it is unclear whether its conformation is maintained in the context of the full-length protein. This could affect binding properties and structural interpretations. The authors should discuss how structural differences between the isolated C-terminus and the full-length Codanin-1 may influence the conclusions.

Response of authors ____#3

3.1 Response: Use of Codanin-1 Fragment as biding part to CDIN1

We thank the reviewer for the important observation regarding the use of the C-terminal fragment of Codanin1. As noted in the manuscript (e.g., p. 30, line 721 and p. 32, line 761), we fully acknowledge that the truncation of Codanin1 may influence its conformational dynamics or contextual folding relative to the full-length protein.

However, several lines of evidence suggest that the C-terminal 223 amino acid residues—responsible for CDIN1 binding—are structurally autonomous and have minimal intramolecular contacts with upstream regions. Published cryo-EM and biochemical data (Jeong, Frater et al. 2025, Sedor and Shao 2025), in conjunction with AlphaFold structural predictions (Fig. 2D) and our co-immunoprecipitation assays (Fig. 3F), consistently support a model wherein the CDIN1-binding region is flexible and spatially isolated from the core structural domains of Codanin1. Additionally, results from our co-immunoprecipitation assay (Fig. 3F) indicate that full-length Codanin1 and truncated Codanin1Cterm interact with CDIN1 similarly, further supporting the isolated manner of the C-terminal fragment. The available data together imply that the C-terminal fragment used in our study retains its native conformation and binding properties when expressed independently.

While our findings are confined to the interaction domain and do not reflect full-length Codanin1’s architecture, we believe the use of the C-terminal minimal fragment of Codanin1 enables precise dissection of the CDIN1-binding interface and yields mechanistic insights without introducing significant structural artifacts.

We agree with the reviewer that future work incorporating full-length Codanin1, especially in a cellular context, will be instrumental to fully characterize higher-order assembly and regulatory functions.

__Reviewer #3 – 2. ____Graphical Abstract and Domain Independence: __

The graphical abstract presents the Codanin-1 C-terminus as an independent domain, but no direct evidence is provided to support its structural autonomy in vivo.

The authors should clarify whether the C-terminal region functions as a distinct domain in the context of the full-length protein.

__3.2 Response –____ Independent C-terminal domain __

We thank the reviewer for bringing up the question of the independence of the C-terminal domain. Although direct in vivo proof of C-terminal autonomy is not yet available, published cryo-EM structures of full-length Codanin1, our biophysical characterization, and AlphaFold models all consistently indicate that the C-terminal 223 amino acid residues of Codanin1 form a structurally independent binding module. In the graphical abstract, we illustrated the C‑terminal domain as a loosely connected part of Codanin1 to highlight its independence and to emphasize the specific focus of our studies.

To articulate limitations of our studies focused on the C-terminal part of Codanin1, we stated in the Functional implications of CDA-I-related mutations in the Discussion, p. 30, l. 721-724: “However, our measurements do not exclude the possible role of the disordered regions in full-length Codanin1. For example, CDIN1 could potentially stabilize full-length Codanin1 by rearranging the disordered regions into a more condensed structure, thereby augmenting the structural stability of Codanin1.”

Reviewer #3 – 3.____Pathogenic Mutations Beyond the Binding Site:

The study highlights a triplet mutation that impairs CDIN1 binding. However, most CDA I‑associated mutations in CDAN1 are dispersed across the entire protein and may not affect CDIN1 interaction directly.

The authors should discuss alternative mechanisms by which mutations in other regions of Codanin-1 might cause disease.

3.3 Response – Pathogenic mutations outside the binding site – alternative mechanisms

We appreciate the reviewer noting that most CDA-I-associated CDAN1 mutations are outside the CDIN1-Codanin1 binding site and suggesting alternative mechanisms. In the revised Discussion, we added a paragraph on alternative pathogenic models, p. 29, l. 702-713:

"Our study centers on the CDIN1-binding C-terminus, however, most CDA-I-associated CDAN1 mutations lie elsewhere and probably act through alternative mechanisms. Mutations such as P672L and F868I in the LOBE2 (452-798 amino acid residue) and F868I in the coiled-coil (841-1000 amino acid residue) domains may disturb Codanin1 homodimerization and higher-order complex assembly, directly affecting ASF1 sequestration (Jeong, T. K. et al. Nature Comm. 2025). Other mutant variants may also interfere with ASF1 sequestration, nuclear targeting, or chromatin-remodeling functions, while destabilizing mutations may induce misfolding and proteasomal degradation. Moreover, CDA-I-associated mutations, such as R714W and R1042W, might compromise the interaction between Codanin1 and ASF1 (Ask, Jasencakova et al. 2012). Collectively, the complementary alternative pathogenic mechanisms associated with Codanin1 mutations in distal regions and mutations in CDIN1‑binding C-terminus of Codanin1 may contribute to erythroid dysfunction in CDA-I."

Reviewer #3 – 4. ____Contradictory Functional Models:

Ask et al. (EMBO J, 2012) reported that Codanin-1 depletion increases nuclear ASF1 and accelerates DNA replication. This contrasts with the current hypothesis that disruption of the Codanin-1/CDIN1 complex reduces nuclear ASF1.

The authors should attempt to reconcile this apparent contradiction, possibly by proposing a context-specific or dual-function model for Codanin-1 in histone trafficking.

3.4 Response – ____Clarified explanation of hypothetical functional model

We thank the reviewer for raising this point, which improved the clarity of our work. There is no real discrepancy between Ask et al. and our findings; both agree that Codanin1 restrains ASF1 in the cytoplasm. Ask et al. examined the complete loss of Codanin1, which abolishes cytoplasmic ASF1 sequestration and thus leads to maximal nuclear accumulation. We suggest the CDA-I-associated mutations selectively disrupt the CDIN1-Codanin1 interface, releasing ASF1 from the cytoplasm into the nucleus.

To enhance clarity, we now state in the legend of Figure 4 describing the hypothesis (p. 31, l. 752-753): "…CDA-I-associated mutations prevent CDIN1-Codanin1 complex formation, thus prevent ASF1 sequestration to cytoplasm; ASF1 remains accumulated in nucleus."

Reviewer #3 – 5. ____Conclusions and Claims:

The proposed model of CDA I pathogenesis (Fig. 4) is plausible but not yet fully supported by the available data. The authors suggest that disruption of the Codanin-1/CDIN1 interaction leads to nuclear histone depletion, but this has not been experimentally confirmed.

Claims about the general pathogenesis of CDA I should be clearly qualified as hypothetical and applicable to a subset of mutations. The presence and localization of ASF1 in the nucleus following disruption of the Codanin-1/CDIN1 complex should be tested experimentally.

3.5 Response – __Tempered ____conclusions and claims: __

We thank the reviewer for underscoring the need to temper our conclusions and to distinguish hypotheses from available results. We fully agree that our Fig. 4 model—linking disruption of the Codanin1-CDIN1 interface to nuclear histone imbalance—remains a working hypothesis, currently supported by indirect biochemical and structural data.

Accordingly, we have:

• Revised the text to explicitly state that this model is hypothetical and pertains to a subset of CDA-I-associated CDAN1 mutations. Specifically, we

• Added to the last paragraph of the section Functional implications of CDA-I-related mutations in Discussion (p. 31, l. 744-749): “In considering functional implications of our findings within available data, it is essential to qualify that mechanistic claims regarding the general pathogenesis of CDA-I remain hypothetical and are restricted to a specific subset of mutations. Furthermore, direct experimental validation, such as immunolocalization or live-cell imaging, to assess ASF1’s nuclear presence and distribution following disruption of the CDIN1-Codanin1 complex is required to substantiate the proposed model.”

• Included in the legend of Fig. 4: ”The proposed model represents a working hypothesis relating to a subset of CDA-I mutations and is not currently substantiated by experimental evidence at the cellular level.”
• Replaced any associated definitive language (e.g., “leads to”) with qualified phrasing (e.g., “may contribute to”) in the legend of Fig. 4.
• Clarified in the Discussion that direct measurement of nuclear ASF1 redistribution and histone levels following interface disruption has not yet been performed. Specifically, we added to the section Functional implications of CDA-I-related mutations in Discussion (p. 30, l. 734-735): “It should be noted, however, that direct quantification of nuclear ASF1 redistribution and histone levels after CDIN1-Codanin1 disruption has not yet been conducted.” Although experimental verification of nuclear ASF1 localization upon CDIN1-Codanin1 complex disruption falls beyond the current manuscript’s scope, we acknowledge its importance and have emphasized the need for such studies in future work within the Future research directions of the Discussion. Specifically, we concluded by stating (p. 32, l. 774-776): “Finally, follow‑up research utilizing erythroblast model cell lines must be conducted to determine if specific mutations that disrupt CDIN1-Codanin1 binding, also affect ASF1 localization and cause a phenotype typical of CDA-I.”

__Reviewer #3 – 6.____Broader Mutation Analysis and ASF1 Localization: __

To strengthen the link between Codanin-1/CDIN1 disruption and disease pathogenesis, it would be important to test the effects of additional CDAN1 mutations, including those outside the C-terminal region. Similarly, the impact on ASF1 nuclear concentration and localization should be directly assessed. These experiments would significantly bolster the central hypothesis. If feasible, they should be pursued or at least acknowledged as important future directions.

3.6 Response – Broader mutation analysis and ASF1 localization in future directions

We thank Reviewer #3 for emphasizing the value of a broader mutation survey and direct ASF1 localization studies. As noted above, our current manuscript is centered on delineating the molecular architecture of the CDIN1-Codanin1Cterm core interface; comprehensive mutational analyses outside the C-terminal binding region and ASF1-dependent functional assays will be critical to extend these findings but fall beyond the scope of the present work and will be the objective of our following studies. To address the reviewer’s concern, we have:

• Expanded the Future Directions section to specify that additional CDA-I-linked CDAN1 variants, including non-C-terminal mutations, and quantitative assessments of ASF1 nuclear localization will be the subject of ongoing and planned investigations. Specifically, we added (p. 32, l. 776-778):” In future work, additional Codanin1 mutations, including those outside the C-terminal region, should be evaluated to determine how the mutations affect ASF1’s nuclear concentration and subcellular localization.”

• Emphasized the need for complementary in vivo validation in erythroblast models to confirm whether the disturbance of CDIN1-Codanin1 binding recapitulates CDA-I phenotypes. We acknowledged the need for cell-line studies in future work within the Future research directions of Discussion (p. 32, l. 774-776): “Finally, follow-up research utilizing erythroblast model cell lines must be conducted to determine if specific mutations that disrupt CDIN1-Codanin1 binding, also affect ASF1 localization and cause a phenotype typical of CDA-I.” We believe these changes more precisely delimit the scope and significance of the current study while laying out a clear roadmap for the essential follow-up experiments.

Reviewer #3 – 7. ____Rigor and Presentation and Cross-commenting

__Minor Comments: __

• Methods and Reproducibility:

The experimental methods are well described, and the results appear reproducible.

• Presentation:

The text and figures are clear and well organized.

Referee Cross-commenting

I agree with reviewer 1 that the paper presents detailed structure study of Codanin-1 and CDIN1 protein. However, as reviewer 2 claims functional studies are missing and therefore the hypothesis regarding the pahtogenesis of CDAI is speculaltive especially with no studies regarding ASF1.

3____.7 Response ____–____ Rigor and Presentation and Cross-commenting:

We thank the reviewers for their positive appraisal of our results' reproducibility, presentation, and method descriptions. We also appreciate the cross-comment that, while our structural analysis of the CDIN1-Codanin1 complex is thorough, functional validation, particularly regarding ASF1, remains to be addressed.

As outlined above, we have revised the manuscript to:

• Emphasize that pathogenic hypotheses drawn from structural data are provisional (refer to Responses 2.2, 2.3, and 3.5).
• Include follow-up studies for ASF1 localization assays and broader mutation profiling in our Future Directions (refer to Responses 2.4, 3.5, 3.6).
• Integrate cautious language throughout to clearly delineate verified findings from model-based speculation (refer to Responses 2.4, 3.5, 3.6). The implemented adjustments ensure that the current work is positioned as a detailed structural and interaction foundation, upon which the essential functional studies will build. We believe that all extensions and clarifications fully satisfy the reviewers’ collective recommendations.

__Reviewer #3 –____ Significance: __

Nature and Significance of the Advance:

This study extends prior work (e.g., Swickley et al., BMC Mol Cell Biol 2020; Shroff et al., Biochem J 2020) on Codanin-1/CDIN1 interaction by applying high-resolution biophysical techniques to identify mutations that disrupt this complex. It provides a plausible cellular mechanism by which specific mutations may lead to CDA I through impaired histone trafficking.

Nevertheless, key question remains: How do mutations outside the Codanin-1 C-terminus contribute to the pathology?

3.8 Response – Significance:

• We thank Reviewer #3 for this important point. Although our work specifically dissects the C-terminal CDIN1-binding domain of Codanin1, we fully acknowledge that CDA-I-associated mutations throughout Codanin1 may operate via additional mechanisms. To address the additional mechanisms, we have added a new paragraph describing other possible pathogenic models to the Discussion (please refer to Response 3.3).
• We also fully acknowledged the need for systematic functional assays of non-C-terminal mutations and their impact on ASF1 localization (please refer to Response 3.6).

• We revised the text to clarify how mutations beyond the C-terminus may contribute to CDA-I pathogenesis and present the significance of our current structural analyses, biophysical characterizations, and molecular insights as a foundation for future research (please refer to Response 3.6). __Audience: __

• Molecular and cellular biologists investigating nuclear-cytoplasmic trafficking mechanisms

• Hematologists and geneticists studying rare red cell disorders
• Clinicians managing CDA I patients and researchers exploring targeted therapies __Reviewer Expertise: __

Pediatric hematologist with over 20 years of research experience in CDA I, including the initial identification of CDAN1 and the elucidation of Codanin-1's role in embryonic erythropoiesis. Not a specialist in the biophysical techniques used in this study.

References

Ask, K., Z. Jasencakova, P. Menard, Y. Feng, G. Almouzni and A. Groth (2012). "Codanin-1, mutated in the anaemic disease CDAI, regulates Asf1 function in S-phase histone supply." The EMBO Journal 31(8): 2013–2023.

Jeong, T.-K., R. C. M. Frater, J. Yoon, A. Groth and J.-J. Song (2025). "CODANIN-1 sequesters ASF1 by using a histone H3 mimic helix to regulate the histone supply." Nature Communications 16(1): 2181.

Sedor, S. F. and S. Shao (2025). "Mechanism of ASF1 engagement by CDAN1." Nature Communications 16(1): 2599.

Swickley, G., Y. Bloch, L. Malka, A. Meiri, S. Noy-Lotan, A. Yanai, H. Tamary and B. Motro (2020). "Characterization of the interactions between Codanin-1 and C15Orf41, two proteins implicated in congenital dyserythropoietic anemia type I disease." Molecular and Cell Biology 21(1).

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Referee #3

Evidence, reproducibility and clarity

Congenital Dyserythropoietic Anemia type I (CDA I) is an autosomal recessive disorder characterized by ineffective erythropoiesis and distinctive nuclear morphology ("Swiss cheese" heterochromatin) in erythroblasts. CDA I is caused by mutations in CDAN1 and CDIN1. Codanin-1, encoded by CDAN1, is part of the cytosolic ASF1-H3.1-H4-Importin-4 complex, which regulates histone trafficking to the nucleus. CDIN1 has been shown to bind the C-terminal domain of Codanin-1, but until now, pathogenic mutations had not been directly linked to the disruption of this interaction. In this study, the authors used biophysical techniques to characterize the interaction between Codanin-1's C-terminal region (residues 1005-1227) and CDIN1, demonstrating high-affinity, equimolar binding. HDX-MS identified interaction hotspots, and disease-associated mutations in these regions disrupted complex formation. The authors propose that such disruption prevents ASF1 sequestration in the cytoplasm, thereby reducing nuclear histone levels and contributing to the chromatin abnormalities seen in CDA I.

Major Comments:

1. Use of Codanin-1 Fragment: Most experiments were conducted using only the C-terminal 223 amino acids of Codanin-1. While this region is known to bind CDIN1, it is unclear whether its conformation is maintained in the context of the full-length protein. This could affect binding properties and structural interpretations. The authors should discuss how structural differences between the isolated C-terminus and the full-length Codanin-1 may influence the conclusions.
2. Graphical Abstract and Domain Independence: The graphical abstract presents the Codanin-1 C-terminus as an independent domain, but no direct evidence is provided to support its structural autonomy in vivo. The authors should clarify whether the C-terminal region functions as a distinct domain in the context of the full-length protein.
3. Pathogenic Mutations Beyond the Binding Site: The study highlights a triplet mutation that impairs CDIN1 binding. However, most CDA I-associated mutations in CDAN1 are dispersed across the entire protein and may not affect CDIN1 interaction directly. The authors should discuss alternative mechanisms by which mutations in other regions of Codanin-1 might cause disease.
4. Contradictory Functional Models: Ask et al. (EMBO J, 2012) reported that Codanin-1 depletion increases nuclear ASF1 and accelerates DNA replication. This contrasts with the current hypothesis that disruption of the Codanin-1/CDIN1 complex reduces nuclear ASF1. The authors should attempt to reconcile this apparent contradiction, possibly by proposing a context-specific or dual-function model for Codanin-1 in histone trafficking.
5. Conclusions and Claims: The proposed model of CDA I pathogenesis (Fig. 4) is plausible but not yet fully supported by the available data. The authors suggest that disruption of the Codanin-1/CDIN1 interaction leads to nuclear histone depletion, but this has not been experimentally confirmed. Claims about the general pathogenesis of CDA I should be clearly qualified as hypothetical and applicable to a subset of mutations. The presence and localization of ASF1 in the nucleus following disruption of the Codanin-1/CDIN1 complex should be tested experimentally.
6. Broader Mutation Analysis and ASF1 Localization: To strengthen the link between Codanin-1/CDIN1 disruption and disease pathogenesis, it would be important to test the effects of additional CDAN1 mutations, including those outside the C-terminal region. Similarly, the impact on ASF1 nuclear concentration and localization should be directly assessed. These experiments would significantly bolster the central hypothesis. If feasible, they should be pursued or at least acknowledged as important future directions.

Minor Comments:

• Methods and Reproducibility: The experimental methods are well described, and the results appear reproducible.
• Presentation: The text and figures are clear and well organized.

Referee Cross-commenting

I agree with reviewer 1 that the paper present detailed strucutre study of Codann-1 and CDIN1 protein. However, as reviewer 2 claims functional studies are missing and therefore the hypothesis regarding the pahtogenesis of CDAI is speculaltive especially with no studies regarding ASF1.

Significance

Nature and Significance of the Advance:

This study extends prior work (e.g., Swickley et al., BMC Mol Cell Biol 2020; Shroff et al., Biochem J 2020) on Codanin-1/CDIN1 interaction by applying high-resolution biophysical techniques to identify mutations that disrupt this complex. It provides a plausible cellular mechanism by which specific mutations may lead to CDA I through impaired histone trafficking. Nevertheless, key question remains: How do mutations outside the Codanin-1 C-terminus contribute to the pathology?

Audience:

Molecular and cellular biologists investigating nuclear-cytoplasmic trafficking mechanisms Hematologists and geneticists studying rare red cell disorders Clinicians managing CDA I patients and researchers exploring targeted therapies

Reviewer Expertise:

Pediatric hematologist with over 20 years of research experience in CDA I, including the initial identification of CDAN1 and the elucidation of Codanin-1's role in embryonic erythropoiesis. Not a specialist in the biophysical techniques used in this study

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Referee #2

Evidence, reproducibility and clarity

This manuscript presents structural and biochemical characterization of the interaction between CDIN1 and the C-terminal domain of Codanin1, shedding light on a complex implicated in Congenital Dyserythropoietic Anemia Type I (CDA-I). While the authors provide valuable structural insights and identify disease-associated mutations that impair CDIN1-Codanin1 binding, I think several important concerns should be addressed to strengthen both the mechanistic claims and their functional relevance.

Contradiction Between Stoichiometry Models:

The authors propose that CDIN1 and Codanin1Cterm primarily form a heterodimer in vitro. However, this appears to contradict previous reports indicating a tetra-heteromeric arrangement. Additionally, while CDIN1 homodimerize seems confusing to me, do the authors suggest it is stable without Codanin1? This seems contrary to findings that CDIN1 is unstable in the absence of Codanin1(Sedor, S.F., Shao, S. nature comm 2025, Swickley, G., Bloch, Y., Malka, L. et al 2020 BMC Mol and Cell Biol). These inconsistencies raise concerns about whether the observed stoichiometries are physiologically relevant or artifacts of in vitro reconstitution, especially since full-length Codanin1 was not studied.

Unvalidated Functional Claims:

The manuscript identifies several CDA-I-associated mutations that disrupt CDIN1-Codanin1 interaction. However, the authors do not test how these mutations affect the biological function of the complex, particularly its role in ASF1 sequestration or histone trafficking. Given the central importance of this axis in their disease model, functional validation (e.g., ASF1 localization, histone deposition assays) is necessary to support these mechanistic conclusions.

Speculative and Potentially Contradictory Model:

The proposed model suggests that CDIN1 competes with ASF1 for Codanin1 binding, thereby indirectly promoting histone delivery to the nucleus. However, emerging data indicate that Codanin1, CDIN1, and ASF1 can form a stable ternary complex, calling into question this competitive binding hypothesis (Sedor, S.F., Shao, S. nature comm 2025). The authors do not acknowledge or discuss these findings, and the model in its current form may therefore be oversimplified or inaccurate.

Significance

Overall, the study adds to our structural understanding of CDIN1 and Codanin1 interactions, but the functional interpretations are currently speculative, and in some cases in conflict with existing literature. The manuscript would benefit significantly from addressing these discrepancies, incorporating relevant data on ASF1, and clarifying whether the observed assemblies reflect physiological complexes.

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Referee #1

Evidence, reproducibility and clarity

This is a rigorous biophysical characterization of a protein-protein interaction relevant to CDA-1 disease. The two proteins were purified in an E. coli host but CD and DLS was performed to ensure that the purified protein is well folded. An impressive native protein EMSA was used to show a 1:1 complex. While common for protein-nucleic acid complexes, EMSAs are much more challenging with protein complexes. A higher-running complex, likely a heterotetramer was implied at higher protein concentrations. These results were supported with SEC-MALS analysis and analytic ultracentrifugation analysis. Thermophoresis and ITC were used to report a nanomolar affinity of the proteins for each other. SEC-SAXS supported the conclusions about stoichiometry and composition inferred from the earlier methods and suggested that the dimerization interface comes from CDIN1. Next HDX-MS was used to identify putative interface residues, which were then mutated in each of the proteins and assessed for binding using coimmunoprecipitation. This study uses at least 10 orthogonal biophysical and/or biochemical methodologies to characterize an important protein-protein interaction and the analysis is clear and so is the writing. I couldn't (reading it once) find any grammatical or other errors in the text or figures. This manuscript is top-quality and suitable for publication.

Significance

Such detailed structural and mechanistic studies are greatly lacking in many clinical conditions for which mutations are known (unless they cause cancer, neurodegenerative disease, and so on). We need more such studies on disease topics! This study will be of interest for the hematologic diseases community.

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Reply to the reviewers

Reply to the Reviewers

I would like to thank the reviewers for their comments and interest in the manuscript and the study.

Reviewer #1

1. I would assume that there are RNA-seq and/or ChIP-seq data out there produced after knockdown of one or more of these DBPs that show directional positioning.

The directional positioning of CTCF-binding sites at chromatin interaction sites was analyzed by CRISPR experiment (Guo Y et al. Cell 2015). We found that the machine learning and statistical analysis showed the same directional bias of CTCF-binding motif sequence and RAD21-binding motif sequence at chromatin interaction sites as the experimental analysis of Guo Y et al. (lines 229-253, Figure 3b, c, d and Table 1). Since CTCF is involved in different biological functions (Braccioli L et al. Essays Biochem. 2019 ResearchGate webpage), the directional bias of binding sites may be reduced in all binding sites including those at chromatin interaction sites (lines 68-73). In our study, we investigated the DNA-binding sites of proteins using the ChIP-seq data of DNA-binding proteins and DNase-seq data. We also confirmed that the DNA-binding sites of SMC3 and RAD21, which tend to be found in chromatin loops with CTCF, also showed the same directional bias as CTCF by the computational analysis.

__2. Figure 6 should be expanded to incorporate analysis of DBPs not overlapping CTCF/cohesin in chromatin interaction data that is important and potentially more interesting than the simple DBPs enrichment reported in the present form of the figure. __

Following the reviewer's advice, I performed the same analysis with the DNA-binding sites that do no overlap with the DNA-binding sites of CTCF and cohesin (RAD21 and SMC3) (Fig. 6 and Supplementary Fig. 4). The result showed the same tendency in the distribution of DNA-binding sites. The height of a peak on the graph became lower for some DNA-binding proteins after removing the DNA-binding sites that overlapped with those of CTCF and cohesin. I have added the following sentence on lines 435 and 829: For the insulator-associated DBPs other than CTCF, RAD21, and SMC3, the DNA-binding sites that do not overlap with those of CTCF, RND21, and SMC3 were used to examine their distribution around interaction sites.

3. Critically, I would like to see use of Micro-C/Hi-C data and ChIP-seq from these factors, where insulation scores around their directionally-bound sites show some sort of an effect like that presumed by the authors - and many such datasets are publicly-available and can be put to good use here.

As suggested by the reviewer, I have added the insulator scores and boundary sites from the 4D nucleome data portal as tracks in the UCSC genome browser. The insulator scores seem to correspond to some extent to the H3K27me3 histone marks from ChIP-seq (Fig. 4a and Supplementary Fig. 3). We found that the DNA-binding sites of the insulator-associated DBPs were statistically overrepresented in the 5 kb boundary sites more than other DBPs (Fig. 4d). The direction of DNA-binding sites on the genome can be shown with different colors (e.g. red and green), but the directionality of insulator-associated DNA-binding sites is their overall tendency, and it may be difficult to notice the directionality from each binding site because the directionality may be weaker than that of CTCF, RAD21, and SMC3 as shown in Table 1 and Supplementary Table 2. We also observed the directional biases of CTCF, RAD21, and SMC3 by using Micro-C chromatin interaction data as we estimated, but the directionality was more apparent to distinguish the differences between the four directions of FR, RF, FF, and RR using CTCF-mediated ChIA-pet chromatin interaction data (lines 287 and 288).

 I found that the CTCF binding sites examined by a wet experiment in the previous study may not always overlap with the boundary sites of chromatin interactions from Micro-C assay (Guo Y et al. *Cell* 2015). The chromatin interaction data do not include all interactions due to the high sequencing cost of the assay, and include less long-range interactions due to distance bias. The number of the boundary sites may be smaller than that of CTCF binding sites acting as insulators and/or some of the CTCF binding sites may not be locate in the boundary sites. It may be difficult for the boundary location algorithm to identify a short boundary location. Due to the limitations of the chromatin interaction data, I planned to search for insulator-associated DNA-binding proteins without using chromatin interaction data in this study.

 I discussed other causes in lines 614-622: Another reason for the difference may be that boundary sites are more closely associated with topologically associated domains (TADs) of chromosome than are insulator sites. Boundary sites are regions identified based on the separation of numerous chromatin interactions. On the other hand, we found that the multiple DNA-binding sites of insulator-associated DNA-binding proteins were located close to each other at insulator sites and were associated with distinct nested and focal chromatin interactions, as reported by Micro-C assay. These interactions may be transient and relatively weak, such as tissue/cell type, conditional or lineage-specific interactions.

 Furthermore, I have added the statistical summary of the analysis in lines 372-395 as follows: Overall, among 20,837 DNA-binding sites of the 97 insulator-associated proteins found at insulator sites identified by H3K27me3 histone modification marks (type 1 insulator sites), 1,315 (6%) overlapped with 264 of 17,126 5kb long boundary sites, and 6,137 (29%) overlapped with 784 of 17,126 25kb long boundary sites in HFF cells. Among 5,205 DNA-binding sites of the 97 insulator-associated DNA-binding proteins found at insulator sites identified by H3K27me3 histone modification marks and transcribed regions (type 2 insulator sites), 383 (7%) overlapped with 74 of 17,126 5-kb long boundary sites, 1,901 (37%) overlapped with 306 of 17,126 25-kb long boundary sites. Although CTCF-binding sites separate active and repressive domains, the limited number of DNA-binding sites of insulator-associated proteins found at type 1 and 2 insulator sites overlapped boundary sites identified by chromatin interaction data. Furthermore, by analyzing the regulatory regions of genes, the DNA-binding sites of the 97 insulator-associated DNA-binding proteins were found (1) at the type 1 insulator sites (based on H3K27me3 marks) in the regulatory regions of 3,170 genes, (2) at the type 2 insulator sites (based on H3K27me3 marks and gene expression levels) in the regulatory regions of 1,044 genes, and (3) at insulator sites as boundary sites identified by chromatin interaction data in the regulatory regions of 6,275 genes. The boundary sites showed the highest number of overlaps with the DNA-binding sites. Comparing the insulator sites identified by (1) and (3), 1,212 (38%) genes have both types of insulator sites. Comparing the insulator sites between (2) and (3), 389 (37%) genes have both types of insulator sites. From the comparison of insulator and boundary sites, we found that (1) or (2) types of insulator sites overlapped or were close to boundary sites identified by chromatin interaction data.

4. The suggested alternative transcripts function, also highlighted in the manuscripts abstract, is only supported by visual inspection of a few cases for several putative DBPs. I believe this is insufficient to support what looks like one of the major claims of the paper when reading the abstract, and a more quantitative and genome-wide analysis must be adopted, although the authors mention it as just an 'observation'.

According to the reviewer's comment, I performed the genome-wide analysis of alternative transcripts where the DNA-binding sites of insulator-associated proteins are located near splicing sites. The DNA-binding sites of insulator-associated DNA-binding proteins were found within 200 bp centered on splice sites more significantly than the other DNA-binding proteins (Fig. 4e and Table 2). I have added the following sentences on lines 405 - 412: We performed the statistical test to estimate the enrichment of insulator-associated DNA-binding sites compared to the other DNA-binding proteins, and found that the insulator-associated DNA-binding sites were significantly more abundant at splice sites than the DNA-binding sites of the other proteins (Fig 4e and Table 2; Mann‒Whitney U test, p value 5. Figure 1 serves no purpose in my opinion and can be removed, while figures can generally be improved (e.g., the browser screenshots in Figs 4 and 5) for interpretability from readers outside the immediate research field.

I believe that the Figure 1 would help researchers in other fields who are not familiar with biological phenomena and functions to understand the study. More explanation has been included in the Figures and legends of Figs. 4 and 5 to help readers outside the immediate research field understand the figures.

6. Similarly, the text is rather convoluted at places and should be re-approached with more clarity for less specialized readers in mind.

Reviewer #2's comments would be related to this comment. I have introduced a more detailed explanation of the method in the Results section, as shown in the responses to Reviewer #2's comments.

Reviewer #2

1. Introduction, line 95: CTCF appears two times, it seems redundant.

On lines 91-93, I deleted the latter CTCF from the sentence "We examine the directional bias of DNA-binding sites of CTCF and insulator-associated DBPs, including those of known DBPs such as RAD21 and SMC3".

2. Introduction, lines 99-103: Please stress better the novelty of the work. What is the main focus? The new identified DPBs or their binding sites? What are the "novel structural and functional roles of DBPs" mentioned?

Although CTCF is known to be the main insulator protein in vertebrates, we found that 97 DNA-binding proteins including CTCF and cohesin are associated with insulator sites by modifying and developing a machine learning method to search for insulator-associated DNA-binding proteins. Most of the insulator-associated DNA-binding proteins showed the directional bias of DNA-binding motifs, suggesting that the directional bias is associated with the insulator.

 I have added the sentence in lines 96-99 as follows: Furthermore, statistical testing the contribution scores between the directional and non-directional DNA-binding sites of insulator-associated DBPs revealed that the directional sites contributed more significantly to the prediction of gene expression levels than the non-directional sites. I have revised the statement in lines 101-110 as follows: To validate these findings, we demonstrate that the DNA-binding sites of the identified insulator-associated DBPs are located within potential insulator sites, and some of the DNA-binding sites in the insulator site are found without the nearby DNA-binding sites of CTCF and cohesin. Homologous and heterologous insulator-insulator pairing interactions are orientation-dependent, as suggested by the insulator-pairing model based on experimental analysis in flies. Our method and analyses contribute to the identification of insulator- and chromatin-associated DNA-binding sites that influence EPIs and reveal novel functional roles and molecular mechanisms of DBPs associated with transcriptional condensation, phase separation and transcriptional regulation.

3. Results, line 111: How do the SNPs come into the procedure? From the figures it seems the input is ChIP-seq peaks of DNBPs around the TSS.

On lines 121-124, to explain the procedure for the SNP of an eQTL, I have added the sentence in the Methods: "If a DNA-binding site was located within a 100-bp region around a single-nucleotide polymorphism (SNP) of an eQTL, we assumed that the DNA-binding proteins regulated the expression of the transcript corresponding to the eQTL".

4. Again, are those SNPs coming from the different cell lines? Or are they from individuals w.r.t some reference genome? I suggest a general restructuring of this part to let the reader understand more easily. One option could be simplifying the details here or alternatively including all the necessary details.

On line 119, I have included the explanation of the eQTL dataset of GTEx v8 as follows: " The eQTL data were derived from the GTEx v8 dataset, after quality control, consisting of 838 donors and 17,382 samples from 52 tissues and two cell lines". On lines 681 and 865, I have added the filename of the eQTL data "(GTEx_Analysis_v8_eQTL.tar)".

5. Figure 1: panel a and b are misleading. Is the matrix in panel a equivalent to the matrix in panel b? If not please clarify why. Maybe in b it is included the info about the SNPs? And if yes, again, what is then difference with a.

The reviewer would mention Figure 2, not Figure 1. If so, the matrices in panels a and b in Figure 2 are equivalent. I have shown it in the figure: The same figure in panel a is rotated 90 degrees to the right. The green boxes in the matrix show the regions with the ChIP-seq peak of a DNA-binding protein overlapping with a SNP of an eQTL. I used eQTL data to associate a gene with a ChIP-seq peak that was more than 2 kb upstream and 1 kb downstream of a transcriptional start site of a gene. For each gene, the matrix was produced and the gene expression levels in cells were learned and predicted using the deep learning method. I have added the following sentences to explain the method in lines 133 - 139: Through the training, the tool learned to select the binding sites of DNA-binding proteins from ChIP-seq assays that were suitable for predicting gene expression levels in the cell types. The binding sites of a DNA-binding protein tend to be observed in common across multiple cell and tissue types. Therefore, ChIP-seq data and eQTL data in different cell and tissue types were used as input data for learning, and then the tool selected the data suitable for predicting gene expression levels in the cell types, even if the data were not obtained from the same cell types.

6. Line 386-388: could the author investigate in more detail this observation? Does it mean that loops driven by other DBPs independent of the known CTCF/Cohesin? Could the author provide examples of chromatin structural data e.g. MicroC?

As suggested by the reviewer, to help readers understand the observation, I have added Supplementary Fig. S4c to show the distribution of DNA-binding sites of "CTCF, RAD21, and SMC3" and "BACH2, FOS, ATF3, NFE2, and MAFK" around chromatin interaction sites. I have modified the following sentence to indicate the figure on line 501: Although a DNA-binding-site distribution pattern around chromatin interaction sites similar to those of CTCF, RAD21, and SMC3 was observed for DBPs such as BACH2, FOS, ATF3, NFE2, and MAFK, less than 1% of the DNA-binding sites of the latter set of DBPs colocalized with CTCF, RAD21, or SMC3 in a single bin (Fig. S4c).

 In Aljahani A et al. *Nature Communications* 2022, we find that depletion of cohesin causes a subtle reduction in longer-range enhancer-promoter interactions and that CTCF depletion can cause rewiring of regulatory contacts. Together, our data show that loop extrusion is not essential for enhancer-promoter interactions, but contributes to their robustness and specificity and to precise regulation of gene expression. Goel VY et al. *Nature Genetics* 2023 mentioned in the abstract: Microcompartments frequently connect enhancers and promoters and though loss of loop extrusion and inhibition of transcription disrupts some microcompartments, most are largely unaffected. These results suggested that chromatin loops can be driven by other DBPs independent of the known CTCF/Cohesin.

I added the following sentence on lines 569-577: The depletion of cohesin causes a subtle reduction in longer-range enhancer-promoter interactions and that CTCF depletion can cause rewiring of regulatory contacts. Another group reported that enhancer-promoter interactions and transcription are largely maintained upon depletion of CTCF, cohesin, WAPL or YY1. Instead, cohesin depletion decreased transcription factor binding to chromatin. Thus, cohesin may allow transcription factors to find and bind their targets more efficiently. Furthermore, the loop extrusion is not essential for enhancer-promoter interactions, but contributes to their robustness and specificity and to precise regulation of gene expression.

 FOXA1 pioneer factor functions as an initial chromatin-binding and chromatin-remodeling factor and has been reported to form biomolecular condensates (Ji D et al. *Molecular Cell* 2024). CTCF have also found to form transcriptional condensate and phase separation (Lee R et al. *Nucleic acids research* 2022). FOS was found to be an insulator-associated DNA-binding protein in this study and is potentially involved in chromatin remodeling, transcription condensation, and phase separation with the other factors such as BACH2, ATF3, NFE2 and MAFK. I have added the following sentence on line 556: FOXA1 pioneer factor functions as an initial chromatin-binding and chromatin-remodeling factor and has been reported to form biomolecular condensates.

7. In general, how the presented results are related to some models of chromatin architecture, e.g. loop extrusion, in which it is integrated convergent CTCF binding sites?

Goel VY et al. Nature Genetics 2023 identified highly nested and focal interactions through region capture Micro-C, which resemble fine-scale compartmental interactions and are termed microcompartments. In the section titled "Most microcompartments are robust to loss of loop extrusion," the researchers noted that a small proportion of interactions between CTCF and cohesin-bound sites exhibited significant reductions in strength when cohesin was depleted. In contrast, the majority of microcompartmental interactions remained largely unchanged under cohesin depletion. Our findings indicate that most P-P and E-P interactions, aside from a few CTCF and cohesin-bound enhancers and promoters, are likely facilitated by a compartmentalization mechanism that differs from loop extrusion. We suggest that nested, multiway, and focal microcompartments correspond to small, discrete A-compartments that arise through a compartmentalization process, potentially influenced by factors upstream of RNA Pol II initiation, such as transcription factors, co-factors, or active chromatin states. It follows that if active chromatin regions at microcompartment anchors exhibit selective "stickiness" with one another, they will tend to co-segregate, leading to the development of nested, focal interactions. This microphase separation, driven by preferential interactions among active loci within a block copolymer, may account for the striking interaction patterns we observe.

 The authors of the paper proposed several mechanisms potentially involved in microcompartments. These mechanisms may be involved in looping with insulator function. Another group reported that enhancer-promoter interactions and transcription are largely maintained upon depletion of CTCF, cohesin, WAPL or YY1. Instead, cohesin depletion decreased transcription factor binding to chromatin. Thus, cohesin may allow transcription factors to find and bind their targets more efficiently (Hsieh TS et al. *Nature Genetics* 2022). Among the identified insulator-associated DNA-binding proteins, Maz and MyoD1 form loops without CTCF (Xiao T et al. *Proc Natl Acad Sci USA* 2021 ; Ortabozkoyun H et al. *Nature genetics* 2022 ; Wang R et al. *Nature communications* 2022). I have added the following sentences on lines 571-575: Another group reported that enhancer-promoter interactions and transcription are largely maintained upon depletion of CTCF, cohesin, WAPL or YY1. Instead, cohesin depletion decreased transcription factor binding to chromatin. Thus, cohesin may allow transcription factors to find and bind their targets more efficiently. I have included the following explanation on lines 582-584: Maz and MyoD1 among the identified insulator-associated DNA-binding proteins form loops without CTCF.

 As for the directionality of CTCF, if chromatin loop anchors have some structural conformation, as shown in the paper entitled "The structural basis for cohesin-CTCF-anchored loops" (Li Y et al. *Nature* 2020), directional DNA binding would occur similarly to CTCF binding sites. Moreover, cohesin complexes that interact with convergent CTCF sites, that is, the N-terminus of CTCF, might be protected from WAPL, but those that interact with divergent CTCF sites, that is, the C-terminus of CTCF, might not be protected from WAPL, which could release cohesin from chromatin and thus disrupt cohesin-mediated chromatin loops (Davidson IF et al. *Nature Reviews Molecular Cell Biology* 2021). Regarding loop extrusion, the 'loop extrusion' hypothesis is motivated by in vitro observations. The experiment in yeast, in which cohesin variants that are unable to extrude DNA loops but retain the ability to topologically entrap DNA, suggested that in vivo chromatin loops are formed independently of loop extrusion. Instead, transcription promotes loop formation and acts as an extrinsic motor that extends these loops and defines their final positions (Guerin TM et al. *EMBO Journal* 2024). I have added the following sentences on lines 543-547: Cohesin complexes that interact with convergent CTCF sites, that is, the N-terminus of CTCF, might be protected from WAPL, but those that interact with divergent CTCF sites, that is, the C-terminus of CTCF, might not be protected from WAPL, which could release cohesin from chromatin and thus disrupt cohesin-mediated chromatin loops. I have included the following sentences on lines 577-582: The 'loop extrusion' hypothesis is motivated by in vitro observations. The experiment in yeast, in which cohesin variants that are unable to extrude DNA loops but retain the ability to topologically entrap DNA, suggested that in vivo chromatin loops are formed independently of loop extrusion. Instead, transcription promotes loop formation and acts as an extrinsic motor that extends these loops and defines their final positions.

 Another model for the regulation of gene expression by insulators is the boundary-pairing (insulator-pairing) model (Bing X et al. *Elife* 2024) (Ke W et al. *Elife* 2024) (Fujioka M et al. *PLoS Genetics* 2016). Molecules bound to insulators physically pair with their partners, either head-to-head or head-to-tail, with different degrees of specificity at the termini of TADs in flies. Although the experiments do not reveal how partners find each other, the mechanism unlikely requires loop extrusion. Homologous and heterologous insulator-insulator pairing interactions are central to the architectural functions of insulators. The manner of insulator-insulator interactions is orientation-dependent. I have summarized the model on lines 559-567: Other types of chromatin regulation are also expected to be related to the structural interactions of molecules. As the boundary-pairing (insulator-pairing) model, molecules bound to insulators physically pair with their partners, either head-to-head or head-to-tail, with different degrees of specificity at the termini of TADs in flies (Fig. 7). Although the experiments do not reveal how partners find each other, the mechanism unlikely requires loop extrusion. Homologous and heterologous insulator-insulator pairing interactions are central to the architectural functions of insulators. The manner of insulator-insulator interactions is orientation-dependent.

8. Do the authors think that the identified DBPs could work in that way as well?

The boundary-pairing (insulator-pairing) model would be applied to the insulator-associated DNA-binding proteins other than CTCF and cohesin that are involved in the loop extrusion mechanism (Bing X et al. Elife 2024) (Ke W et al. Elife 2024) (Fujioka M et al. PLoS Genetics 2016).

 Liquid-liquid phase separation was shown to occur through CTCF-mediated chromatin loops and to act as an insulator (Lee, R et al. *Nucleic Acids Research* 2022). Among the identified insulator-associated DNA-binding proteins, CEBPA has been found to form hubs that colocalize with transcriptional co-activators in a native cell context, which is associated with transcriptional condensate and phase separation (Christou-Kent M et al. *Cell Reports* 2023). The proposed microcompartment mechanisms are also associated with phase separation. Thus, the same or similar mechanisms are potentially associated with the insulator function of the identified DNA-binding proteins. I have included the following information on line 554: CEBPA in the identified insulator-associated DNA-binding proteins was also reported to be involved in transcriptional condensates and phase separation.

9. Also, can the authors comment about the mechanisms those newly identified DBPs mediate contacts by active processes or equilibrium processes?

Snead WT et al. Molecular Cell 2019 mentioned that protein post-transcriptional modifications (PTMs) facilitate the control of molecular valency and strength of protein-protein interactions. O-GlcNAcylation as a PTM inhibits CTCF binding to chromatin (Tang X et al. Nature Communications 2024). I found that the identified insulator-associated DNA-binding proteins tend to form a cluster at potential insulator sites (Supplementary Fig. 2d). These proteins may interact and actively regulate chromatin interactions, transcriptional condensation, and phase separation by PTMs. I have added the following explanation on lines 584-590: Furthermore, protein post-transcriptional modifications (PTMs) facilitate control over the molecular valency and strength of protein-protein interactions. O-GlcNAcylation as a PTM inhibits CTCF binding to chromatin. We found that the identified insulator-associated DNA-binding proteins tend to form a cluster at potential insulator sites (Fig. 4f and Supplementary Fig. 3c). These proteins may interact and actively regulate chromatin interactions, transcriptional condensation, and phase separation through PTMs.

10. Can the author provide some real examples along with published structural data (e.g. the mentioned micro-C data) to show the link between protein co-presence, directional bias and contact formation?

Structural molecular model of cohesin-CTCF-anchored loops has been published by Li Y et al. Nature 2020. The structural conformation of CTCF and cohesin in the loops would be the cause of the directional bias of CTCF binding sites, which I mentioned in lines 539 - 543 as follows: These results suggest that the directional bias of DNA-binding sites of insulator-associated DBPs may be involved in insulator function and chromatin regulation through structural interactions among DBPs, other proteins, DNAs, and RNAs. For example, the N-terminal amino acids of CTCF have been shown to interact with RAD21 in chromatin loops.

 To investigate the principles underlying the architectural functions of insulator-insulator pairing interactions, two insulators, Homie and Nhomie, flanking the *Drosophila even skipped *locus were analyzed. Pairing interactions between the transgene Homie and the eve locus are directional. The head-to-head pairing between the transgene and endogenous Homie matches the pattern of activation (Fujioka M et al. *PLoS Genetics* 2016).

Reviewer #3

Major Comments:

1. Some of these TFs do not have specific direct binding to DNA (P300, Cohesin). Since the authors are using binding motifs in their analysis workflow, I would remove those from the analysis.

When a protein complex binds to DNA, one protein of the complex binds to the DNA directory, and the other proteins may not bind to DNA. However, the DNA motif sequence bound by the protein may be registered as the DNA-binding motif of all the proteins in the complex. The molecular structure of the complex of CTCF and Cohesin showed that both CTCF and Cohesin bind to DNA (Li Y et al. Nature 2020). I think there is a possibility that if the molecular structure of a protein complex becomes available, the previous recognition of the DNA-binding ability of a protein may be changed. Therefore, I searched the Pfam database for 99 insulator-associated DNA-binding proteins identified in this study. I found that 97 are registered as DNA-binding proteins and/or have a known DNA-binding domain, and EP300 and SIN3A do not directory bind to DNA, which was also checked by Google search. I have added the following explanation in line 257 to indicate direct and indirect DNA-binding proteins: Among 99 insulator-associated DBPs, EP300 and SIN3A do not directory interact with DNA, and thus 97 insulator-associated DBPs directory bind to DNA. I have updated the sentence in line 20 of the Abstract as follows: We discovered 97 directional and minor nondirectional motifs in human fibroblast cells that corresponded to 23 DBPs related to insulator function, CTCF, and/or other types of chromosomal transcriptional regulation reported in previous studies.

2. I am not sure if I understood correctly, by why do the authors consider enhancers spanning 2Mb (200 bins of 10Kb around eSNPs)? This seems wrong. Enhancers are relatively small regions (100bp to 1Kb) and only a very small subset form super enhancers.

As the reviewer mentioned, I recognize enhancers are relatively small regions. In the paper, I intended to examine further upstream and downstream of promoter regions where enhancers are found. Therefore, I have modified the sentence in lines 929 - 931 of the Fig. 2 legend as follows: Enhancer-gene regulatory interaction regions consist of 200 bins of 10 kbp between -1 Mbp and 1 Mbp region from TSS, not including promoter.

3. I think the H3K27me3 analysis was very good, but I would have liked to see also constitutive heterochromatin as well, so maybe repeat the analysis for H3K9me3.

Following the reviewer's advice, I have added the ChIP-seq data of H3K9me3 as a truck of the UCSC Genome Browser. The distribution of H3K9me3 signal was different from that of H3K27me3 in some regions. I also found the insulator-associated DNA-binding sites close to the edges of H3K9me3 regions and took some screenshots of the UCSC Genome Browser of the regions around the sites in Supplementary Fig. 3b. I have modified the following sentence on lines 974 - 976 in the legend of Fig. 4: a Distribution of histone modification marks H3K27me3 (green color) and H3K9me3 (turquoise color) and transcript levels (pink color) in upstream and downstream regions of a potential insulator site (light orange color). I have also added the following result on lines 356 - 360: The same analysis was performed using H3K9me3 marks, instead of H3K27me3 (Fig. S3b). We found that the distribution of H3K9me3 signal was different from that of H3K27me3 in some regions, and discovered the insulator-associated DNA-binding sites close to the edges of H3K9me3 regions (Fig. S3b).

4. I was not sure I understood the analysis in Figure 6. The binding site is with 500bp of the interaction site, but micro-C interactions are at best at 1Kb resolution. They say they chose the centre of the interaction site, but we don't know exactly where there is the actual interaction. Also, it is not clear what they measure. Is it the number of binding sites of a specific or multiple DBP insulator proteins at a specific distance from this midpoint that they recover in all chromatin loops? Maybe I am missing something. This analysis was not very clear.

The resolution of the Micro-C assay is considered to be 100 bp and above, as the human nucleome core particle contains 145 bp (and 193 bp with linker) of DNA. However, internucleosomal DNA is cleaved by endonuclease into fragments of multiples of 10 nucleotides (Pospelov VA et al. Nucleic Acids Research 1979). Highly nested focal interactions were observed (Goel VY et al. Nature Genetics 2023). Base pair resolution was reported using Micro Capture-C (Hua P et al. Nature 2021). Sub-kilobase (20 bp resolution) chromatin topology was reported using an MNase-based chromosome conformation capture (3C) approach (Aljahani A et al. Nature Communications 2022). On the other hand, Hi-C data was analyzed at 1 kb resolution. (Gu H et al. bioRxiv 2021). If the resolution of Micro-C interactions is at best at 1 kb, the binding sites of a DNA-binding protein will not show a peak around the center of the genomic locations of interaction edges. Each panel shows the number of binding sites of a specific DNA-binding protein at a specific distance from the midpoint of all chromatin interaction edges. I have modified and added the following sentences in lines 593-597: High-resolution chromatin interaction data from a Micro-C assay indicated that most of the predicted insulator-associated DBPs showed DNA-binding-site distribution peaks around chromatin interaction sites, suggesting that these DBPs are involved in chromatin interactions and that the chromatin interaction data has a high degree of resolution. Base pair resolution was reported using Micro Capture-C.

Minor Comments:

1. PIQ does not consider TF concentration. Other methods do that and show that TF concentration improves predictions (e.g., ____https://www.biorxiv.org/content/10.1101/2023.07.15.549134v2____or ____https://pubmed.ncbi.nlm.nih.gov/37486787____/). The authors should discuss how that would impact their results.

The directional bias of CTCF binding sites was identified by ChIA-pet interactions of CTCF binding sites. The analysis of the contribution scores of DNA-binding sites of proteins considering the binding sites of CTCF as an insulator showed the same tendency of directional bias of CTCF binding sites. In the analysis, to remove the false-positive prediction of DNA-binding sites, I used the binding sites that overlapped with a ChIP-seq peak of the DNA-binding protein. This result suggests that the DNA-binding sites of CTCF obtained by the current analysis have sufficient quality. Therefore, if the accuracy of prediction of DNA-binding sites is improved, although the number of DNA-binding sites may be different, the overall tendency of the directionality of DNA-binding sites will not change and the results of this study will not change significantly.

 As for the first reference in the reviewer's comment, chromatin interaction data from Micro-C assay does not include all chromatin interactions in a cell or tissue, because it is expensive to cover all interactions. Therefore, it would be difficult to predict all chromatin interactions based on machine learning. As for the second reference in the reviewer's comment, pioneer factors such as FOXA are known to bind to closed chromatin regions, but transcription factors and DNA-binding proteins involved in chromatin interactions and insulators generally bind to open chromatin regions. The search for the DNA-binding motifs is not required in closed chromatin regions.

2. DeepLIFT is a good approach to interpret complex structures of CNN, but is not truly explainable AI. I think the authors should acknowledge this.

In the DeepLIFT paper, the authors explain that DeepLIFT is a method for decomposing the output prediction of a neural network on a specific input by backpropagating the contributions of all neurons in the network to every feature of the input (Shrikumar A et al. ICML 2017). DeepLIFT compares the activation of each neuron to its 'reference activation' and assigns contribution scores according to the difference. DeepLIFT calculates a metric to measure the difference between an input and the reference of the input.

 Truly explainable AI would be able to find cause and reason, and to make choices and decisions like humans. DeepLIFT does not perform causal inferences. I did not use the term "Explainable AI" in our manuscript, but I briefly explained it in Discussion. I have added the following explanation in lines 623-628: AI (Artificial Intelligence) is considered as a black box, since the reason and cause of prediction are difficult to know. To solve this issue, tools and methods have been developed to know the reason and cause. These technologies are called Explainable AI. DeepLIFT is considered to be a tool for Explainable AI. However, DeepLIFT does not answer the reason and cause for a prediction. It calculates scores representing the contribution of the input data to the prediction.

 Furthermore, to improve the readability of the manuscript, I have included the following explanation in lines 159-165: we computed DeepLIFT scores of the input data (i.e., each binding site of the ChIP-seq data of DNA-binding proteins) in the deep leaning analysis on gene expression levels. DeepLIFT compares the importance of each input for predicting gene expression levels to its 'reference or background level' and assigns contribution scores according to the difference. DeepLIFT calculates a metric to measure the difference between an input and the reference of the input.

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Referee #3

Evidence, reproducibility and clarity

Summary:

Osato and Hamada propose a systematic approach to identify DNA binding proteins that display directional binding. They used a modified Deep Learning method (DEcode) to investigate binding profiles of 1356 DBP from GTRD database at promoters (30 of 100bp bins around TSS) and enhancers (200 bins of 10Kb around eSNPs) and use this to predict expression of 25,071 genes in Fibroblasts, Monocytes, HMEC and NPC. This method achieves a good prediction power (Spearman correlation between predicted and actual expression of 0.74). They then use PIQ, and overlap predicted binding sites with actual ChIP-seq data to investigate the motifs of TFs that are controlling gene expression. They find 99 insulator proteins showing either a specific directional bias or minor non-directional bias, corresponding to 23 DBP previously reported to have insulator function. Of the 23 proteins they identify as regulating enhancer promoter interactions, 13 are associated with CTCF. They also show that there are significantly more insulator proteins binding sites at borders of polycomb domains, transcriptionally active or boundary regions based on chromatin interactions than other proteins.

Major Comments:

1. Some of these TFs do not have specific direct binding to DNA (P300, Cohesin). Since the authors are using binding motifs in their analysis workflow, I would remove those from the analysis.
2. I am not sure if I understood correctly, by why do the authors consider enhancers spanning 2Mb (200 bins of 10Kb around eSNPs)? This seems wrong. Enhancers are relatively small regions (100bp to 1Kb) and only a very small subset form super enhancers.
3. I think the H3K27me3 analysis was very good, but I would have liked to see also constitutive heterochromatin as well, so maybe repeat the analysis for H3K9me3.
4. I was not sure I understood the analysis in Figure 6. The binding site is with 500bp of the interaction site, but micro-C interactions are at best at 1Kb resolution. They say they chose the centre of the interaction site, but we don't know exactly where there is the actual interaction. Also, it is not clear what they measure. Is it the number of binding sites of a specific or multiple DBP insulator proteins at a specific distance from this midpoint that they recover in all chromatin loops? Maybe I am missing something. This analysis was not very clear.

Minor comments:

1. PIQ does not consider TF concentration. Other methods do that and show that TF concentration improves predictions (e.g., https://www.biorxiv.org/content/10.1101/2023.07.15.549134v2 or https://pubmed.ncbi.nlm.nih.gov/37486787/). The authors should discuss how that would impact their results.
2. DeepLIFT is a good approach to interpret complex structures of CNN, but is not truly explainable AI. I think the authors should acknowledge this.

Referee Cross-Commenting

I would like to mention that I agree with the comments of reviewers 1 and 2.

Significance

General assessment:

This is the first study to my knowledge that attempts to use Deep Learning to identify insulators and directional biases in binding. One of the limitations is that no additional methods were used to show that these DBP have directional binding bias. It is not necessarily to employ additional methods, but it would definitely strengthen the paper.

Advancements:

This is a useful catalogue of potential DNA binding proteins of interest, beyond just CTCF. Some known TFs are there, but also new ones are found.

Audience:

Basic research mainly, with particular focus on chromatin conformation and TF binding fields.

My expertise:

ML/AI methods in genomics, TF binding models, epigenetics and 3D chromatin interactions.

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Referee #2

Evidence, reproducibility and clarity

In this work, the authors describe a deep learning computational tool to identity binding motifs of DNA binding proteins associated to insulators that led to the discovery of 99 motifs related to insulation. This is in turn related to chromatin architecture and highlight the importance of directional bias in order to form chromatin loops.

In general, there are some aspects to be clarified and better explored to make stronger conclusions. In particular, there are some aspects to clarify in the text about the Machine Learning procedure (see my points below). In addition, I have some general questions about the biological implications of the discussed findings, listed in detail in the following list.

Also, I encourage the authors to integrate the current presentation of the data with other (published) data about chromatin architecture, to make more robust the claims and go deeper into the biological implications of the current work. Se my list below.

It follows a specific list of relevant points to be addressed:

Specific points:

1. Introduction, line 95: CTCF appears two times, it seems redundant;
2. Introduction, lines 99-103: Please stress better the novelty of the work. What is the main focus? The new identified DPBs or their binding sites? What are the "novel structural and functional roles of DBPs" mentioned?
3. Results, line 111: How do the SNPs come into the procedure? From the figures it seems the input is ChIP-seq peaks of DNBPs around the TSS;
4. Again, are those SNPs coming from the different cell lines? Or are they from individuals w.r.t some reference genome? I suggest a general restructuring of this part to let the reader understand more easily. One option could be simplifying the details here or alternatively including all the necessary details;
5. Figure 1: panel a and b are misleading. Is the matrix in panel a equivalent to the matrix in panel b? If not please clarify why. Maybe in b it is included the info about the SNPs? And if yes, again, what is then difference with a.
6. Line 386-388: could the author investigate in more detail this observation? Does it mean that loops driven by other DBPs independent of the known CTCF/Cohesin? Could the author provide examples of chromatin structural data e.g. MicroC?
7. In general, how the presented results are related to some models of chromatin architecture, e.g. loop extrusion, in which it is integrated convergent CTCF binding sites?
8. Do the authors think that the identified DBPs could work in that way as well?
9. Also, can the authors comment about the mechanisms those newly identified DBPs mediate contacts by active processes or equilibrium processes?
10. Can the author provide some real examples along with published structural data (e.g. the mentioned micro-C data) to show the link between protein co-presence, directional bias and contact formation?

Significance

In this work, the authors describe a deep learning computational tool to identity binding motifs of DNA binding proteins associated to insulators that led to the discovery of 99 motifs related to insulation. This is in turn related to chromatin architecture and highlight the importance of directional bias in order to form chromatin loops.

In general, chromatin organization is an important topic in the context of a constantly expanding research field. Therefore, the work is timely and could be useful for the community. The paper appears overall well written and the figures look clear and of good quality. Nevertheless, there are some aspects to be clarified and better explored to make stronger conclusions. In particular, there are some aspects to clarify in the text about the Machine Learning procedure (see list of specific points). In addition, I have some general questions about the biological implications of the discussed findings, listed in detail in the above reported points.

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Referee #1

Evidence, reproducibility and clarity

The study by Osato and Hamada aims at computationally identifying a set of novel putative insulator-associated DNA binding proteins (DBPs) via estimation of their contribution to the expression of genes in the same chromosome region of their binding sites (+- 1Mbp from TSS). To achieve this, the authors leverage a deep learning architecture already published via which ChIP-seq peaks of DBPs in the TSS of a given gene are used to predict its expression level in four human cell lines.

Building on this, the authors used another tool called DeepLIFT to evaluate the weight of each DBP binding site on the final gene expression value. Hence they made the assumption that if a given DBP had an insulator function they could restrict the prediction of the gene's expression to the region included between pairs of that DBP binding sites, and evaluate the pair's motif directionality bias in the distribution of weights. They exemplify their approach's validity by the fact that they can predict the known directionality bias of CTCF/cohesin-bound sites as the highest of the lot, with the F-R orientation of the pairs the most enriched, recapitulating what already known in literature: i.e., that F-R chromatin interaction peaks are the most enriched. In addition, they find several new DBPs showing significant directionality bias; hence they could be candidates for insulation activity. They then provide correlation between these putative insulator binding sites and sites of transition between euchromatin and heterochromatin by independently using histone mark and gene expression datasets. This, of course, is not surprising because (a) there is insulation between regions with heterotypic chromatin identities, and (b) it was already known from the first papers describing insulated chromatin domains that their boundaries were well-enriched for active transcription and transcriptional regulators (e.g., Dixon et al, Nature 2012).

Finally, they use chromatin interaction (looping) sites to check the overlap between CTCF and all other DBPs and define a subset of putative insulator DBPs not overlapping CTCF peaks, suggesting potentially new insulatory mechanisms. These factors were all known transcriptional activators, but this part of the findings carry most of the novelty in the work and have the potential of opening up new directions for research in chromatin organization.

Overall, the methodology applied here is adequate, clear, and reproducible. The major issue, in our view, is that the entire manuscript's findings relies on the usage of deepLIFT, a tool which was not benchmarked previously or by the current study. In fact, deepLIFT is public as regards its code, and also appears as a preprint from 2017 on biorXiv and published in the Proceedings of Machine Learning Research conference. Also, this key tool was developed by the Kundaje lab (who produce high quality alogrithms), and not by the authors. Therefore, the manuscript is predominantly based on the execution of existing workflows to publicly-available data. This does not take anything away from the interesting question posed here, but at the same time does not provide the community with any new algorithm/workflow.

Finally, although I appreciate that the authors are purely computational and have likely no capacity for experimental validation of their claims of new DBPs having insulator roles, I would assume that there are RNA-seq and/or ChIP-seq data out there produced after knockdown of one or more of these DBPs that show directional positioning. Using this kind of data, effects on gene expression can at least be tested in regard to the authors' predictions. Moreover, in terms of validation, Figure 6 should be expanded to incorporate analysis of DBPs not overlapping CTCF/cohesin in chromatin interaction data that is important and potentially more interesting than the simple DBPs enrichment reported in the present form of the figure. Critically, I would like to see use of Micro-C/Hi-C data and ChIP-seq from these factors, where insulation scores around their directionally-bound sites show some sort of an effect like that presumed by the authors - and many such datasets are publicly-available and can be put to good use here.

As secondary issues, we would point out that:

• The suggested alternative transcripts function, also highlighted in the manuscript;s abstract, is only supported by visual inspection of a few cases for several putative DBPs. I believe this is insufficient to support what looks like one of the major claims of the paper when reading the abstract, and a more quantitative and genome-wide analysis must be adopted, although the authors mention it as just an 'observation'.
• Figure 1 serves no purpose in my opinion and can be removed, while figures can generally be improved (e.g., the browser screenshots in Figs 4 and 5) for interpretability from readers outside the immediate research field.
• Similarly, the text is rather convoluted at places and should be re-approached with more clarity for less specialized readers in mind.

Significance

The scientific novelty of the work lies primarily in the identification of a set of DBPs that are proposed to confer insulator activity genome-wide. This has been long sought after in human data (whilst it is well understood and defined in Drosophila). The authors produce a quantitative ranking of the putative insulation effect of these DBPs and, most importantly, go on to identify a smaller subset that are apparently non-overlapping with anchors of CTCF-cohesin loop anchors; the presence of strong motif orientation biases in many DBPs can also be of broad interest, especially those that cannot be trivially ascribable to the loop extrusion process.

However, although these findings open the way for speculation on multiple insulation mechanisms via proteins with multiple regulatory functions, the manuscript provide no experimental or computational means to test the proposed roles of these DBPs - and, as such, this limits the potential impact of the work and mostly targets researchers in the field of genome organization that can test these findings. Having said this, if validated, this work can significantly broaden our understanding of how chromatin is organized in 3D nuclear space.

I typically identify myself to the authors: A. Papantonis, expertise in 3D genome architecture, chromatin biology, and genomics/bioinformatics.

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Reply to the reviewers

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

The authors provide a detailed characterization of the tumor microenvironment (TME) of 91 ovarian cancer patients, broken down in long and short-term survivors (post 5 years). The focus on the role of a subgroup of T cells, gamma/delta γδ) T cells with reported anti but also pro tumorigenic properties, Prior work of the lab has established a link between a subgroup of γδ T cells expressing CD73 and poor prognosis, due to the ability of these cells to produce immunosuppressive cytokines, such as IL10 or IL8 and the production of adenosine, by CD73, in the micromilieu. The data is further backed up by the analysis of fresh tumor specimens and tissue culture work.

Here they continue this story by investigating the TME using tumor microarrays (91 samples), single cell RNA seq (12 patients), imaging mass cytometry (> 30 samples) and flow cytometry (form confirmatory purposes) to define cellular neighborhoods of CD73+ and CD73- γδ T cells. This revealed differences in cellular composition and spatial transcriptome analysis further helped to define the transcriptomes in γδ T cells, cancer cells and cancer associated fibroblasts.

The authors conclude the in ovarian cancer γδ T cells expressing CD73 dampen anti-tumor immunity and propose detection and evaluation of CD73+ γδ T cells as prognostic marker.

The manuscript is well written, and despite its descriptive nature, easy to follow. Data is presented in a clear and easy to read fashion.

Reviewer #1 (Significance (Required)):

Using a well characterized cohort of ovarian cancer patients with detailed clinical follow up the authors report on the predictive power of a subset of γδ T cells expressing CD73, with immune suppressive / regulatory capacity, reading out patient survival in high grade serous ovarian cancer, a still deadly disease. As such the identification of reliable markers predicting survival is a clear medical need. These findings contrast others made in different solid cancers, suggesting tumor type specific differences, which are only starting to emerge, but are of clear clinical relevance.

What is unclear to me and needs to be addressed, is if these patient specimens were taken before or after initial therapy, whether the samples have been stratified according the treatment that they got, assuming it will be mostly platinum compounds (but maybe not), and that the p53 status of the tumors are (if genetics are available this would help to add some granularity to the study that, as it stands is largely descriptive, even though with extremely high resolution. This data should be available and could be integrated.

We thank the reviewer for this insightful and constructive comment. We agree that clinical context and treatment stratification are essential to strengthen the interpretation and translational value of our findings.

We confirm that all tumor samples used in this study were obtained prior to any systemic treatment, i.e., before first-line chemotherapy, during the Biopsy realized for the diagnosis. This information has now been clearly stated in the Methods and Results section (page 4, line 103) and also in Table S1.

Although our primary aim was not to evaluate correlations with mutational status, we recognize the critical role that tumor genetics play in shaping the immune microenvironment. Using available clinical genomics data, we found that the TP53 mutational status of our cohort aligns with that of previous analyses. As expected for high-grade serous ovarian cancer (HGSOC), nearly all tumors exhibited TP53 mutations (present in 95% of patients). Due to the lack of variability in TP53 status, no meaningful stratification was observed based on this factor. This information has been added in the Materials and methods part (page 4 lines 104 to 106)

Some minor issues

• I would stick to CD73, and not mix it with NT5E, which is confusing at first (Fig 2).

We appreciate this suggestion. To clarify the nomenclature and avoid confusion, we have consistently indicated throughout the text and figure legends that NT5E refers to the CD73 gene.

• I would ask to compare the overall survival of CD73+ between densities - is it still significantly different in fig 1 - meaning is it about density, CD73 expression, or both. Comparing survival of tumors with a low density of CD73+ γδ T cells does not seem to be different from those having a low density of CD73- γδ T cells, which could be considered in data interpretation. Same for high density tumors.

In the manuscript, the term “density” specifically refers to the density of γδ____ T cells and not the density of CD73 molecules expressed by these cells. Additionally, it is not feasible to conduct a density analysis of molecules using the data obtained from immunofluorescence (IF) staining of sample sections.

Kaplan-Meier analyses were performed to assess patient survival based on the density of total γδ____ T cells, as well as the subsets of CD73⁺ and CD73⁻ γδ T cells. The results indicate that a higher density of γδ____ T cells is associated with poorer patient survival, with a more pronounced effect seen in those with a high density of CD73⁺ γδ T cells compared to those with CD73⁻ γδ T cells.

As the reviewer pointed out, patients with a low density of CD73⁺ γδ T cells do not show significantly different survival outcomes compared to those with a low density of CD73⁻ γδ T cells (IC50 for low CD73⁺ = 6.0 years vs. IC50 for low CD73⁻ = 6.2 years). In response, we have revised the corresponding sentence in the text and included the IC50 values for greater clarity and informativeness (page 9).

• figure 1, caption should include the word "patients" at the end, I guess.

The modification has been done.

• labelling and font can be improved in many panels, eg. the dot plots in Fig 2, panel B, right, same for panel C and D

We appreciate the feedback on figure presentation. We have now updated Figure 2 with improved labeling, consistent font size, and enhanced resolution to ensure better readability across all panels, particularly panels B–D. The revised figure has been updated in the main manuscript.

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

In this manuscript ("Deciphering the tumor-infiltrating CD73+ regulatory γδ T cell ecosystem associated with poor survival of patients with ovarian cancer"), Chabab et al. report on the phenotype and location of CD73+ γδ T cells in ovarian cancer. CD73+ γδ T cells can be immunosuppressive via the production of cytokines (IL-8, IL-10) and the expression of PD-L1. Here, the authors investigated the phenotype and location of CD73+ and -neg γδ T cells in ovarian cancers with a particular focus on the cells surrounding the γδ T cells in the tumour.

Overall, the study is informative and well-performed. However, the way some of the data are presented does not allow to fully evaluate them. Besides this, this reviewer only has some minor comments.

General comments:

• The data provided in this manuscript are descriptive/correlative, and as such, causation cannot be inferred. Therefore, the language needs to reflect this; statements like "we investigated the impact of CD73+ regulatory γδ T cells in ovarian cancer" (L89) and "CD73+ γδ T cells were in close contact with more aggressive tumor cells" (L426), among others, are incorrect without functional data. The authors are advised to adjust the text throughout.

We thank the reviewer for this thoughtful point. We have amended the text to make it consistent with the data.

• Please make the figure legends self-explanatory without the need to search for the information in the M&M. For example, the graphs in fig1 and 3 contain many dots, but it is not explained what these dots represent. Please also add n for each experiment shown and state how often the experiment was performed independently.

As requested by the reviewer, we have revised the figure legends to make them more explicit. We have indicated the number of biological replicates (n) and how many times each experiment was performed independently. This information has been added to each legend where consistent and relevant, to ensure clarity and reproducibility.

• It would be helpful for the reader if abbreviations introduced in the M&M were also explained the first time they appeared in the results section.

This point has been addressed as requested by the reviewer.

• Please explain all abbreviations, e.g. FIGO, CST, NT5E, etc.
• L235: typo 'that' instead of 'than'; L258 'reduced'; L259 'fig1d-f'; L451f twice 'CD73+'; 'naive' instead of 'naïve' throughout; SF2 legend: '2f' instead of '3f', SF9 legend: '1.105'.
• L280ff: "Tumor cells ... were the most important cell type" - it may be clearer to use 'most frequent';

All these points have been addressed.

M&M - Please be consistent, if you provide catalogue numbers or dilutions (antibody, reagents) [which is good, maybe even adding the RRID number], do so for all items.

This point has been addressed as requested by the reviewer.

• The M&M does not state for the CAFs how long they were cultured before the supernatant was taken for the cytokine measurements.

This point has been added in M&M section.

• For the IL-6 ELISA, it is stated that the "cells were harvested"; what happened to them, and how do you get any SN from these cells?

We have amended the protocol of IL-6 Elisa in M&M section for clarification.

Figures Fig.1: - The authors used the word 'predict' in the heading, which seems not appropriate for a retrospective study; something like 'correlate' seems better.

The word “predict” has been replaced by “correlate” as suggested by the reviewer.

• Similarly, the title of the figure legends claims that the 'impact of γδ T cells' is shown, while only a correlation is presented.

The title of the figure has been modified

• For Fig1a-c, only summary data are presented. Please add exemplary pictures as well.

Pictures of IF have been added as Supplementary Fig 1.

• For Fig1d-f, the label for the x-axis is missing.

The figure has been corrected.

Fig.2 - It seems funny to call the patients 'naïve', maybe 'untreated' is clearer.

We appreciate this suggestion and agree that ‘untreated’ is a clearer and more appropriate term in this context. We have replaced all instances of ‘naïve’ with ‘untreated’ throughout the manuscript to avoid ambiguity.

• The graph in Fig2e does not allow comparing the cell frequencies properly. This would require either bar graphs or a table. Furthermore, the statistical analysis is missing. Without that, a statement like "associated with higher proportion of CAFs" (L265) is not supported.

We thank the reviewer for this valuable observation. In response, we have replaced the original visualization in Figure 2E with grouped bar graphs showing the mean ± SEM of the relative proportions of each major cell type in the NT5E_low and NT5E_high groups, based on the median split. This format allows for clearer visual comparison of cell frequencies across conditions.

Furthermore, we performed statistical comparisons using a t-test (a parametric test) on each population to evaluate differences in cell type proportions between the two groups. The results indicate a significantly higher proportion of CAFs and γδ T cells in the NT5E_high tumor profile. The corresponding p-values are provided in the figure legend. We hope this revised analysis and clearer presentation address the reviewer’s concerns.

Fig.3 - For Fig3b+c, the IMC are derived from 4 patients (not clear for the flow data)

As stated in both the figure legend and the text, the IMC analysis was conducted on 38 ROIs from four patient samples, while the flow cytometry analysis was performed on tumor samples from seven ovarian cancer patients.

• did the authors noticed differences between patients?

"As shown in new Figures 3b and 3c, no significant differences were observed between patients. Each individual patient is represented by a different color."

• For Fig3e, the description in the text does not reflect the figure, e.g. cluster 1 does not show LAG3 expression, but this is claimed in the text (other descriptions are off as well).

The text describing Fig. 3e has been amended in the new version of the manuscript.

• In Fig3h, the authors stain cytokines in γδ T cells purified from ovarian cancer samples. The text seems to imply that the cytokine staining was performed directly ex vivo, without an in vitro stimulation of the cells, e.g. with PMA/ionomycin (if so, the description is missing). In any case, the values appear surprisingly high. Exemplary data are needed to clarify how the gating was done (for γδ T cells and the cytokines) and what the primary data looked like.

The protocol has been amended in the “Materials and Methods” section. A gating strategy and primary data analysis from one representative patient are included in a supplementary Figure 4c.

We agree with the reviewer’s comments that it is surprising that γδ T cell stimulation is not required for IL-8, IL10 and IFNγ production. However, one possible explanation is the high reactivity of γδ T cells compared to other T cell subsets, as well as their localization in the tumor microenvironment rather than in healthy tissue or blood.

• In Fig3h, it is not clear what is meant with "IL-8 / IL-10", please explain.

This analysis shows the percentage of cells that are positive for both IL-8 and IL-10.

The figure and its legend have been amended for clarity.

Fig.4 - Please provide the values and the statistical analyses for all cell populations.

We performed statistical analyses (Wilcoxon signed-rank test) for all cell populations and provide the data in the Supplementary Fig. 5A. However, due to the heterogeneity of ROIs, a significant difference was observed for tumor cells, which were more prevalent more in the neighborhood of CD73- than CD73+ γδ T cells (p

Fig.5/6 - In Fig5, the authors state that 8 cell populations were differentially enriched around CD73+ or -neg γδ T cells. However, in Fig4, only 4 of these populations are mentioned. Please add the remaining 4 to fig4 and name the 8 clusters in fig5 in line with the gating strategy used in fig4.

We thank the reviewer for highlighting that the description of Figure 5 in our text was unclear. We have revised the text for clarification and specify that based on Supplementary Figure 7, which shows the number of cells for each cell type found in the neighborhood of all γδ T cell subsets (CD73- and CD73+) in all ROIs. We decided to perform phenotypic analysis on only four cell types (those with a sufficient cell counts), setting the cutoff at 700 cells.

The four cell types are analyzed in Figures 5 and 6. Figure 5A shows tumor cells, with eight clusters identified, while Figure 5B represents fibroblasts, with seven clusters identified. Figure 6A shows CD4 T cells, with eight clusters, and Figure 6B CD8 T cells, with ten clusters.

• Furthermore, the authors want to show in fig5 how the phenotype of these 8 cell populations differs depending on whether they are close to CD73+/- γδT cells. tSNE plots do not allow illustrating this (BTW: the plots lack the colour code). The frequencies of the cell types/phenotypes in the vicinity of CD73+/- γδ T cells need to be depicted differently (e.g. bar graphs). Furthermore, the claim that differences are observed, needs to be supported by showing the statistical values obtained. The same argument applies to Fig6 and SF8.

We have added the code color of tSNE plots in Figures 5, 6, and SF9. The tables in Supplementary Figure 8 show the percentage of cells in each cluster within the vicinity of CD73+/- γδ T cells, allowing for an investigation of the neighborhood of each γδ T cell subset.

• Fig6: This reviewer disagrees with the notion that the expression of HLA-DR or CD279 is enough to imply a functional state of the cell.

As requested by the reviewer, we have amended the text to clarify that: “Cluster analysis revealed that CD4+ T cells in contact with effector γδ T cells (i.e., the CD73- subset) express HLA-DR and/or PD-1, both activation markers.”

Supplements - SF2a: please check the labels; how can CD8+ CD4+ cells be labelled 'CD8 T cells' and why do the authors exclude the possibility that e.g. B cells could express HLA-DR?

We thank the reviewer for pointing out the error in Figure 2a, which has now been corrected. The CD8+ cells have been relabeled as 'CD8 T cells,' and the B cells are now shown expressing HLA-DR.

• SF7 is not clear to this reviewer. If the clusters represent different cell types, how can e.g. tumours be found in all of them?

We believe the reviewer is referring to SF9 rather than SF7 in this comment. SF9 analyzes γδ T cells in proximity to CD73+ and CD73- γδ T cells. As in Figures 5 and 6, γδ T cell neighbors of CD73+ and CD73- γδ T cells were identified, and a clustering analysis revealed five distinct clusters. Tumor cells was not analyzed in this figure. We have clarified the text to prevent confusion

• SF9b lacks a negative control and a statistical analysis, and SF9c lacks the summary data and statistical analysis.

As requested by the reviewer, we have performed statistical analysis for SF9b and added a negative control. Additionally, we have included summary data with a statistical analysis in SF9c.

• In the text, the authors state, "We and others reported that in ovarian tumors, IL-6 is mainly produced by CAFs and induces CD73 expression by γδ T cells (Extended Data Fig. 9 and 15)." The data in SF9b are not enough to make this claim and reference 15 is a review article that does not even mention 'IL-6'. This needs to be corrected.

We have updated Supplementary Figure 9B to provide more robust data. We thank the reviewer for pointing out our error. The publication we intend to cite is a research article, not a review.” Hu G, Cheng P, Pan J, Wang S, Ding Q, Jiang Z, et al. An IL6-Adenosine Positive Feedback Loop between CD73+ γδ Tregs and CAFs Promotes Tumor Progression in Human Breast Cancer. Cancer Immunol Res. 2020;8:1273–86.” we made the correction in the manuscript.

Reviewer #2 (Significance (Required)):

In this manuscript ("Deciphering the tumor-infiltrating CD73+ regulatory γδ T cell ecosystem associated with poor survival of patients with ovarian cancer"), Chabab et al. report on the phenotype and location of CD73+ γδ T cells in ovarian cancer.

CD73+ γδ T cells can be immunosuppressive via the production of cytokines (IL-8, IL-10) and the expression of PD-L1. Here, the authors investigated the phenotype and location of CD73+ and -neg γδ T cells in ovarian cancers with a particular focus on the cells surrounding the γδ T cells in the tumour.

Overall, the study is informative and well-performed. However, the way some of the data are presented does not allow to fully evaluate them. Besides this, this reviewer only has some minor comments.

To enable a full evaluation of the data, we have added new figures, amended others, and clarified certain points in the text, hoping that the reviewer will find these modifications sufficient to consider our manuscript for publication.

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

In this article, Chabab et al. analyze sample from ovarian cancer patients, with a specific focus on gamma-delta T cells (Tγδ). The authors claim that CD73+ cells are associated with poor prognosis in ovarian cancer, and that CD73 expression is correlated with the composition and polarization of the microenvironment. Using imaging mass cytometry data, they also claim that the neighborhoods of CD73+ and CD73- Tγδ cells differs in composition.

Major comments: - The prognostic value of CD73/NT5E is analyzed in TCGA-Ovarian RNAseq data. In the context of this article, it is implied that this should reflect CD73 expression by Tγδ but it is likely that other cell types are contributing to bulk CD73 expression.

We appreciate the reviewer’s insightful comment. In fact, due to low proportion of Tγδ in TME we have stratified on NT5E total expression. We agree that this signal likely includes contributions from multiple cell types beyond γδ T cells, such as cancer-associated fibroblasts and endothelial cells, which are also known to express CD73 (NT5E gene).

The stratification of patient based on NT5E total expression showed an association between high NT5E expression and poorer overall survival and increase in Tγδ gene markers (TRDC, TRGC1/2) and percentage of cells (Fig2E) in the patient cohort (Fig2C). To clarify this point, we have revised the Results and Discussion sections to explicitly state that the TCGA-based survival analysis reflects total intratumoral NT5E enrichment and cannot be attributed specifically to γδ T cells. We now refer to this analysis as an independent validation of the clinical relevance of CD73, while noting that its cell-type-specific contribution remains to be resolved in future studies using spatial transcriptomics or deconvolution approaches.

• In the analysis of scRNAseq data, multiple public datasets are aggregated and the overall level of CD73 is used for stratification. Is this stratification confounded by dataset of origin?

We thank the reviewer for raising this critical point regarding potential batch effects and dataset-driven bias in our stratification strategy. To address this, we performed additional analyses to assess whether NT5E (CD73) expression is confounded by dataset of origin.

First, we verified that all single-cell datasets (GSE147082, GSE241221, and GSE235931) were processed using a harmonized integration workflow, including SCTransform normalization and integration using Seurat’s reciprocal PCA approach, which effectively minimizes batch-related variability.

• The last part of the results discusses the role of IL6 produced by CAFs on Tγδ, but very little data is shown to support the proposed mechanisms. The authors report expression of CD73 by flow cytometry on blood-sorted Tγδ following culture with IL2, IL6, IL21. The data shown however only represents one donor and should therefore be repeated on multiple donors.

We appreciate the reviewer’s insightful comment. We have added data and updated Supplementary Figure 9 to provide more robust findings. Regarding the role of IL-6, our data in ovarian cancer are consistent with the study by Hu et al. in breast cancer, which reports an IL-6-Adenosine Positive Feedback Loop between CD73+ γδ Tregs and CAFs that promotes tumor progression in human breast cancer."

Minor comments:

• The authors stratify their cohort by Tγδ density but I could not find the threshold used for stratification

The threshold has been added in figure and text.

• Labels for CD8+ and CD4+CD8+ T cells are swapped in Extended Data Fig 2A

The correction of figure has been made.

• The legend of graphs shown in multiple panels (for instance: Fig 3F) are not very clear: is each dot representing the average expression of one cluster in one patient?
• In figure 3G there is no color scale, the authors need to add it with appropriate units so that readers can interpret the data shown

These points have all been amended and corrected in the next version of the manuscript.

Reviewer #3 (Significance (Required)):

This paper shows interesting imaging mass cytometry data of ovarian cancer specimens. The focus on CD73 expression by Tγδ is fairly specific, although the exonucleotidases pathway involving CD73 is currently extensively studied for its immunosuppressive role.

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Referee #3

Evidence, reproducibility and clarity

In this article, Chabab et al. analyze sample from ovarian cancer patients, with a specific focus on gamma-delta T cells (Tgd). The authors claim that CD73+ cells are associated with poor prognosis in ovarian cancer, and that CD73 expression is correlated with the composition and polarization of the microenvironment. Using imaging mass cytometry data, they also claim that the neighborhoods of CD73+ and CD73- Tgd cells differs in composition.

Major comments:

• The prognostic value of CD73/NT5E is analyzed in TCGA-Ovarian RNAseq data. In the context of this article, it is implied that this should reflect CD73 expression by Tgd but it is likely that other cell types are contributing to bulk CD73 expression.
• In the analysis of scRNAseq data, multiple public datasets are aggregated and the overall level of CD73 is used for stratification. Is this stratification confounded by dataset of origin ?
• The last part of the results discuss the role of IL6 produced by CAFs on Tgd, but very little data is shown to support the proposed mechanisms. The authors report expression of CD73 by flow cytometry on blood-sorted Tgd following culture with IL2, IL6, IL21. The data shown however only represents one donor and should therefore be repeated on multiple donors.

Minor comments:

• The authors stratify their cohort by Tgd density but I could not find the threshold used for stratification
• Labels for CD8+ and CD4+CD8+ T cells are swapped in Extended Data Fig 2A
• The legend of graphs shown in multiple panels (for instance : Fig 3F) are not very clear : is each dot representing the average expression of one cluster in one patient ?
• In figure 3G there is no color scale, the authors need to add it with appropriate units so that readers can interpret the data shown

Significance

This paper shows interesting imaging mass cytometry data of ovarian cancer specimens. The focus on CD73 expression by Tgd is fairly specific, although the exonucleotidases pathway involving CD73 is currently extensively studied for its immunosuppressive role.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

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Referee #2

Evidence, reproducibility and clarity

In this manuscript ("Deciphering the tumor-infiltrating CD73+ regulatory γδ T cell ecosystem associated with poor survival of patients with ovarian cancer"), Chabab et al. report on the phenotype and location of CD73+ gd T cells in ovarian cancer. CD73+ gd T cells can be immunosuppressive via the production of cytokines (IL-8, IL-10) and the expression of PD-L1. Here, the authors investigated the phenotype and location of CD73+ and -neg gd T cells in ovarian cancers with a particular focus on the cells surrounding the gd T cells in the tumour. Overall, the study is informative and well-performed. However, the way some of the data are presented does not allow to fully evaluate them. Besides this, this reviewer only has some minor comments.

General comments:

• The data provided in this manuscript are descriptive/correlative, and as such, causation cannot be inferred. Therefore, the language needs to reflect this; statements like "we investigated the impact of CD73+ regulatory γδ T cells in ovarian cancer" (L89) and "CD73+ γδ T cells were in close contact with more aggressive tumor cells" (L426), among others, are incorrect without functional data. The authors are advised to adjust the text throughout.
• Please make the figure legends self-explanatory without the need to search for the information in the M&M. For example, the graphs in fig1 and 3 contain many dots, but it is not explained what these dots represent. Please also add n for each experiment shown and state how often the experiment was performed independently.
• It would be helpful for the reader if abbreviations introduced in the M&M were also explained the first time they appeared in the results section.
• Please explain all abbreviations, e.g. FIGO, CST, NT5E, etc.
• L235: typo 'that' instead of 'than'; L258 'reduced'; L259 'fig1d-f'; L451f twice 'CD73+'; 'naive' instead of 'naïve' throughout; SF2 legend: '2f' instead of '3f', SF9 legend: '1.105'.
• L280ff: "Tumor cells ... were the most important cell type" - it may be clearer to use 'most frequent';

M&M

• Please be consistent, if you provide catalogue numbers or dilutions (antibody, reagents) [which is good, maybe even adding the RRID number], do so for all items.
• The M&M does not state for the CAFs how long they were cultured before the supernatant was taken for the cytokine measurements.
• For the IL-6 ELISA, it is stated that the "cells were harvested"; what happened to them, and how do you get any SN from these cells?

Figures

Fig.1:

• The authors used the word 'predict' in the heading, which seems not appropriate for a retrospective study; something like 'correlate' seems better.
• Similarly, the title of the figure legends claims that the 'impact of gd T cells' is shown, while only a correlation is presented.
• For Fig1a-c, only summary data are presented. Please add exemplary pictures as well.
• For Fig1d-f, the label for the x-axis is missing.

Fig.2

• It seems funny to call the patients 'naïve', maybe 'untreated' is clearer.
• The graph in Fig2e does not allow comparing the cell frequencies properly. This would require either bar graphs or a table. Furthermore, the statistical analysis is missing. Without that, a statement like "associated with higher proportion of CAFs" (L265) is not supported.

Fig.3

• For Fig3b+c, the IMC are derived from 4 patients (not clear for the flow data) - did the authors noticed differences between patients?
• For Fig3e, the description in the text does not reflect the figure, e.g. cluster 1 does not show LAG3 expression, but this is claimed in the text (other descriptions are off as well).
• In Fig3h, the authors stain cytokines in gd T cells purified from ovarian cancer samples. The text seems to imply that the cytokine staining was performed directly ex vivo, without an in vitro stimulation of the cells, e.g. with PMA/ionomycin (if so, the description is missing). In any case, the values appear surprisingly high. Exemplary data are needed to clarify how the gating was done (for gd T cells and the cytokines) and what the primary data looked like.
• In Fig3h, it is not clear what is meant with "IL-8 / IL-10", please explain.

Fig.4

• Please provide the values and the statistical analyses for all cell populations.

Fig.5/6

• In Fig5, the authors state that 8 cell populations were differentially enriched around CD73+ or -neg gd T cells. However, in Fig4, only 4 of these populations are mentioned. Please add the remaining 4 to fig4 and name the 8 clusters in fig5 in line with the gating strategy used in fig4.
• Furthermore, the authors want to show in fig5 how the phenotype of these 8 cell populations differs depending on whether they are close to CD73+/- gdT cells. tSNE plots do not allow illustrating this (BTW: the plots lack the colour code). The frequencies of the cell types/phenotypes in the vicinity of CD73+/- gd T cells need to be depicted differently (e.g. bar graphs). Furthermore, the claim that differences are observed, needs to be supported by showing the statistical values obtained. The same argument applies to Fig6 and SF8.
• Fig6: This reviewer disagrees with the notion that the expression of HLA-DR or CD279 is enough to imply a functional state of the cell.

Supplements

• SF2a: please check the labels; how can CD8+ CD4+ cells be labelled 'CD8 T cells' and why do the authors exclude the possibility that e.g. B cells could express HLA-DR?
• SF7 is not clear to this reviewer. If the clusters represent different cell types, how can e.g. tumours be found in all of them?
• SF9b lacks a negative control and a statistical analysis, and SF9c lacks the summary data and statistical analysis.
• In the text, the authors state, "We and others reported that in ovarian tumors, IL-6 is mainly produced by CAFs and induces CD73 expression by γδ T cells (Extended Data Fig. 9 and 15)." The data in SF9b are not enough to make this claim and reference 15 is a review article that does not even mention 'IL-6'. This needs to be corrected.

Significance

In this manuscript ("Deciphering the tumor-infiltrating CD73+ regulatory γδ T cell ecosystem associated with poor survival of patients with ovarian cancer"), Chabab et al. report on the phenotype and location of CD73+ gd T cells in ovarian cancer. CD73+ gd T cells can be immunosuppressive via the production of cytokines (IL-8, IL-10) and the expression of PD-L1. Here, the authors investigated the phenotype and location of CD73+ and -neg gd T cells in ovarian cancers with a particular focus on the cells surrounding the gd T cells in the tumour. Overall, the study is informative and well-performed. However, the way some of the data are presented does not allow to fully evaluate them. Besides this, this reviewer only has some minor comments.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

The authors provide a detailed characterizsation of the tumor microenvironment (TME) of 91 ovarian cancer patients, brokend down in long and short term survivors (post 5 years). The focus on the role of a subgroup of T cells, gamma/delta (gd) T cells with reported anti but also pro tumorigenic properties, Prior work of the lab has established a link between a subgroup of gd T cells expressing CD73 and poor prognosis, due to the ability of these cells to produce immunosuppressive cytokines, such as IL10 or IL8 and the production of adenosine, by CD73, in the micromilieu. The data is further backed up by the analysis of fresh tumor specimens and tissue culture work.

Here they continue this story by investigating the TME using tumor microarrays (91 samples), single cell RNA seq (12 patients), imaging mass cytometry (> 30 samples) and flow cytometry (form confirmatory purposes) to define cellular neighborhoods of CD73+ and CD73- gd T cells. THis revealed differences in cellular composition and spatial transcriptome analysis further helped to define the ttranscriptomes in gd T cells, cancer cells and cancer associated fibroblasts.

The authors conclude the in ovarian cancer gd T cells expressing CD73 dampen anti-tumor immun ity and propose detection and evaluation of CD73+ gd T cells as prognostic marker.

The manuscript is well written, and despite its descriptive nature, easy to follow. Data is presented in a clear and easy to read fashion.

Significance

Using a well characterized cohort of ovarian cancer patients with detailed clinical follow up the authors report on the predictive power of a subset of gd T cells expressing CD73, with immune suppressive / regulatory capacity, reading out patient survival in high grade serous ovarian cancer, a still deadly disease. As such the identificaiton of reliable markers predicting survival is a clear medical need. These findings contrast others made in different solid cancers, suggesting tumor typ specific differences, which are only starting to emerge, but are of clear clinical relevance.

What is unclear to me and needs to be addressed, is if these patient specimens were taken before or after initial therapy, whether the samples have been stratified according the treatment that they got, assuming it will be mostly platinum compounds (but maybe not), and that the p53 status of the tumors are (if genetics are available this would help to add some granularity to the study that, as as it stands is largely descriptive, even though with extremely high resolution. This data should be available and could be integrated.

Some minor issues

• I would stick to CD73, and not mix it with NT5E, which is confusing at first (Fig 2).
• I would ask to compare the overall survival of CD73+ between densities - is it still significantly different in fig 1 - meaning is it about density, CD73 expression, or both. Comparing survival of tumors with a low density of CD73+ gd T cells does not seem to be different from those having a low density of CD73- gd T cells, which could be considered in data interpretation. Same for high density tumors.
• figure 1, caption should include the word "patients" at the end, I guess.
• labelling and font can be improved in many panels, eg. the dot plots in Fig 2, panel B, right, same for panel C and D

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Reply to the reviewers

The authors do not wish to provide a response at this time

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Referee #2

Evidence, reproducibility and clarity

The authors describe a modified version of single molecule Fluorescence In-situ Hybridization (smFISH) method they have adapted to successfully measure RNA levels in isolated human donor T cells, that are very hard to grow on glass and have small amounts of cytoplasm relative to cell size, a challenge for all researchers working with small cells that only grow in suspension cultures. Using this methodology, the authors have queried transcription status and mRNA localization and fate of the two cytokines, IFNG and TNF, upon T-cell activation. The main findings of the study are: (1) activation of T-cells results in rapid accumulation of IFNG an TNF mRNA; there is differential distribution of the cytokine mRNAs between the nucleus and cytoplasm with greater accumulation in the cytoplasm as activation progresses resulting in increased protein production. There is significant transcriptional heterogeneity in response to T-cell activation. (2) The cytokine mRNA turnover appears to be controlled by translation. (3) HUR, an RBP appears to control poly(A) tail length of TNF mRNA in response to T-cell activation. The successful implementation of a modified smFISH protocol used in this study is a welcome resource for all labs that want to study small human primary cells that are difficult to culture on glass coverslips and grow as suspension cultures. Although the authors have very exciting observations, they have shied away from discussing their results in the context of the biology of T-cell activation and how their observations may explain prior studies on cytokine gene expression patterns during T-cell activation.

In my opinion, the authors should discuss their observations in depth from the context of T-cell activation and cytokine expression. I have enumerated several specific comments that may help the authors in revising the manuscript if they choose to do so.

Specific comments:

1. Based on the data presented in Figure 1 D and E, it is clear there is depletion of IFNG and TNF mRNA 4hrs after activation and then the mRNA levels go up at 6h in both cases. However, the authors suggest that only TNF mRNA is depleted at 4hrs of activation (lines 169-172). The median number of IFNG mRNA gradually decreases after 1h of activation and reaches a low at 4h and then substantially increases by 6h. Did the authors measure gene expression of these mRNAs at later time points in the activation process? Perhaps transcription is coupled to mature mRNA levels in the cytoplasm and transcription is ramped up again once the cytoplasmic mRNA levels reach a lower threshold. Is this just an anomaly of the system or is gene expression pattern of cytokines upon T-cell activation cyclical?
2. In data presented Figure 2 and Suppl Figure 2, the authors show correlation between dual cytokine expression and biallelic expression. However, not all dual cytokine expressing cells show bi-allelic expression of both cytokines. It will be useful to know what fraction of cells are biallelic for both genes. Since the experiment was done using two color smFISH, a scatter plot will cluster those dual expressor cells for both cytokines that are also bi-allelic for both genes. Extending this further would be to systematically address protein expression in the various combination of expression patterns. Combining smFISH with immunofluorescence will help address this. Overall, these results will be helpful in getting a better understanding of gene expression patterns during T-cell activation.
3. The mRNA localization data presented in Figure 3A and the associated supplemental figure: A better analysis and representation of the data presented in 3A would be a scatter plot of individual cells for their nuclear and cytoplasmic localization of mature mRNA. The authors might also want to extend this analysis based on the data presented in Figure 2 for dual expressors and bi-allelic expression. In other words, do cells with bi-allelic expression have more mRNA localized in the cytoplasm, and does this hold true in dual expressor cells? In the context of translation dependent decay of mRNA, do the dual expressor cells with biallelic expression fare better thereby producing and secreting cytokines continuously?
4. The data presented for IFNG in Figure 4 is quite intriguing. In HuR-KO cells at 2h post induction, two of the three donors cell lines have only a small fraction of cells producing protein compared to the controls, however, they are substantially higher than the KO cells at time "0". Surprisingly, the amount of protein produced by these cells (panel B), although statistically lower than the control, is substantially higher than KO cells at "0"h. Does the lone donor cell line with higher number of protein producing cells contribute to majority of the protein produced? There appears to be substantial difference between the three donor cell lines in the number of protein producing cells and mature IFNG mRNA after activation (Suppl Figure 1G & H). The authors may wish to compare the results before combining the data of all three donor cell lines before interpreting the data.
5. Also intriguing, HuR knock out results in a significant increase in transcription of IFNG at time "0" (Figure 4, panel E). Despite this, there is a significant loss in transcription of IFNG 2h post activation. However, there is significant accumulation of mature mRNA (panel D). Combined with the protein expression data presented in panels A & B, and the fact that translation induces mRNA decay, how do the authors reconcile this data?
6. The differential effect of HuR knock out on poly(A) tail length of IFNG and TNF mRNA is of great importance and the most striking finding in this study! It is generally accepted that poly(A) tail length contributes to mRNA stability and survival. The results presented in Figures 4 and 5 argue otherwise. Only a small fraction of TNF mRNA have full length poly(A) tails, however, the number of mature TNF mRNA in KO cells is much greater than the control even at "0"h. In addition, the TNF mRNA appear to be well translocated into the cytoplasm and effectively translated. Given these conflicting observations, what possible mechanism do the authors envision that can explain this result.<br /> Again, plotting the data presented in Figure 5A as a scatter plot between # of RNA in the cytosol vs nucleus will give a better picture of the localization changes in individual cells.
7. A more elaborate discussion of the results as it relates to the biology of cytokine gene expression during T-cell activation will immensely strengthen the manuscript.

Minor comment:

1. Images of cells with smFISH data (Figures 1, 3 & 4) must be bigger for better visualization. Show images with only a couple of cells enlarged to show the mRNA spots more visibly. Include images with more cells in the supplement instead.

Referee's cross-commenting

I must confess I am not an immunologist, so my knowledge of the intricacies of gene expression in T-cells in very limited. However, I do have a fair sense of transcription regulation and use single molecule approaches, especially smFISH, to address these questions. I agree with the other reviewer the study is of significance, especially the advancement in the ability to do smFISH in primary cells, a challenge that I know first hand. I also have to agree with the other reviewer that the discussion was too short and the authors shied away from the bigger picture of being able to comment on regulation of expression of cytokines during T-cell activation. It is remarkable that they see heterogeneity in gene expression of the individual target genes and bi-allelic expression. The other point of interest is the difference in p(A) tail length and its potential role in regulating TNF gene expression.

Significance

The successful implementation of a modified smFISH protocol used in this study is a welcome resource for all labs that want to study small human primary cells that are difficult to culture on glass coverslips and grow as suspension cultures.

Overall, this work is of high quality and can be better presented to fully explore and discuss the biological implications of the observations from the study. It is not clear to me if the authors wished to present this manuscript reporting an advancement in technology tool to study gene expression during T-cell activation, or a more in-depth study of gene expression.

The study will benefit the larger community that use single molecule approaches to understand genew expression.

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Referee #1

Evidence, reproducibility and clarity

The manuscript by Lattanzio and colleagues uses advanced single molecule FISH, adapted specifically for T cells, to examine RNA transcriptional dynamics in polyclonally stimulated human T cells. By examining the subcellular localisation of both IFNg and TNF mRNAs (nascent and mature), they are able to characterise rate things like rate of transcription and RNA stability. Key findings include the identification of bi-allelic vs mono-allelic transcription at the single cell level which maps to polyfucntion vs monofunctional T cells. Moreover, they identified distinct mechanisms regulating RNA stability and the role of RNA binding protein HuR in mediating that.

Overall, this is really a proof of concept paper that uses elegant technologies and analysis tools showing just how much information can be obtained from this approach. The ability to examine RNA dynamics and the imapct of RNA binding proteins in regulating RNA stability/translation/transriptoin at a single cell level will be an advance for the field, not just those interested in T cell biology but all cell types.

There are no specific experimental issues that came to mind that need to be addressed and it is really only some minor comments, particularly for the discussion that would strengthen the implicaitons of the study.

1. I might have missed it but it wasn't exactly clear from the results or from the methods exactly how nascent vs mature RNA was discriminated. Was this just from the subcellular localisation (i.e nuclear vs cytoplasmic)? RNA imaged close to the TSS? If so, this should be noted somewhere. If there was some other way of precisely ascribing RNA status, this should be outlined (use of primers that targeted intergenic sequences).
2. The discussion was very brief and would have benefited from a bit more speculation about the implications of their findings. Specifically, why would there be a need for different cytokine RNAs to be regulated in such distinct ways (IFNg vs IL-2)? Do the authors have any thoughts? Another point is the proposed explanations for the distinct T cell subsets observed that produce cytokines at different levels. While the authors propose three possible explanations, they are presented as being mutually exclusive, of course it could be a combination of all three. Moreover, putting the importance of higher functioning T cells (i.e those that produce more cytokines) into context is also important. Early studies from La Gruta et al., (J Immunol, 2004; doi: 10.4049/jimmunol.172.9.5553), Betts et al, (Blood, 2006 doi.org/10.1182/blood-2005-12-4818) and Darrah et al. (Nat Med, 2007 doi.org/10.1038/nm1592) linked higher cytokine production/multifunctionality to better immune outcomes, while Denton et al (PNAS, 2011, 10.1073/pnas.1112520108) linked the extent of cytokine production to cellular differentiation (and epigenetic landscape at the TNF and IFNg locus). These studies should be cited to provide a setting where this approach will be relevant.

A minor point relates to line 329, that sentence stating "Even though most activated Teff cells express cytokine mRNAs, they display a two order of magnitude difference in mRNA and protein expression."

It is not clear what this is relevant or compared to. A two order of magnitude difference compared to what?

Significance

This is a proof of concept study that demonstrates the utility of the T cell smFISH approach to delineate high resolution analysis of cytokine RNA dynamics at a single cell level, for multiple cytokine RNA species. It clearly provides interesting biology and further understanding of RNA dynamics in activated T cells. I especially appreciated the observation of bi-allelic vs mono-allelic transcription, and the ability to explore the role of RNA binding proteins in RNA regulation.

This technique will have broader applicability and hence will be of interest to those outside T cell immunology. It only requires some minor corrections/revisions.

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Reply to the reviewers

Reviewer #1 (Significance (Required)):

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This study aims to bridge a gap between the mechanisms of preeclampsia and neurodegenerative disorders, and this through the existence of misfolded proteins in the preeclamptic placenta which has been reported before, in particular the beta amyloid protein, known as operative in Alzheimer's disease (AD) in particular.

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Our response: We sincerely appreciated the reviewer’s constructive comments.

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

Minor remarks

1. It is classical now to present in extenso the WB as supplementary data for Fig 3, 4 and 5. Our response: We will include the full blots in Supplemental information.

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It seems that the beta amyloid signal is not stronger for the early onset and the late onset PE samples. Have the authors an interpretation?

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Our response: The current manuscript includes both early-onset and late-onset cases. Thus, we are certain that amyloid beta deposition is involved in both early- and late-onset PE. We will discuss this matter.

The figure 4b does not show the BeWo labeling in forskolin with or without beta amyloid peptides, why? It would be illustrative to show a decrease in the fusion processes

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Our response: In Fig. 4A, we pretreated BeWo cells with Aβ fibrils and after that, cell fusion was induced by Fsk. On the other hand, in Fig. 4b, we treated BeWo with Aβ fibrils and investigated the protein levels and subcellular localization of ZO-1 and E-cadherin. Fig.4b shows that expressions of proteins involved in cell-cell interaction were reduced by Aβ fibril treatment without Fsk. Cell-cell interaction before syncytialization is required for cell fusion, and these proteins disappear after cell fusion. Thus, our results demonstrate that elimination of cell-cell interaction by Aβ fibrils resulted in reduced cell fusion induced by Fsk. This is why we treated BeWo cells with Aβ fibrils before the induction of cell fusion by Fsk, and BeWo labeling in forskolin with or without Aβ fibrils will result in a loss of ZO-1 and E-cadherin regardless of the occurrence of cell fusion. We will discuss this matter in more detail.

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How do the authors explain that exposure to fibrils did not seem to slow down significantly the fusion process, even though markers are decreased?

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Our response: Since we previously demonstrated that loss of membrane E-cadherin slows the fusion (Iwahashi et al., Endocrinology, 2019, PMID: 30551188), we believe that reduction of membrane localization of E-cadherin also slows the fusion process. We will discuss this matter further.

• Could the authors attempt a labeling with the Di-8, an interesting quantitative marker of cell fusion (see ref PMID: 38019394).*

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Our response: We have shown that pretreatment of BeWo cells and human primary cytotrophoblasts (CTBs) inhibited induction of syncytin-1 and β-hCG. Syncytin-1 is a critical driver of syncytialization and formation of the syncytiotrophoblast layer, and β-hCG is one of the major products of syncytiotrophoblasts. Thus, induction of these proteins is widely used as syncytialization markers of trophoblasts. On the other hand, Di-8-ANEPPS is a potentiometric fluorescent dye that may be used assess cell fusion simply and economically. Although we understand the robustness of this method, we believe that the current data are sufficient to demonstrate that Aβ fibril pretreatment inhibited syncytialization of BeWo cells and CTBs.

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Reviewer #2 (Significance (Required)):

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Investigating the deposition of Aβ in the placenta could enhance our understanding of pregnancy complications such as PE, fetal growth restriction, and neurodevelopmental risks. However, further research on this topic is necessary.

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Our response: We sincerely appreciate the critical reading and constructive comments of the reviewer. We agree that further research on protein aggregation and the pathogenesis of preeclampsia is necessary. We will discuss this matter in the discussion.

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

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Major comments

• • If CTBs are treated with Aβ, and if it affects STB, what happens with EVT? Why didn't they check with EVT if the authors wanted to link with PE?*
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Our response: We thank the reviewer for the critical comment. We investigated Aβ generation by an EVT model cell, HTR8/SVneo cells. We found that HTR8/SVneo cells produced much less amount of Aβ compared to BeWo cells (unpublished). Gao et al. reported that Aβ aggregates induced autophagy in HTR8/SVneo cells and suggested that an excessive autophagy may be detrimental and be involved in the development of preeclampsia (Gao et al., J Mol Histol, 2024, PMID: 38777993). We will discuss this matter in the discussion.

On the other hand, we have already investigated the effects of Aβ monomers in EVTs, and discovered that even low levels of Aβ produced by EVTs promote EVT invasiveness and have a physiological function. Please see below. We will add these new data in the revised manuscript.

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• • Did the authors look for pathologies related to Aβ deposition on PE placentas?*
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Our response: We did not observe any pathologies near the Aβ deposition.

• • Line# 103, the IF images don't show that BACE1 is around HIF1. There are no merged images, and the results are over- or underestimated.*
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Our response: We agree with the reviewer. There is a time discrepancy between HIF activation and BACE1 induction. Our immunohistochemical analysis showed that PE placentas are in a chronic hypoxia condition and that BACE1 was increased in PE placentas. Our cell-based assay supports that HIF1α stabilization by Roxadustat increased BACE1 levels in BeWo cells. We will tone down the results section of the immunohistochemical analysis.

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• • What is the intended purpose of using Roxadustat? If it inhibits HIF1α, could you explain the reason behind the increased expression of HIF1α? Furthermore, is there evidence to support the efficacy of this compound?*
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Our response: Roxadustat inhibits the proline hydroxylation of HIF1α and thereby inhibits the ubiquitination and degradation of HIF1α via the ubiquitin proteasomal system. In this study, we used Roxadustat as a HIF1α stabilizer to investigate whether BACE1 levels are increased with hypoxia and HIF1. Our data showed that treatment of BeWo cells with Roxadustat increased HIF1α levels, supporting the efficacy of Roxadustat. We will include this information in the result section for clarity.

• • Is Aβ deposition very specific to PE, or can it also occur for other reasons during pregnancy?*
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Our response: To date, no report has been found showing Aβ deposition in placentas other than PE. The deposition of protein aggregates, including those of Aβ and transthyretin, has previously been reported in PE. However, the presence and role of these protein deposits in placentas under pathological conditions, in addition to PE, remains to be elucidated. Several stresses such as hypoxia and ER stress may lead to deposition of protein aggregates in the placenta. These points will be discussed in the discussion.

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• • BACE1 is expressed in Normal#2 and #3 but not in #1, #4, and #5. Why is this expressed in #2 and #3? Is there anything wrong with these samples? If patients had gestational hypertension or some other complications?*
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Our response: We did not find any other complications in the normal placentas. In the brain, Aβ is constitutively generated and thus, thought to play physiological roles. The amount of Aβ is determined by the balance between the production and the clearance. A sustained imbalance of Aβ production and Aβ clearance will lead Aβ aggregation and deposition. We found that BeWo cells expressed BACE1 in a normoxic condition and thus, normal placentas may express BACE1 and generate small amounts of Aβ. Our results suggested that chronic hypoxia in PE placentas resulted in increased BACE1 expression and increased Aβ production, which may eventually result in Aβ aggregation and deposition, because the aggregation process of Aβ is concentration-dependent. We will include this point in the revised manuscript.

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• • PE placentae were compared with GA matched placentae. What is the expression of BACE1 and RB4CD12 in term control placentae?*
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Our response: We used RB4CD12 as a protein aggregation marker. As shown in Table 1, the current study includes 3 placentas whose gestational ages are over 37 weeks. We did not observe RB4CD12 and Aβ deposition in gestational age-matched control and observed BACE1 expression in one 37 weeks gestational age control. We will include these points in the result section.

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• • If AB fibril deposition is hypoxia dependent, what happens at the early gestation, where oxygen conc is 1-2%?*
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Our response: At the early gestation, physiological hypoxia promotes the EVT invasion and helps the remodeling of spiral arteries for oxygen supply. Please see our response above. Severe hypoxia on the CTB side in early gestation may result in a miscarriage before PE develops.

Minor comments

• • The authors only performed IF and IHC. Please confirm and correct the methods accordingly.*
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Our response: We thank the reviewer for pointing this out. We will correct the methods.

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• • Was the BeWo-b21 clone cell line used for all the experiments in this paper? This is the only clone that can be used for BeWo-STB models.*
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Our response: We do not have information about the clone number of BeWo cells used in this study. We purchased them from the American Type Culture Collection (Manassas, VA) and they were authenticated by JCRB Cell Bank (National Institute of Biomedical Innovation Japan, report no. KBN0410). By using the same cells, we published three articles in which we successfully analyzed syncytialization of BeWo cells (Yamamoto et al., Endocrinology, 2017, PMID: 28938427; Iwahashi et al., Endocrinology, 2019, PMID: 30551188; Matsukawa et al., Biomolecules, 2022, PMID: 36008943). We would like to apologize for our mistake in the description of BeWo cells in the methods section and thank the reviewer for providing us with an opportunity to correct our mistake. We will note that BeWo cells were purchased from the American Type Culture Collection (Manassas, VA) and authenticated by JCRB Cell Bank (National Institute of Biomedical Innovation Japan, report no. KBN0410) in the methods section, and will upload the authentication report KBN0410 as a review process file.

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• • Have all the experiments on BeWo only been performed once?*
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Our response: We repeated 6 experiments (the repetitions are biological, not technical, replicates). The results are shown as means ± SEM (n = 6) as stated in the Figure legends.

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Reviewer #3 (Significance (Required)):

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While Aβ is present in human placentas and accumulates in preeclamptic placentas, the production and role of Aβ in the human placenta remain unclear. The current findings suggest that increased Aβ production in cytotrophoblast by hypoxia may lead to the formation of Aβ fibrils, which inhibit syncytiotrophoblast formation and are detrimental to pregnancy, revealing a novel role of Aβ fibrils in the pathogenesis of preeclampsia.

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

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The authors found that Amyloid β suppressed cytotrophoblasts syncytialization, which is innovative. The authors used human patient samples and human primary CTB culture which are powerful data.

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Our response: We appreciate the reviewer’s thoughtful feedback and support.

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Fig. 3. The authors used Roxadustat to stimulate HIF-1α and showed BACE1 increase. It would be better to have the cells in real hypoxia condition.

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Our response: There is a time discrepancy between the increase in HIF-1α levels by hypoxia and induction of BACE1. Because the purpose of this experiment is to show that increased HIF1-α correlated BACE1 induction, we used Roxadustat as a HIF1-α stabilizer and showed that sustained induction of HIF increased BACE1 levels. However, we do understand the reviewer’s concern. We will include data showing an increase in BACE1 in hypoxic conditions by performing new Western blotting experiments.

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Fig. 4 and 5. The authors used external Amyloid β for stimulation. Would the endogenous Amyloid β levels reach the concentration of external one? It would be better to see the quantitative levels of Amyloid β in Fig. 3b.

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Our response: Because the aggregation of Aβ requires a high concentration of a micromolar order, we used synthetic Aβ fibrils for stimulation. We propose that chronic hypoxia in preeclampsia leads to an elevated local concentration of Aβ through a sustained increase in Aβ production, which eventually results in Aβ fibrillogenesis and deposition of Aβ fibrils. Therefore, it will be difficult for the Aβ concentrations generated by BeWo cells to reach a level sufficient for fibrillogenesis. We will discuss this point in the revised manuscript. In addition, we have already performed ELISA assays to quantitatively analyze Aβ generation by BeWo cells. We will include these ELISA data in the revised manuscript.

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Reviewer #4 (Significance (Required)):

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The manuscript addresses an important theme recently identified to address the heterogeneous etiology of preeclampsia. Although the authors have used in vitro approaches, the study could have been a solid if not for some major concerns.

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The authors have focused on an already demonstrated phenomenon but have tried to validate the findings using their in vitro approaches. The manuscript is well written but some lapses for correct references.

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Our response: We thank the reviewer for the critical reading of our manuscript and his/her constructive comments. As the reviewer pointed out, recent studies suggest that preeclampsia is a proteinopathy. However, the mechanisms by which protein aggregate plays detrimental roles in placentation has not been well-understood. In the present study, we discovered a detrimental role of Aβ fibrils in syncytiotrophoblast formation.

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Reviewer #4 (Evidence, reproducibility and clarity (Required)):

Major comments:

1. • In lines 50 and 51 of Introduction, the authors provide references to two publications. However, several other articles have appeared before or after these publications that demonstrated evidence for proteinopathy in the placenta and circulation of preeclampsia patients. The reviewer has gone through the literature and found several publications. For example, Kalkunte et al were the first ones to demonstrate the etiology of proteinopathy in preeclampsia placenta and focused on a protein called transthyretin (Am J Pathol. 2013, 183(5):1425-1436). Similarly, Cheng et al demonstrated using a novel blood test that serum from early onset and late onset preeclampsia manifestations contained Aβ and transthyretin (Nature Sci Rep. 2021;11:15934). Jash et al showed the presence of cis P-tau in the placenta and serum of early and late onset preeclampsia patients (Nat Commun. 2023;14:5414). This article and another article by Cheng et al (Hypertension 79(8):1738-1754) revealed that aggregated cis P-tau and transthyretin are etiologically critical for the onset of preeclampsia. There have been several other review and original articles that have talked about Alzheimer's like etiology in preeclampsia (Olie et al, JAMA Netw Open, 2024; e2412870; Basit et al, BMJ 2018; 363:k4109; Schliep et al, Hypertension 2023; 80:257-267, Cheng et al, Am J Reprod Immunol. 2016;75:372-381).*
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Our response: We sincerely appreciate the reviewer for his/her helpful comment. We will revise the introduction by citing the references recommended by the reviewer.

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• Following up on the comments made above, the authors talk about induction of Aβ in hypoxia-treated human trophoblasts represented by an established cell line, BeWo, and primary human trophoblasts. However, it is not clear whether Aβ42 as stated in the manuscript was detected as an aggregated structure or a protein coupled with RB4CD12 aggregate marker. It would have been helpful if the authors could provide direct evidence for Aβ aggregation.*

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Our response: Based on our previous findings showing that highly sulfated domains of heparan sulfate are common components of protein aggregate deposits, we used RB4CD12, which recognizes these domains, as a marker of protein aggregate deposition. These include aggregates of Aβ in Alzheimer’s disease, transthyretin in ATTR, and p53 aggregates in p53-mutated cancers (Hoshono-fukao et al., Am J Pathol, 2012, PMID: 22429964; Kameyama et al., Am J Pathol, 2019, PMID: 30414409; Iwahashi, PNAS, 2020, PMID: 33318190). Please also see our reply to Comment 5 below. We will perform additional immunohistochemical analysis with the β0001 anti-Aβ antibody and the ProteoStat dye that recognizes protein aggregates.

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• What appeared to be more surprising is the statement on lines 162 and 163 that cultured CTBs produced Aβ40/42. Again, it is not clear whether the authors are talking about aggregated Aβ or just induction of Aβ. Why should normal CTBs produce Aβ? It is not clear whether this is a transient expression or a long-term phenomenon. The issue is distinction between normal and adverse pregnancy conditions, and the latter associated with protein aggregation as suggested in the literature.*

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Our response: BeWo cells and cultured CTBs produce Aβ peptides in a normoxic condition. In the brain, neurons constitutively produce Aβ peptides, which have physiological roles such as controlling neuronal hyperexcitability, enhancing of synaptic plasticity, and improving memory (reviewed in Kent et al., Acta Neuropathol, 2020, PMID: 32728795). The amount of Aβ in the brain is regulated by the balance between Aβ production and Aβ clearance, and the imbalance of the production and the clearance may result in an increase in Aβ local concentration and Aβ aggregation. Our results showing that hypoxia increased Aβ production in BeWo cells suggest that chronic hypoxia, which is a risk of preeclampsia, may lead to a sustained increase in Aβ production and an elevated local concentration of Aβ at or near the site of Aβ production. We will discuss these points in the discussion.

In the present study, we showed that aggregated form of Aβ (i.e., Aβ fibrils) was detrimental to the CTB differentiation. On the other hand, we already found that Aβ monomers promoted EVT invasion (please see the below). We believe that promotion of EVT invasion by Aβ monomers represent a physiological function of Aβ in the placenta. We will include these new data in the revised manuscript and we will also perform experiments with BeWo cells and Aβ monomers in order to investigate whether Aβ monomers have some roles in CTB differentiation.

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• The authors have adequately pointed to importance of hypoxia in the onset of preeclampsia-like features. As a matter of fact, Lai et al demonstrated in a mouse pre-clinical model that hypoxia could induce severe features of preeclampsia (Hypertension. 2011;57:505-514). The use of hypoxia as driver of Aβ induction is appreciated.*

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Our response: We agree with the reviewer that studies using preclinical animal models are an important topic for the future. __We will discuss this point in the discussion. __

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• In Fig. 1, although the authors have used DIC approach, it would have been helpful if they presented individual Aβ and RB4CD12 green and red channels, and a merged profile. For example, PE #4 sample does not appear to have much RB4CD12. Again, there is a question of aggregated or native protein structures. It is difficult to have a satisfactory statistical analysis. Did the authors look for Aβ in the anchoring villi region of the placenta?*

• *

Our response: We will show the green and red channel images individually. We have noticed that we detected Aβ deposition without RB4CD12 signals. Aβ is small peptides of 40 to 42 amino acid residues and is extracellularly released after the production. Non-deposited Aβ monomers are not detected by immunohistochemical analysis, because these soluble Aβ peptides are spread out in the tissue fluid. Thus, in our statistical analysis, we calculated only merged signals of Aβ and RB4CD12, which suggests that our data show the aggregated and deposited Aβ. We will note this point in the results. In addition, we will perform immunohistochemical analysis with the anti-Aβ antibody and the ProteoStat dye. Please also see our response to Comment 2 above. We did not observe Aβ deposition at the anchoring villi.

• *

• Fig. 2 does not show significant staining for HIF1-α in PE placental tissue.*

• *

Our response: In a normoxic condition, HIF1-α is constitutively expressed but degraded via the proline-hydroxylation and the subsequent ubiquitination and degradation in the proteasome. Because the proline-hydroxylation is oxygen-dependent, hypoxia induce HIF1-α accumulation. Thus, our data suggest a hypoxic environment in the preeclamptic placentas. We will note this point in the results section.

• *

• Fig. 3B, why should there be Aβ40/42 under normoxic conditions? This is the most pertinent concern and the authors are validating significant expression of Aβ40/42 under normal conditions. In normal pregnancy placenta, this protein has not been detected.*

• *

Our response: Aβ peptides are constitutively produced in BeWo cells, and the production was enhanced by hypoxia. Aβ is small peptides of 40 to 42 amino acid residues. We did not observe Aβ signals in the immunohistochemical analysis of the normal pregnancy placentas, because Aβ peptides that do not aggregate and deposit in the placenta were distributed in the tissue fluid and lost before and during the processing of the placentas for the paraffin-embedding and immunostaining. Our immunohistochemical analysis detects only Aβ deposition. Thus, the absence of Aβ signals in the immunohistochemical analysis of normal placentas does not mean that normal placenta does not produce any Aβ peptides.

• *

• Figs. 4 and 5 present the crux of the conclusions that the authors are trying to draw from their study. Aβ peptide solution was incubated for 5 days at 370C to prepare so called Aβ fibril-like structures. What is the purity of fibril structures? Does this preparation show toxic effects on cell viability? Human trophoblasts expressing E-cadherin fail to participate in endovascular cross-talk with endothelial cells, a process required for spiral arteries. It appears that either BeWo cells or primary trophoblasts used in this study represent trophoblasts from third trimester. It is not clear why should Aβ fibril like structures should inhibit ZO-1 and E-cadherin or β-hCG (Fig. 5) for that matter. In Fig. 5C, there does not seem to be a major effect of Aβ fibrils. Did the authors try synthetic Aβ as a control. These experiments could have been meaningful but for proper controls.*

• *

Our response: Synthetic Aβ was purchased from Peptide Institute (Osak, Japan). The purity is >95%. We will include the data sheet as a review process file. In case that the reviewer wants to know the fibril content of the preparation, we will calculate the fibril content by using Native PAGE followed by Western blotting. We did not observe any cytotoxicity of the preparation as shown in Supplemental Fig. S3.

We previously showed that membrane localization of cell-cell interaction proteins such as ZO-1 and E-cadherin in cytotrophoblasts is required for syncytialization (Iwahashi et al., Endocrinology, 2019, PMID: 30551188; Matsukawa et al., Biomolecules, 2022, PMID: 36008943). Because Aβ aggregates disrupt membrane localization of tight junction proteins partly by inducing excess autophagy (Marco et al., Neurosci Lett, 2006, PMID: 16644119; Chan et al., Exp Cell Res, 2012, PMID: 29856989), we hypothesized that Aβ fibrils may also disrupt membrane localization of ZO-1 and E-cadherin in BeWo cells. We are focusing on the effect of Aβ fibrils on cytotrophoblasts at the late stage of pregnancy when the remodeling of spiral arteries is completed. We understand the importance of investigating the effects of Aβ and Aβ fibrils on early pregnancy. We will cite an article showing the effects of Aβ aggregates on EVTs (Gao et al., J Mol Histol, 2024, PMID: 38777993) and include our data showing the Aβ monomer functions on EVT invasion. Please also see our reply to Comment 3 above. As for Fig. 5C, we will improve the quality of images. We will also perform experiments to investigate whether Aβ monomers alone affect syncytialization of BeWo cells.

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Referee #4

Evidence, reproducibility and clarity

This manuscript focuses on the role of amyloid β (Aβ) in hypoxia-exposed human trophoblasts. Recent reports in the literature have confirmed the presence Aβ and other proteins, including Tau, transthyretin, and TDP-43, in placental tissue derived from preeclampsia deliveries. These proteins are recognized as hallmark causative factors for Alzheimer's disease related dementias. Hypoxia has also been shown to induce expression of these proteins, including Aβ, in human trophoblasts. In this regard, detection of Aβ hypoxia-exposed human trophoblast may not be a novel finding. This said, the manuscript presents some solid information and could have been very informative study. However, several conceptual, technical and literature concerns remain unaddressed and dampen the reviewer's enthusiasm for this study.

Major comments:

1. In lines 50 and 51 of Introduction, the authors provide references to two publications. However, several other articles have appeared before or after these publications that demonstrated evidence for proteinopathy in the placenta and circulation of preeclampsia patients. The reviewer has gone through the literature and found several publications. For example, Kalkunte et al were the first ones to demonstrate the etiology of proteinopathy in preeclampsia placenta and focused on a protein called transthyretin (Am J Pathol. 2013, 183(5):1425-1436). Similarly, Cheng et al demonstrated using a novel blood test that serum from early onset and late onset preeclampsia manifestations contained Aβ and transthyretin (Nature Sci Rep. 2021;11:15934). Jash et al showed the presence of cis P-tau in the placenta and serum of early and late onset preeclampsia patients (Nat Commun. 2023;14:5414). This article and another article by Cheng et al (Hypertension 79(8):1738-1754) revealed that aggregated cis P-tau and transthyretin are etiologically critical for the onset of preeclampsia. There have been several other review and original articles that have talked about Alzheimer's like etiology in preeclampsia (Olie et al, JAMA Netw Open, 2024; e2412870; Basit et al, BMJ 2018; 363:k4109; Schliep et al, Hypertension 2023; 80:257-267, Cheng et al, Am J Reprod Immunol. 2016;75:372-381).
2. Following up on the comments made above, the authors talk about induction of Aβ in hypoxia-treated human trophoblasts represented by an established cell line, BeWo, and primary human trophoblasts. However, it is not clear whether Aβ42 as stated in the manuscript was detected as an aggregated structure or a protein coupled with RB4CD12 aggregate marker. It would have been helpful if the authors could provide direct evidence for Aβ aggregation.
3. What appeared to be more surprising is the statement on lines 162 and 163 that cultured CTBs produced Aβ40/42. Again, it is not clear whether the authors are talking about aggregated Aβ or just induction of Aβ. Why should normal CTBs produce Aβ? It is not clear whether this is a transient expression or a long-term phenomenon. The issue is distinction between normal and adverse pregnancy conditions, and the latter associated with protein aggregation as suggested in the literature.
4. The authors have adequately pointed to importance of hypoxia in the onset of preeclampsia-like features. As a matter of fact, Lai et al demonstrated in a mouse pre-clinical model that hypoxia could induce severe features of preeclampsia (Hypertension. 2011;57:505-514). The use of hypoxia as driver of Aβ induction is appreciated.
5. In Fig. 1, although the authors have used DIC approach, it would have been helpful if they presented individual Aβ and RB4CD12 green and red channels, and a merged profile. For example, PE #4 sample does not appear to have much RB4CD12. Again, there is a question of aggregated or native protein structures. It is difficult to have a satisfactory statistical analysis. Did the authors look for Aβ in the anchoring villi region of the placenta?
6. Fig. 2 does not show significant staining for HIF1-α in PE placental tissue.
7. Fig. 3B, why should there be Aβ40/42 under normoxic conditions? This is the most pertinent concern and the authors are validating significant expression of Aβ40/42 under normal conditions. In normal pregnancy placenta, this protein has not been detected.
8. Figs. 4 and 5 present the crux of the conclusions that the authors are trying to draw from their study. Aβ peptide solution was incubated for 5 days at 370C to prepare so called Aβ fibril-like structures. What is the purity of fibril structures? Does this preparation show toxic effects on cell viability? Human trophoblasts expressing E-cadherin fail to participate in endovascular cross-talk with endothelial cells, a process required for spiral arteries. It appears that either BeWo cells or primary trophoblasts used in this study represent trophoblasts from third trimester. It is not clear why should Aβ fibril like structures should inhibit ZO-1 and E-cadherin or β-hCG (Fig. 5) for that matter. In Fig. 5C, there does not seem to be a major effect of Aβ fibrils. Did the authors try synthetic Aβ as a control. These experiments could have been meaningful but for proper controls.

Significance

The manuscript addresses an important theme recently identified to address the heterogeneous etiology of preeclampsia. Although the authors have used in vitro approaches, the study could have been a solid if not for some major concerns.

The authors have focused on an already demonstrated phenomenon but have tried to validate the findings using their in vitro approaches. The manuscript is well written but some lapses for correct references.

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Referee #3

Evidence, reproducibility and clarity

The authors found that Amyloid β suppressed cytotrophoblasts syncytialization, which is innovative. The authors used human patient samples and human primary CTB culture which are powerful data.

Fig. 3. The authors used Roxadustat to stimulate HIF-1α and showed BACE1 increase. It would be better to have the cells in real hypoxia condition.

Fig. 4 and 5. The authors used external Amyloid β for stimulation. Would the endogenous Amyloid β levels reach the concentration of external one? It would be better to see the quantitative levels of Amyloid β in Fig. 3b.

Significance

While Aβ is present in human placentas and accumulates in preeclamptic placentas, the production and role of Aβ in the human placenta remain unclear. The current findings suggest that increased Aβ production in cytotrophoblast by hypoxia may lead to the formation of Aβ fibrils, which inhibit syncytiotrophoblast formation and are detrimental to pregnancy, revealing a novel role of Aβ fibrils in the pathogenesis of preeclampsia.

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Referee #2

Evidence, reproducibility and clarity

In this manuscript, the authors examine the deposition of amyloid-β (A β) peptides that accumulate in the brains of patients with Alzheimer's disease (AD). The authors demonstrated the expression of HIF-1 in the pre-eclamptic (PE) placental tissue using immunofluorescence (which is not novel), alongside the expression of BACE1. These experiments were also validated using BeWo and primary trophoblast cells cultured under hypoxia to mimic one of the characteristics of PE. However, this manuscript is quite preliminary, and many additional experiments are necessary to confirm the deposition of Aβ fibrils in PE. The authors treated CTB and observed the effects on STB, but in PE, the main cell lineage affected is extravillous trophoblast (EVT) cells, which invade the spiral artery. The defect in this invasion is one of the major causes of PE. Therefore, the authors should investigate the effect of hypoxia and Aβ deposition on EVT invasion. Overall, this work appears very incomplete, and further experiments are warranted.

Major comments

• If CTBs are treated with Aβ, and if it affects STB, what happens with EVT? Why didn't they check with EVT if the authors wanted to link with PE?
• Did the authors look for pathologies related to Aβ deposition on PE placentas?
• Line# 103, the IF images don't show that BACE1 is around HIF1. There are no merged images, and the results are over- or underestimated.
• What is the intended purpose of using Roxadustat? If it inhibits HIF1, could you explain the reason behind the increased expression of HIF1? Furthermore, is there evidence to support the efficacy of this compound?
• Is Aβ deposition very specific to PE, or can it also occur for other reasons during pregnancy?
• BACE1 is expressed in Normal#2 and #3 but not in #1, #4, and #5. Why is this expressed in #2 and #3? Is there anything wrong with these samples? If patients had gestational hypertension or some other complications?
• PE placentae were compared with GA matched placentae. What is the expression of BACE1 and RB4CD12 in term control placentae?
• If AB fibril deposition is hypoxia dependent, what happens at the early gestation, where oxygen conc is 1-2%?

Minor comments

• The authors only performed IF and IHC. Please confirm and correct the methods accordingly.
• Was the BeWo-b21 clone cell line used for all the experiments in this paper? This is the only clone that can be used for BeWo-STB models.
• Have all the experiments on BeWo only been performed once?

Significance

Investigating the deposition of Aβ in the placenta could enhance our understanding of pregnancy complications such as PE, fetal growth restriction, and neurodevelopmental risks. However, further research on this topic is necessary.

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Referee #1

Evidence, reproducibility and clarity

Proving that more Beta-amyloid are produced in preeclampsia, and that impacts negatively trophoblast cell fusion is interesting and provides a potential mechanism for interpreting some specific cases of preeclampsia. The authors analyzed the placenta from five control and five preeclamptic pregnancies (4 early onset et 1 late onset).

The authors show first by IHC that amyloid beta and aggregate markers are apparently exclusively detected in the PE samples, the same observation is done for detection of HIF1alpha and BACE1, the enzyme that is responsible for the generation of amyloid peptides from digestion of the APP membrane neuron protein. After having used placental samples, the authors moved to the BeWo cell model, where they could analyze specifically cell biology in the context of syncytialization. The authors inhibited HIF1a prolylation (thus stabilizing it even in normoxia), and this leaded to the increase of BACE1, of beta-amyloid molecules, as shown by WB analyses; the same result was obtained by exposure to hypoxia, while a BACE1 inhibitor had the opposite effect.

An interesting issue is the demonstration provided by the authors that in this model, syncytialization is decreased by Beta-amyloid fibrils, together with decreased hCG expression and decreased Syncytin-1. The authors also validate these results on primary human CTB from the third trimester.

Minor remarks

1. It is classical now to present in extenso the WB as supplementary data for Fig 3, 4 and 5.
2. It seems that the beta amyloid signal is not stronger for the early onset and the late onset PE samples. Have the authors an interpretation?
3. The figure 4b does not show the BeWo labeling in forskolin with or without beta amyloid peptides, why? It would be illustrative to show a decrease in the fusion processes
4. How do the authors explain that exposure to fibrils did not seem to slow down significantly the fusion process, even though markers are decreased?
5. Could the authors attempt a labeling with the Di-8, an interesting quantitative marker of cell fusion (see ref PMID: 38019394).

Significance

This study aims to bridge a gap between the mechanisms of preeclampsia and neurodegenerative disorders, and this through the existence of misfolded proteins in the preeclamptic placenta which has been reported before, in particular the beta amyloid protein, known as operative in Alzheimer's disease (AD) in particular.

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Reply to the reviewers

General Statement

*Our lab was totally destroyed on June 15th by an Iranian missile. All stocks, equipment and reagents were lost. While we performed many of the experiments requested by the reviewers, unfortunately some were never completed. We thank you for your understanding. *

We thank the three reviewers for their thoughtful comments and useful suggestions on how to improve our paper. Some of the reviewers claimed that the paper is “preliminary”. We would like to highlight that in our opinion “preliminary” has two possible meanings in this context: 1) the data does not yet support the claims that the authors wrote; 2) the story is short and should be extended. While we totally agree that type 1 “preliminary” should be addressed (and we have addressed that to the best of our abilities), type 2 “preliminary” is a matter of scope, the length of the paper/project and the publication home. We believe that this story, which has been led by an outstanding master’s student (and as such has had a limited timespan) is worthwhile of publication in its current scope.

2. Point-by-point description of the revisions

Reviewers’ comments are in BLUE while our responses are in BLACK.

Reviewer 1 Summary: This study reports a role for matrix metalloproteinases (MMPs) in the developmental pruning of gamma Kenyon cells (KCs) in the fruit fly Mushroom Body during larval-pupal metamorphosis. The authors show through gene expression studies that MMP genes are upregulated in late larval stages as part of the early program for this type of neuronal pruning. They show through cell-targeted RNAi studies of both secreted MMP-1 and membrane-anchored MMP-2, that both genes are required in glial cells and to a lesser extent within KCs.

Both MMPs have secreted and membrane-anchored isoforms and we did not assess whether the secreted/anchored isoforms are involved; e.g. see LaFever et al. 2017.

The authors show that MMP secreted from glial is required for normal levels of Mushroom Body developmental neuronal pruning. They mention that MMP genes have been identified in schizophrenic patient screens in patients, and that perhaps a comparable pruning mechanism could be involved in the loss of grey matter (loss of synapses) in patients. The authors propose that MMP levels may be a potential therapeutic marker in the future.

We thank the reviewer for his comments. We find it important to clarify that we do not think our work suggests that the MMPs levels may be a potential therapeutic marker without much additional work in the future. In the original text we added a claim from another paper suggesting MMPs as therapeutic target. However, due to the arising confusion, we decided to delete this statement from the text (original line 198). We also added a general disclaimer towards the end of the discussion regarding the genetic power of Drosophila but its limited implication into human health (new lines 276-278).

Major Comments: Overall, the work is of a reasonable standard, but very preliminary

Please see general note on two types of “preliminary” – we thank the reviewer for helping us substantiate our claims and strengthen our paper but we do not plan to significantly increase its scope.

The study lacks the substance to completely convince me of any of the results. There is SUBSTANTIAL work that needs to be done to make this publishable. There are a lot of writing mistakes; so many that I do not list them in detail here

We are not absolutely sure that we understand to which mistakes this reviewer is eluding. However, we carefully rewrote the manuscript, streamlined many of our claims and added many new and more recent references.

The references citations are fairly old, but I do not list update replacements here

Thanks – we added many newer and relevant citations.

The text is very brief, and the overall writing needs to include significantly more description and detail

We have included more descriptions and details, as will be elaborated later on, but – again - this is a short report and will remain as such.

This is evident in all aspects of the manuscript, but especially notable in the Methods and Figure Legends

Thanks for raising this comment, which was reverberated also by other reviewers – we have now included more details, with a particular focus on the genotypes (Table 2), that somehow were erroneously not included in the original submission, as well as more detailed figure legends.

None of the Figure Legends include full genotypes of any of the fly lines, and these full fly lines are also not included in the Methods. This is vital to compare the experimental lines to the controls

True – our apologies for this mistake, we now added the full genotypes in Table 2.

Major points are listed below:

1. Figure 2: It is important to note of the specific age of animals in these images when talking about the loss of genes in development. Are all the animals age-matched? High levels of synaptic pruning occur post-eclosion), and it is important to understand when these pruning defects occur. It is mentioned that that overlap for the gene expression data is upregulated during 6-18h APF is this when these images are taken? This is very important in the context of pruning as SCZ symptom presentation is very late relative to these early events.

We thank the reviewer for this comment which suggests we were not clear enough in our description. We do not claim to have generated an SCZ model and have clarified this better in the text (lines 275-278). Furthermore, axon pruning happens during pupal development, but in all the main figures in this manuscript we dissected young adult flies (3-5 days post eclosion) and show the remnants of unpruned axons (as we have done in numerous studies). To make sure that initial development occurred normally, we also include larval brains in the Figure S7. We now clarified the fact that we are imaging adult brains as a readout to investigate whether pruning occurred during metamorphosis or not (line 124-126).

1. Figure 2: In the figure legend, it is indicated that the arrows are unpruned axons, however in the controls these areas appear to be highly innervated. Further explanation is needed about the context of the arrows, as there are clear visual differences between these images and the controls, but they appear to have a more expansive phenotype than "unpruned axons". The data does not match the visual representation in comparison to the control.

We apologize for this confusion. Unfortunately, the driver which we use to label the γ-axons, R71G10-QF2, is not absolutely specific to the γ type KCs but also expressed (sometimes) in the ɑ/β KCs. As the ɑ/β axons are very stereotypic in shape and also express high levels of FasII (which we stain for), we can easily distinguish between the ɑ lobe and unpruned γ axons. To clarify this point, we now clearly demarcate all lobes in the control images and specifically the ɑ lobe in all panels. Additionally, we added new schemes in Figure 2A and 2O to better clarify the anatomy and experimental design.

1. Figure 2: There needs to be more descriptive definitions and clarifications to the defects labeled in panel K. This could be done in the figure legend, but it would be more useful to label the images provided. For example, if Mmp2 is a "mild pruning affect, put that in the pie chart somewhere, to help guide the description of the phenotype to what those confocal images look like.

We understand that the pie chart in Figure 2 was confusing and therefore simplified it in the current version (Fig. 2B and 2P). Also, thanks to this great point, we now include a new Figure S3 that includes examples for the ranking categories, which were now performed by two independent investigators in a blind manner.

Figure 3: The time points of the images of the Mushroom Body (MB) are vital to understanding the process and regulation of these genes.

Please see our comment to point #1 – unless specifically stated otherwise, all images are MBs of adult flies, as now clearly mentioned in the figure legends, in the text and in the Material and Methods section.

1. Figure 3D: Significant description of this graph needs to be added for clarity. What parameters separate each phenotypic defect? Labeling the images and showing images that belong in different groups would be very helpful and improve the paper significantly.

We now included a new Figure S3 (also see our response to comment #3).

1. Figure S1: Additional experiments would help answer the strength of the phenotype for the ALG-Gal 4 driver. The authors need to perform the rescue experiment. Use a MMP-2 null and then drive it back in the ALG-GAL4 to see if this is sufficient to rescue the neuron pruning. This also isolates the mechanisms to one subtype of glia.

These are excellent suggestions that are, unfortunately, not doable. To perform a rescue experiment, one would need a viable loss-of-function phenotype of an Mmp2 mutant. There is one published Mmp2 loss-of-function null allele which is lethal during pupal development (Page-McCaw et al, 2003). Our previous data, using tissue specific (ts)CRISPR, suggested the involvement of Mmp2 in neurons for their remodeling (Meltzer et al, 2019). We therefore independently generated an Mmp2 germline mutant using CRISPR (harboring an indel resulting in a premature stop codon and predicted to encode a truncated, 77 amino-acid long protein), now described in Fig. S5A (and in the Materials and Methods). This allele is, as expected, unfortunately also lethal. We attempted to overcome lethality by generating MARCM (mosaic) clones in neurons, but as expected, because Mmp2 is largely secreted, there was no pruning defect phenotype (Fig. S5B-C). Unfortunately, it is not yet possible to generate glial clones.

Figure 3 and 4: The other glial subtypes need to be analyze to make any conclusion about their involvement, as well as the involvement of the astrocytes. Running these exact same experiments on the cortex glial and ensheathing glia will provide essential insight into what glial subtype is involved. The presumed lack of phenotypes in these other glial subtypes will also strengthen the argument that the astrocytes are specifically involved in this process. These are vital experiments.

We currently limited our analysis (and conclusions) to astrocytes. Despite the fact that this experiment is beyond our initial scope, we obtained reagents and performed preliminary experiments (using the R77A03-Gal4 driver for cortex glia, and the R83E12-Gal4 for ensheathing glia). In both cases, we observed extremely mild pruning defects, not comparable to those with Repo- or Alrm-Gal4. In these preliminary experiments we lacked a proper control, and now, unfortunately, due to the loss of our lab, we are unable to complete these experiments in a reasonable amount of time.

1. Figure 4: Again, description of the phenotypes and examples of these would improve the quality of this figure substantially.

Absolutely agree – see our response to comment #3 (and Fig. S3).

1. Figure 5: An improvement on the quantifications of these phenotypes would strengthen the paper substantially. More detailed description of the phenotypes and how they related to the control would significantly improve the overall quality of the work.

Thanks again for highlighting that we neglected to include the full genotypes that are now added (Table 2). We also thank the reviewer for raising the point regarding quantification. First, we generated a new Fig. S3A-E to show examples of the ranking by two independent rankers. Second, ranking was performed by looking at TdTomato positive vertical axons that are outside of the ɑ lobe (high FasII) – this is now better explained in the materials and methods. Additionally, while we would love to have a better scoring, and automatic, system – and even published a semi-automated scoring algorithm in Alyagor et al. 2018 (Figure 3O in the Alyagor paper), because the driver also labels vertical axons (ɑ/β) and because unpruned γ axons often express FasII, this quantification method does not always work. What we have done in previous cases, as we have also done here, is to provide independent ranking by two investigators and compare their ranking (Fig. S3F-G). Finally, we are working with our AI hub to develop automatic scoring systems that will not require human ranking – however this is beyond the scope for this manuscript.

Minor Comments: 1. Figure 1A: I would suggest labeling the KC (gamma) and potentially one of the others (a/B, a'/B') to orient the reader to the differences between these two subsets of the KCs, and to emphasize which neurons are undergoing pruning and where the cell bodies are and where the axons project.

Thanks for the suggestions – we now better annotated the scheme in Figure 1A as well as additional schematics in Figure 2 and, finally, better annotations in selected panels. Specifically, the ɑ lobe is outlined in magenta throughout all relevant panels.

1. Figure 1C: This panel needs further labeling to explain the findings in the heat map. Labeling some of the genes that were found and where they were would be helpful. This could also be done in the figure legend, however without any further labeling or context the heatmap is confusing.

We apologize for the incomplete figure. We did not want to overload the figure with data, which is why we are showing only the important clusters and did not include gene names. To keep the figure simple, but at the same time provide the complete information, we now include the full data in Fig. S1 (that includes the original heatmap with all the dynamic clusters I-IX, and including all the gene names). For the full raw data, including non-dynamic clusters, the reader is referred to look in Supplemental excel file 1. We hope this provides the clarity that this reviewer rightfully asks for.

1. Figure 3B,C: The full genotypes need to be labeled. What is the exact genotype used for the control?

The full genotypes of all figure panels are now included in Table 2 in the Materials and Methods.

1. Figure S1: The stock number for the ALG-GAL4 is missing, there are multiple different drivers, therefore this could be helpful in understanding this phenotype, as some are better than others.

Indeed, Alrm-Gal4 comes on two chromosomes – we used BDSC #67032, which is on chromosome III and this is now clearly mentioned the Materials and Methods section.

1. Figures 3 and 4: Labeling needs to remain consistent; Figure 3 "Glia-Gal4", Figure 4 "glia-gal4".

Thanks, done.

Reviewer #1 (Significance (Required)):

General Assessment: An interesting study on MMP function during an unusual type of neural development (axon pruning). Most of the MMP function appears to be in glia, although the MMP role in this context in unclear. The MMP function in the neurons being pruned is unexpected and even less clear. The study is somewhat poorly described in terse language lacking essential information, which gives the overall impression of a preliminary report.

Advance: Glial MMP function has been described for neuronal clearance mechanisms following injury. The main advance here is to describe a similar function during normal development. Audience: Developmental neuroscientists, MMP biologists, possibly schizophrenia clinician researchers

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

Neuropsychiatric conditions are often influenced by genetic factors. Schizophrenia is a complex mental disorder characterised by a mixture of hallucinations, delusions and disorganised thinking that causes lifelong problems in daily life. GWAS have identified a number of genes associated with the risk of developing schizophrenia, although genetic predisposition alone is not sufficient and additional environmental factors are required. In the current manuscript, the authors aim to exploit the strength of the Drosophila system to explore a link between schizophrenia-associated genes and neuronal remodelling during development. They focus on the mushroom body in the adult brain, where pronounced neuronal remodelling occurs during metamorphosis. To assess the potential role of the genes identified by the GWAS, they performed a targeted RNAi-based screen. They focus on the role of metalloproteases and find that they are required in neurons and in glia for the pruning of mushroom body axons. The study starts with a selection of 32 genes, 29 of which are listed (a bit hidden) in materials and methods and the identification of the Drosophila orthologs. The expression patterns of these genes in Kenyon cells are presented in Figure 1 - but unfortunately no information is given on who is expressed when

We apologize for the confusion. We attempted to keep Figure 1 simple but this resulted in the absence of critical information, as the reviewer suggests. We now include a Figure S1 that includes the entire heatmap of the dynamically expressed clusters I-IX with all the gene names. Additionally, we now augmented the information in Table 1 to include the screen phenotypes. Finally, Supplemental excel file 1, also included in our original submission, includes all the data, and is now better referred to throughout the text.

In a next step, Kenyon cell specific RNAi knockdown experiments are shown that identify a pruning phenotype for several genes. They demonstrate that Mmp2 (and similarly Mmp1) is also required in glia. Although Mmp2 was identified by neuronal RNAi-based knockdown, double knockdown experiments led the authors conclude that its primary function is in glia. The study emphasises the use of the advanced genetic model to understand complex human diseases. However, the paper does not go far enough in making use of the excellent genetics available. Basically, the report is about the identification of a few hits in a small RNAi screen, which is fine in itself, but leaves many questions unanswered. Do mmp1/2 mutants have a phenotype?

This is a very important question that cannot be answered, unfortunately. There is one published Mmp2 loss of function null allele which is lethal during pupal development (Page-MaCaw et al, 2003). Our previous data, using tissue specific (ts)CRISPR, suggested the involvement of Mmp2 in neurons for their remodeling (Meltzer et al, 2019). We therefore independently generated an Mmp2 germline mutant using CRISPR (harboring an indel resulting in a premature stop codon and predicted to encode a truncated, 77 amino-acid long protein), now described in Fig. S5A (and in the Materials and Methods). This allele is, as expected, unfortunately also lethal. We attempted to overcome lethality by generating MARCM (mosaic) clones in neurons, but as expected, because Mmp2 is largely secreted, there was no pruning defect phenotype (Fig. S5B-C). Unfortunately, it is not yet possible to generate glial clones. Additionally, available Mmp1 mutants are, sadly, also homozygous lethal. That said, in our revised manuscript we now include data demonstrating that expression of a dominant negative variant of Mmp1 inhibits pruning (Fig. 3J-K). We strengthened the evidence regarding the reliability of Mmp1 RNAi using an antibody mix (Fig. S4), and for Mmp2 – we refer to a manuscript that tested its efficiency (Harmansa et al., 2023). Lastly, we added new data using an additional RNAi line targeting Mmp2 from the VDRC collection (Fig. 3L).

Can the phenotype be rescued?

Unfortunately, without a viable mutant LOF phenotype, a rescue experiment is impossible. Regardless, in an attempt to rescue the RNAi phenotype, we designed and generated an RNAi-resistant Mmp2 overexpression transgene. Unfortunately, due to the destruction of our lab – several days after we received this transgenic line from Bestgene – this experiment is not included in the revision.

Does TIMP expression lead to similar phenotypes?

This is an interesting question which we addressed in our experiments but did not include in the text. Unfortunately, overexpression of TIMP did not have any effect on MB development. We are adding this figure here as Reviewer Figure 1, but we think that adding this information to the paper will not improve it for several reasons. The lack of phenotype by overexpression of Timp can result from a technical issue such as low expression or mislocalization of the protein, or a biological issue such as more complicated involvement of TIMP or other MMP inhibitors.

What is the temporal requirement for Mmp1/2?

This is an excellent suggestion, not an easy experiment, but one that we initiated, using a temperature sensitive Gal80 to control the expression of the RNAi only during metamorphosis. However, to the unfortunate destruction of our lab, this experiment was never completed.

What are the target proteins of Mmp2?

This is the million-dollar question – but unfortunately is beyond the scope of this short report.

Is Mmp2 still required when astrocyte motility is blocked? What is the morphology of glia after Mmp1/2 knockdown?

Thank you for this wonderful suggestion. We initiated two types of experiments using sparse labeling techniques (both MARCM and SPARC) to identify the morphology of single astrocytes in WT vs. MMP KD. However, these are complicated crosses that were not completed prior to the destruction of our lab.

Reviewer #2 (Significance (Required)):

The strength of the study is to identify a pruning phenotype after RNAi-based knockdown. The limitations is that this study is very superficial, it is the beginning of a paper. The initial claim to use Drosophila because to its advanced genetics is not met. The results section is shorter than the discussion.

While we agree with much of the reviewer’s statement this also relates to our general comment about “preliminary” type 1 and type 2 – True, this could be the beginning of a big paper and it would definitely be a more comprehensive and deep story. Most of the papers from my lab are indeed a 5 year endeavor. However, this short report (which is now longer, more detailed, and includes additional experiments) is a result of the work of an outstanding master’s student who came up with the idea for the project entirely by herself. Thus – given the data that she has acquired, and the fact that my lab will not continue to study MMPs or schizophrenia, the question needs to be whether the data supports the claims and whether this is an advance of science worthwhile of publication in a respectable journal. Our clear and decisive opinion is that the answer to that question is yes.

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

In this work, Schuldiner and colleagues explore the role of Mmp1 and Mmp2 in neuronal remodeling in the mushroom body of Drosophila. Overall, this work is very interesting, but in its current form seems quite preliminary. The biggest limitation of the study is that single RNAi lines are used with no validation that the lines are working, despite the fact that Mmp antibodies are available as are endogenously tagged Mmp lines that could have been used to validate the genetic manipulations. Specific concerns are listed below.

We thank reviewer 3 for his generally positive assessment of our work and we now performed additional experiments to strengthen and validate the original RNAi findings – for specifics see our reply to the points below.

Major concerns 1) The scoring system for pruning of mushroom body neurons seems very variable, even in controls (where scoring can range from very mild to moderate), and it is very hard to assess from the images what one is looking at (rather than using our own judgment, we rely on the authors' words). It would be necessary to have better labeling and examples of what phenotypes are considered "mild", "severe", "wild type-like". It would also help to understand how phenotype assessment is guided by the overlap between the signals from TdTomato fluorescence and FasII stain.

We thank the reviewer for raising this point, that has also been highlighted by other reviewers in some form. First, we have generated Figure S3A-E to show examples of the ranking, which was now performed by two independent investigators. Second, ranking was performed by looking at TdTomato positive vertical axons that are outside of the αlobe (high FasII) – this is now better explained in the materials and methods. Additionally, while we would love to have a better scoring, and automatic, system – and even published a semi-automated scoring algorithm in Alyagor et al. 2018 (Figure 3O in the Alyagor paper), because the driver also labels vertical axons (ɑ/β) and because unpruned γ axons often express FasII, this quantification method does not always work. What we have done in previous cases, as we have also done here, is to provide independent ranking by two investigators and compare their ranking (Fig. S3F-G). Finally, we are working with our AI hub to develop automatic scoring systems that will not require human ranking – however this is beyond the scope for this manuscript.

2) The biggest limitations of the approach are that single RNAi lines are used to screen, with no accompanying validation of the tool (see above)

We agree. Unfortunately not all RNAis are “equal” and thus not all of them work. To support the RNAi data, we have better clarified previous experiments that demonstrate the importance of neuronal Mmp2 via tissue specific (ts) CRISPR (Meltzer, et al, 2019). Unfortunately, the Mmp2 null mutant that is available is lethal during pupal development (Page-MaCaw et al, 2003). We therefore independently generated an Mmp2 germline mutant using CRISPR (harboring an indel resulting in a premature stop codon and predicted to encode a truncated, 77 amino-acid long protein), now described in Fig. S5A (and in the Materials and Methods). This allele is, as expected, unfortunately also lethal. We attempted to overcome lethality by generating MARCM (mosaic) clones in neurons, but as expected, because Mmp2 is largely secreted, there was no pruning defect phenotype (Fig. S5B-C). Unfortunately, it is not yet possible to generate glial clones. Additionally, available Mmp1 mutants are, sadly, also homozygous lethal. That said, in our revised manuscript we now include data demonstrating that expression of a dominant negative variant of Mmp1 inhibits pruning (Fig. 3J-K). We strengthened the evidence regarding the reliability of Mmp1 RNAi using an antibody mix (Fig. S4), and for Mmp2 – we refer to a manuscript that tested its efficiency (Harmansa et al., 2023). Lastly, we added new data using an additional RNAi line targeting Mmp2 from the VDRC collection (Fig. 3L).

3) RNAi-based knockdown is used to infer epistatic information-this is not appropriate as epistasis experiments need to be done with null alleles to make firm conclusions. Additional concerns: ● Even with the same driver, knockdown efficiency for 2 different genes could be variable and dependent of the specific RNAi used. ● The comparison between drivers is even harder, as driver strength varies greatly. ● The knockdown efficiency drops with increasing numbers of RNAi used. ● The specific genotypes used for this experiment should be clarified, as it would be very important to ensure that the UAS dosage is equal across conditions.

We agree that RNAi is not optimal to assess epistasis. And indeed, we did not mean to claim epistasis relationship between Mmp1 and Mmp2, nor between neurons and glia. We now use better language to clarify this. To define epistatic relationships, the use of mutants would be required, unfortunately the use of nulls is not possible because they are lethal and secreted (thus not enabling mosaic analyses). We agree that increasing the number of RNAi lines is expected to reduce their efficiency – this is why it is even more significant when we see an increased defective phenotype in the double knockdown experiments. Finally, we totally agree about the genotype comment and apologize that it was erroneously omitted in the original submission– all of which have been now added (Table 2 in materials and methods).

4) To further deepen the rigor of this work, a few simple yet important things could have been done. First, it would be important to rule out that knocking down Mmps does not affect astrocyte numbers and health (could be assessed by counting numbers and observing their morphology). Also, the authors previously showed that astrocytes actively infiltrate the axon bundle prior to pruning to facilitate axon defasciculation and pruning (Marmor-Kollet et al., 2023). It would have provided an important insight to examine if astrocytes can infiltrate the axon bundle if Mmp2 and/or Mmp1 are knocked down.

Thank you for these wonderful suggestions. We embarked on a few experiments as detailed below, unfortunately these are complicated crosses that were not completed prior to the destruction of our lab. 1) We initiated two types of experiments using sparse labeling techniques (both MARCM and SPARC) to identify the morphology of single astrocytes in WT vs. MMP KD. 2) Testing astrocytic infiltrations requires three binary systems, we obtained and generated stocks required for these experiments, but these were prematurely terminated. 3) We initiated experiments to count the number of glial nuclei in the vicinity of the degenerating axonal lobe (at the onset of pruning). Preliminary experiments with a small n (3 controls, 4 Mmp1 RNAi, and 5 Mmp2 RNAi) suggest that the number of glial nuclei is not significantly different between these conditions.

Minor The introduction puts big emphasis on the role of glia, but then to narrows down candidate genes for the screen a γ-KCs transcriptional data set is used, and the initial screen is done via knockdown of those candidates in neurons (there is a disconnect between rationale and approach).

We totally agree with this reviewer which is why we now changed the paper to include both neuronal and glial loss-of-function screens. Figure 1 is now augmented with the glial data.

Rationale for looking into axon pruning and how that translates into insights about synaptic pruning defects in schizophrenia should be more clearly stated.

Indeed, our belief that synapse pruning and axon pruning share molecular mechanisms remains yet unproven. However, both are steps during neuronal remodeling, which has been previously implicated in schizophrenia. That said, we now added an additional disclaimer to acknowledge the limitation of our findings in the context of human disease and synapse elimination (lines 275-279).

Figure 1C: data visualization for this heat map should be improved. Parts of the data are faded, and the differences between gene clusters are unclear.

We apologize for the incomplete figure. We did not want to overload the figure with data, which is why we are showing only the important clusters and did not include gene names. To keep the figure simple, but at the same time provide the complete information, we now include the full data in Fig. S1 (that includes the original heatmap with all the dynamic clusters I-IX, and including all the gene names). For the full raw data, including non-dynamic clusters, the reader is referred to look in Supplemental excel file 1. We hope this provides the clarity that this reviewer rightfully asks for.

Reviewer #3 (Significance (Required)):

In this work, Schuldiner and colleagues explore the role of Mmp1 and Mmp2 in neuronal remodeling in the mushroom body of Drosophila. Overall, this work is very interesting, but in its current form seems quite preliminary. The biggest limitation of the study is that single RNAi lines are used with no validation that the lines are working, despite the fact that Mmp antibodies are available as are endogenously tagged Mmp lines that could have been used to validate the genetic manipulations.

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Referee #3

Evidence, reproducibility and clarity

In this work, Schuldiner and colleagues explore the role of Mmp1 and Mmp2 in neuronal remodeling in the mushroom body of Drosophila. Overall, this work is very interesting, but in its current form seems quite preliminary. The biggest limitation of the study is that single RNAi lines are used with no validation that the lines are working, despite the fact that Mmp antibodies are available as are endogenously tagged Mmp lines that could have been used to validate the genetic manipulations. Specific concerns are listed below.

Major concerns

1. The scoring system for pruning of mushroom body neurons seems very variable, even in controls (where scoring can range from very mild to moderate), and it is very hard to assess from the images what one is looking at (rather than using our own judgment, we rely on the authors' words). It would be necessary to have better labeling and examples of what phenotypes are considered "mild", "severe", "wild type-like". It would also help to understand how phenotype assessment is guided by the overlap between the signals from TdTomato fluorescence and FasII stain.
2. The biggest limitations of the approach are that single RNAi lines are used to screen, with no accompanying validation of the tool (see above)
3. RNAi-based knockdown is used to infer epistatic information-this is not appropriate as epistasis experiments need to be done with null alleles to make firm conclusions. Additional concerns:
   • Even with the same driver, knockdown efficiency for 2 different genes could be variable and dependent of the specific RNAi used.
   • The comparison between drivers is even harder, as driver strength varies greatly.
   • The knockdown efficiency drops with increasing numbers of RNAi used.
   • The specific genotypes used for this experiment should be clarified, as it would be very important to ensure that the UAS dosage is equal across conditions.
4. To further deepen the rigor of this work, a few simple yet important things could have been done. First, it would be important to rule out that knocking down Mmps does not affect astrocyte numbers and health (could be assessed by counting numbers and observing their morphology). Also, the authors previously showed that astrocytes actively infiltrate the axon bundle prior to pruning to facilitate axon defasciculation and pruning (Marmor-Kollet et al., 2023). It would have provided an important insight to examine if astrocytes can infiltrate the axon bundle if Mmp2 and/or Mmp1 are knocked down.

Minor

The introduction puts big emphasis on the role of glia, but then to narrows down candidate genes for the screen a γ-KCs transcriptional data set is used, and the initial screen is done via knockdown of those candidates in neurons (there is a disconnect between rationale and approach).

Rationale for looking into axon pruning and how that translates into insights about synaptic pruning defects in schizophrenia should be more clearly stated.

Figure 1C: data visualization for this heat map should be improved. Parts of the data are faded, and the differences between gene clusters are unclear.

Significance

In this work, Schuldiner and colleagues explore the role of Mmp1 and Mmp2 in neuronal remodeling in the mushroom body of Drosophila. Overall, this work is very interesting, but in its current form seems quite preliminary. The biggest limitation of the study is that single RNAi lines are used with no validation that the lines are working, despite the fact that Mmp antibodies are available as are endogenously tagged Mmp lines that could have been used to validate the genetic manipulations.

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Referee #2

Evidence, reproducibility and clarity

Neuropsychiatric conditions are often influenced by genetic factors. Schizophrenia is a complex mental disorder characterised by a mixture of hallucinations, delusions and disorganised thinking that causes lifelong problems in daily life. GWAS have identified a number of genes associated with the risk of developing schizophrenia, although genetic predisposition alone is not sufficient and additional environmental factors are required.

In the current manuscript, the authors aim to exploit the strength of the Drosophila system to explore a link between schizophrenia-associated genes and neuronal remodelling during development. They focus on the mushroom body in the adult brain, where pronounced neuronal remodelling occurs during metamorphosis. To assess the potential role of the genes identified by the GWAS, they performed a targeted RNAi-based screen. They focus on the role of metalloproteases and find that they are required in neurons and in glia for the pruning of mushroom body axons.

The study starts with a selection of 32 genes, 29 of which are listed (a bit hidden) in materials and methods and the identification of the Drosophila orthologs. The expression patterns of these genes in Kenyon cells are presented in Figure 1 - but unfortunately no information is given on who is expressed when. In a next step, Kenyon cell specific RNAi knockdown experiments are shown that identify a pruning phenotype for several genes. They demonstrate that Mmp2 (and similarly Mmp1) is also required in glia. Although Mmp2 was identified by neuronal RNAi-based knockdown, double knockdown experiments led the authors conclude that its primary function is in glia.

The study emphasises the use of the advanced genetic model to understand complex human diseases. However, the paper does not go far enough in making use of the excellent genetics available. Basically, the report is about the identification of a few hits in a small RNAi screen, which is fine in itself, but leaves many questions unanswered. Do mmp1/2 mutants have a phenotype? Can the phenotype be rescued? Does TIMP expression lead to similar phenotypes? What is the temporal requirement for Mmp1/2? What are the target proteins of Mmp2? Is Mmp2 still required when astrocyte motility is blocked? What is the morphology of glia after Mmp1/2 knockdown?

Significance

The strength of the study is to identify a pruning phenotype after RNAi-based knockdown. The limitations is that this study is very superficial, it is the beginning of a paper. The initial claim to use Drosophila because to its advanced genetics is not met. The results section is shorter than the discussion.

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Referee #1

Evidence, reproducibility and clarity

Summary:

This study reports a role for matrix metalloproteinases (MMPs) in the developmental pruning of gamma Kenyon cells (KCs) in the fruit fly Mushroom Body during larval-pupal metamorphosis. The authors show through gene expression studies that MMP genes are upregulated in late larval stages as part of the early program for this type of neuronal pruning. They show through cell-targeted RNAi studies of both secreted MMP-1 and membrane-anchored MMP-2, that both genes are required in glial cells and to a lesser extent within KCs. The authors show that MMP secreted from glial is required for normal levels of Mushroom Body developmental neuronal pruning. They mention that MMP genes have been identified in schizophrenic patient screens in patients, and that perhaps a comparable pruning mechanism could be involved in the loss of grey matter (loss of synapses) in patients. The authors propose that MMP levels may be a potential therapeutic marker in the future.

Major Comments:

Overall, the work is of a reasonable standard, but very preliminary. The study lacks the substance to completely convince me of any of the results. There is SUBSTANTIAL work that needs to be done to make this publishable. There are a lot of writing mistakes; so many that I do not list them in detail here. The references citations are fairly old, but I do not list update replacements here. The text is very brief, and the overall writing needs to include significantly more description and detail. This is evident in all aspects of the manuscript, but especially notable in the Methods and Figure Legends. None of the Figure Legends include full genotypes of any of the fly lines, and these full fly lines are also not included in the Methods. This is vital to compare the experimental lines to the controls. Major points are listed below:

1. Figure 2: It is important to note of the specific age of animals in these images when talking about the loss of genes in development. Are all the animals age-matched? High levels of synaptic pruning occur post-eclosion), and it is important to understand when these pruning defects occur. It is mentioned that that overlap for the gene expression data is upregulated during 6-18h APF is this when these images are taken? This is very important in the context of pruning as SCZ symptom presentation is very late relative to these early events.
2. Figure 2: In the figure legend, it is indicated that the arrows are unpruned axons, however in the controls these areas appear to be highly innervated. Further explanation is needed about the context of the arrows, as there are clear visual differences between these images and the controls, but they appear to have a more expansive phenotype than "unpruned axons". The data does not match the visual representation in comparison to the control.
3. Figure 2: There needs to be more descriptive definitions and clarifications to the defects labeled in panel K. This could be done in the figure legend, but it would be more useful to label the images provided. For example, if Mmp2 is a "mild pruning affect, put that in the pie chart somewhere, to help guide the description of the phenotype to what those confocal images look like.
4. Figure 3: The time points of the images of the Mushroom Body (MB) are vital to understanding the process and regulation of these genes.
5. Figure 3D: Significant description of this graph needs to be added for clarity. What parameters separate each phenotypic defect? Labeling the images and showing images that belong in different groups would be very helpful and improve the paper significantly.
6. Figure S1: Additional experiments would help answer the strength of the phenotype for the ALG-Gal 4 driver. The authors need to perform the rescue experiment. Use a MMP-2 null and then drive it back in the ALG-GAL4 to see if this is sufficient to rescue the neuron pruning. This also isolates the mechanisms to one subtype of glia.
7. Figure 3 and 4: The other glial subtypes need to be analyze to make any conclusion about their involvement, as well as the involvement of the astrocytes. Running these exact same experiments on the cortex glial and ensheathing glia will provide essential insight into what glial subtype is involved. The presumed lack of phenotypes in these other glial subtypes will also strengthen the argument that the astrocytes are specifically involved in this process. These are vital experiments.
8. Figure 4: Again, description of the phenotypes and examples of these would improve the quality of this figure substantially.
9. Figure 5: An improvement on the quantifications of these phenotypes would strengthen the paper substantially. More detailed description of the phenotypes and how they related to the control would significantly improve the overall quality of the work.

Minor Comments:

1. Figure 1A: I would suggest labeling the KC (gamma) and potentially one of the others (a/B, a'/B') to orient the reader to the differences between these two subsets of the KCs, and to emphasize which neurons are undergoing pruning and where the cell bodies are and where the axons project.
2. Figure 1C: This panel needs further labeling to explain the findings in the heat map. Labeling some of the genes that were found and where they were would be helpful. This could also be done in the figure legend, however without any further labeling or context the heatmap is confusing.
3. Figure 3B,C: The full genotypes need to be labeled. What is the exact genotype used for the control?
4. Figure S1: The stock number for the ALG-GAL4 is missing, there are multiple different drivers, therefore this could be helpful in understanding this phenotype, as some are better than others.
5. Figures 3 and 4: Labeling needs to remain consistent; Figure 3 "Glia-Gal4", Figure 4 "glia-gal4".

Significance

General Assessment: An interesting study on MMP function during an unusual type of neural development (axon pruning). Most of the MMP function appears to be in glia, although the MMP role in this context in unclear. The MMP function in the neurons being pruned is unexpected and even less clear. The study is somewhat poorly described in terse language lacking essential information, which gives the overall impression of a preliminary report.

Advance: Glial MMP function has been described for neuronal clearance mechanisms following injury. The main advance here is to describe a similar function during normal development.

Audience: Developmental neuroscientists, MMP biologists, possibly schizophrenia clinician researchers

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Reply to the reviewers

We thank the reviewers for providing us the opportunity to revise our manuscript titled “Identifying regulators of associative learning using a protein-labelling approach in C. elegans.” We appreciate the insightful feedback that we received to improve this work. In response, we have extensively revised the manuscript with the following changes: we have (1) clarified the criteria used for selecting candidate genes for behavioural testing, presenting additional data from ‘strong’ hits identified in multiple biological replicates (now testing 26 candidates, previously 17), (2) expanded our discussion of the functional relevance of validated hits, including providing new tissue-specific and neuron class-specific analyses, and (3) improved the presentation of our data, including visualising networks identified in the ‘learning proteome’, to better highlight the significance of our findings. We also substantially revised the text to indicate our attempts to address limitations related to background noise in the proteomic data and outlined potential refinements for future studies. All revisions are clearly marked in the manuscript in red font. A detailed, point-by-point response to each comment is provided below.

1. Point-by-point description of the revisions

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

Summary:

Rahmani et al., utilize the TurboID method to characterize the global proteome changes in the worm's nervous system induced by a salt-based associative learning paradigm. Altogether, Rahmani et al., uncover 706 proteins that are tagged by the TurboID method specifically in samples extracted from worms that underwent the memory inducing protocol. Next, the authors conduct a gene enrichment analysis that implicates specific molecular pathways in salt-associative learning, such as MAP-kinase and cAMP-mediated pathways. The authors then screen a representative group of the hits from the proteome analysis. The authors find that mutants of candidate genes from the MAP-kinase pathway, namely dlk-1 and uev-3, do not affect the performance in the learning paradigm. Instead multiple acetylcholine signaling mutants significantly affected the performance in the associative memory assay, e.g., acc-1, acc-3, gar-1, and lgc-46. Finally, the authors demonstrate that the acetylcholine signaling mutants did not exhibit a phenotype in similar but different conditioning paradigms, such as aversive salt-conditioning or appetitive odor conditioning, suggesting their effect is specific to appetitive salt conditioning.

Major comments:

1. The statistical approach and analysis of the behavior assay: The authors use a 2-way ANOVA test which assumes normal distribution of the data. However, the chemotaxis index used in the study is bounded between -1 and 1, which prevents values near the boundaries to be normally distributed.

Since most of the control data in this assay in this study is very close to 1, it strongly suggests that the CI data is not normally distributed and therefore 2-way ANOVA is expected to give skewed results.

I am aware this is a common mistake and I also anticipate that most conclusions will still hold also under a more fitting statistical test.

We appreciate the point raised by Reviewer 1 and understand the importance of performing the correct statistical tests.

The statistical tests used in this study were chosen since parametric tests, particularly ANOVA tests to assess differences between multiple groups, are commonly used to assess behaviour in the C. elegans learning and memory field. Below is a summary of the tests used by studies that perform similar behavioural tests cited in this work, as examples:

Table 1 | A summary for the statistical tests performed by similar studies for chemotaxis assay data. References (listed in the leftmost column) were observed to (A) use parametric tests only or (B) performed either a parametric or non-parametric test on each chemotaxis assay dataset depending on whether the data passed a normality test. Listings for ANOVA tests are in bold to demonstrate their common use in the C. elegans learning and memory field.

Reference

Parametric test/s used in the reference

Non-parametric test/s used in the reference

Beets et al., 2020

Two-way ANOVA

None

Hiroki & Iino 2022

One-way ANOVA

None

Hiroki et al., 2022

One-way ANOVA

None

Hukema et al., 2006

T-tests

None

Hukema et al., Learn. Mem. 2008

T-tests

None

Jang et al., 2019

ANOVA

None

Kitazono et al., 2017

Two-way ANOVA and t-tests

None

Lans et al., 2004

One-way ANOVA

None

Lim et al., 2018

Two-way ANOVA

Wilcoxon rank sum test adjusted with the Benjamini–Hochberg method

Lin et al., 2010

Two-way or three-way ANOVA

None

Nagashima et al., 2019

One-way ANOVA

None

Ohno et al., 2014

None

Sakai et al., 2017

One-way ANOVA or t-tests

None

Stein & Murphy 2014

Two-way ANOVA and t-tests

None

Tang et al., 2023

One-way ANOVA or t-tests

None

Tomioka et al., 2006

T tests

None

Watteyne et al., 2020

One-way ANOVA

Two-sided Kruskal–Wallis

We note Reviewer 1's concern that this may stem from a common mistake. As stated, Two-way ANOVA generally relies on normally distributed data. We used GraphPad Prism to perform the Shapiro-Wilk normality test on our chemotaxis assay data as it is generally appropriate for sample sizes Table 2 | Shapiro-Wilk normality test results for chemotaxis assay data in Figure S8C. Chemotaxis assay data was generated to assess salt associative learning capacity for wild-type (WT) versus lgc-46(-) mutant C. elegans. Three experimental groups were prepared for each C. elegans strain (naïve, high-salt control, and trained). From top-to-bottom, the data below displays the ‘W’ value, ‘P value’, a binary yes/no for whether the data passes the Shapiro-Wilk normality test, and a ‘P value summary’ (ns = non-significant). W values measure the similarity between a normal distribution and the chemotaxis assay data. Data is considered normal in the Shapiro-Wilk normality test when a W value is near 1.0 and the null hypothesis is not rejected (i.e., P value > 0.05).*

WT naïve

WT high-salt control

WT trained

lgc-46 naïve

lgc-46 high-salt control

lgc-46 trained

W

0.9196

0.9114

0.8926

0.8334

0.8151

0.8769

P value

0.5272

0.4758

0.3705

0.1475

0.1070

0.2954

Passed normality test (alpha=0.05)?

Yes

Yes

Yes

Yes

Yes

Yes

P value summary

ns

ns

ns

ns

ns

ns

The manuscript now includes the use of the Shapiro-Wilk normality test to assess chemotaxis assay data before using two-way ANOVA on page 51.

Nevertheless an appropriate statistical analysis should be performed. Since I assume the authors would wish to take into consideration both the different conditions and biological repeats, I can suggest two options:

• Using a Generalized linear mixed model, one can do with R software.

• Using a custom bootstrapping approach. We thank Reviewer 1 for suggesting these two options. We carefully considered both approaches and consulted with the in-house statistician at our institution (Dr Pawel Skuza, Flinders University) for expert advice to guide our decision. In summary:

• Generalised linear mixed models: Generalised linear mixed models (GLMMs) are generally most appropriate for nested/hierarchal data. However, our chemotaxis assay data does not exhibit such nesting. Each biological replicate (N) consists of three technical replicates, which are averaged to yield a single chemotaxis index per N. Our statistical comparisons are based solely on these averaged values across experimental groups, making GLMMs less applicable in this context.

• __Bootstrapping: __Based on advice from our statistician, while bootstrapping can be a powerful tool, its effectiveness is limited when applied to datasets with a low number of biological replicates (N). Bootstrapping relies on resampling existing data to simulate additional observations, which may artificially inflate statistical power and potentially suggest significance where the biological effect size is minimal or not meaningful. Increasing the number of biological replicates to accommodate bootstrapping could introduce additional variability and compromise the interpretability of the results. The total number of assays, especially controls, varies quite a bit between the tested mutants. For example compare the acc-1 experiment in Figure 4.A., and gap-1 or rho-1 in Figure S4.A and D. It is hard to know the exact N of the controls, but I assume that for example, lowering the wild type control of acc-1 to equivalent to gap-1 would have made it non significant. Perhaps the best approach would be to conduct a power analysis, to know what N should be acquired for all samples.

We thoroughly evaluated performing the power analysis: however, this is typically performed with the assumption that an N = 1 represents a singular individual/person. An N =1 in this study is one biological replicate that includes hundreds of worms, which is why it is not typically employed in our field for this type of behavioural test.

Considering these factors, we have opted to continue using a two-way ANOVA for our statistical analysis. This choice aligns with recent publications that employ similar experimental designs and data structures. Crucially, we have verified that our data meet the assumptions of normality, addressing key concerns regarding the suitability of parametric testing. We believe this approach is sufficiently rigorous to support our main conclusions. This rationale is now outlined on page 51.

To be fully transparent, our aim is to present differences between wild-type and mutant strains that are clearly visible in the graphical data, such that the choice of statistical test does not become a limiting factor in interpreting biological relevance. We hope this rationale is understandable, and we sincerely appreciate the reviewer’s comment and the opportunity to clarify our analytical approach.

We hope that Reviewer 1 will appreciate these considerations as sufficient justification to retain the statistical tests used in the original manuscript. Nevertheless, to constructively address this comment, we have performed the following revisions:

1. __Consistent number of biological replicates: __We performed additional biological replicates of the learning assay to confirm the behavioural phenotypes for the key candidates described (KIN-2 , F46H5.3, ACC-1, ACC-3, LGC-46). We chose N = 5 since most studies cited in this paper that perform similar behavioural tests do the same (see the table below). Table 3 | A summary for sample sizes generated by similar studies for chemotaxis assay data. References (listed in the leftmost column) were observed to the sample sizes (N) below corresponding to biological replicates of chemotaxis assay data. N values are in bold when the study uses N ≤ 5.

Reference

N used in the study for chemotaxis assay data

Beets et al., 2020

8

Hiroki & Iino 2022

5-8

Hiroki et al., 2022

6-7

Hukema et al., 2006

≥ 4

Hukema et al., Learn. Mem. 2008

≥ 4

Jang et al., 2019

≥ 4

Kitazono et al., 2017

≥ 4

Kauffman et al., 2010

≥ 3

Kauffman et al., J. Vis. Exp. 2011

≥ 3

Lans et al., 2004

2

Lim et al., 2018

2-4

Lin et al., 2010

≥ 4

Nagashima et al., 2019

≥ 7

Ohno et al., 2014

≥ 11

Sakai et al., 2017

≥ 4

Stein & Murphy 2014

3-5

Tang et al., 2023

≥ 9

Watteyne et al., 2020

≥ 10

__Grouped presentation of behavioural data: __We now present all behavioural data by grouping genotypes tested within the same biological replicate, including wild-type controls, rather than combining genotypes tested separately. This ensures that each graph displays data from genotypes sharing the same N, also an important consideration for performing parametric tests. Accordingly, we re-performed statistical analyses using this reduced Nfor relevant graphs. As anticipated, this rendered some comparisons non-significant. All statistical comparisons are clearly indicated on each graph. Improved clarity of figure legends: __We revised figure legends for __Figures 5, 6, S7, S8, & S9 to make clear how many biological replicates have been performed for each genotype by adding N numbers for each genotype in all figures.

The authors use the phrasing "a non-significant trend", I find such claims uninterpretable and should be avoided. Examples: Page 16. Line 7 and Page 18, line 16.

This is an important point. While we were not able to find the specific phrasing "a non-significant trend" from this comment in the original manuscript, we acknowledge that referring to a phenotype as both a trend and non-significant may confuse readers, which was originally stated in the manuscript in two locations.

The main text has been revised on pages 27 & 28 when describing comparisons between trained groups between two C. elegans lines, by removing mentions of trends and retaining descriptions of non-significance.

Neuron-specific analysis and rescue of mutants:

Throughout the study the authors avoid focusing on specific neurons. This is understandable as the authors aim at a systems biology approach, however, in my view this limits the impact of the study. I am aware that the proteome changes analyzed in this study were extracted from a pan neuronally expressed TurboID. Yet, neuron-specific changes may nevertheless be found. For example, running the protein lists from Table S2, in the Gene enrichment tool of wormbase, I found, across several biological replicates, enrichment for the NSM, CAN and RIG neurons. A more careful analysis may uncover specific neurons that take part in this associative memory paradigm. In addition, analysis of the overlap in expression of the final gene list in different neurons, comparing them, looking for overlap and connectivity, would also help to direct towards specific circuits.

This is an important and useful suggestion. We appreciate the benefit in exploring the data from this study from a neuron class-specific lens, in addition to the systems-level analyses already presented.

The WormBase gene enrichment tool is indeed valuable for broad transcriptomic analyses (the findings from utilising this tool are now on page 16); however, its use of Anatomy Ontology (AO) terms also contains annotations from more abundant non-neuronal tissues in the worm. To strengthen our analysis and complement the Wormbase tool, we also used the CeNGEN database as suggested by Reviewer 3 Major Comment 1 (Taylor et al., 2021), which uses single cell RNA-Seq data to profile gene expression across the C. elegans nervous system. We input our learning proteome data into CeNGEN as a systemic analysis, identifying neurons highly represented by the learning proteome (on pages 16-20). To do this, we specifically compared genes/proteins from high-salt control worms and trained worms to identify potential neurons that may be involved in this learning paradigm. Briefly, we found:

• WormBase gene enrichment tool: Enrichment for anatomy terms corresponding to specific interneurons (ADA, RIS, RIG), ventral nerve cord neurons, pharyngeal neurons (M1, M2, M5, I4), PVD sensory neurons, DD motor neurons, serotonergic NSM neurons, and CAN.
• CeNGEN analysis: Representation of neurons previously implicated in associative learning (e.g., AVK interneurons, RIS interneurons, salt-sensing neuron ASEL, CEP & ADE dopaminergic neurons, and AIB interneurons), as well as neurons not previously studied in this context (pharyngeal neurons I3 & I6, polymodal neuron IL1, motor neuron DA9, and interneuron DVC). Methods are detailed on pages 50 & 51. These data are summarised in the revised manuscript as Table S7 & Figure 4.

To further address the reviewer’s suggestion, we examined the overlap in expression patterns of the validated learning-associated genes acc-1, acc-3, lgc-46, kin-2, and F46H5.3 across the neuron classes above, using the CeNGEN database. This was done to explore potential neuron classes in which these regulators may act in to regulate learning. This analysis revealed both shared and distinct expression profiles, suggesting potential functional connectivity or co-regulation among subsets of neurons. To summarise, we found:

• All five learning regulators are expressed in RIM interneurons and DB motor neurons.
• KIN-2 and F46H5.3 share the same neuron expression profile and are present in many neurons, so they may play a general function within the nervous system to facilitate learning.
• ACC-3 is expressed in three sensory neuron classes (ASE, CEP, & IL1).
• In contrast, ACC-1 and LGC-46 are expressed in neuron classes (in brackets) implicated in gustatory or olfactory learning paradigms (AIB, AVK, NSM, RIG, & RIS) (Beets et al., 2012, Fadda et al., 2020, Wang et al., 2025, Zhou et al., 2023, Sato et al., 2021), neurons important for backward or forward locomotion (AVE, DA, DB, & VB) (Chalfie et al., 1985), and neuron classes for which their function is yet detailed in the literature (ADA, I4, M1, M2, & M5). These neurons form a potential neural circuit that may underlie this form of behavioural plasticity, which we now describe in the main text on pages 16-20 & 34-35 and summarise in Figure 4.

OPTIONAL: A rescue of the phenotype of the mutants by re-expression of the gene is missing, this makes sure to avoid false-positive results coming from background mutations. For example, a pan neuronal or endogenous promoter rescue would help the authors to substantiate their claims, this can be done for the most promising genes. The ideal experiment would be a neuron-specific rescue but this can be saved for future works.

We appreciate this suggestion and recognise its potential to strengthen our manuscript. In response, we made many attempts to generate pan-neuronal and endogenous promoter re-expression lines. However, we faced several technical issues in transgenic line generation, including poor survival following microinjection likely due to protein overexpression toxicity (e.g., C30G12.6, F46H5.3), and reduced animal viability for chemotaxis assays, potentially linked to transgene-related reproductive defects (e.g., ACC-1). As we have previously successfully generated dozens of transgenic lines in past work (e.g. Chew et al., Neuron 2018; Chew et al., Phil Trans B 2018; Gadenne/Chew et al., Life Science Alliance 2022), we believe the failure to produce most of these lines is not likely due to technical limitations. For transparency, these observations have been included in the discussion section of the manuscript on pages 39 & 40 as considerations for future troubleshooting.

Fortunately, we were able to generate a pan-neuronal promoter line for KIN-2 that has been tested and included in the revised manuscript. This new data is shown in Figure 5B __and described on __pages 23 & 24. Briefly, this shows that pan-neuronal expression of KIN-2 from the ce179 mutant allele is sufficient to reproduce the enhanced learning phenotype observed in kin-2(ce179) animals, confirming the role of KIN-2 in gustatory learning.

To address the potential involvement of background mutations (also indicated by Reviewer 4 under ‘cross-commenting’), we have also performed experiments with backcrossed versions of several mutants. These experiments aimed to confirm that salt associative learning phenotypes are due to the expected mutation. Namely, we assessed kin-2(ce179) mutants that had been backcrossed previously by another laboratory, as well as C30G12.6(-) and F46H5.3(-) animals backcrossed in this study. Although not all backcrossed mutants retained their original phenotype (i.e., C30G12.6) (Figure 6D, a newly added figure), we found that backcrossed versions of KIN-2 and F46H5.3 both robustly showed enhanced learning (Figures 5A & 6B). This is described in the text on pages 23-26.

__Minor comments: __

1. Lack of clarity regarding the validation of the biotin tagging of the proteome. The authors show in Figure 1 that they validated that the combination of the transgene and biotin allows them to find more biotin-tagged proteins. However there is significant biotin background also in control samples as is common for this method. The authors mention they validated biotin tagging of all their experiments, but it was unclear in the text whether they validated it in comparison to no-biotin controls, and checked for the fold change difference.

This is an important point: We validated our biotin tagging method prior to mass spectrometry by comparing ‘no biotin’ and ‘biotin’ groups. This is shown in Figure S1 in the revised manuscript, which includes a western blot comparing untreated and biotin treated animals that are non-transgenic or expressing TurboID. As expected, by comparing biotinylated protein signal for untreated and treated lanes within each line, biotin treatment increased the signal 1.30-fold for non-transgenic and 1.70-fold for TurboID C. elegans. This is described on __page 8 __of the revised manuscript.

To clarify, for mass spectrometry experiments, we tested a no-TurboID (non-transgenic) control, but did not perform a no-biotin control. We included the following four groups: (1) No-TurboID ‘control’ (2) No-TurboID ‘trained’, (3) pan-neuronal TurboID ‘control’ and (4) pan-neuronal TurboID ‘trained’, where trained versus control refers to whether ‘no salt’ was used as the conditioned stimulus or not, respectively (illustrated in Figure 1A). Due to the complexity of the learning assay (which involves multiple washes and handling steps, including a critical step where biotin is added during the conditioning period), and the need to collect sufficient numbers of worms for protein extraction (>3,000 worms per experimental group), adding ‘no-biotin’ controls would have doubled the number of experimental groups, which we considered unfeasible for practical reasons. This is explained on __pages 8 & 9 __of the revised manuscript.

Also, it was unclear which exact samples were tested per replicate. In Page 9, Lines 17-18: "For all replicates, we determined that biotinylated proteins could be observed ...", But in Page 8, Line 24 : "We then isolated proteins from ... worms per group for both 'control' and 'trained' groups,... some of which were probed via western blotting to confirm the presence of biotinylated proteins".

• Could the authors specify which samples were verified and clarify how?

Thank you for pointing out these unclear statements: We have clarified the experimental groups used for mass spectrometry experiments as detailed in the response above on pages 8 &____ 9. In addition, western blots corresponding to each biological replicate of mass spectrometry data described in the main text on page 10 and have been added to the revised manuscript (as Figure S3). These western blots compare biotinylation signal for proteins extracted from (1) No-TurboID ‘control’ (2) No-TurboID ‘trained’, (3) pan-neuronal TurboID ‘control’ and (4) pan-neuronal TurboID ‘trained’. These blots function to confirm that there were biotinylated proteins in TurboID samples, before enrichment by streptavidin-mediated pull-down for mass spectrometry.

OPTIONAL: include the fold changes of biotinylated proteins of all the ones that were tested. Similar to Figure 1.C.

This is an excellent suggestion. As recommended by the reviewer, we have included fold-changes for biotinylated protein levels between high-salt control and trained groups (on pages 9 & 10 for replicate #1 and in __Table S2 __for replicates #2-5). This was done by measuring protein levels in whole lanes for each experimental group per biological replicate within western blots (__Figure 1C __for replicate #1 and __Figure S3 __for replicates #2-5) of protein samples generated for mass spectrometry (N = 5).

Figure 2 does not add much to the reader, it can be summarized in the text, as the fraction of proteins enriched for specific cellular compartments.

• I would suggest to remove Figure 2 (originally written as figure 3) to text, or transfer it to the supplementry material.

As noted in cross-comment response to Reviewer 4, there were typos in the original figure references, we have corrected them above. Essentially, this comment is referring to Figure 2.

We appreciate this feedback from Reviewer 1. We agree that the original __Figure 2 __functions as a visual summary from analysis of the learning proteome at the subcellular compartment level. However, it also serves to highlight the following:

• Representation for neuron-specific GO terms is relatively low, but even this small percentage represents entire protein-protein networks that are biologically meaningful, but that are difficult to adequately describe in the main text.
• TurboID was expressed in neurons so this figure supports the relevance of the identified proteome to biological learning mechanisms.

• Many of these candidates could not be assessed by learning assay using single mutants since related mutations are lethal or substantially affect locomotion. These networks therefore highlight the benefit in using strategies like TurboID to study learning. We have chosen to retain this figure, moving it to the supplementary material as Figure S4 in the revised manuscript, as suggested.

• OPTIONAL- I would suggest the authors to mark in a pathway summary figure similar to Figure 3 (originally written as Figure 4) the results from the behavior assay of the genetic screen. This would allow the reader to better get the bigger picture and to connect to the systemic approach taken in Figures 2 and 3.

We think this is a fantastic suggestion and thank Reviewer 1 for this input. In the revised manuscript, we have added Figure 7, which summarises the tested candidates that displayed an effect on learning, mapped onto potential molecular pathways derived from networks in the learning proteome. This figure provides a visual framework linking the behavioural outcomes to the network context. This is described in the main text on pages 32-33.

Typo in Figure 3: the circle of PPM1: The blue right circle half is bigger than the left one.

We thank the Reviewer for noticing this, the node size for PPM-1.A has been corrected in what is now Figure 2 in the revised work.

Unclarity in the discussions. In the discussion Page 24, Line 14, the authors raise this question: "why are the proteins we identified not general learning regulators?. The phrasing and logic of the argumentation of the possible answers was hard to follow. - Can you clarify?

We appreciate this feedback in terms of unclarity, as we strive to explain the data as clearly and transparently as possible. Our goal in this paragraph was to discuss why some candidates were seen to only affect salt associative learning, as opposed to showing effects in multiple learning paradigms (i.e., which we were defining as a ‘general learning regulator’). We have adjusted the wording in several places in this paragraph now on pages 36 & 37 to address this comment. We hope the rephrased paragraph provides sufficient rationalisation for the discussion regarding our selection strategy used to isolate our protein list of potential learning regulators, and its potential limitations.

***Cross-Commenting** *

Firstly, we would like to express our appreciation for the opportunity for reviewers to cross-comment on feedback from other reviewers. We believe this is an excellent feature of the peer review process, and we are grateful to the reviewers for their thoughtful engagement and collaborative input.

I would like to thank Reviewer #4 for the great cross comment summary, I find it accurate and helpful.

I also would like to thank Reviewer #4 for spotting the typos in my minor comments, their page and figure numbers are the correct ones.

We have corrected these typos in the relevant comments, and have responded to them accordingly.

Small comment on common point 1 - My feeling is that it is challanging to do quantitative mass spectrometry, especially with TurboID. In general, the nature of MS data is that it hints towards a direction but a followup validation work is required in order to assess it. For example, I am not surprised that the fraction of repeats a hit appeared in does not predict well whether this hit would be validated behavioraly. Given these limitations, I find the authors' approach reasonable.

We thank Reviewer 1 for this positive and thoughtful feedback. We also appreciate Reviewer 4’s comment regarding quantitative mass spectrometry and have addressed this in detail below (see response to Reviewer 4). However, we agree with Reviewer 1 that there are practical challenges to performing quantitative mass spectrometry with TurboID, primarily due to the enrichment for biotinylated proteins that is a key feature of the sample preparation process.

Importantly, we whole-heartedly agree with Reviewer 1’s statement that “In general, the nature of MS data is that it hints towards a direction but a follow-up validation work is required in order to assess it”. This is the core of our approach: however, we appreciate that there are limitations to a qualitative ‘absent/present’ approach. We have addressed some of these limitations by clarifying the criteria used for selecting candidate genes, based additionally on the presence of the candidate in multiple biological replicates (categorised as ‘strong’ hits). Based on this method, we were able to validate the role of several novel learning regulators (Figures 5, 6, & S7). We sincerely hope that this manuscript can function as a direction for future research, as suggested by this Reviewer.

I also would like to highlight this major comment from reviewer 4:

"In Experimental Procedures, authors state that they excluded data in which naive or control groups showed average CI 0.5499 for N2 (page 36, lines 5-7). "

This threshold seems arbitrary to me too, and it requires the clarifications requested by reviewer 4.

As detailed in our response to Reviewer 4, Major Comment 2, data were excluded only in rare cases, specifically when N2 worms failed to show strong salt attraction prior to training, or when trained N2 worms did not exhibit the expected behavioural difference compared to untrained controls – this can largely be attributed to clear contamination or over-population issues, which are visible prior to assessing CTX plates and counting chemotaxis indices.

These criteria were initially established to provide an objective threshold for excluding biological replicates, particularly when planning to assay a large number of genetic mutants. However, after extensive testing across many replicates, we found that N2 worms (that were not starved, or not contaminated) consistently displayed the expected phenotype, rendering these thresholds unnecessary. We acknowledge that emphasizing these criteria may have been misleading, and have therefore removed them from page 50 in the revised manuscript to avoid confusion and ensure clarity.

Reviewer #1 (Significance (Required)):

This study does a great job to effectively utilize the TurboID technique to identify new pathways implicated in salt-associative learning in C. elegans. This technique was used in C. elegans before, but not in this context. The salt-associative memory induced proteome list is a valuable resource that will help future studies on associative memory in worms. Some of the implicated molecular pathways were found before to be involved in memory in worms like cAMP, as correctly referenced in the manuscript. The implication of the acetylcholine pathway is novel for C. elgeans, to the best of my knowledge. The finding that the uncovered genes are specifically required for salt associative memory and not for other memory assays is also interesting.

However overall I find the impact of this study limited. The premise of this work is to use the Turbo-ID method to conduct a systems analysis of the proteomic changes. The work starts by conducting network analysis and gene enrichment which fit a systemic approach. However, since the authors find that ~30% of the tested hits affect the phenotype, and since only 17/706 proteins were assessed, it is challenging to draw conclusive broad systemic claims. Alternatively, the authors could have focused on the positive hits, and understand them better, find the specific circuits where these genes act. This could have increased the impact of the work. Since neither of these two options are satisfied, I view this work as solid, but not wide in its impact and therefore estimate the audience of this study would be more specialized.

My expertise is in C. elegans behavior, genetics, and neuronal activity, programming and machine learning.

We thank the Reviewer for these comments and appreciate the recognition of the value of the proteomic dataset and the identification of novel molecular pathways, including the acetylcholine pathway, as well as the specificity of the uncovered genes to salt-associative memory.

Regarding the reviewer’s concern about the overall impact and scope of the study, we respectfully offer the following clarification. Our aim was to establish a systems-level approach for investigating learning-related proteomic changes using TurboID, and we acknowledge that only a subset of the identified proteins was experimentally tested (now 26/706 proteins in the revised manuscript). Although only five of the tested single gene mutants showed a robust learning phenotype in the revised work (after backcrossing, more stringent candidate selection, improved statistical analysis in addressing reviewer comments), our proteomic data provides us a unique opportunity to define these candidates within protein-protein networks (as illustrated in Figure 7). Importantly, our functional testing focused on single-gene mutants, which may not reveal phenotypes for genes that act redundantly (now mentioned on pages 28-30). This limitation is inherent to many genetic screens and highlights the value of our proteomic dataset, which enables the identification of broader protein-protein interaction networks and molecular pathways potentially involved in learning.

To support this systems-level perspective, we have added Figure 7, which visually integrates the tested candidates into molecular pathways derived from the learning proteome for learning regulators KIN-2 and F46H5.3. We also emphasise more explicitly in the text (on pages 32-33) the value of our approach by highlighting the functional protein networks that can be derived from our proteomics dataset.

We fully acknowledge that the use of TurboID across all neurons limits the resolution needed to pinpoint individual neuron contributions, and understand the benefit in further experiments to explore specific circuits. Many circuits required for salt sensing and salt-based learning are highly explored in the literature and defined explicitly (see Rahmani & Chew, 2021), so our intention was to complement the existing literature by exploring the protein-protein networks involved in learning, rather than on neuron-neuron connectivity. However, we recognise the benefit in integrating circuit-level analyses, given that our proteomic data suggests hundreds of candidates potentially involved in learning. While validating each of these candidates is beyond the scope of the current study, we have taken steps to suggest candidate neurons/circuits by incorporating tissue enrichment analyses and single-cell transcriptomic data (Table S7 & Figure 4). These additions highlight neuron classes of interest and suggest possible circuits relevant to learning.

We hope this clarification helps convey the intended scope and contribution of our study. We also believe that the revisions made in response to Reviewer 1’s feedback have strengthened the manuscript and enhanced its significance within the field.

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

__Summary: __

In this study by Rahmani in colleagues, the authors sought to define the "learning proteome" for a gustatory associative learning paradigm in C. elegans. Using a cytoplasmic TurboID expressed under the control of a pan-neuronal promoter, the authors labeled proteins during the training portion of the paradigm, followed by proteomics analysis. This approach revealed hundreds of proteins potentially involved in learning, which the authors describe using gene ontology and pathways analysis. The authors performed functional characterization of some of these genes for their requirement in learning using the same paradigm. They also compared the requirement for these genes across various learning paradigms, and found that most hits they characterized appear to be specifically required for the training paradigm used for generating the "learning proteome".

Major Comments:

1. The definition of a "hit" from the TurboID approach is does not appear stringent enough. According to the manuscript, a hit was defined as one unique peptide detected in a single biological replicate (out of 5), which could give rise to false positives. In figure S2, it is clear that there relatively little overlap between samples with regards to proteins detected between replicates, and while perhaps unintentional, presenting a single unique peptide appears to be an attempt to inflate the number of hits. Defining hits as present in more than one sample would be more rigorous. Changing the definition of hits would only require the time to re-list genes and change data presented in the manuscript accordingly. We thank Reviewer 2 for this valuable comment, and the following related suggestion. We agree with the statement that “Defining hits as present in more than one sample would be more rigorous”. Therefore, to address this comment, we have now separated candidates into two categories in Table 2 __in the revised manuscript: ‘__strong’ (present in 3 or more biological replicates) and ‘weak’ candidates (present in 2 or fewer biological replicates). However, we think these weaker candidates should still be included in the manuscript, considering we did observe relationships between these proteins and learning. For example, ACC-1, which influences salt associative learning in C. elegans, was detected in one replicate of mass spectrometry as a potential learning regulator (Figure S8A). We describe this classification in the main text on pages 21-22.

We also agree with Reviewer 2 that the overlap between individual candidate hits is low between biological replicates; the inclusion of Figure S2 __in the original manuscript serves to highlight this limitation. However, it is also important to consider that there is notable overlap for whole molecular pathways between biological replicates of mass spectrometry data as shown in __Figure 2 __in the revised manuscript (this consideration is now mentioned on __pages 13-14). We have included Figure 3 to illustrate representation for two metabolic processes across several biological replicates normally indispensable to animal health, as an example to provide additional visual aid for the overlap between replicates of mass spectrometry. We provide this figure (described on pages 13 & 15) to demonstrate the strength of our approach in that it can detect candidates not easily assessable by conventional forward or reverse genetic screens.

We also appreciate the opportunity to explain our approach. The criteria of “at least one unique peptide” was chosen based on a previous work for which we adapted for this manuscript (Prikas et al., 2020). It was not intended to inflate the number of hits but rather to ensure sensitivity in detecting low-abundance neuronal proteins. We have clarified this in our Methods (page 46).

The "hits" that the authors chose to functionally characterize do not seem like strong candidate hits based on the proteomics data that they generated. Indeed, most of the hits are present in a single, or at most 2, biological replicate. It is unclear as to why the strongest hits were not characterized, which if mutant strains are publicly available, would not be a difficult experiment to perform.

We thank the reviewer for this important suggestion. To address this, we have described two molecular pathways with multiple components that appear in more than one biological replicate of mass spectrometry data in Figure 3 (main text on page 13). In addition, we have included __Figures 6 & S7 __where 9 additional single mutants corresponding to candidates in three or more biological replicates of mass spectrometry were tested for salt associative learning. Briefly, we found the following (number of replicates that a protein was unique to TurboID trained animals is in brackets):

• Novel arginine kinase F46H5.3 (4 replicates) displays an effect in both salt associative learning and salt aversive learning in the same direction (Figures 6A, 6B, & S9A, pages 31-32 & 37-38).
• Worms with a mutation for armadillo-domain protein C30G12.6 (3 replicates) only displayed an enhanced learning phenotype when non-backcrossed, not backcrossed. This suggests the enhanced learning phenotype was caused by a background mutation (Figure 6, pages 24-25).
• We did not observe an effect on salt associative learning when assessing mutations for the ciliogenesis protein IFT-139 (5 replicates), guanyl nucleotide factors AEX-3 or TAG-52 (3 replicates), p38/MAPK pathway interactor FSN-1 (3 replicates), IGCAM/RIG-4 (3 replicates), and acetylcholine components ACR-2 (4 replicates) and ELP-1 (3 replicates) (Figure S7, on pages 27-30). However, we note throughout the section for which these candidates are described that only single gene mutants were tested, meaning that genes that function in redundant or compensatory pathways may not exhibit a detectable phenotype. Because of the lack of strong evidence that these are indeed proteins regulated in the context of learning based on proteomics, including evidence of changes in the proteins (by imaging expression changes of fluorescent reporters or a biochemical approach), would increase confidence that these hits are genuine.

We thank Reviewer 2 for this suggestion – we agree that it would have been ideal to have additional evidence suggesting that changes in candidate protein levels are associated directly with learning. Ideally, we would have explored this aspect further; however, as outlined in response to Reviewer 1 Major Comment 2 (OPTIONAL), this was not feasible within the scope of the current study due to several practical challenges. Specifically, we attempted to generate pan-neuronal and endogenous promoter rescue lines for several candidates, but encountered significant challenges, including poor survival post-microinjection (likely due to protein overexpression toxicity) and reduced viability for behavioural assays, potentially linked to transgene-related reproductive defects. This information is now described on pages 39 & 40 of the revised work.

To address these limitations, we performed additional behavioural experiments where possible. We successfully generated a pan-neuronal promoter line for kin-2, which was tested and included in the revised manuscript (Figure 5B, pages 30 & 31). In addition, to confirm that observed learning phenotypes were due to the expected mutations and not background effects, we conducted experiments using backcrossed versions of several mutant lines as suggested by Reviewer 4 Cross Comment 3 (Figure 6, pages 23-24 & 24-26). Briefly, this shows that pan-neuronal expression of KIN-2 from the ce179 mutant allele is sufficient to repeat the enhanced learning phenotype observed in backcrossed kin-2(ce179) animals, providing additional evidence that the identified hits are required for learning. We also confirmed that F46H5.3 modulates salt associative learning, given both non-backcrossed and backcrossed F46H5.3(-) mutants display a learning enhancement phenotype. The revised text now describes this data on the page numbers mentioned above.

Minor Comments:

1. The authors highlight that the proteins they discover seem to function uniquely in their gustatory associative paradigm, but this is not completely accurate. kin-2, which they characterize in figure 4, is required for positive butanone association (the authors even say as much in the manuscript) in Stein and Murphy, 2014. We appreciate this correction and thank the Reviewer for pointing this out. We have amended the wording appropriately on page 31 to clarify our meaning.

2. “Although kin-2(ce179) mutants were not shown to impact salt aversive learning, they have been reported previously to display impaired intermediate-term memory (but intact learning and short-term memory) for butanone appetitive learning (Stein and Murphy, 2014).”*

Reviewer #2 (Significance (Required)):

• General Assessment: The approach used in this study is interesting and has the potential to further our knowledge about the molecular mechanisms of associative behaviors. Strengths of the study include the design with carefully thought out controls, and the premise of combining their proteomics with behavioral analysis to better understand the biological significance of their proteomics findings. However, the criteria for defining hits and prioritization of hits for behavioral characterizations were major wweaknesses of the paper.
• Advance: There have been multiple transcriptomic studies in the worm looking at gene expression changes in the context of behavioral training (Lakhina et al., 2015, Freytag 2017). This study compliments and extends those studies, by examining how the proteome changes in a different training paradigm. This approach here could be employed for multiple different training paradigms, presenting a new technical advance for the field.
• Audience: This paper would be of interest to the broader field of behavioral and molecular neuroscience. Though it uses an invertebrate system, many findings in the worm regarding learning and memory translate to higher organisms.
• I am an expert in molecular and behavioral neuroscience in both vertebrate and invertebrate models, with experience in genetics and genomics approaches. We appreciate Reviewer 2’s thoughtful assessment and constructive feedback. In response to concerns regarding definition and prioritisation of hits, we have revised our approach as detailed above to place more consideration on ‘strong’ hits present in multiple biological replicates. We have also added new behavioural data for additional mutants that fall into this category (Figures 6 & S7). We hope these revisions strengthen our study and enhance its relevance to the behavioural/molecular neuroscience community.

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

__Summary: __

In the manuscript titled "Identifying regulators of associative learning using a protein-labelling approach in C. elegans" the authors attempted to generate a snapshot of the proteomic changes that happen in the C. elegans nervous system during learning and memory formation. They employed the TurboID-based protein labeling method to identify the proteins that are uniquely found in samples that underwent training to associate no-salt with food, and consequently exhibited lower attraction to high salt in a chemotaxis assay. Using this system they obtained a list of target proteins that included proteins represented in molecular pathways previously implicated in associative learning. The authors then further validated some of the hits from the assay by testing single gene mutants for effects on learning and memory formation.

Major Comments:

In the discussion section, the authors comment on the sources of "background noise" in their data and ways to improve the specificity. They provide some analysis on this aspect in Supplementary figure S2. However, a better visualization of non-specificity in the sample could be a GO analysis of tissue-specificity, and presented as a pie chart as in Figure 2A. Non-neuronal proteins such as MYO-2 or MYO-3 repeatedly show up on the "TurboID trained" lists in several biological replicates (Tables S2 and S3). If a major fraction of the proteins after subtraction of control lists are non-specific, that increases the likelihood that the "hits" observed are by chance. This analysis should be presented in one of the main figures as it is essential for the reader to gauge the reliability of the experiment.

We agree with this assessment and thank Reviewer 3 for this constructive suggestion. In response, we have now incorporated a comprehensive tissue-specific analysis of the learning proteome in the revised manuscript. Using the single neuron RNA-Seq database CeNGEN, we identified the proportion of neuronal vs non-neuronal proteins from each biological replicate of mass spectrometry data. Specifically, we present Table 1 __on page 17 (which we originally intended to include in the manuscript, but inadvertently left out), which shows that 87-95% (i.e. a large majority) of proteins identified across replicates corresponded to genes detected in neurons, supporting that the TurboID enzyme was able to target the neuronal proteome as expected. __Table 1 is now described in the main text of the revised work on page 16.

In addition, we performed neuron-specific analyses using both the WormBase gene enrichment tool and the CeNGEN single-cell transcriptomic database, which we describe in detail on our response to Reviewer 1 Major Comment 2. To summarise, these analyses revealed enrichment of several neuron classes, including those previously implicated in associative learning (e.g., ASEL, AIB, RIS, AVK) as well as neurons not previously studied in this context (e.g., IL1, DA9, DVC) (summarised in Table S7). By examining expression overlap across neuron types, we identified shared and distinct profiles that suggest potential functional connectivity and candidate circuits underlying behavioural plasticity (Figure 4). Taken together, these data show that the proteins identified in our dataset are (1) neuronal and (2) expressed in neurons that are known to be required for learning. Methods are detailed on pages 50-51.

Other than the above, the authors have provided sufficient details in their experimental and analysis procedures. They have performed appropriate controls, and their data has sufficient biological and technical replaictes for statistical analysis.

We appreciate this positive feedback and thank the Reviewer for acknowledging the clarity of our experimental and analysis procedures.

Minor Comments:

There is an error in the first paragraph of the discussion, in the sentences discussing the learning effects in gar-1 mutant worms. The sentences in lines 12-16 on page 22 says that gar-1 mutants have improved salt-associative learning and defective salt-aversive learning, while in fact the data and figures state the opposite.

We appreciate the Reviewer noting this discrepancy. As clarified in our response to Reviewer 1, Major Comment 1 above, we reanalysed the behavioural data to ensure consistency across genotypes by comparing only those tested within the same biological replicates (thus having the same N for all genotypes). Upon this reanalysis, we found that the previously reported phenotype for gar-1 mutants in salt-associative learning was not statistically different from wild-type controls. Therefore, we have removed references to GAR-1 from the manuscript.

__Reviewer #3 (Significance (Required)): __Strengths and limitations: This study used neuron-specific TurboID expression with transient biotin exposure to capture a temporally restricted snapshot of the C. elegans nervous system proteome during salt-associative learning. This is an elegant method to identify proteins temporally specific to a certain condition. However, there are several limitations in the way the experiments and analyses were performed which affect the reliability of the data. As the authors themselves have noted in the discussion, background noise is a major issue and several steps could be taken to improve the noise at the experimental or analysis steps (use of integrated C. elegans lines to ensure uniformity of samples, flow cytometry to isolate neurons, quantitative mass spec to detect fold change vs. strict presence/absence). Advance: Several studies have demonstrated the use of proximity labeling to map the interactome by using a bait protein fusion. In fact, expressing TurboID not fused to a bait protein is often used as a negative control in proximity labeling experiments. However, this study demonstrates the use of free TurboID molecules to acquire a global snapshot of the proteome under a given condition. Audience: Even with the significant limitations, this study is specifically of interest to researchers interested in understanding learning and memory formation. Broadly, the methods used in this study could be modified to gain insights into the proteomic profiles at other transient developmental stages. The reviewer's field of expertise: Cell biology of C. elegans neurons.

We thank the reviewer for their thoughtful evaluation of our work. We appreciate the recognition of the novelty and potential of using neuron-specific TurboID to capture a temporally restricted snapshot of the C. elegans nervous system proteome during learning. We agree that this approach offers a unique opportunity to identify proteins associated with specific behavioural states in future studies.

We also appreciate the reviewer’s comments regarding limitations in experimental and analytical design. In revising the manuscript, we have taken several steps to address these concerns and improve the clarity, rigour, and interpretability of our data. Specifically:

• We now provide a frequency-based representation of proteomic hits (Table 2), which helps clarify how candidate proteins were selected and highlights differences between trained and control groups.
• We have added neuron-specific enrichment analyses using both WormBase and CenGEN databases (Table S7 & Figure 4), which help identify candidate neurons and potential circuits involved in learning (methods on pages 50-51).
• We have clarified the rationale for using qualitative proteomics in the context of TurboID, in addition to acknowledging the challenges of integrating quantitative mass spectrometry with biotin-based enrichment (page 39). Additional methods for improving sample purity, such as using integrated lines or FACS-enrichment of neurons, could further refine this approach in future studies. For transparency, we did attempt to integrate the TurboID transgenic line to improve the strength and consistency of biotinylation signals. However, despite four rounds of backcrossing, this line exhibited unexpected phenotypes, including a failure to respond reliably to the established training protocol. As a result, we were unable to include it in the current study. Nonetheless, we believe our current approach provides a valuable proof-of-concept and lays the groundwork for future refinement. By addressing the major concerns of peer reviewers, we believe our study makes a significant and impactful contribution by demonstrating the feasibility of using TurboID to capture learning-induced proteomic changes in the nervous system. The identification of novel learning-related mutants, including those involved in acetylcholine signalling and cAMP pathways, provides new directions for future research into the molecular and circuit-level mechanisms of behavioural plasticity.

Reviewer #4 (Evidence, reproducibility and clarity (Required)):

Summary:

In this manuscript, authors used a learning paradigm in C. elegans; when worms were fed in a saltless plate, its chemotaxis to salt is greatly reduced. To identify learning-related proteins, authors employed nervous system-specific transcriptome analysis to compare whole proteins in neurons between high-salt-fed animals and saltless-fed animals. Authors identified "learning-specific genes" which are observed only after saltless feeding. They categorized these proteins by GO analyses and pathway analyses, and further stepped forward to test mutants in selected genes identified by the proteome analysis. They find several mutants that are defective or hyper-proficient for learning, including acc-1/3 and lgc-46 acetylcholine receptors, gar-1 acetylcholine receptor GPCR, glna-3 glutaminase involved in glutamate biosynthesis, and kin-2, a cAMP pathway gene. These mutants were not previously reported to have abnormality in the learning paradigm.

Major comments:

1) There are problems in the data processing and presentation of the proteomics data in the current manuscript which deteriorates the utility of the data. First, as the authors discuss (page 24, lines 5-12), the current approach does not consider amount of the peptides. Authors state that their current approach is "conservative", because some of the proteins may be present in both control and learned samples but in different amounts. This reviewer has a concern in the opposite way: some of the identified proteins may be pseudo-positive artifacts caused by the analytical noise. The problem is that authors included peptides that are "present" in "TurboID, trained" sample but "absent" in the "Non-Tg, trained" and "TurboID, control" samples in any one of the biological replicates, to identify "learning proteome" (706 proteins, page 8, last line - page 9, line 8; page 32, line 21-22). The word "present" implies that they included even peptides whose amounts are just above the detection threshold, which is subject to random noise caused by the detector or during sample collection and preparation processes. This consideration is partly supported by the fact that only a small fraction of the proteins are common between biological replicates (honestly and respectably shown in Figure S2). Because of this problem, there is no statistical estimate of the identity in "learning proteome" in the current manuscript. Therefore, the presentation style in Tables S2 and S3 are not very useful for readers, especially because authors already subtracted proteins identified in Non-Tg samples, which must also suffer from stochastic noise. I suggest either quantifying the MS/MS signal, or if authors need to stick to the "present"/"absent" description of the MS/MS data, use the number of appearances in biological replicates of each protein as estimate of the quantity of each protein. For example, found in 2 replicates in "TurboID, learned" and in 0 replicates in "Non-Tg, trained". One can apply statistics to these counts. This said, I would like to stress that proteins related to acquisition of memory may be very rare, especially because learning-related changes likely occur in a small subset of neurons. Therefore, 1 time vs 0 time may be still important, as well as something like 5 times vs 1 time. In summary, quantitative description of the proteomics results is desired.

We thank the reviewer for these valuable comments and suggestions.

We acknowledge that quantitative proteomics would provide beneficial information; however, as also indicated by Reviewer 1 (in cross-comment), it is practically challenging to perform with TurboID. We have included discussion of potential future experiments involving quantitative mass spectrometry, as well as a comprehensive discussion of some of the limitations of our approach as summarised by this Reviewer, in the Discussion section (page 39). However, we note that our qualitative approach also provides beneficial knowledge, such as the identification of functional protein networks acting within biological pathways previously implicated in learning (Figure 2), and novel learning regulators ACC-1/3, LGC-46, and F46H5.3.

We agree with the assessment that the frequency of occurrence for each candidate we test per biological replicate is useful to disclose in the manuscript as a proxy for quantification. This was also highlighted by Reviewer 2 (Major Comment 1). As detailed above in response to R2, we have now separated candidates into two categories: ‘strong’ (present in 3 or more biological replicates) and ‘weak’ candidates (present in 2 or fewer biological replicates). We have also added behavioural data after testing 9 of these strong candidates in Figures 6 & S7.

We have also added Table 2 to the revised manuscript, which summarises the frequency-based representation of the proteomics results, as suggested. This is described on pages 22-23. Briefly, this shows the range of candidates further explored using single mutant testing. Specifically, this data showed that many of the tested candidates were more frequently detected in trained worms compared to high-salt controls. This includes both strong and weak candidates, providing a clearer view of how proteomic frequency informed our selection for functional testing.

2) There is another problem in the treatment of the behavioural data. In Experimental Procedures, authors state that they excluded data in which naive or control groups showed average CI 0.5499 for N2 (page 36, lines 5-7). How were these values determined? One common example for judging a data point as an outlier is > mean + 1.5, 2 or 3 SD, or Thank you for pointing this out. As mentioned by both Reviewer 1 and Reviewer 4, the original manuscript states the following: “Data was excluded for salt associative learning experiments when wild-type N2 displayed (1) an average CI ≤ 0.6499 for naïve or control groups and/or (2) an average CI either 0.5499 for trained groups.”

To clarify, we only excluded experiments in rare cases where N2 worms did not display robust high salt attraction before training, or where trained N2 did not display the expected behavioural difference compared to untrained or high-salt control N2. These anomalies were typically attributable to clear contamination or starvation issues that could clearly be observed prior to counting chemotaxis indices on CTX plates.

We established these exclusion criteria in advance of conducting multiple learning assays to ensure an objective threshold for identifying and excluding assays affected by these rare but observable issues. However, these criteria were later found to be unnecessary, as N2 worms robustly displayed the expected untrained and trained phenotypes for salt associative learning when not compromised by starvation or contamination.

We understand that the original criteria may have appeared to introduce arbitrary bias in data selection. To address this concern, we have removed these criteria from the revised manuscript from page 50.

Minor comments:

1) Related to Major comments 1), the successful effect of neuron-specific TurboID procedure was not evaluated. Authors obtained both TurboID and Non-Tg proteome data. Do they see enrichment of neuron-specific proteins? This can be easily tested, for example by using the list of neuron-specific genes by Kaletsky et al. (http://dx.doi.org/10.1038/nature16483 or http://dx.doi.org/10.1371/journal.pgen.1007559), or referring to the CenGEN data.

We thank this Reviewer for this helpful suggestion, which was echoed by Reviewer 3 (Major Comment 1). As indicated in the response to R3 above, the revised manuscript now includes Table 1 as a tissue-specific analysis of the learning proteome, using the single neuron RNA-Seq database CeNGEN to identify the proportion of neuronal proteins from each biological replicate of mass spectrometry data. Generally, we observed a range of 87-95% of proteins corresponded to genes from the CeNGEN database that had been detected in neurons, providing evidence that the TurboID enzyme was able to target the neuronal proteome as expected. Table 1 is now described in the main text of the revised work on pages 16 & 17.

2) The behavioural paradigm needs to be described accurately. Page 5, line 16-17, "C. elegans normally have a mild attraction towards higher salt concentration": in fact, C. elegans raised on NGM plates, which include approximately 50mM of NaCl, is attracted to around 50mM of NaCl (Kunitomo et al., Luo et al.) but not 100-200 mM.

We thank the Reviewer for pointing this out. We agree that clarification is necessary. The revised text reads as follows on page 5: “C. elegans are typically grown in the presence of salt (usually ~ 50 mM) and display an attraction toward this concentration when assayed for chemotaxis behaviour on a salt gradient (Kunitomo et al., 2013, Luo et al., 2014). Training/conditioning with ‘no salt + food’ partially attenuates this attraction (group referred to ‘trained’).”

Authors call this assay "salt associative learning", which refers to the fact that worms associate salt concentration (CS) and either presence or absence of food (appetitive or aversive US) during conditioning (Kunitomo et al., Luo et al., Nagashima et al.) but they are looking at only association with presence of food, and for proteome analysis they only change the CS (NaCl concentration, as discussed in Discussion, p24, lines 4-5). It is better to attempt to avoid confusion to the readers in general.

Thank you Reviewer 4 for highlighting this clarity issue. We clarify our definition of “salt associative learning” for the purpose of this study in the revised manuscript on page 6 with the following text:

“Similar behavioural paradigms involving pairings between salt/no salt and food/no food have been previously described in the literature (Nagashima et al. 2019). Here, learning experiments were performed by conditioning worms with either ‘no salt + food’ (referred to as ‘salt associative learning’) or ‘salt + no food’ (called ‘salt aversive learning’).”

3) page 32, line 23: the wording "excluding" is obscure and misleading because the elo-6 gene was included in the analysis.

We appreciate this Reviewer for pointing out this misleading comment, which was unintentional. We have now removed it from the text (on page 21).

4) Typo at page 24, line 18: "that ACC-1" -> "than ACC-1".

This has been corrected (on page 37).

5) Reference. In "LEO, T. H. T. et al.", given and sir names are flipped for all authors. Also, the paper has been formally published (http://dx.doi.org/10.1016/j.cub.2023.07.041).

We appreciate the Reviewer drawing our attention to this – the reference has been corrected and updated.

I would like to express my modest cross comments on the reviews:

1) Many of the reviewers comment on the shortage in the quantitative nature of the proteome analysis, so it seems to be a consensus.

Thank you Reviewer 4 for this feedback. We appreciate the benefit in performing quantitative mass spectrometry, in that it provides an additional way to parse molecular mechanisms in a biological process (e.g., fold-changes in protein expression induced by learning). However, we note that quantitative mass spectrometry is challenging to integrate with TurboID due to the requirement to enrich for biotinylated peptides during sample processing (we now mention this on page 39). Nevertheless, it would be exciting to see this approach performed in a future study.

To address the limitations of our original qualitative approach and enhance the clarity and utility of our dataset, we have made the following revisions in the manuscript:

• Candidate selection criteria: We now clearly define how candidates were selected for functional testing, based on their frequency across biological replicates. Specifically, “strong candidates” were detected in three or more replicates, while “weak candidates” appeared in two or fewer.
• Frequency-based representation (_Table 2_):__We appreciate the suggestion by Reviewer 4 (Major Comment 1) to quantify differences between high-salt control and trained groups. We now provide the frequency-based representation of the candidates tested in this study within our proteomics data in __Table 2. This data showed that many of the tested candidates were more frequently detected in trained worms compared to high-salt controls. This includes both strong and weak candidates We hope these additions help clarify our approach and demonstrate the value of the dataset, even within the constraints of qualitative proteomics.

2) Also, tissue- or cell-specificity of the identified proteins were commonly discussed. In reviewer #3's first Major comment, appearance of non-neuronal protein in the list was pointed out, which collaborate with my (#4 reviewer's) question on successful identification of neuronal proteins by this method. On the other hand, reviewer #1 pointed out subset neuron-specific proteins in the list. Obviously, these issues need to be systematically described by the authors.

We agree with Reviewer 4 that these analyses provide a critical angle of analysis that is not explored in the original manuscript.

Tissue analysis (Reviewer 3 Major Comment 1): We have used the single neuron RNA-Seq database CeNGEN, to identify that 87-95% (i.e. a large majority) of proteins identified across replicates corresponded to genes detected in neurons. These findings support that the TurboID enzyme was able to target the neuronal proteome as expected. Table 1 provides this information as is now described in the main text of the revised work on page 16.

__Neuron class analyses (Reviewer 1 Major Comment 2): __In response, we have used the suggested Wormbase gene enrichment tool and CeNGEN. We specifically input proteins from the learning proteome into Wormbase, after filtering for proteins unique to TurboID trained animals. For CeNGEN, we compared genes/proteins from control worms and trained worms to identify potential neurons that may be involved in this learning paradigm.

Briefly, we found highlight a range of neuron classes known in learning (e.g., RIS interneurons), cells that affect behaviour but have not been explored in learning (e.g., IL1 polymodal neurons), and neurons for which their function/s are unknown (e.g., pharyngeal neuron I3). Corresponding text for this new analysis has been added on pages 16-20, with a new table and figure added to illustrate these findings (Table S7 & Figure 4). Methods are detailed on pages 50-51.

3) Given reviewer #1's OPTIONAL Major comment, as an expert of behavioral assays in C. elegans, I would like to comment based on my experience that mutants received from Caenorhabditis Genetics Center or other labs often lose the phenotype after outcrossing by the wild type, indicating that a side mutation was responsible for the observed behavioral phenotype. Therefore, outcrossing may be helpful and easier than rescue experiments, though the latter are of course more accurate.

Thank you for this suggestion. To address the potential involvement of background mutations, we have done experiments with backcrossed versions of mutants tested where possible, as shown in Figure 6. We found that F46H5.3(-) mutants maintained enhanced learning capacity after backcrossing with wild type, compared to their non-backcrossed mutant line. This was in contrast to C30G12.6(-) animals which lost their enhanced learning phenotype following backcrossing using wild type worms. This is described in the text on pages 24-26.

4) Just let me clarify the first Minor comment by reviewer #2. Authors described that the kin-2 mutant has abnormality in "salt associative learning" and "salt aversive learning", according to authors' terminology. In this comment by reviewer #2, "gustatory associative learning" probably refers to both of these assays.

Reviewer 4 is correct. We have amended the wording appropriately on page 31 to clarify our meaning to address Reviewer 2’s comment.

• “Although kin-2(ce179) mutants were not shown to impact salt aversive learning, they have been reported previously to display impaired intermediate-term memory (but intact learning and short-term memory) for butanone appetitive learning (Stein and Murphy, 2014).”*

5) There seem to be several typos in reviewer #1's Minor comments.

"In Page 9, Lines 17-18" -> "Page 8, Lines 17-18".

"Page 8, Line 24" -> "Page 7, Line 24".

"I would suggest to remove figure 3" -> "I would suggest to remove figure 2"

"summary figure similar to Figure 4" -> "summary figure similar to Figure 3"

"In the discussion Page 24, Line 14" -> "In the discussion Page 23, Line 14"

(I note that because a top page was inserted in the "merged" file but not in art file for review, there is a shift between authors' page numbers and pdf page numbers in the former.)

It would be nice if reviewer #1 can confirm on these because I might be wrong.

We appreciate Reviewer 4 noting this, and can confirm that these are the correct references (as indicated by Reviewer 1 in their cross-comments)

Reviewer #4 (Significance (Required)):

1) Total neural proteome analysis has not been conducted before for learning-induced changes, though transcriptome analysis has been performed for odor learning (Lakhina et al., http://dx.doi.org/10.1016/j.neuron.2014.12.029). This guarantees the novelty of this manuscript, because for some genes, protein levels may change even though mRNA levels remain the same. We note an example in which a proteome analysis utilizing TurboID, though not the comparison between trained/control, has led to finding of learning related proteins (Hiroki et al., http://dx.doi.org/10.1038/s41467-022-30279-7). As described in the Major comments 1) in the previous section, improvement of data presentation will be necessary to substantiate this novelty.

We appreciate this thoughtful feedback. We agree that while the neuronal transcriptome has been explored in Lakhina et al., 2015 for C. elegans in the context of memory, our study represents the first to examine learning-induced changes in the total neuronal proteome. We particularly agree with the statement that “for some genes, protein levels may change even though mRNA levels remain the same”. This is essential rationale that we now discuss on page 42.

Additionally, we acknowledge the relevance of the study by Hiroki et al., 2022, which used TurboID to identify learning-related proteins, though not in a trained versus control comparison. Our work builds on this by directly comparing trained and control conditions, thereby offering new insights into the proteomic landscape of learning. This is now clarified on page 36.

To substantiate the novelty and significance of our approach, we have revised the data presentation throughout the manuscript, including clearer candidate selection criteria, frequency-based representation of proteomic hits (Table 2), and neuron-specific enrichment analyses (Table S7 & Figure 4). We hope these improvements help convey the unique contribution of our study to the field.

2) Authors found six mutants that have abnormality in the salt learning (Fig. 4). These genes have not been described to have the abnormality, providing novel knowledge to the readers, especially those who work on C. elegans behavioural plasticity. Especially, involvement of acetylcholine neurotransmission has not been addressed. Although site of action (neurons involved) has not been tested in this manuscript, it will open the venue to further determine the way in which acetylcholine receptors, cAMP pathway etc. influences the learning process.

Thank you Reviewer 4, for this encouraging feedback. To further strengthen the study and expand its relevance, we have tested additional mutants in response to Reviewer 3’s comments, as shown in Figures 6 & S7. These results provide even more candidate genes and pathways for future exploration, enhancing the significance and impact of our study.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

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Referee #4

Evidence, reproducibility and clarity

Summary:

In this manuscript, authors used a learning paradigm in C. elegans; when worms were fed in a saltless plate, its chemotaxis to salt is greatly reduced. To identify learning-related proteins, authors employed nervous system-specific transcriptome analysis to compare whole proteins in neurons between high-salt-fed animals and saltless-fed animals. Authors identified "learning-specific genes" which are observed only after saltless feeding. They categorized these proteins by GO analyses and pathway analyses, and further stepped forward to test mutants in selected genes identified by the proteome analysis. They find several mutants that are defective or hyper-proficient for learning, including acc-1/3 and lgc-46 acetylcholine receptors, gar-1 acetylcholine receptor GPCR, glna-3 glutaminase involved in glutamate biosynthesis, and kin-2, a cAMP pathway gene. These mutants were not previously reported to have abnormality in the learning paradigm.

Major comments:

1. There are problems in the data processing and presentation of the proteomics data in the current manuscript which deteriorates the utility of the data. First, as the authors discuss (page 24, lines 5-12), the current approach does not consider amount of the peptides. Authors state that their current approach is "conservative", because some of the proteins may be present in both control and learned samples but in different amounts. This reviewer has a concern in the opposite way: some of the identified proteins may be pseudo-positive artifacts caused by the analytical noise. The problem is that authors included peptides that are "present" in "TurboID, trained" sample but "absent" in the "Non-Tg, trained" and "TurboID, control" samples in any one of the biological replicates, to identify "learning proteome" (706 proteins, page 8, last line - page 9, line 8; page 32, line 21-22). The word "present" implies that they included even peptides whose amounts are just above the detection threshold, which is subject to random noise caused by the detector or during sample collection and preparation processes. This consideration is partly supported by the fact that only a small fraction of the proteins are common between biological replicates (honestly and respectably shown in Figure S2). Because of this problem, there is no statistical estimate of the identity in "learning proteome" in the current manuscript. Therefore, the presentation style in Tables S2 and S3 are not very useful for readers, especially because authors already subtracted proteins identified in Non-Tg samples, which must also suffer from stochastic noise. I suggest either quantifying the MS/MS signal, or if authors need to stick to the "present"/"absent" description of the MS/MS data, use the number of appearances in biological replicates of each protein as estimate of the quantity of each protein. For example, found in 2 replicates in "TurboID, learned" and in 0 replicates in "Non-Tg, trained". One can apply statistics to these counts. This said, I would like to stress that proteins related to acquisition of memory may be very rare, especially because learning-related changes likely occur in a small subset of neurons. Therefore, 1 time vs 0 time may be still important, as well as something like 5 times vs 1 time. In summary, quantitative description of the proteomics results is desired.
2. There is another problem in the treatment of the behavioural data. In Experimental Procedures, authors state that they excluded data in which naive or control groups showed average CI < 0.6499, and/or trained groups showed average CI < -0.0499 or > 0.5499 for N2 (page 36, lines 5-7). How were these values determined? One common example for judging a data point as an outlier is > mean + 1.5, 2 or 3 SD, or < mean - 1.5, 2 or 3 SD. Are these values any of these standards, or determined through other methods? If these values were determined simply by authors' decision, it could potentially introduce a bias and in the worst cases lead to incorrect conclusions. A related question is: authors state "trained animals showed a lower CI (~0.3)" where in the referred Figure 1B, the corresponding data shows averages close to 0. Why is the inconsistency? The assay that authors use is close to those described in the previous literature (Kunitomo et al., http://dx.doi.org/10.1038/ncomms3210). In this previous paper, it was described that animals conditioned under no salt with food show negative CI and are attracted to the low salt concentration area. Quantitative analysis of behavioural patterns showed migration bias towards lower salt concentrations (negative chemotaxis). Essentially the same concept was reported by Luo et al. (http://dx.doi.org/10.1016/j.neuron.2014.05.010). The experimental procedure employed in the current work is very similar with those by the Japanese group, with a notable difference: the chemotaxis assay plate included 50mM NaCl in Kunitomo et al, while authors used chemotaxis plate without added NaCl (p35, line 18). The latter is expected to cause shallow gradient towards the low-salt area, which may be the reason for the weak negative CI in the trained animals. In any case, the value of CI itself is not a problem, and authors' current assay is valid. The only concern of mine is the potential of author-introduced cognitive bias, possibly affecting, for example, whether a certain mutant has a significant defect or not. What happens if the cut-offs of -0.0499 and 0.5499 are omitted and all data were included in the analyses? What are the average CIs of N2 in all performed experiments for each of naive, control and trained groups?

Minor comments:

1. Related to Major comments 1), the successful effect of neuron-specific TurboID procedure was not evaluated. Authors obtained both TurboID and Non-Tg proteome data. Do they see enrichment of neuron-specific proteins? This can be easily tested, for example by using the list of neuron-specific genes by Kaletsky et al. (http://dx.doi.org/10.1038/nature16483 or http://dx.doi.org/10.1371/journal.pgen.1007559), or referring to the CenGEN data.
2. The behavioural paradigm needs to be described accurately. Page 5, line 16-17, "C. elegans normally have a mild attraction towards higher salt concentration": in fact, C. elegans raised on NGM plates, which include approximately 50mM of NaCl, is attracted to around 50mM of NaCl (Kunitomo et al., Luo et al.) but not 100-200 mM. Authors call this assay "salt associative learning", which refers to the fact that worms associate salt concentration (CS) and either presence or absence of food (appetitive or aversive US) during conditioning (Kunitomo et al., Luo et al., Nagashima et al.) but they are looking at only association with presence of food, and for proteome analysis they only change the CS (NaCl concentration, as discussed in Discussion, p24, lines 4-5). It is better to attempt to avoid confusion to the readers in general.
3. page 32, line 23: the wording "excluding" is obscure and misleading because the elo-6 gene was included in the analysis.
4. Typo at page 24, line 18: "that ACC-1" -> "than ACC-1".
5. Reference. In "LEO, T. H. T. et al.", given and sir names are flipped for all authors. Also, the paper has been formally published (http://dx.doi.org/10.1016/j.cub.2023.07.041).

Cross-Commenting

I would like to express my modest cross comments on the reviews:

1. Many of the reviewers comment on the shortage in the quantitative nature of the proteome analysis, so it seems to be a consensus.
2. Also, tissue- or cell-specificity of the identified proteins were commonly discussed. In reviewer #3's first Major comment, appearance of non-neuronal protein in the list was pointed out, which collaborate with my (#4 reviewer's) question on successful identification of neuronal proteins by this method. On the other hand, reviewer #1 pointed out subset neuron-specific proteins in the list. Obviously, these issues need to be systematically described by the authors.
3. Given reviewer #1's OPTIONAL Major comment, as an expert of behavioral assays in C. elegans, I would like to comment based on my experience that mutants received from Caenorhabditis Genetics Center or other labs often lose the phenotype after outcrossing by the wild type, indicating that a side mutation was responsible for the observed behavioral phenotype. Therefore, outcrossing may be helpful and easier than rescue experiments, though the latter are of course more accurate.
4. Just let me clarify the first Minor comment by reviewer #2. Authors described that the kin-2 mutant has abnormality in "salt associative learning" and "salt aversive learning", according to authors' terminology. In this comment by reviewer #2, "gustatory associative learning" probably refers to both of these assays.
5. There seem to be several typos in reviewer #1's Minor comments. "In Page 9, Lines 17-18" -> "Page 8, Lines 17-18". "Page 8, Line 24" -> "Page 7, Line 24". "I would suggest to remove figure 3" -> "I would suggest to remove figure 2" "summary figure similar to Figure 4" -> "summary figure similar to Figure 3" "In the discussion Page 24, Line 14" -> "In the discussion Page 23, Line 14" (I note that because a top page was inserted in the "merged" file but not in art file for review, there is a shift between authors' page numbers and pdf page numbers in the former.) It would be nice if reviewer #1 can confirm on these because I might be wrong.

Significance

1. Total neural proteome analysis has not been conducted before for learning-induced changes, though transcriptome analysis has been performed for odor learning (Lakhina et al., http://dx.doi.org/10.1016/j.neuron.2014.12.029). This guarantees the novelty of this manuscript, because for some genes, protein levels may change even though mRNA levels remain the same. We note an example in which a proteome analysis utilizing TurboID, though not the comparison between trained/control, has led to finding of learning related proteins (Hiroki et al., http://dx.doi.org/10.1038/s41467-022-30279-7). As described in the Major comments 1) in the previous section, improvement of data presentation will be necessary to substantiate this novelty.
2. Authors found six mutants that have abnormality in the salt learning (Fig. 4). These genes have not been described to have the abnormality, providing novel knowledge to the readers, especially those who work on C. elegans behavioural plasticity. Especially, involvement of acetylcholine neurotransmission has not been addressed. Although site of action (neurons involved) has not been tested in this manuscript, it will open the venue to further determine the way in which acetylcholine receptors, cAMP pathway etc. influences the learning process.

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Referee #3

Evidence, reproducibility and clarity

Summary:

In the manuscript titled "Identifying regulators of associative learning using a protein-labelling approach in C. elegans" the authors attempted to generate a snapshot of the proteomic changes that happen in the C. elegans nervous system during learning and memory formation. They employed the TurboID-based protein labeling method to identify the proteins that are uniquely found in samples that underwent training to associate no-salt with food, and consequently exhibited lower attraction to high salt in a chemotaxis assay. Using this system they obtained a list of target proteins that included proteins represented in molecular pathways previously implicated in associative learning. The authors then further validated some of the hits from the assay by testing single gene mutants for effects on learning and memory formation.

Major comments:

In the discussion section, the authors comment on the sources of "background noise" in their data and ways to improve the specificity. They provide some analysis on this aspect in Supplementary figure S2. However, a better visualization of non-specificity in the sample could be a GO analysis of tissue-specificity, and presented as a pie chart as in Figure 2A. Non-neuronal proteins such as MYO-2 or MYO-3 repeatedly show up on the "TurboID trained" lists in several biological replicates (Tables S2 and S3). If a major fraction of the proteins after subtraction of control lists are non-specific, that increases the likelihood that the "hits" observed are by chance. This analysis should be presented in one of the main figures as it is essential for the reader to gauge the reliability of the experiment.

Other than the above, the authors have provided sufficient details in their experimental and analysis procedures. They have performed appropriate controls, and their data has sufficient biological and technical replaictes for statistical analysis.

Minor comments:

There is an error in the first paragraph of the discussion, in the sentences discussing the learning effects in gar-1 mutant worms. The sentences in lines 12-16 on page 22 says that gar-1 mutants have improved salt-associative learning and defective salt-aversive learning, while in fact the data and figures state the opposite.

Significance

Strengths and limitations:

This study used neuron-specific TurboID expression with transient biotin exposure to capture a temporally restricted snapshot of the C. elegans nervous system proteome during salt-associative learning. This is an elegant method to identify proteins temporally specific to a certain condition. However, there are several limitations in the way the experiments and analyses were performed which affect the reliability of the data. As the authors themselves have noted in the discussion, background noise is a major issue and several steps could be taken to improve the noise at the experimental or analysis steps (use of integrated C. elegans lines to ensure uniformity of samples, flow cytometry to isolate neurons, quantitative mass spec to detect fold change vs. strict presence/absence).

Advance:

Several studies have demonstrated the use of proximity labeling to map the interactome by using a bait protein fusion. In fact, expressing TurboID not fused to a bait protein is often used as a negative control in proximity labeling experiments. However, this study demonstrates the use of free TurboID molecules to acquire a global snapshot of the proteome under a given condition.

Audience:

Even with the significant limitations, this study is specifically of interest to researchers interested in understanding learning and memory formation. Broadly, the methods used in this study could be modified to gain insights into the proteomic profiles at other transient developmental stages.

The reviewer's field of expertise: Cell biology of C. elegans neurons.

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Referee #2

Evidence, reproducibility and clarity

Summary:

In this study by Rahmani in colleagues, the authors sought to define the "learning proteome" for a gustatory associative learning paradigm in C. elegans. Using a cytoplasmic TurboID expressed under the control of a pan-neuronal promoter, the authors labeled proteins during the training portion of the paradigm, followed by proteomics analysis. This approach revealed hundreds of proteins potentially involved in learning, which the authors describe using gene ontology and pathways analysis. The authors performed functional characterization of some of these genes for their requirement in learning using the same paradigm. They also compared the requirement for these genes across various learning paradigms, and found that most hits they characterized appear to be specifically required for the training paradigm used for generating the "learning proteome".

Major Comments:

• The definition of a "hit" from the TurboID approach is does not appear stringent enough. According to the manuscript, a hit was defined as one unique peptide detected in a single biological replicate (out of 5), which could give rise to false positives. In figure S2, it is clear that there relatively little overlap between samples with regards to proteins detected between replicates, and while perhaps unintentional, presenting a single unique peptide appears to be an attempt to inflate the number of hits. Defining hits as present in more than one sample would be more rigorous. Changing the definition of hits would only require the time to re-list genes and change data presented in the manuscript accordingly.
• The "hits" that the authors chose to functionally characterize do not seem like strong candidate hits based on the proteomics data that they generated. Indeed, most of the hits are present in a single, or at most 2, biological replicate. It is unclear as to why the strongest hits were not characterized, which if mutant strains are publicly available, would not be a difficult experiment to perform. Because of the lack of strong evidence that these are indeed proteins regulated in the context of learning based on proteomics, including evidence of changes in the proteins (by imaging expression changes of fluorescent reporters or a biochemical approach), would increase confidence that these hits are genuine.

Minor Comments:

• The authors highlight that the proteins they discover seem to function uniquely in their gustatory associative paradigm, but this is not completely accurate. kin-2, which they characterize in figure 4, is required for positive butanone association (the authors even say as much in the manuscript) in Stein and Murphy, 2014.

Significance

• General Assessment: The approach used in this study is interesting and has the potential to further our knowledge about the molecular mechanisms of associative behaviors. Strengths of the study include the design with carefully thought out controls, and the premise of combining their proteomics with behavioral analysis to better understand the biological significance of their proteomics findings. However, the criteria for defining hits and prioritization of hits for behavioral characterizations were major wweaknesses of the paper.
• Advance: There have been multiple transcriptomic studies in the worm looking at gene expression changes in the context of behavioral training (Lakhina et al., 2015, Freytag 2017). This study compliments and extends those studies, by examining how the proteome changes in a different training paradigm. This approach here could be employed for multiple different training paradigms, presenting a new technical advance for the field.
• Audience: This paper would be of interest to the broader field of behavioral and molecular neuroscience. Though it uses an invertebrate system, many findings in the worm regarding learning and memory translate to higher organisms.
• I am an expert in molecular and behavioral neuroscience in both vertebrate and invertebrate models, with experience in genetics and genomics approaches.

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Referee #1

Evidence, reproducibility and clarity

Summary:

Rahmani et al., utilize the TurboID method to characterize the global proteome changes in the worm's nervous system induced by a salt-based associative learning paradigm. Altogether, Rahmani et al., uncover 706 proteins that are tagged by the TurboID method specifically in samples extracted from worms that underwent the memory inducing protocol. Next, the authors conduct a gene enrichment analysis that implicates specific molecular pathways in salt-associative learning, such as MAP-kinase and cAMP-mediated pathways. The authors then screen a representative group of the hits from the proteome analysis. The authors find that mutants of candidate genes from the MAP-kinase pathway, namely dlk-1 and uev-3, do not affect the performance in the learning paradigm. Instead multiple acetylcholine signaling mutants significantly affected the performance in the associative memory assay, e.g., acc-1, acc-3, gar-1, and lgc-46. Finally, the authors demonstrate that the acetylcholine signaling mutants did not exhibit a phenotype in similar but different conditioning paradigms, such as aversive salt-conditioning or appetitive odor conditioning, suggesting their effect is specific to appetitive salt conditioning.

Major comments:

1. The statistical approach and analysis of the behavior assay:
   • The authors use a 2-way ANOVA test which assumes normal distribution of the data. However, the chemotaxis index used in the study is bounded between -1 and 1, which prevents values near the boundaries to be normally distributed. Since most of the control data in this assay in this study is very close to 1, it strongly suggests that the CI data is not normally distributed and therefore 2-way ANOVA is expected to give skewed results. I am aware this is a common mistake and I also anticipate that most conclusions will still hold also under a more fitting statistical test. Nevertheless an appropriate statistical analysis should be performed. Since I assume the authors would wish to take into consideration both the different conditions and biological repeats, I can suggest two options:
   • Using a Generalized linear mixed model, one can do with R software.
   • Using a custom bootstrapping approach.
   • The total number of assays, especially controls, varies quite a bit between the tested mutants. For example compare the acc-1 experiment in Figure 4.A., and gap-1 or rho-1 in Figure S4.A and D. It is hard to know the exact N of the controls, but I assume that for example, lowering the wild type control of acc-1 to equivalent to gap-1 would have made it non significant. Perhaps the best approach would be to conduct a power analysis, to know what N should be acquired for all samples.
   • The authors use the phrasing "a non-significant trend", I find such claims uninterpretable and should be avoided. Examples: Page 16. Line 7 and Page 18, line 16.
2. Neuron-specific analysis and rescue of mutants:
   • Throughout the study the authors avoid focusing on specific neurons. This is understandable as the authors aim at a systems biology approach, however, in my view this limits the impact of the study. I am aware that the proteome changes analyzed in this study were extracted from a pan neuronally expressed TurboID. Yet, neuron-specific changes may nevertheless be found. For example, running the protein lists from Table S2, in the Gene enrichment tool of wormbase, I found, across several biological replicates, enrichment for the NSM, CAN and RIG neurons. A more careful analysis may uncover specific neurons that take part in this associative memory paradigm. In addition, analysis of the overlap in expression of the final gene list in different neurons, comparing them, looking for overlap and connectivity, would also help to direct towards specific circuits.
   • OPTIONAL: A rescue of the phenotype of the mutants by re-expression of the gene is missing, this makes sure to avoid false-positive results coming from background mutations. For example, a pan neuronal or endogenous promoter rescue would help the authors to substantiate their claims, this can be done for the most promising genes. The ideal experiment would be a neuron-specific rescue but this can be saved for future works.

Minor comments:

1.Lack of clarity regarding the validation of the biotin tagging of the proteome. The authors show in Figure 1 that they validated that the combination of the transgene and biotin allows them to find more biotin-tagged proteins. However there is significant biotin background also in control samples as is common for this method. The authors mention they validated biotin tagging of all their experiments, but it was unclear in the text whether they validated it in comparison to no-biotin controls, and checked for the fold change difference. Also, it was unclear which exact samples were tested per replicate. In Page 9, Lines 17-18: "For all replicates, we determined that biotinylated proteins could be observed ...", But in Page 8, Line 24 : "We then isolated proteins from ... worms per group for both 'control' and 'trained' groups,... some of which were probed via western blotting to confirm the presence of biotinylated proteins". - Could the authors specify which samples were verified and clarify how? - OPTIONAL: include the fold changes of biotinylated proteins of all the ones that were tested. Similar to Figure 1.C. 2.Figure 2 does not add much to the reader, it can be summarized in the text, as the fraction of proteins enriched for specific cellular compartments. - I would suggest to remove figure 3 to text, or transfer it to the supplementry material. - OPTIONAL: I would suggest the authors to mark in a pathway summary figure similar to Figure 4 the results from the behavior assay of the genetic screen. This would allow the reader to better get the bigger picture and to connect to the systemic approach taken in Figures 2 and 3. 3. Typo in Figure 3: the circle of PPM1: The blue right circle half is bigger than the left one. 4. Unclarity in the discussions. In the discussion Page 24, Line 14, the authors raise this question: "why are the proteins we identified not general learning regulators?. The phrasing and logic of the argumentation of the possible answers was hard to follow. - Can you clarify?

Cross-Commenting

I would like to thank Reviewer #4 for the great cross comment summary, I find it accurate and helpful. I also would like to thank Reviewer #4 for spotting the typos in my minor comments, their page and figure numbers are the correct ones.

Small comment on common point 1 - My feeling is that it is challanging to do quantitative mass spectrometry, especially with TurboID. In general, the nature of MS data is that it hints towards a direction but a followup validation work is required in order to assess it. For example, I am not surprised that the fraction of repeats a hit appeared in does not predict well whether this hit would be validated behavioraly. Given these limitations, I find the authors' approach reasonable.

I also would like to highlight this major comment from reviewer 4: "In Experimental Procedures, authors state that they excluded data in which naive or control groups showed average CI < 0.6499, and/or trained groups showed average CI < -0.0499 or > 0.5499 for N2 (page 36, lines 5-7). " This threshold seems arbitrary to me too, and it requires the clarifications requested by reviewer 4.

Significance

This study does a great job to effectively utilize the TurboID technique to identify new pathways implicated in salt-associative learning in C. elegans. This technique was used in C. elegans before, but not in this context. The salt-associative memory induced proteome list is a valuable resource that will help future studies on associative memory in worms. Some of the implicated molecular pathways were found before to be involved in memory in worms like cAMP, as correctly referenced in the manuscript. The implication of the acetylcholine pathway is novel for C. elgeans, to the best of my knowledge. The finding that the uncovered genes are specifically required for salt associative memory and not for other memory assays is also interesting.

However overall I find the impact of this study limited. The premise of this work is to use the Turbo-ID method to conduct a systems analysis of the proteomic changes. The work starts by conducting network analysis and gene enrichment which fit a systemic approach. However, since the authors find that ~30% of the tested hits affect the phenotype, and since only 17/706 proteins were assessed, it is challenging to draw conclusive broad systemic claims. Alternatively, the authors could have focused on the positive hits, and understand them better, find the specific circuits where these genes act. This could have increased the impact of the work. Since neither of these two options are satisfied, I view this work as solid, but not wide in its impact and therefore estimate the audience of this study would be more specialized.

My expertise is in C. elegans behavior, genetics, and neuronal activity, programming and machine learning.

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Reply to the reviewers

The authors do not wish to provide a response at this time

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Referee #3

Evidence, reproducibility and clarity

In this study, Wasilewska and colleagues generated tmbim5-/- zebrafish line and demonstrated that tmbim5 loss of function leads to decrease in zebrafish size and induces muscle atrophy. Authors used immunohistochemistry to suggest that tmbim5-/- zebrafish shows reduced glycogen levels in muscle and liver. However, most of the immunohistochemistry is not quantitated and only qualitative differences are shown. Next, the authors measured mitochondrial calcium levels in the brain of tmbim5-/- zebrafish but there was no behavioral phenotype in the fish. It would have be better to measure mitochondrial calcium levels in the muscles of tmbim5-/- zebrafish as phenotype is muscle atrophy. Further, it is reported that the mitochondrial membrane potential and glycogen levels were perturbed in tmbim5-/- zebrafish.

Next, the authors generated a scl8b1-/- (a probable NCLX ortholog in zebrafish) zebrafish, which did not show any drastic phenotype. However, neither slc8b1 function nor the phenotype of scl8b1-/- zebrafish was well characterized. Further, authors created two double knockout zebrafish lines i.e. tmbim5-/-/mcu-/- and tmbim5-/-/slc8b1-/-. Interestingly, both these lines were viable and do not show any drastic phenotypes. The authors concluded that in these transgenic fishes compensatory and/or alternative mitochondrial Ca2+ mobilization pathways counterbalance the effects of silencing of these proteins.

Although it is an interesting study, the conclusions are not well supported with the data. At several places only qualitative images are shown and quantitative data is missing. Similarly, Ca2+ imaging in muscles of tmbim5-/- zebrafish is not performed. Finally, no molecular mechanism or molecular details are provided. Though Tmbim5's potential role in EMRE degradation is discussed, it is not experimentally investigated. The quality of the manuscript would significantly enhance if authors perform the suggested experiments.

Major Comments:

1. As a potential mechanism, Tmbim5's potential role in EMRE degradation is discussed but it is not experimentally investigated. It is very easy to test this hypothesis. If this is the case, it would be a very good contribution to the field.
2. On Page 16, authors state that slc8b1 does not constitutes the major mitochondrial Ca2+ efflux transport system. Authors should do calcium imaging experiments just like they did with tmbim5 and mcu double knockouts (data presented in Figure 4C) to make any comments on functioning of slc8b1 in mitochondrial Ca2+ transport. This is important because slc8b1 is only a predictive ortholog of human NCLX and it is not experimentally examined yet.
3. The data presented in Fig. 4C is very important but it is not fully explained and discussed in the results. Please discuss all the data sets presented in Fig4C in detail. As such, it is very difficult to follow and interpret the data.
4. In tmbim5-/- zebrafish, what happens to mitochondrial Ca2+ signaling in muscle as phenotype is muscle atrophy only?
5. Please validate the observation of decreased glycogen levels in tmbim5-/- fish by one more way. Only immunohistochemistry that too without quantitation is not convincing (Fig. 2E-H).

Minor Comments:

1. Authors state that tmbim5 loss of function leads to metabolic changes but the only data provided is decrease in glycogen levels. It would be helpful for the authors to focus comments specifically on the data presented in the manuscript to avoid potential over-interpretation.
2. While discussing Fig4., authors mention that Tmbim5 may act as a MCU independent Ca2+ uptake mechanism and therefore they crossed tmbim5 mutants with mcu KO fish. But from the data presented in Fig.3 and as concluded by the authors themselves tmbim5 mutants do not show changes in the mitochondrial Ca2+ levels. Authors may clarify this point.
3. Does tmbim5 contributes to mitochondrial Ca2+ uptake in presence or along with MCU. Further analysis of Fig4C may shed some light on this. Authors should test significance between tmbim5-/- and WT as well as between tmbim5-/- and tmbim5+/+ in mcu-/- background.
4. Please check the labeling on traces in Fig3D.
5. Please include quantitation of data presented in EV2E-F.
6. Please include quantitation of immunohistochemistry data presented in 2E-H.

Referee cross-commenting

Several comments are common between the reviewers highlighting that those experiments are critical. Secondly, I agree with the concerns raised by other two reviewers.

Significance

In this study, authors report couple of new transgenic zebrafish lines. However, further characterization of slc8b1-/- is required. This study reinforces the existing idea that there are very robust compensatory mechanisms that maintain mitochondrial Ca2+ homeostasis. While the work provides useful insights, it could benefit from a broader scope to provide substantial advancement to existing knowledge.

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Referee #2

Evidence, reproducibility and clarity

Summary: The work of Wasilewska et al. focusses on the MCU independent basal Ca2+ uptake mechanisms and the effects of MCU, NCLX, and TMBIM5 KO on Zebrafish Ca2+ homeostasis, mortality, anatomy and metabolism. The authors found evidence that tmbim5 potentially has a bidirectional mode of operation and is able to extrude Ca2+ from the matrix as well as transfer Ca2+ into mitochondria. Further, a reduced membrane potential in tmbim5-/- fish and altered metabolism was found. While the conclusion drawn are well argumented, a few points have to be addressed.

Major Points:

1. While all mitochondrial genes seem collectively reduced compared to control, it would be interesting to assess the mitochondrial mass and/or mitochondrial turnover rate in regard to e.g. mitophagy. The reduced membrane potential could lead to PINK1 accumulation on the outer mitochondrial membrane to mediate mitophagy leading overall to reduced mitochondrial count and mass.
2. The characterization of slc8b1-KO fish needs some improvement to facilitate a better understanding of the molecular interactions of slc8b1 and tmbim5. This would also greatly improve the understanding of the phenotypical characterization and behavioral response to CGP.
3. Functional Ca2+ measurements of the activity of slc8b1 gene product have to be done to ensure a KO phenotype. Especially in light of the surprising results presented in Figure 6A showing an effect of CGP on slc8b1-KO fish but not on tmbim5-KO fish I advise mitochondrial isolation to conduct mitochondrial basal and extrusion Ca2+experiments of slc8b1-KO fish, tmbim5-KO fish, and double KO-fish.

Minor Points:

The authors claim that mRNA levels of mitochondrial proteins involved in Ca2+ transport in tmbim5-/- are unaffected (Figure EV3). While the T-tests show no significant alteration, what happens if a 2-way ANOVA shows a more general effect revealed between WT and TMBIM5-/-?

Significance

This is a well-designed and carefully executed piece of work. The experimental design is thoughtfully elaborated, and the topic is worthy of investigation. The strengths of this study lie in translating our knowledge of TMBIN5 from single cells to organism and organ function. Moreover, the work provides important new information that will help the scientific community working on mitochondrial regulation AND muscle diseases to understand how ions coordinately regulate mitochondrial function.

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Referee #1

Evidence, reproducibility and clarity

Although the experimental approach is promising (see below), the results do not significantly expand our current understanding. This is partly due to the challenges of interpreting negative results, which are nonetheless worth reporting. Some of the conclusions and interpretations of the results could benefit from further clarification and contextualization to enhance their impact:

• Figure 1D: The distribution of fiber size in wt vs. Tmbim5-ko fish shows a notable difference limited to one size range. Can the authors clarify this observation? Could this indicate a switch in fiber type? Is there a correlation between this finding and the differential PAS staining?
• Figure 3: one of the advantages of the zebrafish model is its transparency, allowing for fluorescence imaging. Unfortunately, this proves to be impossible in the case of cepia2mt. The data provided by the authors show that the fluorescence of this probe does not vary following physiological stimuli. The only change is that induced by CCCP (Fig 3C-D), which according to the authors causes a discharge of mitochondrial calcium. However, the use of CCCP with GFP-based probes should be avoided, as the acidification caused by CCCP treatment leads to quenching of the fluorophore, resulting in a fluorescence decrease which is independent of Ca2+ levels. Although the experimental approach aims to detect dynamic changes in mitochondrial Ca2+ levels, the presented results in Figure 3 do not provide conclusive evidence to support this capability. While significant experimental effort is evident, these findings may require further validation or additional data to strengthen their impact. Alternatively, the authors could remove this Figure 3 and relevant text from the manuscript.
• Figure 6A: In my opinion, this dataset is impossible to understand. To my knowledge, the precise molecular target of CGP-37157 remains elusive. While CGP is often considered an NCLX inhibitor, this classification lacks definitive experimental support. Although CGP is known to inhibit mitochondrial Na+-dependent Ca2+ extrusion, direct binding of CGP to NCLX has yet to be conclusively demonstrated. With this in mind, the authors show that pharmacological intervention with CGP elicits a distinct phenotype in the fish model. While this effect appears to persist in SLC8B1-KO fish, it is absent in Tmbim5-KO fish, suggesting Tmbim5 as a potential molecular target for CGP. However, this interpretation is inconsistent with the following observations: i) CGP remains effective in Tmbim5/Slc8b1 double-KO fish and ii) Tmbim5-KO fish exhibit no discernible phenotype. A comprehensive explanation that reconciles these findings is sought.
• Figure 6B: according to the authors, the phenotype induced by CGP treatment is specific because a different substance with a completely different effect, CCCP, causes the same phenotype in both wt and Tmbim5-KO fish. Also in this case, the rationale and reasoning behind this experiment in not very evident. As I see it, CCCP blocks zebrafish motility because it is a metabolic poison, and its effect does not depend on any transporter.

Significance

The manuscript submitted by Wasilewska et al investigates the functional relationship between different mitochondrial calcium transporters using zebrafish as a model. The topic is of great interest. In the last 15 years, many mitochondrial calcium transporters have been identified. In some cases, their mechanism is not fully understood, such as in the case of TMBIM5, recently described by some as an H/Ca exchanger, or as a Ca channel by others. Furthermore, the functional relationship between different transporters has so far been studied in a partial and superficial way. I believe that this work is therefore of great interest because it aims to contribute to a fundamental problem that is still poorly studied. The idea of using zebrafish is interesting, as it is an organism that is easy to manipulate and phenotype, and because it is transparent, making it possible to use specific biosensors to characterize mitochondrial calcium dynamics, at least in principle. The paper therefore deserves attention.

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Reply to the reviewers

We thank the reviewers for their helpful comments and suggestions. Below you may find the point-by-point replies to their concerns.

Reviewer #1

“The research is meticulously conducted, and the data are compelling, as they demonstrate that the Nova-agrin-Lrp4-MuSK axis is also operational in non-vertebrates. The conclusions drawn by the authors are generally adequate; however, I find some instances of "it is the first time..." to be unnecessary.”

We have removed all unnecessary claims to that effect.

“The work also presents an unexpected finding that mouse Nova protein is unable to splice the Ciona agrin mini-gene (Figure 3). I believe the inability of mouse Nova1 and Nova2 to splice the Ciona agrin could also be due to insufficient expression levels of the mouse proteins. Therefore, the authors should include either a positive control (e.g., mouse agrin mini-gene) or demonstrate that the proteins are expressed at comparable levels.”

We have now included two additional datasets supporting our conclusion. First, we have included the positive control with the mouse Agrin minigene as suggested by the reviewer, which shows that mouse Nova1 and Nova2 are indeed still able to splice the mouse Agrin minigene in our assay (Figure 3C). Second, we included fluorescence images of the GFP-fused mouse Nova1 and Nova2 showing their proper expression in the cells (Figure S7).

“I am also not fully convinced that the model of autoinhibition for Ciona Nova is supported by sufficient experimental data. Again, there are no data showing that the levels of the various deletion mutants of Nova are consistent and hence, there could be issues with the stbsility of some of the deletion mutants and this could explain the observed difference in activity.”

We have added a few more datasets to further investigate the model. First, we have added an independent biological replicate of the “MLN” Nova isoform deletion mutant assays (Figure S8), as well as a separate assay using deletion mutants based on the “MMM” isoform (Figure S9). The results were consistent in both cases, confirming our initial observations. Next, we tested more directly the idea proposed by the reviewer that there are issues with stability, by looking at the fluorescence of the GFP-fused mutants. We did notice that the N/C-terminal deletion mutants were not expressed as well, but this was always mitigated by concurrent deletion of the KH3 domain. We have now expanded our discussion in the text to propose that there may be a negative effect of the KH3 domain on Nova expression/stability in the absence of the N/C termini. Although different from the model in which KH3 directly inhibits KH1/KH2, there does seem to be some inhibitory effect of KH3 on Nova expression/stability. “- In all schematic presentations, exon Z6 appears larger than exon Z5. However, Z6 is only 24 bp long, while Z5 is 3434 bp long. Please adjust this representation.”

To clarify, in Ciona Z6 is 18 bp long, and Z5 is 15 bp long, hence they code for 6 and 5 amino-acids, respectively. This is different from the mammalian Z exons, which may be the source of the confusion here. In our schematics, we are only representing the Ciona Z exons.

“- Is there consistency in the relative proportions of the 24-bp (Z6), 33-bp (Z5), and 57-bp (Z6 + Z5) PCR products? Studies in vertebrates have shown that AChR clustering activity is highest with the Z8 and Z19 products, while the Z11 product appears to be somewhat less active. It would be nice to also point out the different splice products are detected in Ciona.”

It was not clear if there was any consistency in the relative proportions of Ciona Agrin splice products in the minigene assays as performed in cultured mammalian cells, though in Figure 1 we have pointed out a more detailed characterization of the different splice products in vivo in Ciona. The different splice products’ confirmed sequences are also shown in the supplemental sequences file.

“Line 111: 'Z11' Agrin should be corrected to 'Z19' Agrin.”

To clarify again, we are only referring to the Ciona Agrin Z exons, which are not the same sizes as the mammalian Z exons. While Z19 would refer to the combination of exons Z8 and Z11 (8+11 = 19) in mammals, here in Ciona the equivalent combination is Z11 (Z5 + Z6).

“Line 168: "Figure H" should be updated to "Figure 2H."”

Fixed.

Reviewer #2:

__*“44 - ALS, references 8-12. These are old papers. A new review should be cited, either instead of in addition.”

*__

We have read some newer reviews and cite three more recent reviews (references 10-12) now.

__* 56 - "many" cases of CMS - some are not due to mutations in this pathway

*__

We have altered this to say “many”.

__* 57 - refs 29-46. This is a very large number of references for a point this is quite unimportant to the story. It would be better to cite recent reviews.

*__

We have removed some references and also cited more recent reviews here (references 38, 39).

__* 168 - should be 2H

*__

Fixed.

__* 205 - make N terminal extension more apparent in Figure 3D

*__

We have recolored the N terminus to be red, as to make it more apparent, in figures 3 and S8 and S9.

__* 235 - not a complete sentence

*__

Fixed.

308+ - can the authors clarify whether EBF knockdown has a selective effect on Nova vs general failure of the neurons to acquire a MN phenotype

We have been investigating this in a separate study on MN specification and differentiation in Ciona, which will be published as a preprint soon. EBF does not have a selective effect on Nova expression, as it appears to be regulating multiple aspects of neuronal differentiation, consistent with its role as previously studied in Ciona and other organisms (e.g. Kratsios et al. 2012, Catela et al. 2019, etc).__*

614 - explain in figure legend the decrease in apparent MR from left to right in 4B

*__

This is just an example of “bowed” or “curved” bands frequently seen in electrophoresis, usually due to uneven heat dissipation or other electrophoresis issues. However, the bands all correspond to the same products (Z+). We added an explanation in the legend.

General - three other key components of the pathway are MuSK, rapsyn, and DOK-7. Functional studies of these genes fall beyond the scope of this paper, but it would be helpful to know whether they are expressed in muscle and, if so, whether expression is muscle-specific.

We have added this to the discussion. While Musk and Dok-7 remain unstudied in Ciona, it has been shown that Rapsyn is muscle-specific in Ciona (Nishino et al. 2011).

Reviewer #3:

__*“1) The authors report two main Nova isoforms that seem to be produced by alternative promoters. They also claim that the MLN isoform is more strongly expressed in two of the studied conditions compared to the MMM protein (eggs and heart in Fig 1G), while both are equally abundant in st. 22.5 embryos and brain (Fig S1 and line 130). Therefore, both isoforms are likely involved in the regulation of the Agrin AS event. When performing the experiments that require to express the Nova protein, the authors choose to work with the "MLN" isoform arguing that it is more "ubiquitous" than the "MMM" isoform, although the last has a more evident nuclear localization signal (NLS) sequence. In the minigene analysis, the MLN isoform fails to produce transcripts with Z6 exon (which seems to be the most common Z+ isoform in the brain), and the amount of Z11-containing transcripts is very low compared to st. 22.5. Given that the N-terminal domain has a regulatory influence, as demonstrated by the authors, and that the MMM isoform is potentially more "neural-restricted" than the MLN, an intriguing possibility is that the MMM isoform might enhance the inclusion of Z6 and Z11 isoforms. To solve this issue, I suggest two experiments:

• Perform the minigene assay with the MMM isoform of Nova and the wild type version of the minigene to check the level of inclusion of Z6 and Z6+Z5 (Z11) exons.*__”

We have added additional minigene assay data using the MMM isoform (S9). We did not detect Z6 isoforms with MMM, though there may be slight differences in the ratio of Z5 and Z11 compared to the MLN assay. We believe this indicates that nuclear localization is not rate-limiting in our heterologous mammalian cell minigene assay, although it very well may regulate splicing activity more meaningfully in vivo in Ciona. This may be especially true in post-mitotic cells, as opposed to during embryogenesis when actively proliferating cells will break down and then reconstitute their nuclear envelopes over and over again, thus potentially allowing some of the MLN isoform to find its way into the nucleus. We still believe the production of the Z6 isoform may depend on additional Ciona-specific factors missing from the mammalian cells in our heterologous assay.

“- Test the regulatory activity of the upstream genomic region of exon 1a, in an equivalent way as for exon 1b in Fig 7A and B, to explore whether the promoter of the MMM isoform has a neural-restricted expression that could explain the AS pattern observed in st. 22.5 and brain.” We have done this, shown in Figure S15, which revealed that the promoter upstream of exon 1a (encoding the MMM isoform) drives only expression in mesenchyme and some epidermal cells, with no neuronal expression visible. This suggests that the majority of the neural expression is due to the cis-regulatory elements in the region between exons 1a and 1b. However, this region does not necessarily activate transcription only at exon 1b (encoding MLN isoform), as intronic elements can loop back and regulate transcription off “upstream” promoters. Thus we propose that the Nova [1b] -2011/+6 region drives expression of both MLN and MMM isoforms, though this remains to be fully tested. We believe the regulation and function of the different Nova isoforms in Ciona is beyond the scope of the current paper, though we are interested in investigating this more thoroughly in follow-up studies.

__*“2) The authors unveil the conservation of an Agrin AS event between mammals and a tunicate species with similar functional consequences for AChR clustering. While this is absolutely correct, the relatively low similarity of the AS exons between Ciona and mammals shown in Fig 1A may raise confusion or doubts in the readers regarding the homology of the event (as it did in my own case before I checked it in more detail). Therefore, an explicit alignment of both constitutive and alternative exons in a supplementary figure to clearly demonstrate the homology of the AS event across major taxonomic groups (with a few vertebrate and tunicate species) might help.

Furthermore, expression of Nova in motor neurons of amphioxus (Branchiostoma lanceolatum) was previously reported (ref. 60), and a quick look into publicly available Agrin transcripts (____https://www.ncbi.nlm.nih.gov/gene/136443694____) reveals a homologous AS event in this cephalochordate species.

C1 "Z7/Z6/Z8" C2 (partial)

Bla QADPAPLRQEGVG--LDGTTILNYPNAINK ... E-SNSIRE ... QEPNQDDNHFEVTFRTTSDHGLLLWNHKPGGG-DFIALAI Cro HSTDLLQDEQATAIYLDGTTKIMYRNAVKA ... --PNDFRE ... SRART-HNNYEIVFRTTARHGLLLMVGKAREGVDYIALAI Mmu IVEKSVGDLETLA--FDGRTYIEYLNAVTE ... ELTNEIPA ... EKALQ-SNHFELSLRTEATQGLVLWIGKVGERADYMALAI : . :** * : * **:. .*.: ... *::*: :** : :**:* * *::****

These two facts suggests a potential origin of the Nova-Agrin regulation at the base of the chordate phylum (and not restricted to Olfactores), which could be mentioned in the discussion as a relevant possibility.*__”

We thank the reviewer for this suggestion. Indeed, we have now added a more detailed alignment with Agrin sequences from more species in Figures S2 and S3, including amphioxus as so helpfully identified by the reviewer. We have added the observation that amphioxus Agrin appears to have a single Z exon encoding the NxI/V motif (no evidence for two Z exons as in tunicates or vertebrates). This indeed suggests that this pathway may be a chordate innovation, as we now discuss. We also add AlphaFold-assisted predictions of the NxF motif binding to the equivalent pocket in Lrp4 in both Ciona and mammals (Figure S1).

Line 168: Figure 2H instead of Figure H.

Fixed.

Line 287: "Taken together, these results reveal that a Nova-Agrin-Lrp4 pathway for AChR receptor clustering at the neuromuscular synapse is conserved from mammals to tunicates." While this sentence might be true, from mammals to tunicates might imply that it is conserved in all vertebrate and tunicate lineages, and this is not explored in the manuscript (there might be secondary losses). It would be more technically correct to say something similar like "...the neuromuscular synapse is conserved in the studied mammalian and tunicate lineages" or "...the neuromuscular synapse originated before the evolutionary divergence of tunicates and vertebrates"

We have fixed this now in a few places.

“Line 342. At the end of this paragraph, the possibility of conservation of the mechanism also in amphioxus could be discussed.”

We now discuss the amphioxus sequence and the idea that this mechanism was present in the last common chordate ancestor.

“Line 383: "the the apparent".”

Fixed.

“I agree that the mouse-specific agrin minigene to test the functionality of Nova1 and Nova2 would be a suitable positive control to discard protein stability/expression issues.”

We have tested this now with GFP fusion images (Figure S7) and using the mouse Agrin minigene (Figure 3C). Both indicate proper expression/splicing activity of mouse Nova1 and Nova2, supporting the idea that there is still some type of cross-species incompatibility as tested in mammalian cells.

“The only minor limitation, in my opinion, is that it lacks testing of the MMM Nova isoform in the minigene assay, to explore whether it has (or not) a complementary function to the MLN isoform that could fully explain the endogenous AS pattern.”

We have added MMM minigene assays, and these were largely identical to MLN assays. We propose that the N-terminus and nuclear localization do not significantly impact activity of Ciona Nova as tested in mammalian cells, however we cannot exclude the possibility that things may be different in vivo in Ciona.

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Referee #3

Evidence, reproducibility and clarity

Summary: The manuscript reports the conservation of the Nova-Agrin-Lrp4 pathway for AChR clustering in neuromuscular junctions beyond vertebrates, using the tunicate Ciona robusta as a model species. In addition, it also reveals Ebf as a key transcriptional activator of Nova in the motor neurons of Ciona. One of the main focuses of the work is the detailed study of an alternative splicing event in the Agrin gene of Ciona, demonstrating its regulation by Nova and the developmental cascade of consequences in AChR clustering due to misregulation of the Nova-Agrin-Lrp4 pathway through multiple functional experiments. Furthermore, it also explores molecular elements involved in the regulation of this event in trans and cis, including the KH and N-terminal domains of Nova (and their interactions) and the intronic YCAY binding domains.

Major comments: The claims and conclusions of the manuscript are generally very well supported with appropriate and reproducible functional experiments. For instance, the work demonstrates a key regulatory link between Nova and the studied AS event of Agrin using both a minigene system in human cells and a set of CRISPR/Cas9 Ciona mutants. Although analyzing mosaic embryos can be challenging, the authors successfully test different combinations of gRNAs to achieve efficient mutagenesis. Moreover, using the AChRA1::GFP clusters to measure the impact of the different mutants is very convincing.

While generally very robust and satisfying, the manuscript could benefit from addressing a few issues to improve its quality:

1. The authors report two main Nova isoforms that seem to be produced by alternative promoters. They also claim that the MLN isoform is more strongly expressed in two of the studied conditions compared to the MMM protein (eggs and heart in Fig 1G), while both are equally abundant in st. 22.5 embryos and brain (Fig S1 and line 130). Therefore, both isoforms are likely involved in the regulation of the Agrin AS event. When performing the experiments that require to express the Nova protein, the authors choose to work with the "MLN" isoform arguing that it is more "ubiquitous" than the "MMM" isoform, although the last has a more evident nuclear localization signal (NLS) sequence. In the minigene analysis, the MLN isoform fails to produce transcripts with Z6 exon (which seems to be the most common Z+ isoform in the brain), and the amount of Z11-containing transcripts is very low compared to st. 22.5. Given that the N-terminal domain has a regulatory influence, as demonstrated by the authors, and that the MMM isoform is potentially more "neural-restricted" than the MLN, an intriguing possibility is that the MMM isoform might enhance the inclusion of Z6 and Z11 isoforms. To solve this issue, I suggest two experiments:
   • Perform the minigene assay with the MMM isoform of Nova and the wild type version of the minigene to check the level of inclusion of Z6 and Z6+Z5 (Z11) exons.
   • Test the regulatory activity of the upstream genomic region of exon 1a, in an equivalent way as for exon 1b in Fig 7A and B, to explore whether the promoter of the MMM isoform has a neural-restricted expression that could explain the AS pattern observed in st. 22.5 and brain.
2. The authors unveil the conservation of an Agrin AS event between mammals and a tunicate species with similar functional consequences for AChR clustering. While this is absolutely correct, the relatively low similarity of the AS exons between Ciona and mammals shown in Fig 1A may raise confusion or doubts in the readers regarding the homology of the event (as it did in my own case before I checked it in more detail). Therefore, an explicit alignment of both constitutive and alternative exons in a supplementary figure to clearly demonstrate the homology of the AS event across major taxonomic groups (with a few vertebrate and tunicate species) might help.

Furthermore, expression of Nova in motor neurons of amphioxus (Branchiostoma lanceolatum) was previously reported (ref. 60), and a quick look into publicly available Agrin transcripts (https://www.ncbi.nlm.nih.gov/gene/136443694) reveals a homologous AS event in this cephalochordate species.

              C1                   "Z7/Z6/Z8"            C2 (partial)

Bla QADPAPLRQEGVG--LDGTTILNYPNAINK ... E-SNSIRE ... QEPNQDDNHFEVTFRTTSDHGLLLWNHKPGGG-DFIALAI Cro HSTDLLQDEQATAIYLDGTTKIMYRNAVKA ... --PNDFRE ... SRART-HNNYEIVFRTTARHGLLLMVGKAREGVDYIALAI Mmu IVEKSVGDLETLA--FDGRTYIEYLNAVTE ... ELTNEIPA ... EKALQ-SNHFELSLRTEATQGLVLWIGKVGERADYMALAI : . : * : * :. ..: ... ::: : : :: * ::***

These two facts suggests a potential origin of the Nova-Agrin regulation at the base of the chordate phylum (and not restricted to Olfactores), which could be mentioned in the discussion as a relevant possibility.

Minor comments:

Line 168: Figure 2H instead of Figure H.

Line 287: "Taken together, these results reveal that a Nova-Agrin-Lrp4 pathway for AChR receptor clustering at the neuromuscular synapse is conserved from mammals to tunicates." While this sentence might be true, from mammals to tunicates might imply that it is conserved in all vertebrate and tunicate lineages, and this is not explored in the manuscript (there might be secondary losses). It would be more technically correct to say something similar like "...the neuromuscular synapse is conserved in the studied mammalian and tunicate lineages" or "...the neuromuscular synapse originated before the evolutionary divergence of tunicates and vertebrates"

Line 342. At the end of this paragraph, the possibility of conservation of the mechanism also in amphioxus could be discussed.

Line 383: "the the apparent".

Referees cross-commenting

I agree that the mouse-specific agrin minigene to test the functionality of Nova1 and Nova2 would be a suitable positive control to discard protein stability/expression issues.

Significance

General assessment: This manuscript describes and demonstrates the deep evolutionary origin of a complex molecular pathway in the neuromuscular synapses of chordates. This work takes advantage of the broad genetic tools available in the tunicate Ciona robusta to support its main claims rigorously and strongly with a focused set of functional experiments. Moreover, it expands the known pathway revealing an upstream regulator of Nova in Ciona (Ebf) and opening a new research line in vertebrate motor neurons. The only minor limitation, in my opinion, is that it lacks testing of the MMM Nova isoform in the minigene assay, to explore whether it has (or not) a complementary function to the MLN isoform that could fully explain the endogenous AS pattern. Nevertheless, the current version of the manuscript is sufficiently robust to sustain its main conclusions.

Advance: Previous studies have reported deeply conserved AS events regulated by homologous tissue-specific splicing factors suggesting a putative similar function, such as the case of Esrp regulating the splicing of FGFRs in amphioxus and vertebrates (Burguera et al. 2017). However, to my knowledge, this work is the first to analyse the functional conservation of an alternative splicing event between chordate clades in its endogenous context while demonstrating an homologous ontogenetic role. In addition, it provides new insights of the molecular interactions between the N-terminal and KH domains of Nova and how they bind to the NISE elements in the Agrin pre-mRNA.

Audience: I consider this work interesting for a substantially broad audience, given that it reveals a surprisingly deep conservation of a molecular pathway across chordate lineages that is essential for the proper establishment of neuromuscular synapses. Thus, this study is imaginably interesting for evolutionary and molecular biologists, physiologists and even biomedical researchers that might be interested to explore a potential regulatory connection between Ebf genes and Nova in human motor neurons.

Fields of expertise: evo-devo, alternative splicing, chordates, transcriptomic and genome evolution.

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Referee #2

Evidence, reproducibility and clarity

Summary: Formation of the postsynaptic apparatus at the mammalian skeletal neuromuscular junction is controlled by a signaling pathway in which NOVA-mediated splicing generates an active form of the proteoglycan agrin (z-agrin), which is released from motoneurons, and interacts with LRP4 in muscle, leading to clustering of acetylcholine receptors beneath the nerve termina. This delightful paper demonstrates striking conservation of the pathway in the non-vertebrate chordate Ciona robusta, and also reveals some striking differences.

Major comments: none

Minor comments:

44 - ALS, references 8-12. These are old papers. A new review should be cited, either instead of in addition.

56 - "many" cases of CMS - some are not due to mutations in this pathway

57 - refs 29-46. This is a very large number of references for a point this is quite unimportant to the story. It would be better to cite recent reviews.

168 - should be 2H

205 - make N terminal extension more apparent in Figure 3D

235 - not a complete sentence

308+ - can the authors clarify whether EBF knockdown has a selective effect on Nova vs general failure of the neurons to acquire a MN phenotype

614 - explain in figure legend the decrease in apparent MR from left to right in 4B

General - three other key components of the pathway are MuSK, rapsyn, and DOK-7. Functional studies of these genes fall beyond the scope of this paper, but it would be helpful to know whether they are expressed in muscle and, if so, whether expression is muscle-specific.

Significance

The paper is complete, and the results are compelling, nicely explained, and carefully documented. My comments are minor.

It provides an interesting example of ways in which a pathway for synaptic development is conserved across distant vertebrate species, as well as ways inhich it is modified. I know of no other papers that do this.

Audience: basic research interested in neuroscience, evolution and development

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Referee #1

Evidence, reproducibility and clarity

This manuscript examines the role of the splicing factor Nova in Ciona robusta, a tunicate that is the closest relative to vertebrates. The authors demonstrate the co-expression of Agrn and Nova mRNA during development in motor neurons, highlighting the correlative appearance of Nova-spliced exons Z6 and Z5. Importantly, CRISPR/Cas9-mediated inhibition of agrin splicing, deletion of its receptor Lrp4, and loss of Nova result in a significant reduction in the number of motor neuron-muscle synapses. This finding supports the notion that neuromuscular synapse formation is similarly regulated in non-vertebrates as it is in vertebrates. The authors subsequently investigate the domains within Nova responsible for agrin splicing and identify the transcription factor Ebf as a regulator of Nova expression in motor neurons.

The research is meticulously conducted, and the data are compelling, as they demonstrate that the Nova-agrin-Lrp4-MuSK axis is also operational in non-vertebrates. The conclusions drawn by the authors are generally adequate; however, I find some instances of "it is the first time..." to be unnecessary.

The work also presents an unexpected finding that mouse Nova protein is unable to splice the Ciona agrin mini-gene (Figure 3). I believe the inability of mouse Nova1 and Nova2 to splice the Ciona agrin could also be due to insufficient expression levels of the mouse proteins. Therefore, the authors should include either a positive control (e.g., mouse agrin mini-gene) or demonstrate that the proteins are expressed at comparable levels.

I am also not fully convinced that the model of autoinhibition for Ciona Nova is supported by sufficient experimental data. Again, there are no data showing that the levels of the various deletion mutants of Nova are consistent and hence, there could be issues with the stbsility of some of the deletion mutants and this could explain the observed difference in activity.

Minor Points:

• In all schematic presentations, exon Z6 appears larger than exon Z5. However, Z6 is only 24 bp long, while Z5 is 3434 bp long. Please adjust this representation.
• Is there consistency in the relative proportions of the 24-bp (Z6), 33-bp (Z5), and 57-bp (Z6 + Z5) PCR products? Studies in vertebrates have shown that AChR clustering activity is highest with the Z8 and Z19 products, while the Z11 product appears to be somewhat less active. It would be nice to also point out the different splice products are detected in Ciona.
• Writing errors:

Line 111: 'Z11' Agrin should be corrected to 'Z19' Agrin.

Line 168: "Figure H" should be updated to "Figure 2H."

Referees cross-commenting

In my view, the other reviews provide interesting insights that will further strengthen the manuscript.

Significance

This manuscript examines the role of the splicing factor Nova in Ciona robusta, a tunicate that is the closest relative to vertebrates. The authors demonstrate the co-expression of Agrn and Nova mRNA during development in motor neurons, highlighting the correlative appearance of Nova-spliced exons Z6 and Z5. Importantly, CRISPR/Cas9-mediated inhibition of agrin splicing, deletion of its receptor Lrp4, and loss of Nova result in a significant reduction in the number of motor neuron-muscle synapses. This finding supports the notion that neuromuscular synapse formation is similarly regulated in non-vertebrates as it is in vertebrates. The authors subsequently investigate the domains within Nova responsible for agrin splicing and identify the transcription factor Ebf as a regulator of Nova expression in motor neurons.

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Reply to the reviewers

Note : The original preprint version of our manuscript has been reviewed by 3 subject experts for Review Commons. All the three reviewers’ comments on the original version of our manuscript have been fully addressed. Their input was extremely valuable in helping us clarify and refine the presentation of our results and conclusions. Their feedback contributed to making the study both more thoroughly developed and more accessible to a broad readership, while preserving its mechanistic depth. We believe that this revised version more effectively highlights the conceptual advances brought by our findings.

Reviewer #1

Evidence, reproducibility and clarity

The manuscript "Key roles of the zona pellucida and perivitelline space in promoting gamete fusion and fast block to polyspermy inferred from the choreography of spermatozoa in mice oocytes" by Dr. Gourier and colleagues explores the poorly understood process of gamete fusion and the subsequent block to polyspermy by live-cell imaging of mouse oocytes with intact zona pellucida in vitro. The new component in this study is the presence of the ZP, which in prior studies of live-cell imaging had been removed before. This allowed the authos to examine contributions of the ZP to the block in polyspermy in relation to the timing of sperm penetrating the ZP and sperm fusing with the oocyte. By carefully analysing the timing of the cascade of events, the authors find that the first sperm that reaches the membrane of the mouse oocyte is not necessarily the one that fertilizes the oocytes, revealing that other mechanisms post-ZP-penetration influence the success of individual sperm. While the rate of ZP penetration remains constant in unfertilized oocytes, it decreases upon fertilization for subsequent sperm, providing direct evidence for the known 'slow block to polyspermy' provided by changes to the ZP adhesion/ability to be penetrated. Careful statistical analyses allow the authors to revisit the role of the ZP in preventing polyspermy: They show that the ZP block resulting from the cortical reaction is too slow (in the range of an hour) to contribute to the immediate prevention of polyspermy in mice. The presented analyses reveal that the ZP does contribute to the block to polyspermy in two other ways, namely by effectively limiting the number of sperm that reach the oocyte surface in a fertilization-independent manner, and by retaining components like JUNO and CD9, that are shed from the oocyte plasma membrane after fertilization, in the perivitelline space, which may help neutralize surplus spermatozoa that are already present in the PVS. Lastly, the authors report that the ZP may also contribute to channeling the flagellar oscillations of spermatozoa in the PVS to promote their fusion competence.

Major comments:

• Are the key conclusions convincing?

The authors provide a careful analysis of the dynamics of events, though the analyses are correlative, and can only be suggestive of causation. While this is a limitation of the study, it provides important analysis for future research. Moreover, by analysing also control oocytes without fertilization and the timing of events, the authors have in some instances clear 'negative controls' for comparison.

Some claims would benefit from rewording or rephrasing to put the findings better in the context of what is already known and what is novel:

• the phrasing 'challenging prior dogma' might be too strong since it had been observed before that it is not necessarily the first sperm that gets through the ZP that fertilizes the egg (though I am afraid that I do not have any citations or references for this). However, given that in the field people generally think it is not necessarily and always the first sperm, the authors may want to consider weakening this claim.

Only real-time imaging of in vitro fertilization of zona pellucida-intact oocytes, as performed in our study, is capable of determining which spermatozoon crossing the zona pellucida fuses with the oocyte. However, such studies are rare, and most do not specifically address this question. As Reviewers 1 & 3, we have not found any citation or reference telling or showing that it is not necessarily the first spermatozoon to penetrate the zona pellucida that fertilizes the egg. In contrast, at least one reference (Sato et al., 1979) explicitly reports the opposite. If, as suggested by Reviewer 1 and 3, it has indeed been observed before that the first sperm to pass the ZP is not always the one that fertilizes, and if this idea is generally accepted in the field, then it is all the more important that a study demonstrates and publishes this point. This is precisely what our study makes possible. However, in case we may have overlooked a previous reference making the same observation as ours, we have removed the phrasing ‘challenging prior dogma’. That being said, the key issue is not so much that it is not necessarily the first spermatozoon penetrating the perivitelline space that fertilizes, but rather why spermatozoa that successfully reach the PVS of an unfertilized oocyte may fail to achieve fertilization. This is one of the central questions our study sought to address.

• I do think the cortical granule release could still contribute to the block to polyspermy though - as the authors here nicely show - at a later time-point only, and thus not the major and not the immediate block as previously thought. The wording in the abstract should therefore be adjusted (since it could still contribute...)

We are concerned that we may disagree on this point. The penetration block resulting from cortical granule release progressively reduces the permeability of the zona pellucida to spermatozoa, relative to its baseline permeability prior to sperm–oocyte fusion. Any decrease in this baseline permeability occurring before the fusion block becomes fully effective can contribute to the prevention of polyspermy by limiting the number of sperm that can access the oolemma at a time when fusion is still possible. In contrast, once the fusion block is fully established, limiting the number of spermatozoa traversing the ZP becomes irrelevant regarding the block to polyspermy, as the fusion block alone is sufficient to prevent additional fertilizations, rendering the penetration block obsolete. The only scenario that could challenge this obsolescence is if the fusion block were transient. In that case, as Reviewer 1 suggests, the penetration block could indeed play a role at a later time-point. However, taken together, our study and that of Nozawa et al. (2018) support the conclusion that this is not the case in mice:

• Our in vitro study using kinetic tracking shows that the time constant for completion of the fusion block is typically 6.2 ± 1.3 minutes. During this time window, we observe that the permeability of the zona pellucida to spermatozoa does not yet decrease significantly from the baseline level it exhibited prior to sperm–oocyte fusion (see Figures 5B and S1B in the revised manuscript, and Figures 5A and 5B in the initial version). Consequently, before the fusion block is fully established, the penetration block can contribute only marginally—if at all—to the prevention of polyspermy. In contrast, the naturally low baseline permeability of the ZP—independent of any fertilization-triggered penetration block—as well as the relatively long timing of fusion ( minutes on average) after sperm penetration in the perivitelline space, are factors that contribute to the preservation of monospermic while the fusion block is still being established.
• Our in vitro study using kinetic tracking shows that once the fusion block is completed following the first fusion event, no additional spermatozoa are able to fuse with the oocyte until the end of the experiment, 4 hours post-insemination (see blue points and fitting curve in Figure 5C). Meanwhile, one or more additional spermatozoa—most of them motile and therefore viable—are present in the perivitelline space in 50% of the oocytes analyzed (purple point in Figure 5C). This demonstrates that, once established, the fusion block remains effective for at least the entire duration of the experiment, supporting the idea of a fully functional and long-lasting fusion block.
• Nozawa et al. (2018) found that female mice lacking ovastacin—the protease released during the cortical reaction that renders the zona pellucida impenetrable—are normally fertile. They additionally reported that the oocytes recovered from these females after mating are monospermic despite the systematic presence of additional spermatozoa in the perivitelline space. These findings further support the conclusion that in mice the fusion block is both permanent and sufficient to prevent polyspermy. For all these reasons, we believe that even at a later time-point, the penetration block does not contribute to the prevention of polyspermy in mice.

To clarify the fact that the penetration block does not necessarily contribute to prevent polyspermy, which indeed challenges the commonly accepted view, we have substantially revised the discussion. Furthermore, Figure 9 from the initial version of the manuscript has been replaced by Figure 8 in the revised version. This new figure provides a more didactic illustration of the inefficacy of the penetration block in preventing polyspermy in mice, by showing the respective impact of the fusion block, the penetration block, as well as fusion timing and the natural baseline permeability of the zona pellucida, on the occurrence of polyspermy.

As for the abstract, it has also been thoroughly revised. The content related to this section is now expressed in a way that emphasizes the factors that actively contribute to the prevention of polyspermy in mice, rather than those with no or marginal contribution (such as the penetration block in this case).

• release of OPM components - in the abstract it's unclear what the authors mean by this - in the results part it becomes clear. Please already make it clear in the abstract that it is the fertility factors JUNO/CD9 that could bind to sperm heads upon their release and thus 'neutralize' them? I would also recommend not referring to it as 'outer' plasma membrane (there is no 'inner plasma membrane'). Moreover, in the abstract please clarify that this release is happening only after fusion of the first sperm and not all the time. In the abstract it sounds as if this was a completely new idea, but there is good prior evidence that this is in fact happening (as also then cited in the results part) - maybe frame it more as the retention inside the PVS as new finding.

We thank reviewer 1 for pointing out the lack of precision in the abstract regarding the “components” released from the oolemma, and the fact that our phrasing may have given the impression that the post-fertilization release of CD9 and JUNO is a novel observation. The new observation is that CD9 and JUNO, which are known to be massively released from the oolemma after fertilization, bind to spermatozoa in the perivitelline space. However, we cannot rule out the possibility that other oocyte-derived molecules not investigated here may undergo a similar process. This is why we employed the broader term “components”, which encompasses both CD9 and JUNO as well as potential additional molecules. That said, we acknowledge the lack of precision introduced by this terminology. To address this, we have revised the corresponding sentence in the abstract to better reflect our new findings relative to previous ones, and to eliminate the ambiguity introduced by the word “component”.

The revised sentence of the abstract reads as follows:

“Our observation that non-fertilizing spermatozoa in the perivitelline space are coated with CD9 and JUNO oocyte’s proteins, which are known to be massively released from the oolemma after gamete fusion, supports the hypothesis that the fusion block involves an effective perivitelline space-block contribution consisting in the neutralization of supernumerary spermatozoa in the perivitelline space by these and potentially other oocyte-derived factors.”

Moreover, we cannot state in the abstract that the release of CD9 and JUNO occurs only after the fusion of the first spermatozoon and not before, since some CD9 and JUNO are already detectable in the perivitelline space (PVS) prior to fusion. What our study shows is that, before fertilization, CD9 and JUNO are predominantly localized at the oocyte membrane. In contrast, after fusion (four hours post-insemination), oocyte CD9 is distributed between the membrane and the PVS, and the only JUNO signal detectable in the oocyte is found in the PVS. This is what we describe in the Results section on page 15.

Regarding the acronym “OPM” in the initial version of the manuscript, although it was defined in the introduction as referring to the oocyte plasma membrane and not the outer plasma membrane (which, indeed, would not be meaningful), we acknowledge that it may have caused confusion to people in the field due to its resemblance to the commonly used meaningful acronym “OAM” for outer acrosomal membrane. To avoid any ambiguity, we have replaced the acronym “OPM” throughout the revised manuscript with the term “oolemma”, which unambiguously refers to the plasma membrane of the oocyte.

It is unclear to me what the relevance of dividing the post-fusion/post-engulfment into different phases as done in Fig 2 (phase 1, and phase 2) - also for the conclusions of this paper this seems rather irrelevant and overly complicated, since the authors never get back to it and don't need it (it's not related to the polyspermy block analyses). I would remove it from the main figures and not divide into those phases since it is distracting from the main focus.

Sperm engulfment and PB2 extrusion are two processes that follow sperm–oocyte fusion. As such, they are clear indicators that fusion has occurred and that meiosis has resumed. Their progression over time is readily identifiable in bright-field imaging: sperm engulfment is characterized by the gradual disappearance of the spermatozoon head from the oolemma, whereas PB2 extrusion is observed as the progressive emergence of a rounded protrusion from the oocyte membrane (Figure 2 in the initial manuscript and Figure S2 A&B in the revised version). The kinetics of these events, measured from the arrest of “push-up–like” movement of the sperm head against the oolemma —assumed to coincide with sperm-oocyte fusion, as further justified in a later response to Reviewer 1—provide reliable temporal landmarks for estimating the timing of fusion when the fusion event itself is not directly observed in real time (Figure S2 C&D).

The four landmarks used in this estimation are:

(i) the disappearance of the sperm head from the oolemma due to internalization (28 ± 2 minutes post-arrest, mean ± SD);

(ii) the onset of PB2 protrusion from the oolemma (28 ± 2 minutes post-arrest);

(iii) the moment when the contact angle between the PB2 protrusion and the oolemma shifts from greater than to less than 90° (49 ± 6 minutes post-arrest);

(iv) the completion of PB2 extrusion (73 ± 10 minutes post-arrest).

The approach used to determine the fusion time window of a fertilizing spermatozoon from these landmarks is detailed in the “Determination of the Fertilization Time Windows” section of the Materials and Methods. Compared to the initial version of the manuscript, we have added a paragraph explaining the rationale for using the arrest of the push-up–like movement as a reliable indicator for sperm–oocyte fusion and have clarified the description of the approach used to determine fertilization timing.

The timed characterization of sperm engulfment and PB2 extrusion kinetics is highly relevant to the analysis of the penetration and fusion blocks, however we agree that its place is more appropriate in the Supplementary Information than in the main text. In accordance with the reviewer’s recommendation, this section has therefore been moved to the Supplementary Information SI2.

For the statistical analysis, I am not sure whether the assumption "assumption that the probability distribution of penetration or fertilization is uniform within a given time window" is in fact true since the probability of fertilizing decreases after the first fertilization event.... Maybe I misunderstood this, but this needs to be explained (or clarified) better, or the limitation of this assumption needs to be highlighted.

During in vitro fertilization experiments with kinetic tracking, each oocyte is observed sequentially in turn. As a result, sperm penetration into the perivitelline space or fusion with the oolemma may occur either during an observation round or in the interval between two rounds. In the former case, penetration or fusion is directly observed in real time, allowing for high temporal precision in determining the moment of the event. In contrast, when penetration or fusion occurs between two observation rounds, the precise timing cannot be directly determined. We can only ascertain that the event took place within the time window we have determined. Because, within a given penetration or fusion time window, we do not know the exact moment at which the event occurred, there is no reason to favor one time over another. This justifies the assumption that all time points within the window are equally probable. This explanation has been added in the section Statistical treatment of penetration and fertilization chronograms to study the kinetics of fertilization, penetration block and fusion block of the main text and in the section Statistical treatment of penetrations and fertilizations chronograms to study penetration and fusion blocks of the material and methods.

-Suggestion for additional experiments:

If I understood correctly, the onset of fusion in Fig 2C is defined by stopping of sperm beating? If it is by the sudden stop of the beating flagellum, this should be confirmed in this situation (with the ZP intact) that it correctly defines the time-point of fusion since this has not been measured in this set-up before as far as I understand. In order to measure this accurately, the authors will need to measure this accurate to be able to acquire those numbers (of time from fusion to end of engulfment), e.g. by pre-loading the oocyte with Hoechst to transfer Hoechst to the fusing sperm upon membrane fusion.

The nuclear dye Hoechst is widely used as a marker of gamete fusion, as it transfers from the ooplasm—when preloaded with the dye—into the sperm nucleus upon membrane fusion, thereby signaling the happening of the fusion event. This technique is applicable in the context of in vitro fertilization using ZP-free oocytes. However, it is not suitable when cumulus–oocyte complexes are inseminated, as is the case in both in vitro experimental conditions of the present study (standard IVF and IVF with kinetic tracking). Indeed, when cumulus–oocyte complexes are incubated with Hoechst to preload the oocytes, the numerous surrounding cumulus cells also take up the dye. Consequently, upon insemination, spermatozoa acquire fluorescence while traversing and dispersing the cumulus mass—before reaching the ZP—thus rendering Hoechst labeling ineffective as a specific marker of membrane fusion. This remains true even under optimized conditions involving brief Hoechst incubation of cumulus–oocyte complexes ( Nonetheless, we have strong evidence supporting the use of the arrest of sperm movement as a surrogate marker for the moment of fusion. In our previous study (Ravaux et al., 2016; ref. 4 in the revised manuscript), we investigated the temporal relationship between the abrupt cessation of sperm head movement on the oolemma—resulting from strong flagellar beating arrest—and the fusion event, using ZP-free oocytes preloaded with Hoechst. That study revealed a temporal delay of less than one minute between the cessation of sperm oscillations and the actual membrane fusion, thereby supporting the conclusion that in ZP-free oocytes, the arrest of vigorous sperm movement at the oolemma is a reliable indicator of the moment at which fusion occurs. In the same study, the kinetics of sperm head internalization into the ooplasm were also characterized, typically concluding within 20–30 minutes after movement cessation. These findings are fully consistent with our current observations in ZP-intact oocytes, where sperm head engulfment was completed approximately 24 ± 3 minutes after the arrest of sperm oscillations. Taken together, these results strongly support the conclusion that, in both ZP-free and ZP-intact oocytes, the arrest of sperm movement is a reliable indicator of the fusion event. This assumption formed the basis for our determination of fertilization time points in the present study.

These justifications were not fully detailed in the original version of the manuscript. We have addressed this in the revised version by explicitly presenting this rationale in the Materials and Methods section under Determination of the Fertilization Time Windows.

Fig 8: 2 comments

• To better show JUNO/CD9 pre-fusion attachment to the oocyte surface and post-fusion loss from the oocyte surface (but persistence in the PVS), an image after removal of the ZP (both for pre-fertilization and post-fertilization) would be helpful - the combination of those images with the ones you have (ZP intact) would make your point more visible.

We have followed this recommendation. Figure 8 of the initial manuscript has been replaced by Figure 6 in the revised manuscript, which illustrates the four situations encountered in this study: fertilized and unfertilized oocytes, each with and without unfused spermatozoa in their PVS. To better show JUNO/CD9 pre-fusion presence to the oocyte plasma membrane, as well as their post-fusion partial (for CD9) and near-complete (for JUNO) loss from the oocyte membrane (but persistence in the PVS), paired images of the same oocyte before and after of ZP removal are now provided, both for unfertilized (Figure 6A) and fertilized oocytes (Figure 6C).

• You show that the heads of spermatozoa post fusion are covered in CD9 and JUNO, yet I was missing an image of sperm in the PVS pre-fertilization (which should then not yet be covered).

As staining and confocal imaging of the oocytes were performed 4 hours after insemination, images of sperm in the PVS of an oocyte “pre-fertilization” cannot be strictly obtained. However, we can have images of spermatozoa present in the PVS of oocytes that remained unfertilized. This situation, now illustrated in Figure 6B of the revised manuscript, shows that these spermatozoa are also covered in JUNO and CD9, which they may have progressively acquired over time from the baseline presence of these proteins in the PVS of unfertilized oocytes. This also may provide a mechanistic explanation for their inability to fuse with the oolemma, and, consequently, for the failure of fertilization in these oocytes.

Minor comments:

• The videos were remarkable to look at, and great to view in full. However, for the sake of time, the authors might want to consider cropping them for the individual phases to have a shorter video (with clear crop indicators) with the most important different stages visible in a for example 1 min video (e.g. video.

We have followed this recommendation. The videos have been cropped and annotated in order to highlight the key events that support the points made in the result section from page 9 to 11 in the revised manuscript.

• In general, given that the ZP, PVS and oocyte membrane are important components, a general scheme at the very beginning outlining the relative positioning of each before and during fertilization (and then possibly also including the second polar body release) would be extremely helpful for the reader to orient themselves.

A general scheme addressing Reviewer 1 request, summarizing the key components and concepts discussed in the article and intended to help guide the reader, has been added to the introduction of the revised manuscript as Figure 1.

• first header results "Multi-penetration and polyspermy under in vivo conditions and standard and kinetics in vitro fertilization conditions" is hard to understand - simplify/make clearer (comparison of in vivo and in vitro conditions? Establishing the in vitro condition as assay?)

The title of the first Results section has been revised in accordance with Reviewer 1 suggestion. It now reads: Comparative study of penetration and fertilization rates under in vivo and two distinct in vitro fertilization conditions.

• Large parts of the statistical analysis (the more technical parts) could be moved to the methods part since it disrupts the flow of the text.

In the revised version of our manuscript, we have restructured this part of the analysis to ensure that more technical or secondary elements do not disrupt the flow of the main text. Accordingly, the equations have been reduced to only what is strictly necessary to understand our approach, their notation has been greatly simplified, and the statistical analysis of unfertilized oocytes whose zona pellucida was traversed by one or more spermatozoa has been moved to the Supplementary Information (SI1).

• To me, one of the main conclusions was given in the text of the results part, namely that "This suggests that first fertilization contributes effectively to the fertilization-block, but less so to the penetration block". I would suggest that the authors use this conclusion to strengthen their rationale and storyline in the abstract.

We agree with Reviewer 1 suggestion. Accordingly, we have not only thoroughly revised our abstract, but also the introduction and discussion, in order to better highlight the rationale of our study, its storyline, and the new findings which not only challenge certain established views but also open new research directions in the mechanisms of gamete fusion and polyspermy prevention.

• Wording: To characterize the kinetics with which penetration of spermatozoa in the PVS falls down after a first fertilization," falls down should be replaced with decreases (page 10 and page 12)

Falls down has been removed from the new version and replaced with decreases

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Significance

Overall, this manuscript provides very interesting and carefully obtained data which provides important new insights particularly for reproductive biology. I applaud the authors on first establishing the in vivo conditions (how often do multiple sperm even penetrate the ZP in vivo) since studies have usually just started with in vitro condition where sperm at much higher concentration is added to isolated oocyte complexes. Thank you for providing an in vivo benchmark for the frequency of multiple sperm being in the PVS. While this frequency is rather low (somewhat expectedly, with 16% showing 2-3 sperm in the PVS), this condition clearly exists, providing a clear rationale for the investigation of mechanisms that can prevent additional sperm from entering.

My own expertise is experimentally - thus I don't have sufficient expertise to evaluate the statistical methods employed here.

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Reviewer #2

Evidence, reproducibility and clarity

Overall, this is a very interesting and relevant work for the field of fertilization. In general, the experimental strategies are adequate and well carried out. I have some questions and suggestions that should be considered before the work is published.

1) Why are the cumulus cells not mentioned when the AR is triggered before or while the sperms cross it? It seems the paper assumes from previous work that all sperm that reach ZP and the OPM have carried out the acrosome reaction. This, though probably correct, is still a matter of controversy and should be discussed. It is in a way strange that the authors do not make some controls using sperm from mice expressing GFP in the acrosome, as they have used in their previous work.

We do not mention the cumulus cells or whether the acrosome reaction is triggered before, during, or after their traversal (i.e., upon sperm binding to the ZP), as this question, while scientifically relevant, pertains to a distinct line of investigation that lies beyond the scope of the present study. Even with the use of spermatozoa expressing GFP in the acrosome, addressing this question would require a complete redesign of our kinetic tracking protocol, which was specifically conceived to monitor in bright field the dynamic behavior of spermatozoa from the moment they begin to penetrate the perivitelline space of an oocyte. Accordingly, we imaged oocytes that were isolated 15 minutes after insemination of the cumulus–oocyte complexes, by which time most (if not all) cumulus cells had detached from the oocytes, as explained in the fourth paragraph of the material and methods of both the initial and revised versions of the manuscript. The spermatozoa we had access to were therefore already bound to the zona pellucida at the time of removal from the insemination medium, and had thus necessarily passed through the cumulus layer. It is unclear for us why Reviewer 2 believes that we “assume from previous work that all sperm that reach ZP has carried out the acrosome reaction”. We could not find any statement in our manuscript suggesting, let alone asserting, such an assumption, which we know to be incorrect. Based on both published work from Hirohashi’s group in 2011 (Jin et al., 2011, DOI: 10.1073/pnas.1018202108) and our own unpublished observation (both involving cumulus-oocyte masses inseminated with spermatozoa expressing GFP in the acrosome), it is established that only a subset of spermatozoa reaching the ZP after crossing the cumulus layer has undergone acrosome reaction. Moreover, from the same sources—as well as from a recent publication by Buffone’s group (Jabloñsky et al., 2023 DOI: 10.7554/eLife.93792 ) which is the one to which reviewer 2 refers in her/his 3rd comment, it is also well established that spermatozoa have all undergone acrosome reaction when they enter the PVS. To the best of our knowledge, this latter point has long been widely accepted and is not questioned. Therefore, stating this in the first paragraph of the Discussion in the revised manuscript, while referencing the two aforementioned published studies, should be appropriate. What remains a matter of ongoing debate, however, is the timing and the physiological trigger(s) of the acrosome reaction in fertilizing spermatozoa. The 2011 study by Hirohashi’s group challenged the previously accepted view that ZP binding induces the acrosome reaction, showing instead that most spermatozoa capable of crossing the ZP and fertilizing the oocyte had already undergone the acrosome reaction prior to ZP binding. However, as this issue lies beyond the scope of our study, we do not consider it appropriate to include a discussion of it in the manuscript.

2) In the penetration block equations, it is not clear to me why (𝑡𝑃𝐹1) refers to both PIPF1 and 𝜎𝜎𝑃I𝑃𝐹1. Is it as function off?

That is correct: (tPF1) means function of the time post-first fertilization. Both the post-first fertilization penetration index (i.e. PIPF1) and its incertainty (i.e. 𝜎𝑃I𝑃𝐹1 ) vary as a function of this time. However, as mentioned in a previous response to Reviewer 1, this section has been rewritten to improve clarity and readability. The equations have been limited to those strictly necessary for understanding our approach, and their notation has been significantly simplified.

3) Why do the authors think that the flagella stops. The submission date was 2024-10-01 07:27:26 and there has been a paper in biorxiv for a while that merits mention and discussion in this work (bioRxiv [Preprint]. 2024 Jul 2:2023.06.22.546073. doi: 10.1101/2023.06.22.546073.PMID: 37904966).

Our experimental approach allows us to determine when the spermatozoon stops moving, but not why it stops. We thank Reviewer 3 for pointing out this very relevant paper from Buffone’s group (doi: 10.7554/eLife.93792) which shows the existence of two distinct populations of live, acrosome-reacted spermatozoa. These correspond to two successive stages, which occur either immediately upon acrosome reaction in a subset of spermatozoa, or after a variable delay in others, during which the sperm transitions from a motile to an immotile state. The transition from the first to the second stage was shown to follow a defined sequence: an increase in the sperm calcium concentration, followed by midpiece contraction associated with a local reorganization of the helical actin cortex, and ultimately the arrest of sperm motility. For fertilizing spermatozoa in the PVS, this transition was shown to occur upon fusion. However, it was also reported in some non-fertilizing spermatozoa that this transition took place within the PVS. These findings are consistent with the requirement for sperm motility in order to achieve fusion with the oolemma. Moreover, the fact that some spermatozoa may prematurely transition to the immotile state within the PVS can therefore be added to the list of possible reasons why a spermatozoon that penetrates the PVS of an oocyte might fail to fuse.

This discussion has been added to the first paragraph of the Discussion section of our revised manuscript.

4) Please correct at the beginning of Materials and Methos: Sperm was obtained from WT male mice, it should say were.

Thank you, the correction has been done.

5) This is also the case in the fourth paragraph of this section: oocyte were not was.

The sentence in question has been modified as followed: “In the in vitro fertilization experiments with kinetic tracking, a subset of oocytes—together with their associated ZP-bound spermatozoa—was isolated 15 minutes post-insemination and transferred individually into microdrops of fertilization medium to enable identification.”

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Significance

Understanding mammalian gamete fusion and polyspermy inhibition has not been fully achieved. The authors examined real time brightfield and confocal images of inseminated ZP-intact mouse oocytes and used statistical analyses to accurately determine the dynamics of the events that lead to fusion and involve polyspermy prevention under conditions as physiological as possible. Their kinetic observations in mice gamete interactions challenge present paradigms, as they document that the first sperm is not necessarily the one that fertilizes, suggesting the existence of other post-penetration fertilization factors. The authors find that the zona pellucida (ZP) block triggered by the cortical reaction is too slow to prevent polyspermy in this species. In contrast, their findings indicate that ZP directly contributes to the polyspermy block operating as a naturally effective entry barrier inhibiting the exit from the perivitelline space (PVS) of components released from the oocyte plasma membrane (OPM), neutralizing unwanted sperm fusion, aside from any block caused by fertilization. Furthermore, the authors unveil a new important ZP role regulating flagellar beat in fertilization by promoting sperm fusion in the PVS.

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

SUMMARY: This study by Dubois et al. utilizes live-cell imaging studies of mouse oocytes undergoing fertilization. A strength of this study is their use of three different conditions for analyses of events of fertilization: (1) eggs undergoing fertilization retrieved from females at 15 hr after mating (n = 211 oocytes); (2) cumulus-oocyte complexes inseminated in vitro (n = 220 oocytes), and (3) zona pellucida (ZP)-intact eggs inseminated in vitro, transferred from insemination culture once sperm were observed bound to the ZP for subsequent live-cell imaging (93 oocytes). This dataset and these analyses are valuable for the field of fertilization biology. Limitations of this manuscript are challenges arise with some conclusions, and the presentation of the manuscript. There are some factual errors, and also some places where clearer explanations should to be provided, in the text and potentially augmented with illustrations to provide more clarity on the models that the authors interpret from their data.

MAJOR COMMENTS:

The authors are congratulated on their impressive collection of data from live-cell imaging. However, the writing in several sections is challenging to understand or seems to be of questionable accuracy. The lack of accuracy is suspected to be more an effect of overly ambitious attempts with writing style, rather than to mislead readers. Nevertheless, these aspects of the writing should be corrected. There also are multiple places where the manuscript contradicts itself. These contradictions should be corrected. Finally, there are factual points from previous studies that need correction.

Second, certain claims and the conclusions as presented are not always clearly supported by the data. This may be connected to the issues with writing style, word and phrasing choices, etc. The conclusions could be expressed more clearly, and thus may not require additional experiments or analyses to support them. The authors might also consider illustrations as ways to highlight the points they wish to make. (Figure 7 is a strong example of how they use illustrations to complement the text).

In response to Reviewer 3's concern about the writing style, which made several sections difficult to understand, we have thoroughly revised the entire manuscript to improve clarity, and precision. To further enhance comprehension, we have added illustrations in the revised version of the manuscript:

• Figure 1A presents the gamete components; Figure 1B depicts the main steps of fertilization considered in the present study; and Figure 1C illustrates the penetration and fusion blocks, along with the respective contributing mechanisms: the ZP-block for the penetration block, and the membrane-block and PVS-block for the fusion block

• Figure 2A provides a description of the three experimental protocols used in this study: Condition 1, in vivo fertilization after mating; Condition 2, standard in vitro fertilization following insemination of cumulus-oocyte complexes; and Condition 3, in vitro fertilization with kinetic tracking of oocytes isolated from the insemination medium 15 min after insemination of the cumulus-oocyte complexes.

• Figure 4 (formerly Figure 7 in the initial version) now highlights all fusing and non-fusing situations documented in videos 1-6 and associated paragraphs of the Results section.

• In the Discussion, Figure 9 from the original version has been replaced by Figure 8, which now provides a more pedagogical illustration of the inefficacy of the penetration block in preventing polyspermy in mice. This figure illustrates the respective contributions of the fusion block, the penetration block, fusion timing, and the intrinsic permeability of the zona pellucida to the occurrence of polyspermy.

We hope that this revised version of the article will guide the reader smoothly throughout, without causing confusion.

Regarding the various points that Reviewer 3 perceives as contradictions or factual errors, or the claims and the conclusions which, as presented, should not always supported by the data, we will provide our perspective on each of them as they are raised in the review.

SPECIFIC COMMENTS:

(1) The authors should use greater care in describing the blocks to polyspermy, particularly because they appear to be wishing to reframe views about prevention of polyspermic fertilization. The title mentions of "the fast block to polyspermy;" this problematic for a couple of different reasons. There is no strong evidence for block to polyspermy in mammals that occurs quickly, particularly not in the same time scale as the first-characterized fast block to polyspermy. To many biologists, the term "fast block to polyspermy" refers to the block that has been described in species like sea urchins and frogs, meaning a rapid depolarization of the egg plasma membrane. However, such depolarization events of the egg membrane have not been detected in multiple mammalian species. Moreover, the change in the egg membrane after fertilization does not occur in as fast a time scale as the membrane block in sea urchins and frogs (i.e., is not "fast" per se), and instead occurs in a comparable time frame as the conversation of the ZP associated with the cleavage of ZP2. Thus, it is misleading to use the terms "fast block" and "slow block" when talking about mammalian fertilization. This also is an instance of where the authors contradict themselves in the manuscript, stating, "the membrane block and the ZP block are established in approximatively the same time frame" (third paragraph of Introduction). This statement is indeed accurate, unlike the reference to a fast block to polyspermy in mammals.

We fully agree with Reviewer 3 on the importance of clearly defining the two blocks examined in the present study—the penetration block and the fusion block (as referred to in the revised version) —and of situating them in relation to the three blocks described in the literature: the ZP-block, membrane-block, and PVS-block. We acknowledge that this distinction was not sufficiently clear in the original version of the manuscript. In the revised version, these two blocks and their relationship to the ZP-, membrane-, and PVS-blocks are now clearly introduced in the second paragraph of the Introduction section and illustrated in the first figure of the manuscript (Fig. 1C). They are then discussed in detail in two dedicated paragraphs of the Discussion, entitled Relation between the penetration block and the ZP-block and Relation between the fusion block and the membrane- and PVS-blocks.

The penetration block refers to the time-dependent decrease in the number of spermatozoa penetrating the perivitelline space (PVS) following fertilization, whereas the fusion block refers to the time-dependent decrease in sperm-oolemma fusion events after fertilization. It is precisely to the characterization of these two blocks that our in vitro fertilization experiments with kinetic tracking allow us to access.

In this study, as in the literature, fusion-triggered modifications of the ZP that hinder sperm traversal of the ZP are referred to as the ZP-block (also known as ZP hardening). The ZP-block thus contributes to the post-fertilization reduction in sperm penetration into the PVS and thereby underlies the penetration block. Similarly, fusion-triggered alterations of the PVS and the oolemma that reduce the likelihood of spermatozoa that have reached the PVS successfully to fuse with the oolemma are referred to as the PVS-block and membrane-block, respectively. These two blocks act together to reduce the probability of sperm-oolemma fusion after fertilization, and thus contribute to the fusion block.

The time constant of the penetration block was found to be 48.3 ± 9.7 minutes, which is consistent with the typical timeframe of ZP-block completion—approximately one hour post-fertilization in mice—as reported in the literature. By contrast, the time constant of the fusion block was determined to be 6.2 ± 1.3 minutes, which is markedly faster than the time typically reported in the literature for the completion of the fusion-block (more than one hour in mice). This strongly suggests that the kinetics of the fusion block are not primarily governed by its membrane-block component, but rather by its PVS-block component—about which little to nothing was previously known.

Contrary to what Reviewer 3 appears to have understood from our initial formulation, there is therefore no contradiction or error in stating that "the membrane block and the ZP block are established within approximately the same timeframe", while the fusion block, which proceeds much more rapidly, is likely to rely predominantly on the PVS-block. We have thoroughly revised the manuscript to clarify this key message of the study.

However, we understand Reviewer 3’s objection to referring to the fusion block (or the PVS-block) as a fast block, given that this term is conventionally reserved for the immediate fertilization-triggered membrane depolarization occurring in sea urchins and frogs. Although the kinetics we report for the fusion block are considerably faster than those of the penetration block, they occur on the scale of minutes, and not seconds. In line with the reviewer's recommendation, we have therefore modified both the title and the relevant passages in the text to remove all references to the term fast block in the revised version.

(2) The authors aim to make the case that events occurring in the perivitelline space (PVS) prevent polyspermic fertilization, but the data that they present is not strong enough to make this conclusion. Additional experiments would optional for this study, but data from such additional experiments are needed to support the authors' claims regarding these functions in fertilization. Without additional data, the authors need to be much more conservative in interpretations of their data. The authors have indeed observed phenomena (the presence of CD9 and JUNO in the PVS) that could be consistent with a molecular basis of a means to prevent fertilization by a second sperm. However, the authors would need additional data from additional experimental studies, such as interfering with the release of CD9 and JUNO and showing that this experimental manipulation leads to increased polyspermy, or creating an experimental situation that mimics the presence of CD9 and JUNO (in essence, what the authors call "sperm inhibiting medium" on page 20) and showing that this prevents fertilization.

A major section of the Results section here (starting with "The consequence is that ... ") is speculation. Rather than be in the Results section, this should be in the Discussion. The language should be also softened regarding the roles of these proteins in the perivitelline space in other portions of the manuscript, such as the abstract and the introduction.

Finally, the authors should do more to discuss their results with the results of Miyado et al. (2008), which interestingly, posited that CD9 is released from the oocytes and that this facilitates fertilization by rendering sperm more fusion-competent. There admittedly are two reports that present data that suggest lack of detection of CD9-containing exosomes from eggs (as proposed by Miyado et al.), but nevertheless, the authors should put their results in context with previous findings.

We generally agree with all the remarks and suggestions made here. In the revised version of the manuscript, we have retained in the Results section (pp. 14–15) only the factual data concerning the localization of CD9 and JUNO in unfertilized and fertilized oocytes, as well as in the spermatozoa present in the PVS of these oocytes. We have taken care not to include any interpretive elements in this section, which are now presented exclusively in a dedicated paragraph of the Discussion, entitled “Possible molecular bases of the membrane-block and ZP-block contributing to the fusion block” (p. 21). There, we develop our hypothesis and discuss it in light of both the findings from the present study and previous work by other groups. In doing so, we also address the data reported by Miyado et al. (2008, https://doi.org/10.1073/pnas.0710608105), as well as subsequent studies by two other groups—Gupta et al. (2009, https://doi.org/10.1002/mrd.21040) and Barraud-Lange et al. (2012, https://doi.org/10.1530/REP-12-0040)—that have challenged Miyado’s findings.

We are fully aware that our interpretation of the coverage of unfused sperm heads in the perivitelline space (PVS) by CD9 and JUNO, released from the oolemma—as a potential mechanism of sperm neutralization contributing to the PVS block—remains, at this stage, a plausible hypothesis or working model that, as such, warrants further experimental investigation. It is precisely in this spirit that we present it—first in the abstract (p.1), then in the Discussion section (p. 21), and subsequently in the perspective part of the Conclusion section (p. 22).

(3) Many of the authors' conclusions focus on their prior analyses of sperm interaction - beautifully illustrated in Figure 7. However, the authors need to be cautious in their interpretations of these data and generalizing them to mammalian fertilization as a whole, because mouse and other rodent sperm have sperm head morphology that is quite different from most other mammalian species.

In a similar vein, the authors should be cautious in their interpretations regarding the extension of these results to mammalian species other than mouse, given data on numbers of perivitelline sperm (ranging from 100s in some species to virtually none in other species), suggesting that different species rely on different egg-based blocks to polyspermy to varying extents. While these observations of embryos from natural matings are subject to numerous nuances, they nevertheless suggest that conclusions from mouse might not be able to be extended to all mammalian species.

It is not clear to us whether Reviewer 3’s comment implies that we have, at some point in the manuscript, generalized conclusions obtained in mice to other mammalian species—which we have not—or whether it is simply a general, common-sense remark with which we fully agree: that findings established in one species cannot, by default, be assumed to apply to another.

We would like to emphasize that throughout the manuscript, we have taken care to restrict our interpretations and conclusions to the mouse model, and we have avoided any unwarranted extrapolation to other species.

To definitively close this matter—if there is indeed a matter—we have added the following clarifying statements in the revised version of the manuscript:

In the introduction, second paragraph (pp. 2–3):"The variability across mammalian species in both the rate of fertilized oocytes with additional spermatozoa in their PVS (from 0 to more than 80%) after natural mating and the number of spermatozoa present in the PVS of these oocytes (from 0 to more than a hundred) suggests that the time for completion of the penetration block and thus its efficiency to prevent polyspermy can vary significantly between species."

At the end of the preamble to the Results section (p. 4):"This experimental study was conducted in mice, which are the most widely used model for studying fertilization and polyspermy blocks in mammals. While there are many interspecies similarities, the findings presented here should not be directly extrapolated to humans or other mammalian species without species-specific validation."

In the Conclusion, the first sentence is (p.22) : “This study sheds new light on the complex mechanisms that enable fertilization and ensure monospermy in mouse model.”

Within the Conclusion section, among the perspectives of this work (p. 22):"In parallel, comparative studies in other mammalian species will be needed to assess the generality of the PVS-block and its contribution relative to the membrane-block and ZP-blocks, as well as the generality of the mechanical role played by flagellar beating and ZP mechanical constraint in membrane fusion."

(4) Results, page 4 - It is very valuable that the authors clearly define what they mean by a penetrating spermatozoon and a fertilizing spermatozoon. However, they sometimes appear not to adhere to these definitions in other parts of the manuscript. An example of this is on page 10; the description of penetration of spermatozoon seems to be referring to membrane fusion with the oocyte plasma membrane, which the authors have alternatively called "fertilizing" or fertilization - although this is not entirely clear. The authors should go through all parts of the manuscript very carefully and ensure consistent use of their intended terminology.

Overall, while these definitions on page 4 are valuable, it is still recommended that the authors explicitly state when they are addressing penetration of the ZP and fertilization via fusion of the sperm with the oocyte plasma membrane. This help significantly in comprehension by readers. An example is the section header in the middle of page 9 - this could be "Spermatozoa can penetrate the ZP after the fertilization, but have very low chances to fertilize."

We chose to define our use of the term penetration at the beginning of the Results section because, as readers of fertilization studies, we have encountered on multiple occasions ambiguity as to whether this term was referring to sperm entry into the perivitelline space following zona pellucida traversal, or to the fusion of the sperm with the oolemma. To avoid such ambiguity, we were particularly careful throughout the writing of our original manuscript to use the term penetration exclusively to describe sperm entry into the PVS. The terms fertilizing and fusion were reserved specifically for membrane fusion between the gametes. However, as occasional lapses are always possible, we followed Reviewer 3’s recommendation and carefully re-examined the entire manuscript to ensure consistent use of our intended terminology. We did not identify any inconsistencies, including on page 10, which was cited as an example by Reviewer 3. We therefore confirm that, in accordance with our predefined terminology, all uses of the term penetration, on that page and anywhere else in our original manuscript, refer exclusively to sperm entry into the PVS and do not pertain to fusion with the oolemma.

That said, it is important that all readers— including those who may only consult selected parts of the article—are able to understand it clearly. Therefore, despite the potential risk of slightly overloading the text, Reviewer 3’s suggestion to systematically associate the term penetration with ZP seems to us a sound one. However, we have opted instead to associate penetration with PVS, as our study focuses on the timing of sperm penetration into the perivitelline space, rather than on the traversal of the zona pellucida itself. Accordingly, except in a few rare instances where ambiguity seemed impossible, we have systematically used the phrasing “penetration into the PVS” throughout the revised version of the manuscript.

Another variation of this is in the middle of page 9, where the authors use the terms "fertilization block" and "penetration block." These are not conventional terms, and venture into being jargon, which could leave some readers confused. The authors could clearly define what they mean, particularly with respect to "penetration block,"

This point has already been addressed in our response to Comment 1 from Reviewer 3. We invite Reviewer 3 to refer to that response.

This extends to other portions of the manuscript as well, such as Figure 2C, with the label on the y-axis being "Time after fertilization." It seems that what the authors actually observed here was the cessation of sperm tail motility. (It is not evident they they did an assessment of sperm-oocyte fusion here.)

Regarding Figure 2C (original version), it has been merged with Figure 2B (original version) to form a single figure (Figure S2D), now included in Supplementary Information SI2. This new figure retains all the information originally presented in Figure 2C and indicates the time axis origin as the time when oscillatory movements of the sperm cease.

That said, for the reasons detailed in our response to Reviewer 1 and in the Materials and Methods, we explain why it is legitimate to use the cessation of sperm head oscillations on the oolemma as a marker for the timing of the fusion event. We invite the reviewers to refer to that response for a full explanation of our rationale.

(5) Several points that the authors try to make with several pieces of data do not come across clearly in the text, including Figure 2 on page 6, Figure 4 on page 9, and the various states utilized for the statistical treatment, "post-first penetration, post-first fertilization, no fertilization, penetration block and polyspermy block" on page 10. Either re-writing and clearer definitions'explanations are needed, and/or schematic illustrations could be considered to augment re-written text. Illustrations could be a valuable way present the intended concepts to readers more clearly and accurately. For example, Figure 4 and the associated text on page 9 get particularly confusing - although this sounds like a quite impressive dataset with observations of 138 sperm. Illustrations could be helpful, in the spirit of "a picture is worth 1000 words," to show what seem to be three different situations of sequences of events with the sperm they observed. Finally, the text in the Results about the 138 sperm is quite difficult to follow. It also might help comprehension to augment the percentages with the actual numbers of sperm - e.g., is 48.6% referring 67 of the total 138 sperm analyzed? Does the 85.1% refer to 57 of these 67 sperm?

Figure 2 in the original version of our manuscript concerns sperm engulfment and PB2 extrusion. As already mentioned in our response to Reviewer 1, the characterization of sperm engulfment and PB2 extrusion kinetics is highly relevant to the analysis of the penetration and fusion blocks. However, we agree that its presence in the main text may distract the reader from the main focus of the study. Therefore, this figure and the associated text have been moved to the Supplementary Information in the revised manuscript (SI 2, pages 26–27).

Regarding Figure 4 (original version), in response to Reviewer 3’s concern about the difficulty in grasping the message conveyed in its three graphs and associated text we have completely rethought the way these data are presented. Since the three graphs of Figure 4 were directly derived from the experimental timing data of sperm entry in the PVS and fusion with the oolemma in fertilized oocytes (originally shown in Figure 3A), we have combined them into a single figure in the revised manuscript: Figure 3 (page 8). This new Figure 3 now comprises three components:

• Figure 3A remains unchanged from the original version and shows the timing of sperm penetration and fusion in fertilized oocytes. Each sperm category (fused or non-fused , penetrated in the PVS before fusion or after fusion) is represented using a color code clearly explained in the main text (last paragraph of page 7).
• Figure 3B focuses specifically on the first spermatozoon to penetrate the PVS of each oocyte. It reports how many of these first-penetrating spermatozoa succeeded in fusing versus how many failed to do so, highlighting that being the first to arrive is not sufficient for fusion—other factors are involved. This is explained simply in the first paragraph of page 9.
• Figure 3C considers all spermatozoa that entered the PVS of fertilized oocytes, classifying them into three categories: those that penetrated the PVS before fertilization, those that did so after fertilization, and those for which the timing could not be precisely determined. Such classification makes it apparent that the number of spermatozoa penetrating before and after fertilization is of the same order of magnitude, indicating that fertilization is not very effective at preventing further sperm entry into the PVS for the duration of our observations (~4 hours). To facilitate the identification of these three categories, the same color code used in Figure 3A is applied. In addition, within each category, the number of spermatozoa that successfully fused are indicated in black. This allows the reader to quickly assess the fertilization probability for each category—high for sperm entering before fertilization, very low or null for those entering after fertilization. This analysis shows that fertilization is far more effective at blocking sperm fusion than at blocking sperm penetration. This is clearly explained in the second paragraph of page 9. Regarding__ statistical analysis__, as already mentioned in our responses to Reviewers 1 and 2, this section has been rewritten to improve clarity and readability. The notation has also been significantly simplified. To improve the overall fluidity of the text related to the statistical analysis, Figure 3B (original version), which presented the timing of penetration into the perivitelline space of oocytes that remained unfertilized, along with its associated statistical analysis previously in Figure 5B), have been revised and transferred together in a single Figure S1 of the Supplementary Information (SI1, pages 26; now Figures S1A and S1B).

(6) Introduction, page 2 - it is inaccurate to state that only diploid zygotes can develop into a "new being." Triploid zygotes typically fail early in develop, but can survive and, for example, contribute to molar pregnancies. Additionally, it would be beneficial to be more scientifically precise term than saying "development into a new being." This is recommended not only for scientific accuracy, but also due to current debates, including in lay public circles, about what defines "life" or human life.

In response to Reviewer 3’s comment, we no longer state in the revised version of the manuscript that only diploid zygotes can develop into a new being. We have modified our wording as follows, on page 2, second paragraph: “In mammals, oocytes fertilized by more than one spermatozoon cannot develop into viable offspring.”

(7) Introduction, page 2 - The mammalian sperm must pass through three layers, not just two as stated in the first paragraph of the Introduction. The authors should include the cumulus layer in this list of events of fertilization.

The sentence from the introduction from the original manuscript mentioned by Reviewer 3 was: “To fertilize, a spermatozoon must successively pass two oocyte’s barriers.” This statement is accurate in the sense that the cumulus cell layer is not part of the oocyte itself, unlike the two oocyte’s barriers: the zona pellucida and the oolemma. Moreover, the traversal of the cumulus layer is not within the scope of our study, unlike the traversal of the zona pellucida and fusion with the oolemma. However, it is also correct that in our study the spermatozoa have passed through the cumulus layer before reaching the oocyte. Therefore, in response to Reviewer 3’s comment, we have revised the sentence to clarify this point as follows:

“Once a spermatozoon has passed through the cumulus cell layer surrounding the oocyte, it still must overcome two oocyte’s barriers to complete fertilization.”

(8) Introduction, page 2 - While there is evidence that zinc is released from mouse egg upon fertilization, the evidence is not convincing or conclusive that zinc is released from cortical granules or via cortical granule exocytosis.

To better highlight the rationale, storyline, and scope of our study, the introduction has been thoroughly streamlined. In this context, the section discussing the cortical reaction and zinc release seemed more appropriate in the Discussion, specifically within the paragraph titled “Relationship between the penetration block and the ZP-block.”

To address the uncertainty raised by Reviewer 3 regarding the origin of the zinc spark release, we have rephrased this part as follows:

“The fertilization-triggered processes responsible for the changes in ZP properties are generally attributed to the cortical reaction—a calcium-induced exocytosis of secretory granules (cortical granules) present in the cortex of unfertilized mammalian oocytes—and to zinc sparks. As a result, proteases, glycosidases, lectins, and zinc are released into the perivitelline space (PVS), where they act on the components of the zona pellucida. This leads to a series of modifications collectively referred to as ZP hardening or the ZP-block”.

(9) The authors inaccurately state, "only if monospermic multi-penetrated oocytes are able to develop normally, which to our knowledge has never been proven in mice" (page 4) - This was demonstrated with the Astl knockout, assuming that the authors use of "multi-penetrated oocytes" here refers to the definition of penetration that they use, namely penetrating the ZP. This also is one of the instances where the authors contradict themselves, as they note the results with this knockout on page 18.

Thank you for bringing this point to our attention. Nozawa et al. (2018) found that female mice lacking ovastacin (Astl)—the protease released during the cortical reaction that plays a key role in rendering the zona pellucida impenetrable—are normally fertile. They also reported that oocytes recovered from these females after mating were monospermic, despite the consistent presence of additional spermatozoa in the perivitelline space. We can indeed consider that taken together these findings demonstrate that the presence of multiple spermatozoa in the PVS does not impair normal development, as long as the oocyte remains monospermic. In our study, we re-demonstrated this in a different way (by reimplantation of monospermic oocytes with additional spermatozoa in their PVS) in a more physiological context of WT oocytes, but we agree that we cannot state: “which to our knowledge has never been proven in mice.” This part of the sentence has therefore been removed. In the revised version of the manuscript, the sentence is now formulated in the first paragraph of page 5 as follows: “However, the contribution of the fusion block to prevent polyspermy has physiological significance only if monospermic oocytes with additional spermatozoa in their PVS can develop into viable pups.”

Minor comments:

There are numerous places where this reader marked places of confusion in the text. A sample of some of these:

We will indicate hereinafter how we have modified the text in the specific examples provided by Reviewer 3. Beyond these, however, we would like to emphasize that we have thoroughly revised the entire manuscript to improve clarity and precision.

Page 4 - "continuously relayed by other if they detach" - don't know what this means

Replaced now p 5 by “can be replaced by others if they detach”

Page 6 - "hernia" - do the authors mean "protrusion" on the oocyte surface?

The paragraph from the Results section in question has now been moved to the Supplementary Information, on pages 26 and 27. The term hernia has been systematically replaced with protrusion, including in the Materials and Methods section on page 24.

Page 10 - "penetration of spermatozoa in the PVS falls down" - don't know what this means

Falls down has been removed from the new version and replaced with decreases

Page 12 - "spermatozoa linked to the oocyte ZP" - not clear what "linked" means here

Replaced now page 16 by “spermatozoa bound to the oocyte ZP”

Page 14 - "by dint of oscillations" - don't know what this means

Replaced now page 10 by “the persistent flagellum movements”

Specifics for Materials and Methods:

Exact timing of females receiving hCG and then being put with males for mating - assume this was immediate but this is an important detail regarding the timing for the creation of embryos in vivo.

That is correct: females were placed with males for mating immediately after receiving hCG. This clarification has been added in the revised version of the manuscript.

Please provide the volumes in which inseminations occurred, and how many eggs were placed in this volume with the 10^6 sperm/ml.

The number of eggs may vary from one cumulus–oocyte complex to another. It is therefore not possible to specify exactly how many eggs were inseminated. However, we now indicate on page 23 the number of cumulus–oocyte complexes inseminated (4 per experiment), the volume in which insemination was performed (200 mL), and the sperm concentration used 106 sperm/mL.

**Referees cross-commenting**

I concur with Reviewer 1's comment, that the 'challenging prior dogma' about the first sperm not always being the one to fertilize the egg is too strong. As Reviewer 1 notes, "it had been observed before that it is not necessarily the first sperm that gets through the ZP that fertilizes the egg." I even thought about adding this comment to my review, although held off (I was hoping to find references, but that was taking too long).

Please refer to our response to Reviewer 1 regarding this point.

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Referee #3

Evidence, reproducibility and clarity

Summary:

This study by Dubois et al. utilizes live-cell imaging studies of mouse oocytes undergoing fertilization. A strength of this study is their use of three different conditions for analyses of events of fertilization: (1) eggs undergoing fertilization retrieved from females at 15 hr after mating (n = 211 oocytes); (2) cumulus-oocyte complexes inseminated in vitro (n = 220 oocytes), and (3) zona pellucida (ZP)-intact eggs inseminated in vitro, transferred from insemination culture once sperm were observed bound to the ZP for subsequent live-cell imaging (93 oocytes). This dataset and these analyses are valuable for the field of fertilization biology. Limitations of this manuscript are challenges arise with some conclusions, and the presentation of the manuscript. There are some factual errors, and also some places where clearer explanations should to be provided, in the text and potentially augmented with illustrations to provide more clarity on the models that the authors interpret from their data.

Major comments:

The authors are congratulated on their impressive collection of data from live-cell imaging. However, the writing in several sections is challenging to understand or seems to be of questionable accuracy. The lack of accuracy is suspected to be more an effect of overly ambitious attempts with writing style, rather than to mislead readers. Nevertheless, these aspects of the writing should be corrected. There also are multiple places where the manuscript contradicts itself. These contradictions should be corrected. Finally, there are factual points from previous studies that need correction.

Second, certain claims and the conclusions as presented are not always clearly supported by the data. This may be connected to the issues with writing style, word and phrasing choices, etc. The conclusions could be expressed more clearly, and thus may not require additional experiments or analyses to support them. The authors might also consider illustrations as ways to highlight the points they wish to make. (Figure 7 is a strong example of how they use illustrations to complement the text).

Specific comments:

1. The authors should use greater care in describing the blocks to polyspermy, particularly because they appear to be wishing to reframe views about prevention of polyspermic fertilization. The title mentions of "the fast block to polyspermy;" this problematic for a couple of different reasons. There is no strong evidence for block to polyspermy in mammals that occurs quickly, particularly not in the same time scale as the first-characterized fast block to polyspermy. To many biologists, the term "fast block to polyspermy" refers to the block that has been described in species like sea urchins and frogs, meaning a rapid depolarization of the egg plasma membrane. However, such depolarization events of the egg membrane have not been detected in multiple mammalian species. Moreover, the change in the egg membrane after fertilization does not occur in as fast a time scale as the membrane block in sea urchins and frogs (i.e., is not "fast" per se), and instead occurs in a comparable time frame as the conversation of the ZP associated with the cleavage of ZP2. Thus, it is misleading to use the terms "fast block" and "slow block" when talking about mammalian fertilization.

This also is an instance of where the authors contradict themselves in the manuscript, stating, "the membrane block and the ZP block are established in approximatively the same time frame" (third paragraph of Introduction). This statement is indeed accurate, unlike the reference to a fast block to polyspermy in mammals.<br /> 2. The authors aim to make the case that events occurring in the perivitelline space (PVS) prevent polyspermic fertilization, but the data that they present is not strong enough to make this conclusion. Additional experiments would optional for this study, but data from such additional experiments are needed to support the authors' claims regarding these functions in fertilization. Without additional data, the authors need to be much more conservative in interpretations of their data. The authors have indeed observed phenomena (the presence of CD9 and JUNO in the PVS) that could be consistent with a molecular basis of a means to prevent fertilization by a second sperm. However, the authors would need additional data from additional experimental studies, such as interfering with the release of CD9 and JUNO and showing that this experimental manipulation leads to increased polyspermy, or creating an experimental situation that mimics the presence of CD9 and JUNO (in essence, what the authors call "sperm inhibiting medium" on page 20) and showing that this prevents fertilization.

A major section of the Results section here (starting with "The consequence is that ... ") is speculation. Rather than be in the Results section, this should be in the Discussion. The language should be also softened regarding the roles of these proteins in the perivitelline space in other portions of the manuscript, such as the abstract and the introduction.

Finally, the authors should do more to discuss their results with the results of Miyado et al. (2008), which interestingly, posited that CD9 is released from the oocytes and that this facilitates fertilization by rendering sperm more fusion-competent. There admittedly are two reports that present data that suggest lack of detection of CD9-containing exosomes from eggs (as proposed by Miyado et al.), but nevertheless, the authors should put their results in context with previous findings. 3. Many of the authors' conclusions focus on their prior analyses of sperm interaction - beautifully illustrated in Figure 7. However, the authors need to be cautious in their interpretations of these data and generalizing them to mammalian fertilization as a whole, because mouse and other rodent sperm have sperm head morphology that is quite different from most other mammalian species.

In a similar vein, the authors should be cautious in their interpretations regarding the extension of these results to mammalian species other than mouse, given data on numbers of perivitelline sperm (ranging from 100s in some species to virtually none in other species), suggesting that different species rely on different egg-based blocks to polyspermy to varying extents. While these observations of embryos from natural matings are subject to numerous nuances, they nevertheless suggest that conclusions from mouse might not be able to be extended to all mammalian species.<br /> 4. Results, page 4 - It is very valuable that the authors clearly define what they mean by a penetrating spermatozoon and a fertilizing spermatozoon. However, they sometimes appear not to adhere to these definitions in other parts of the manuscript. An example of this is on page 10; the description of penetration of spermatozoon seems to be referring to membrane fusion with the oocyte plasma membrane, which the authors have alternatively called "fertilizing" or fertilization - although this is not entirely clear. The authors should go through all parts of the manuscript very carefully and ensure consistent use of their intended terminology.

Overall, while these definitions on page 4 are valuable, it is still recommended that the authors explicitly state when they are addressing penetration of the ZP and fertilization via fusion of the sperm with the oocyte plasma membrane. This help significantly in comprehension by readers. An example is the section header in the middle of page 9 - this could be "Spermatozoa can penetrate the ZP after the fertilization, but have very low chances to fertilize."

Another variation of this is in the middle of page 9, where the authors use the terms "fertilization block" and "penetration block." These are not conventional terms, and venture into being jargon, which could leave some readers confused. The authors could clearly define what they mean, particularly with respect to "penetration block,"

This extends to other portions of the manuscript as well, such as Figure 2C, with the label on the y-axis being "Time after fertilization." It seems that what the authors actually observed here was the cessation of sperm tail motility. (It is not evident they they did an assessment of sperm-oocyte fusion here.) 5. Several points that the authors try to make with several pieces of data do not come across clearly in the text, including Figure 2 on page 6, Figure 4 on page 9, and the various states utilized for the statistical treatment, "post-first penetration, post-first fertilization, no fertilization, penetration block and polyspermy block" on page 10 . Either re-writing and clearer definitions'explanations are needed, and/or schematic illustrations could be considered to augment re-written text. Illustrations could be a valuable way present the intended concepts to readers more clearly and accurately. For example, Figure 4 and the associated text on page 9 get particularly confusing - although this sounds like a quite impressive dataset with observations of 138 sperm. Illustrations could be helpful, in the spirit of "a picture is worth 1000 words," to show what seem to be three different situations of sequences of events with the sperm they observed. Finally, the text in the Results about the 138 sperm is quite difficult to follow. It also might help comprehension to augment the percentages with the actual numbers of sperm - e.g., is 48.6% referring 67 of the total 138 sperm analyzed? Does the 85.1% refer to 57 of these 67 sperm?<br /> 6. Introduction, page 2 - it is inaccurate to state that only diploid zygotes can develop into a "new being." Triploid zygotes typically fail early in develop, but can survive and, for example, contribute to molar pregnancies. Additionally, it would be beneficial to be more scientifically precise term than saying "development into a new being." This is recommended not only for scientific accuracy, but also due to current debates, including in lay public circles, about what defines "life" or human life. <br /> 7. Introduction, page 2 - The mammalian sperm must pass through three layers, not just two as stated in the first paragraph of the Introduction. The authors should include the cumulus layer in this list of events of fertilization. 8. Introduction, page 2 - While there is evidence that zinc is released from mouse egg upon fertilization, the evidence is not convincing or conclusive that zinc is released from cortical granules or via cortical granule exocytosis.<br /> 9. The authors inaccurately state, "only if monospermic multi-penetrated oocytes are able to develop normally, which to our knowledge has never been proven in mice" (page 4) - This was demonstrated with the Astl knockout, assuming that the authors use of "multi-penetrated oocytes" here refers to the definition of penetration that they use, namely penetrating the ZP. This also is one of the instances where the authors contradict themselves, as they note the results with this knockout on page 18.

Minor comments:

There are numerous places where this reader marked places of confusion in the text. A sample of some of these:

Page 4 - "continuously relayed by other if they detach" - don't know what this means

Page 6 - "hernia" - do the authors mean "protrusion" on the oocyte surface?

Page 10 - "penetration of spermatozoa in the PVS falls down" - don't know what this means

Page 12 - "spermatozoa linked to the oocyte ZP" - not clear what "linked" means here

Page 14 - "by dint of oscillations" - don't know what this means

Specifics for Materials and Methods:

Exact timing of females receiving hCG and then being put with males for mating - assume this was immediate but this is an important detail regarding the timing for the creation of embryos in vivo.

Please provide the volumes in which inseminations occurred, and how many eggs were placed in this volume with the 10^6 sperm/ml.

Referees cross-commenting

I concur with Reviewer 1's comment, that the 'challenging prior dogma' about the first sperm not always being the one to fertilize the egg is too strong. As Reviewer 1 notes, "it had been observed before that it is not necessarily the first sperm that gets through the ZP that fertilizes the egg." I even thought about adding this comment to my review, although held off (I was hoping to find references, but that was taking too long).

Significance

This manuscript brings interesting new observations for the field of gamete and fertilization biology. For very obvious reasons, the understanding of mammalian fertilization has lagged behind the understanding of fertilization of species with external fertilization. Decades ago, developmental biologists first focused on studies of fertilization on gametes from species that release sperm and egg into water, either spontaneously or with relatively easy stimulation, and gametes that could be easily cultured and enabled to create embryos as researchers watched. Studies of mammalian fertilization have since caught up, with the elucidation of conditions that support in vitro fertilization in various mammalian species, most notably mouse as an experimental model.

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Referee #2

Evidence, reproducibility and clarity

Overall, this is a very interesting and relevant work for the field of fertilization. In general, the experimental strategies are adequate and well carried out. I have some questions and suggestions that should be considered before the work is published.

1. Why are the cumulus cells not mentioned when the AR is triggered before or while the sperms cross it? It seems the paper assumes from previous work that all sperm that reach ZP and the OPM have carried out the acrosome reaction. This, though probably correct, is still a matter of controversy and should be discussed. It is in a way strange that the authors do not make some controls using sperm from mice expressing GFP in the acrosome, as they have used in their previous work.
2. In the penetration block equations, it is not clear to me why (𝑡𝑃𝐹1) refers to both PIPF1 and 𝜎𝜎𝑃I𝑃𝐹1. Is it as function off?
3. Why do the authors think that the flagella stops. The submission date was 2024-10-01 07:27:26 and there has been a paper in biorxiv for a while that merits mention and discussion in this work (bioRxiv [Preprint]. 2024 Jul 2:2023.06.22.546073. doi: 10.1101/2023.06.22.546073.PMID: 37904966).
4. Please correct at the beginning of Materials and Methos: Sperm was obtained from WT male mice, it should say were.
5. This is also the case in the fourth paragraph of this section: oocyte were not was.

Significance

Understanding mammalian gamete fusion and polyspermy inhibition has not been fully achieved. The authors examined real time brightfield and confocal images of inseminated ZP-intact mouse oocytes and used statistical analyses to accurately determine the dynamics of the events that lead to fusion and involve polyspermy prevention under conditions as physiological as possible. Their kinetic observations in mice gamete interactions challenge present paradigms, as they document that the first sperm is not necessarily the one that fertilizes, suggesting the existence of other post-penetration fertilization factors. The authors find that the zona pellucida (ZP) block triggered by the cortical reaction is too slow to prevent polyspermy in this species. In contrast, their findings indicate that ZP directly contributes to the polyspermy block operating as a naturally effective entry barrier inhibiting the exit from the perivitelline space (PVS) of components released from the oocyte plasma membrane (OPM), neutralizing unwanted sperm fusion, aside from any block caused by fertilization. Furthermore, the authors unveil a new important ZP role regulating flagellar beat in fertilization by promoting sperm fusion in the PVS.

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Referee #1

Evidence, reproducibility and clarity

The manuscript "Key roles of the zona pellucida and perivitelline space in promoting gamete fusion and fast block to polyspermy inferred from the choreography of spermatozoa in mice oocytes" by Dr. Gourier and colleagues explores the poorly understood process of gamete fusion and the subsequent block to polyspermy by live-cell imaging of mouse oocytes with intact zona pellucida in vitro. The new component in this study is the presence of the ZP, which in prior studies of live-cell imaging had been removed before. This allowed the authos to examine contributions of the ZP to the block in polyspermy in relation to the timing of sperm penetrating the ZP and sperm fusing with the oocyte. By carefully analysing the timing of the cascade of events, the authors find that the first sperm that reaches the membrane of the mouse oocyte is not necessarily the one that fertilizes the oocytes, revealing that other mechanisms post-ZP-penetration influence the success of individual sperm. While the rate of ZP penetration remains constant in unfertilized oocytes, it decreases upon fertilization for subsequent sperm, providing direct evidence for the known 'slow block to polyspermy' provided by changes to the ZP adhesion/ability to be penetrated. Careful statistical analyses allow the authors to revisit the role of the ZP in preventing polyspermy: They show that the ZP block resulting from the cortical reaction is too slow (in the range of an hour) to contribute to the immediate prevention of polyspermy in mice. The presented analyses reveal that the ZP does contribute to the block to polyspermy in two other ways, namely by effectively limiting the number of sperm that reach the oocyte surface in a fertilization-independent manner, and by retaining components like JUNO and CD9, that are shed from the oocyte plasma membrane after fertilization, in the perivitelline space, which may help neutralize surplus spermatozoa that are already present in the PVS. Lastly, the authors report that the ZP may also contribute to channeling the flagellar oscillations of spermatozoa in the PVS to promote their fusion competence.

Major comments:

• Are the key conclusions convincing?

The authors provide a careful analysis of the dynamics of events, though the analyses are correlative, and can only be suggestive of causation. While this is a limitation of the study, it provides important analysis for future research. Moreover, by analysing also control oocytes without fertilization and the timing of events, the authors have in some instances clear 'negative controls' for comparison.

Some claims would benefit from rewording or rephrasing to put the findings better in the context of what is already known and what is novel: - the phrasing 'challenging prior dogma' might be too strong since it had been observed before that it is not necessarily the first sperm that gets through the ZP that fertilizes the egg (though I am afraid that I do not have any citations or references for this). However, given that in the field people generally think it is not necessarily and always the first sperm, the authors may want to consider weakening this claim. - I do think the cortical granule release could still contribute to the block to polyspermy though - as the authors here nicely show - at a later time-point only, and thus not the major and not the immediate block as previously thought. The wording in the abstract should therefore be adjusted (since it could still contribute...) - the finding that the ZP presents a natural effective barrier for sperm entry is not that novel (as suggested here) - there are mutants that prevent sperm from getting through the ZP and thus to the oocyte and those lead to sterility - release of OPM components - in the abstract it's unclear what the authors mean by this - in the results part it becomes clear. Please already make it clear in the abstract that it is the fertility factors JUNO/CD9 that could bind to sperm heads upon their release and thus 'neutralize' them? I would also recommend not referring to it as 'outer' plasma membrane (there is no 'inner plasma membrane'). Moreover, in the abstract please clarify that this release is happening only after fusion of the first sperm and not all the time. In the abstract it sounds as if this was a completely new idea, but there is good prior evidence that this is in fact happening (as also then cited in the results part) - maybe frame it more as the retention inside the PVS as new finding.

It is unclear to me what the relevance of dividing the post-fusion/post-engulfment into different phases as done in Fig 2 (phase 1, and phase 2) - also for the conclusions of this paper this seems rather irrelevant and overly complicated, since the authors never get back to it and don't need it (it's not related to the polyspermy block analyses). I would remove it from the main figures and not divide into those phases since it is distracting from the main focus.

For the statistical analysis, I am not sure whether the assumption "assumption that the probability distribution of penetration or fertilization is uniform within a given time window" is in fact true since the probability of fertilizing decreases after the first fertilization event.... Maybe I misunderstood this, but this needs to be explained (or clarified) better, or the limitation of this assumption needs to be highlighted. - Suggestion for additional experiments:

If I understood correctly, the onset of fusion in Fig 2C is defined by stopping of sperm beating? If it is by the sudden stop of the beating flagellum, this should be confirmed in this situation (with the ZP intact) that it correctly defines the time-point of fusion since this has not been measured in this set-up before as far as I understand. In order to measure this accurately, the authors will need to measure this accurate to be able to acquire those numbers (of time from fusion to end of engulfment), e.g. by pre-loading the oocyte with Hoechst to transfer Hoechst to the fusing sperm upon membrane fusion.

Fig 8: 2 comments - To better show JUNO/CD9 pre-fusion attachment to the oocyte surface and post-fusion loss from the oocyte surface (but persistence in the PVS), an image after removal of the ZP (both for pre-fertilization and post-fertilization) would be helpful - the combination of those images with the ones you have (ZP intact) would make your point more visible. - You show that the heads of spermatozoa post fusion are covered in CD9 and JUNO, yet I was missing an image of sperm in the PVS pre-fertilization (which should then not yet be covered).

Minor comments:

• The videos were remarkable to look at, and great to view in full. However, for the sake of time, the authors might want to consider cropping them for the individual phases to have a shorter video (with clear crop indicators) with the most important different stages visible in a for example 1 min video (e.g. video 1)
• In general, given that the ZP, PVS and oocyte membrane are important components, a general scheme at the very beginning outlining the relative positioning of each before and during fertilization (and then possibly also including the second polar body release) would be extremely helpful for the reader to orient themselves.
• first header results "Multi-penetration and polyspermy under in vivo conditions and standard and kinetics in vitro fertilization conditions" is hard to understand - simplify/make clearer (comparison of in vivo and in vitro conditions? Establishing the in vitro condition as assay?)
• Large parts of the statistical analysis (the more technical parts) could be moved to the methods part since it disrupts the flow of the text.
• To me, one of the main conclusions was given in the text of the results part, namely that "This suggests that first fertilization contributes effectively to the fertilization
• block, but less so to the penetration block". I would suggest that the authors use this conclusion to strengthen their rationale and storyline in the abstract.
• Wording: To characterize the kinetics with which penetration of spermatozoa in the PVS falls down after a first fertilization," falls down should be replaced with decreases (page 10 and page 12)

Significance

Overall, this manuscript provides very interesting and carefully obtained data which provides important new insights particularly for reproductive biology. I applaud the authors on first establishing the in vivo conditions (how often do multiple sperm even penetrate the ZP in vivo) since studies have usually just started with in vitro condition where sperm at much higher concentration is added to isolated oocyte complexes. Thank you for providing an in vivo benchmark for the frequency of multiple sperm being in the PVS. While this frequency is rather low (somewhat expectedly, with 16% showing 2-3 sperm in the PVS), this condition clearly exists, providing a clear rationale for the investigation of mechanisms that can prevent additional sperm from entering.

My own expertise is experimentally - thus I don't have sufficient expertise to evaluate the statistical methods employed here.

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

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Reply to the reviewers

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

The authors use Dyngo-4a, a known Dynami inhibitor to test its influence on caveolar assembly and surface mobility. They investigate, whether it incorporates into membranes with Quartz-Crystal Microbalance, they investigate how it is organized in membranes using simulations. Finally, they use lipid-packing sensitive dyes to investigate lipid packing in the presence of Dyngo-4a, membrane stiffness using AFM and membrane undulation using fluorescence microscopy. They also use a measure they call "caveola duration time" to claim that something happens to caveolae after Dyngo-4a addition and using this parameter, they do indeed see an increase in it in response to Dyngo-4a, which is reduced back to the baseline after addition of cholesterol.

Overall, the authors claim: 1) Dyngo-4a inserts into the membrane and this 2) results in "a dramatic dynamin-independent inhibition of caveola scission". 3) Dyngo-4a was inserted and positioned at the level of cholesterol in the bilayer and 4) Dyngo-4a-treatment resulted in decreased lipid packing in the outer leaflet of the plasma membrane 5) but Dyngo-4a did not affect caveola morphology, caveolae- associated proteins, or the overall membrane stiffness 6) acute addition of cholesterol counteracts the block in caveola scission caused by Dyngo-4a

Overall, in this reviewers opinion, claims 1, 3, 4, 5 are well-supported by the presented data from electron and live cell microscopy, QCM-D and AFM. However, there is no convincing assay for caveolar endocytosis presented besides the "caveola duration" which although unclearly described seems to be the time it takes in imaging until a caveolae is not picked up by the tracking software anymore in TIRF microscopy. Since the main claim of the paper is a mechanism of caveolar endocytosis being blocked by Dyngo-4a, a true caveolar internalization assays is required to make this claim. This means either the intracellular detection of not surface connected caveolar cargo or the quantification of caveolar movement from TIRF into epifluorescence detection in the fluorescence microscope. Otherwise, the authors could remove the claim and just claim that caveolar mobility is influenced.

Response: We thank the reviewer for the nice constructive comments, and we very much appreciate the positive critique. We have now included a FRAP experiment of endocytic Cav1-GFP supporting the effect on internalization. In addition, we are currently preforming CTxB HRP experiments to quantify the number of caveolae at PM using EM but due to reasons out of our control we have not managed to finish these on time, they will be included in the manuscript once they are ready in hopefully not too long.

Reviewer #1 (Significance (Required)):

A number of small molecule inhibitors for the GTPase dynamics exist, that are commonly used tools in the investigation of endocytosis. This goes as far that the use of some of these inhibitors alone is considered in some publications as sufficient to declare a process to be dynamin-dependent. However, this is not correct, as there are considerable off-target effects, including the inhibition of caveolar internalization by a dynamin-independent mechanism. This is important, as for example the influence of dynamin small molecule inhibitors on chemotherapy resistance is currently investigated (see for example Tremblay et al., Nature Communications, 2020).

The investigation of the true effect of small molecules discovered as and used as specific inhibitors and their offside effects is extremely important and this reviewer applauds the effort. It is important that inhibitors are not used alone, but other means of targeting a mechanism are exploited as well in functional studies. The audience here thus is besides membrane biophysicists interested in the immediate effect of the small molecule Dyngo-4a also cell biologists and everyone using dynamic inhibitors to investigate cellular function.

__Reviewer #2 (Evidence, reproducibility and clarity (Required)): __

This manuscript uses the small molecule dynamin inhibitors dynasore and dyngo to show that in dynamin triple knockout cells that these inhibitors impact lipid packing and organization in the plasma membrane. Data showing that dyngo affects caveolin dynamics using tirf microscopy is also shown and is interpreted to reflect inhibition of caveolae scission from the membrane.

This data showing that dyngo and dynasore target membrane order is quite compelling and argues that the effects of these inhibitors is not dynamin specific and that inhibition of endocytosis by these small molecule inhibitors is dynamin-independent. The in vitro and in vivo data they provide is convincing.

Similarly, the data showing that dynasore and dyngo affect caveolin dynamics and clathrin endocytosis (transferrin) is quite convincing and argues that altered lipid packing is impacting membrane dynamics at the plasma membrane. What is less convincing is the conclusion is that dyngo is preventing caveolae scission from the membrane. Study of caveolae endocytosis is based on a TIRF assay that has inherent limitations: - Caveolae are defined as bright cav1-positive spots in diffraction limited TIRF and their disappearance presumed to be endocytic events. Cav1 spots are presumed to be caveolae but the authors do not consider that they may be flat non-caveolar oligomers. The diffraction limited TIRF approach interprets the large structures as caveolae but evidence to that effect is lacking.

Response: This is a valid comment and to address this we have now included data showing colocalization of cavin1 and EHD2 to the Cav1-GFP spots. We can however not determine if they are flat or invaginated. We do have extensive experience imaging caveolae using TIRF microscopy and carefully chose cells that display low expression of fluorescently labelled caveolin to avoid non-caveolar structures.

• The analysis (and the diagram presented in figure 4) considers that caveolae can either diffuse laterally in the membrane or internalize and does not consider that caveolae can flatten and possibly fragment in the membrane. Is it not possible that loss of Cav1 spots is a fragmentation event and not necessarily a scission event?

Response: This is a good question, yet, fragmentation and disassembly would result in shorter track durations and this is not what is observed in data. We have now also included data showing that cavin1 is persistently associated with the Cav1 spots identified as caveolae during Dyngo-4a treatment indicating that these are caveolae. Furthermore, IF stainings showing colocalization of Cav1GFP with cavin1 or EHD2 after Dyngo-4a treatment have also been added. We have now also expanded on the different interpretations of the data in the results section.

• The analysis is based on overexpression of Cav1-GFP that may alter the stoichiometry between Cav1 and cavin1 such that while caveolae may be expressed, larger non-caveolar structures may accumulate.

Response: Yes, this is correct, we have specifically imaged cell expressing low levels of Cav1-GFP to avoid accumulated non-caveolar structures that can be spotted in cells with high expression.

• Cav1 has been shown to be internalized via the CLIC pathway (Chaudary et al, 2014) and if dyngo is impacting clathrin then maybe it is also impacting CLIC endocytosis and thereby Cav1 endocytosis via this pathway?

Response: Dyngo-4a has been shown to not affect CLIC endocytosis (McCluskey et al., 2013) and in our data we do not see internalization following Dyngo-4a treatment.

• The longer Cav1 TIRF track time and shorter displacement with dyngo is consistent with inhibition of caveolae scission. However, as the authors discuss, could not reduced membrane undulations due to dyngo's impact on membrane order be responsible for the longer tracks? Alternatively, perhaps the altered lipid packing is corralling Cav1 movement and reducing non-caveolar Cav1 endocytosis, resulting in shorter tracks of longer duration? The proposed interaction of dyngo with cholesterol could prevent scission but also stabilize large (flat?) Cav1 oligomers in the membrane, perhaps reducing Cav1 oligomer fragmentation.

Response: We completely agree that membrane undulations contribute to instability of the TIRF-field and therefore disruption of cav1-GFP tracks as we discuss in the results section and have been described in previous work (Larsson et al., 2023). Yet, we have also shown that internalization of caveolae results in shorter tracks (Hubert et al., 2020; Larsson et al., 2023; Mohan et al., 2015). Furthermore, the tracked Cav1-GFP spots are persistently positive for cavin1 both with and without Dyngo-4a treatment showing that the majority do not disassemble become internalized by other pathways. Additionally, the added IF stainings after 30 min Dyngo-4a treatment also show that the Cav1-GFP spots remain positive for cavin1 and EHD2 just as ctrl-treated cells.

My point here is not to discredit the data but only to suggest that the TIRF approach used is an indirect measure of caveolae scission from the membrane that requires substantiation using other approaches.

Response: We appreciate these comments and have tried to address these by adding new data and discussions on the interpretation of the tracking data in the results section.

Dyngo is certainly generally affecting lipid packing via cholesterol and thereby affecting Cav1 dynamics in the plasma membrane. The claim of caveolae scission should be qualified and alternative possibilities considered and discussed. If the authors persist in arguing that dyngo is affecting caveolae scission then the effect should be substantiated by accumulation of caveolae by quantitative EM and high spatial and temporal resolution imaging of Cav1 and cavin1 to define the endocytic events. As the latter represents a new, and potentially very challenging, line of experimentation, I would suggest that it is beyond the scope of the current study. As indicated above the additional experiments are not necessary and qualification of the claims would be sufficient.

-Response: We have now included a FRAP experiment of endocytic Cav1-GFP supporting the effect on internalization. We are also currently preforming CTxB HRP experiments to quantify the number of caveolae at the PM using EM but due to reasons out of our control we have not managed to finish these on time, they will be included in the manuscript once they are ready in hopefully not too long.

Other points

Figure 1C - Cav1 positive spots cannot be interpreted to be caveolae from diffraction limited confocal images. Same comment applies to Fig 4G - caveola? duration.

-Response: We completely agree with this and that the claims should be qualified. We have added IF stainings showing that the Cav1-GFP structures are also positive for cavin1. We have now clarified that we cannot distinguish between flat or different curved states of caveolae using this methodology. We have also changed the labelling of Fig. 4G.

Figure 4C - it is not clear why this EM data is not quantified - for both the number of caveolae and clathrin coated pits - as this would help clarify the interpretation of the effect reported.

-Response: We are currently preforming CTxB HRP experiments to quantify the number of caveolae using EM but due to reasons out of our control we have not managed to finish these on time, they will be included in the manuscript once they are ready in hopefully not too long.

Figure 4D - the AFM experiments should perhaps be repeated as the non-significant effect of dyngo on the Young's modulus may be a result of insufficient n values. -Response: We would like to clarify that to ensure the robustness of our AFM measurements, we performed the experiments with sufficient biological and technical replicates. Specifically, each data point shown in Figure 4D represents a Young’s modulus value averaged from approximately sixty force-distance curves per cell. For each condition, we collected force-distance maps on eight to nine individual cells, obtained from two separate petri dishes per day. We repeated this process on two independent days. In total, we analysed thirty-one cells for the DMSO control and thirty-three cells for the Dyngo-4a treatment. We performed the “student’s t-test with Welch’s correction” to access the statistical significance between the two conditions, as described in the main text. We believe that the sample size and statistical approach are sufficient to support the conclusions presented. Furthermore, we also analysed cell stiffness by calculating the slope of the linear portion of the force-distance curves. This analysis also did not reveal any statistically significant differences between the conditions (data not shown), further supporting our conclusion that Dyngo-4a treatment does not significantly alter the Young’s modulus under our experimental setup (or conditions).

Reviewer #2 (Significance (Required)):

This data showing that dyngo and dynasore target membrane order is quite compelling and argues that the effects of these inhibitors is not dynamin specific and that inhibition of endocytosis by these small molecule inhibitors is dynamin-independent. The in vitro and in vivo data they provide is convincing.

Similarly, the data showing that dynasore and dyngo affect caveolin dynamics and clathrin endocytosis (transferrin) is quite convincing and argues that altered lipid packing is impacting membrane dynamics at the plasma membrane. What is less convincing is the conclusion is that dyngo is preventing caveolae scission from the membrane.

__Reviewer #3 (Evidence, reproducibility and clarity (Required)): __

Larsson et al present experimental and computational data on the role of Dyngo4a (a compound that was developed to inhibit dynamin) on the dynamics of caveolae. The manuscript mostly documents effects of Dyngo on caveolae, with one experiment to suggest a mechanism for this result. This one rather unconvincing result forms the focus of the manuscript contributing to a disconnect between the data and the presentation. Additionally, there are concerns with data interpretation. The writing could also benefit from revision to address grammar mistakes, strengthen referencing, and increase precision. Overall, the manuscript requires substantial revisions before being considered for publication. The central claim, in particular, needs stronger evidence to support the proposed mechanism. -Response: We thank the reviewer for the thorough review and for experimental suggestions that we believe has strengthened our data further.

Significant issues (in approximate order of importance): 1. The data supporting the central mechanistic explanation appears limited. There is no evidence that Dyngo remains in one leaflet

Response:The simulations show that the energy barrier for moving in between bilayers is very high. Furthermore, simulations of C-Laurdan has shown that it does not readily flip in between membrane leaflets (Barucha-Kraszewska et al., 2013) supporting that it reports on the outer lipid leaflet when added to cells. We have however now changed this and state that Dyngo-4a decreased the lipid order in the plasma membrane.

the GP of the PM is very low compared to previous measurements,

Response: The absolute GP-values will vary between setups depending on what filters are used so they are not comparable between laboratories. What is of importance is that we found a significant change in the relative GP-values in cells treated with Dyngo-4a and control cells. It is this change that we report. We have not performed any GP-measurements on this cell type earlier so it is unclear what previous measurements reviewer #3 are referring to.

effects on other membranes are not explored,

Response: The order of the intracellular membranes is as expected lower than that of the plasma membrane. Differentiating different intracellular membranes of interest like endocytotic vesicles from other intracellular membranes would be very difficult but, more importantly, our study is focused on what is happening in the plasma membrane where caveolae reside and would be of minor interest for plasma membrane dynamics.

dynamin-directed effects of Dyngo are not considered,

Response: In the discussion section we discuss the difficulties with disentangling dynamin-direct and indirect effects.

The QCM-D measurements and claims require explanation as several aspects remains unclear. In Fig S2, the 'softness' (what does this mean?) changes by 4-fold with DMSO alone (what does this mean?), then fractionally more with Dyngo. Then fractionally more again when Dyngo is removed (why?). Then it remains somewhat higher when both Dyngo and DMSO are removed, which is somehow interpreted as Dyngo remaining in the bilayer, but not DMSO.

Response:We understand the confusion of the reviewer and hope our explanations provide clarity. QCM-D measurements are based on an oscillating quartz crystal sensor. Specifically, alterations in oscillation frequency (ΔF) and the rate of energy dissipation from the sensor surface (ΔD) are what is measured. Allowing the measurement of: 1) materials adsorbing to the sensor surface, 2) changes in the viscoelastic properties of a solution in contact with the sensor surface, 3) changes in the material adsorbed to the sensor surface upone exposure to different solutions. The ratio of ΔD/-ΔF reports the mechanical softness or rigidity of an adsorbed material, in this case the SLB.A “buffer shift” is the term used when there is not an adsorption to the sensor surface, but rather an effect from altering the solution above the sensor surface. One reason is because different solutions can have different densities (e.g., a DMSO-buffer mixture vs buffer alone), which impacts the oscillations of the sensor. It was observed that the DMSO-buffer mixture alone gave a large buffer shift in comparison to the adsorption of the Dyngo-4a into the SLB, thereby muddling the data interpretation. Thus, in Fig. S2 the system was first equilibrated with the DMSO-buffer mixture prior to addition of the Dyngo-4a solution to allow for clearer visualization of the two events. In QCMD to assess if something has made a permeant change to the system you change back to the solutions used before the addition, thus first we washed with a DMSO-Buffer mixture followed by buffer alone. Control experiments were carried out in which no Dyngo-4a was added (also shown in Fig. S2). The control shows the same “buffer shift” from the DMSO-buffer mixture occurs in both systems and that upon returning to a buffer only condition there is no permanent change to the system caused from exposure to the DMSO. In contrast, once the system that received Dyngo-4a is changes back to a buffer only system we see that mass has been added to the system (ΔF) with little change to the dissipation (ΔD), thereby resulting in a lower ratio of ΔD/-ΔF, which is to say that the SLB after the adsorption of Dyngo-4a was more rigid that the SLB without Dyngo-4a.

These interpretations are difficult to grasp, as the authors seem to be implying simple amphiphilic partitioning into the membrane, which should all be removable by efficient washing.

Response: Amphiphilic partitioning is not fully reversible by “efficient washing” it depends on partitioning coefficients.

I do not doubt that this compound interacts with membranes, but the quantifications appear ambiguous. A bilayer with 16 mol% (or worse, 30% if all in one leaflet) Dyngo is very unlikely (to remain a bilayer). Even if such a bilayer was conceivable, the authors are claiming an ADDITION of Dyngo that would INCREASE the area of one leaflet by 30%, which needs explanation as it appears unlikely.

-Response: We understand that in our attempt provide numbers in the results section for the amount of binding observed in QCM-D, this can easily be interpreted as this is what is observed to insert into the PM. However, as discussed in the discussion, we also see aggregations of Dyngo-4a that associate with the membrane in the simulations which likely could contribute to the binding observed in QCM-D prior to washing. The precise amount of membrane inserted Dyngo-4a is difficult to measure as we discuss in the text. In order to make this clearer, we have now moved all these details to the discussion section where we elaborate on this. Furthermore, since Dyngo-4a, like cholesterol, is intercalating in between the head groups of the lipids the area would not increase in direct proportion to the mol%.

Also, there are no replicates shown, so unclear how reproducible these effects are?

Response: For clarity, only single experiments are shown. However, multiple experiments were performed and the range in measured values for 3 technical repeats can be observed in the standard deviations found in the main text (e.g., 6 ± 2 mol%).

The simulations are insufficiently described and difficult to interpret. How big are these systems? Why do the figures show the aqueous system with lateral boundaries?

Response: There are no explicit boundaries used in the simulations, periodic boundary conditions are applied in all three dimensions. The lateral boundaries observed in the figures correspond to the simulation box edges and are a visual artifact of 2D projections with QuickSurf representation. No artificial wall or constraints were introduced laterally. Additional technical details, including the system size and periodic boundary conditions have now been added to the methods section.

It seems quite important that multiple Dyngo molecules aggregate rather than partition into membranes - is this likely to occur in experiment?

Response: Yes, this is important and with the additional simulation experiments suggested by Reviewer #3 it has been clarified that they contribute a great deal to the change in lipid packing of lipid bilayers containing cholesterol. However, it is hard to test aggregation is the cellular system, but we believe that this happens and contribute to the effect on membranes. We have now emphasized the effect of the aggregates in the text.

PMF simulations are strongly suggesting that Dyngo does not spontaneously cross membranes, which is inconsistent with its drug-like amphiphilicity (cLogP~2.5 is optimally suited for membrane permeation) and known effects on intracellular proteins. This suggests an artefact in these PMFs.

Response:As stated in the submitted version of the manuscript, logP was used to validate the topology and the observed value was in a very good agreement with cLogP. Moreover, this validation complemented the standard procedure of CHARMM-GUI ligand modelling, that provided a reasonable penalty score (around 20) for the Dyngo-4a topology. POPC and cholesterol molecules are standard in the force field and validated by numerous studies. The parameters used for the membrane simulations and AWH in particular are very common for this type of studies. Thus, we do not see what may cause any artifacts in the free energy profile construction. In fact, amphiphilicity of the molecule may be one of the key reasons that Dyngo-4a molecule remains at the aqueous interface of the membrane and does not cross the membrane spontaneously. Also, we believe that the energy barrier of 40-60 kJ/mol is not prohibitively high and Dyngo-4a molecules may still overcome the barrier eventually, though we expect majority to reside in the upper leaflet*. *

The authors should experimentally measure the permeation of Dyngo through bilayers (or lack thereof), to more robustly support their finding that Dyngo does not cross membranes spontaneously.

-Response: We thank the reviewer for the suggestion, however this if very technically challenging and would require establishment of precise systems which is beyond the scope of this manuscript.

Why not measure effect of Dyngo on lipid packing directly and more broadly in model membranes?

-Response: With the added modelling experiments supporting the previous simulations and the calculated GP values from the C-Laurdan experiments on cellular plasma membrane, we do not find it necessary to include more model membranes experiments than the already existing ones on lipid monolayers and supported lipid bilayers.

Statistics should not be done on individual cells (n>26), but rather on independent experiment (N=3?)

-Response: We have performed the statistics on live cell particle tracking according to previous literature on similar systems (Boucrot et al., 2011; Larsson et al., 2023; Shvets et al., 2015; Stoeber et al., 2012).

Fig 1G is important but rather unclear. Firstly, these kymographs are an odd way to show that the caveolae are not moving. More importantly, caveolae in normal cells have been shown to be quite stable and immobile (eg doi: 10.1074/jbc.M117.791400), yet here they are claimed to be very mobile.

-Response: Although this might be an odd and unconventional way to depict dynamic processes, we believe that this is a very illustrative way to show track stability over time in bulk rather than just a kymograph over a few structures in a cell. Furthermore, we are not claiming that caveolae are very mobile but rather the opposite very stable in agreement with previous work (Boucrot et al., 2011; Larsson et al., 2023; Mohan et al., 2015). We have now edited the text to make this even clearer.

Also, if Dyngo prevents caveolae scission, there should be more of them at the membrane - why no quantification like Fig 1C to show accumulation of caveolae upon Dyngo treatment? Or directly counting caveolae via EM, as in Fig 4C?

-Response: We are currently preforming CTxB HRP experiments using EM but due to reasons out of our control we have not managed to finish these on time, they will be included in the manuscript once they are ready in hopefully not too long. However, Dynasore has previously been shown, by EM, to increase the number of caveolae at the PM (Moren et al., 2012; Sinha et al., 2011).

The writing can be made more precise and referencing could be strengthened. Response: The introduction was written in a short format, and we have now extended this and made it more precise. Some examples: (a) 'scissoned' is not a word in English,

Response: Thanks, we have now changed this.

(b) what is meant by "Cav1 assembly is driven by high chol content"? There are many types of caveolin assemblies.

Response: We agree that this can be made more precise and have now clarified this in the introduction.

(c) "This generates a unique membrane domain with distinct lipid packing and a very high curvature." Unclear what 'this' refers to and there is no reference here, so what is the evidence for either of these claims? Caveolin-8S oligomers are not curved. Perhaps 'this' is caveolae, but they are relatively large and also not very highly curved and I am unaware of measurements of lipid packing therein.

Response: caveolae are around 50 nm which in biology is a very high curvature of a membrane. It has been extensively proven that caveolae have a distinct lipid composition highly enriched in cholesterol and sphingolipids, which thereby also will generate a unique lipid packing as compared to the surrounding membrane. Yet, the reviewer is correct that lipid packing has not been measured in a caveola for obvious technical challenges. Thus, we have now changed the text to “special lipid composition”.

The sentence following that one again makes a specific, but unreferenced, claim. (d) intro claims that lipid packing is critical for fission, but it is unclear quite what is meant by this claim. The references do not help, as they are often about the basic biophysics of lipids, rather than how packing affects fission.

Response: We have now edited the text.

(e) intro strongly implies that caveolae remain membrane attached because of stalled scission. How strong is the evidence for this? The fact that EHD2 is at the neck is not definitive,

Response: We used the term stalled scission to describe that all omega shaped membrane invaginations do not scission in the same automatic way as clathrin coated vesicles. We have now changed this in the text. Caveolae are shown to be released (undergo scission) and be detected as internal caveolae if the protein EHD2 is removed. Hence this must be interpreted as if EHD2 stalls scission. The evidence includes data compiled over the last 12 years from others and us which include for example: 1) Caveolae with EHD2 have a longer duration time (Larsson et al., 2023; Mohan et al., 2015; Moren et al., 2012; Stoeber et al., 2012), Knock down of EHD2 results in more internalized caveolae as measured by CTxB HRP using EM (Moren et al., 2012) and shorter duration time at the PM (Hubert et al., 2020; Larsson et al., 2023; Mohan et al., 2015; Stoeber et al., 2012). 2) EHD2 overexpression results in less internalized caveolae as measured by CTxB HRP using EM (Stoeber et al., 2012). Furthermore, 3) overexpression or acute addition of purified EHD2 via microinjection counteracts lipid induced scission of caveolae and hence result in caveolae stabilization at the PM (Hubert et al., 2020). It is very hard to see that the release and internalization of caveolae could result from anything else than that these have undergone scission. EHD2 has been found around the rim of caveolae (Matthaeus et al., 2022) and overexpression of EHD2 oligomerizing mutants have been shown to expand the caveola neck (Hoernke et al., 2017; Larsson et al., 2023).

(f) unclear what is meant by 'lipid packing frustration' and how Dyngo supposedly induces it.

Response: Lipid packing frustration refers to what is usually referred to as lipid packing defect, but since lipid membranes are describe as a fluid system it should not have defects whereby, we believe that lipid packing frustration is more accurate. However, we have now changed the text and use “decreased lipid packing” or “decreased lipid order” more thoroughly to describe the effect on the plasma membrane.

IF of Cav1 is insufficient to claim puncta as caveolae. Co-stained puncta of caveolin with cavin are much stronger evidence. Same issue for Cav1-GFP puncta.

Response: We agree and have now provided IF showing cavin1 and EHD2 colocalization to Cav1GFP in non and Dyngo-4a-treated cells.

Fig 3E claims that "preferred position of Dyngo-4a was closer to the head groups" but the minimum looks to be in similar place as Fig 3B without cholesterol.

Response:We appreciate the reviewer’s observation. The PMF minima in the POPC and POPC:Chol membranes are indeed close in absolute position (~1.1–1.2 nm from the bilayer center). However, as clarified in the revised text, the presence of cholesterol leads to a slight shift of Dyngo-4a closer to the headgroup region and broadens the positional distribution. This is also evident from the added density profiles (Fig. S3A) and is now described more precisely in the manuscript.

Critically, these results do not support the notion that Dyngo affects lipid packing sufficiently, which is not measured in the simulations (though could be).

-Response: We thank the reviewer for the excellent suggestion. In response, we have now included a detailed analysis of Dyngo-4a’s effect on lipid packing in the simulations. As described in the revised manuscript, we measured deuterium order parameters, area per lipid (APL), and lipid–Dyngo–cholesterol spatial distributions (Figs. 3-H, S3C-E). The results demonstrate that Dyngo-4a decreases lipid order in POPC:Chol membranes. Both single molecules and clusters reduce the order parameter by up to 0.04 units, particularly in the upper leaflet, where Dyngo-4a reside.The reduction is most pronounced in the midchain region of the sn1 tail and around the double bond of the sn2 tail. These effects were accompanied by increased APL in POPC:Chol membranes and by colocalization of Dyngo-4a near cholesterol-rich regions. Together, these data confirm that Dyngo-4a perturbs membrane organization and lipid packing in a composition-dependent manner. We believe these additions directly address the concern and demonstrate that the simulations indeed support the conclusion that Dyngo-4a modulates lipid packing.

Finally, the simulation data do not show "that Dyngo-4a is competing with cholesterol"; it is unclear what 'competition' means in this context, but regardless, the data only shows that Dyngo sits at a similar location as cholesterol.

We agree with the reviewer that “competition” was an imprecise term. We have rephrased the relevant sections to clarify that Dyngo-4a and cholesterol localize to overlapping regions and exhibit spatial coordination. As now stated in the manuscript, cholesterol appears to partially displace Dyngo-4a from its preferred depth seen in pure POPC, broadens its membrane distribution, and alters lipid packing. According to the order parameters there is an interplay between chol and Dyngo-4a and the heatmaps show that the distribution of chol in the membrane gets less uniform in the presence of Dyngo-4a. These interactions suggest that Dyngo-4a perturbs cholesterol-rich domains.

As new analysis routines were added to the study, we have now also added the details on those to the Methods section of the text.

AFM measures the stiffness of the cell (as correctly explained in Results section) not "overall stiffness of the PM" as stated in the Discussion.

Response: We thank the reviewer for pointing this out, we have now altered this in the discussion section.

Fig2A: what was the starting lipid surface pressure? How does Dyngo insertion depend on initial lipid packing?

Response: The starting pressure lipid pressure was 20 mN m-1 which we now have incorporated in the figure legend. We performed several such experiments with a starting pressure ranging from 20-23 mN m-1 showing consistent results which we described in the materials and methods section. Given that we also performed QCMD analysis and simulations on bilayers showing that Dyngo-4a adsorbed and inserted respectively, we have not performed a titration of starting pressures resulting in a MIP of Dygo-4a.

Fig 4B is a strange approach to measure membrane motion. Why not RMSD or some other displacement based method? As its shown, it implies that the area of the cell changes.

Response: The method that we used to quantify the area of the cell which is attached (or close to) the glass and thereby is visible in TIRF microscopy. This is area indeed changes over time which has been frequently observed and used to describe and quantify the mobility, lamellipodia and filopodia formation among other things. We agree that RMSD can also be used to analyze the data before and after treatments and we have now included RMSD­­­­ analysis in the manuscript.

Reviewer #3 (Significance (Required)):

The title, abstract, and introduction of the manuscript are largely framed around lipid packing, but most of the data investigate other unexpected effects of treating cells with Dyngo4a. The only measurement for lipid packing (or any other membrane properties) is Fig 4E-F. Therefore, this paper is effectively an investigation of an artefact of a common reagent, which itself could be a valuable contribution. However, the mechanism to explain its effect requires stronger evidence, and its broad biological significance needs further exploration.

Overall, the impact of documenting the effects of Dyngo4a on membranes appears modest but may be valuable to the membrane trafficking community.

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Referee #3

Evidence, reproducibility and clarity

Larsson et al present experimental and computational data on the role of Dyngo4a (a compound that was developed to inhibit dynamin) on the dynamics of caveolae. The manuscript mostly documents effects of Dyngo on caveolae, with one experiment to suggest a mechanism for this result. This one rather unconvincing result forms the focus of the manuscript contributing to a disconnect between the data and the presentation. Additionally, there are concerns with data interpretation. The writing could also benefit from revision to address grammar mistakes, strengthen referencing, and increase precision.

Overall, the manuscript requires substantial revisions before being considered for publication. The central claim, in particular, needs stronger evidence to support the proposed mechanism.

Significant issues (in approximate order of importance):

1. The data supporting the central mechanistic explanation appears limited. There is no evidence that Dyngo remains in one leaflet, the GP of the PM is very low compared to previous measurements, effects on other membranes are not explored, dynamin-directed effects of Dyngo are not considered,
2. The QCM-D measurements and claims require explanation as several aspects remains unclear. In Fig S2, the 'softness' (what does this mean?) changes by 4-fold with DMSO alone (what does this mean?), then fractionally more with Dyngo. Then fractionally more again when Dyngo is removed (why?). Then it remains somewhat higher when both Dyngo and DMSO are removed, which is somehow interpreted as Dyngo remaining in the bilayer, but not DMSO. These interpretations are difficult to grasp, as the authors seem to be implying simple amphiphilic partitioning into the membrane, which should all be removable by efficient washing. I do not doubt that this compound interacts with membranes, but the quantifications appear ambiguous. A bilayer with 16 mol% (or worse, 30% if all in one leaflet) Dyngo is very unlikely (to remain a bilayer). Even if such a bilayer was conceivable, the authors are claiming an ADDITION of Dyngo that would INCREASE the area of one leaflet by 30%, which needs explanation as it appears unlikely. Also, there are no replicates shown, so unclear how reproducible these effects are?
3. The simulations are insufficiently described and difficult to interpret. How big are these systems? Why do the figures show the aqueous system with lateral boundaries? It seems quite important that multiple Dyngo molecules aggregate rather than partition into membranes - is this likely to occur in experiment? PMF simulations are strongly suggesting that Dyngo does not spontaneously cross membranes, which is inconsistent with its drug-like amphiphilicity (cLogP~2.5 is optimally suited for membrane permeation) and known effects on intracellular proteins. This suggests an artefact in these PMFs. The authors should experimentally measure the permeation of Dyngo through bilayers (or lack thereof), to more robustly support their finding that Dyngo does not cross membranes spontaneously.
4. Why not measure effect of Dyngo on lipid packing directly and more broadly in model membranes?
5. Statistics should not be done on individual cells (n>26), but rather on independent experiment (N=3?)
6. Fig 1G is important but rather unclear. Firstly, these kymographs are an odd way to show that the caveolae are not moving. More importantly, caveolae in normal cells have been shown to be quite stable and immobile (eg doi: 10.1074/jbc.M117.791400), yet here they are claimed to be very mobile. Also, if Dyngo prevents caveolae scission, there should be more of them at the membrane - why no quantification like Fig 1C to show accumulation of caveolae upon Dyngo treatment? Or directly counting caveolae via EM, as in Fig 4C?
7. The writing can be made more precise and referencing could be strengthened. Some examples: (a) 'scissoned' is not a word in English, (b) what is meant by "Cav1 assembly is driven by high chol content"? There are many types of caveolin assemblies. (c) "This generates a unique membrane domain with distinct lipid packing and a very high curvature." Unclear what 'this' refers to and there is no reference here, so what is the evidence for either of these claims? Caveolin-8S oligomers are not curved. Perhaps 'this' is caveolae, but they are relatively large and also not very highly curved and I am unaware of measurements of lipid packing therein. The sentence following that one again makes a specific, but unreferenced, claim. (d) intro claims that lipid packing is critical for fission, but it is unclear quite what is meant by this claim. The references do not help, as they are often about the basic biophysics of lipids, rather than how packing affects fission. (e) intro strongly implies that caveolae remain membrane attached because of stalled scission. How strong is the evidence for this? The fact that EHD2 is at the neck is not definitive, (f) unclear what is meant by 'lipid packing frustration' and how Dyngo supposedly induces it.
8. IF of Cav1 is insufficient to claim puncta as caveolae. Co-stained puncta of caveolin with cavin are much stronger evidence. Same issue for Cav1-GFP puncta.
9. Fig 3E claims that "preferred position of Dyngo-4a was closer to the head groups" but the minimum looks to be in similar place as Fig 3B without cholesterol. Critically, these results do not support the notion that Dyngo affects lipid packing sufficiently, which is not measured in the simulations (though could be). Finally, the simulation data do not show "that Dyngo-4a is competing with cholesterol"; it is unclear what 'competition' means in this context, but regardless, the data only shows that Dyngo sits at a similar location as cholesterol.
10. AFM measures the stiffness of the cell (as correctly explained in Results section) not "overall stiffness of the PM" as stated in the Discussion.
11. Fig2A: what was the starting lipid surface pressure? How does Dyngo insertion depend on initial lipid packing?
12. Fig 4B is a strange approach to measure membrane motion. Why not RMSD or some other displacement based method? As its shown, it implies that the area of the cell changes.

Significance

The title, abstract, and introduction of the manuscript are largely framed around lipid packing, but most of the data investigate other unexpected effects of treating cells with Dyngo4a. The only measurement for lipid packing (or any other membrane properties) is Fig 4E-F. Therefore, this paper is effectively an investigation of an artefact of a common reagent, which itself could be a valuable contribution. However, the mechanism to explain its effect requires stronger evidence, and its broad biological significance needs further exploration.

Overall, the impact of documenting the effects of Dyngo4a on membranes appears modest but may be valuable to the membrane trafficking community.

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Referee #2

Evidence, reproducibility and clarity

This manuscript uses the small molecule dynamin inhibitors dynasore and dyngo to show that in dynamin triple knockout cells that these inhibitors impact lipid packing and organization in the plasma membrane. Data showing that dyngo affects caveolin dynamics using tirf microscopy is also shown and is interpreted to reflect inhibition of caveolae scission from the membrane.

This data showing that dyngo and dynasore target membrane order is quite compelling and argues that the effects of these inhibitors is not dynamin specific and that inhibition of endocytosis by these small molecule inhibitors is dynamin-independent. The in vitro and in vivo data they provide is convincing.

Similarly, the data showing that dynasore and dyngo affect caveolin dynamics and clathrin endocytosis (transferrin) is quite convincing and argues that altered lipid packing is impacting membrane dynamics at the plasma membrane. What is less convincing is the conclusion is that dyngo is preventing caveolae scission from the membrane. Study of caveolae endocytosis is based on a TIRF assay that has inherent limitations:

• Caveolae are defined as bright cav1-positive spots in diffraction limited TIRF and their disappearance presumed to be endocytic events. Cav1 spots are presumed to be caveolae but the authors do not consider that they may be flat non-caveolar oligomers. The diffraction limited TIRF approach interprets the large structures as caveolae but evidence to that effect is lacking.
• The analysis (and the diagram presented in figure 4) considers that caveolae can either diffuse laterally in the membrane or internalize and does not consider that caveolae can flatten and possibly fragment in the membrane. Is it not possible that loss of Cav1 spots is a fragmentation event and not necessarily a scission event?
• The analysis is based on overexpression of Cav1-GFP that may alter the stoichiometry between Cav1 and cavin1 such that while caveolae may be expressed, larger non-caveolar structures may accumulate.
• Cav1 has been shown to be internalized via the CLIC pathway (Chaudary et al, 2014) and if dyngo is impacting clathrin then maybe it is also impacting CLIC endocytosis and thereby Cav1 endocytosis via this pathway?
• The longer Cav1 TIRF track time and shorter displacement with dyngo is consistent with inhibition of caveolae scission. However, as the authors discuss, could not reduced membrane undulations due to dyngo's impact on membrane order be responsible for the longer tracks? Alternatively, perhaps the altered lipid packing is corralling Cav1 movement and reducing non-caveolar Cav1 endocytosis, resulting in shorter tracks of longer duration? The proposed interaction of dyngo with cholesterol could prevent scission but also stabilize large (flat?) Cav1 oligomers in the membrane, perhaps reducing Cav1 oligomer fragmentation.

My point here is not to discredit the data but only to suggest that the TIRF approach used is an indirect measure of caveolae scission from the membrane that requires substantiation using other approaches.

Dyngo is certainly generally affecting lipid packing via cholesterol and thereby affecting Cav1 dynamics in the plasma membrane. The claim of caveolae scission should be qualified and alternative possibilities considered and discussed. If the authors persist in arguing that dyngo is affecting caveolae scission then the effect should be substantiated by accumulation of caveolae by quantitative EM and high spatial and temporal resolution imaging of Cav1 and cavin1 to define the endocytic events. As the latter represents a new, and potentially very challenging, line of experimentation, I would suggest that it is beyond the scope of the current study. As indicated above the additional experiments are not necessary and qualification of the claims would be sufficient.

Other points

Figure 1C - Cav1 positive spots cannot be interpreted to be caveolae from diffraction limited confocal images. Same comment applies to Fig 4G - caveola? duration.

Figure 4C - it is not clear why this EM data is not quantified - for both the number of caveolae and clathrin coated pits - as this would help clarify the interpretation of the effect reported.

Figure 4D - the AFM experiments should perhaps be repeated as the non-significant effect of dyngo on the Young's modulus may be a result of insufficient n values.

Significance

This data showing that dyngo and dynasore target membrane order is quite compelling and argues that the effects of these inhibitors is not dynamin specific and that inhibition of endocytosis by these small molecule inhibitors is dynamin-independent. The in vitro and in vivo data they provide is convincing.

Similarly, the data showing that dynasore and dyngo affect caveolin dynamics and clathrin endocytosis (transferrin) is quite convincing and argues that altered lipid packing is impacting membrane dynamics at the plasma membrane.

What is less convincing is the conclusion is that dyngo is preventing caveolae scission from the membrane.

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Referee #1

Evidence, reproducibility and clarity

The authors use Dyngo-4a, a known Dynami inhibitor to test its influence on caveolar assembly and surface mobility. They investigate, whether it incorporates into membranes with Quartz-Crystal Microbalance, they investigate how it is organized in membranes using simulations. Finally, they use lipid-packing sensitive dyes to investigate lipid packing in the presence of Dyngo-4a, membrane stiffness using AFM and membrane undulation using fluorescence microscopy. They also use a measure they call "caveola duration time" to claim that something happens to caveolae after Dyngo-4a addition and using this parameter, they do indeed see an increase in it in response to Dyngo-4a, which is reduced back to the baseline after addition of cholesterol.

Overall, the authors claim: 1) Dyngo-4a inserts into the membrane and this 2) results in "a dramatic dynamin-independent inhibition of caveola scission". 3) Dyngo-4a was inserted and positioned at the level of cholesterol in the bilayer and 4) Dyngo-4a-treatment resulted in decreased lipid packing in the outer leaflet of the plasma membrane 5) but Dyngo-4a did not affect caveola morphology, caveolae- associated proteins, or the overall membrane stiffness 6) acute addition of cholesterol counteracts the block in caveola scission caused by Dyngo-4a

Overall, in this reviewers opinion, claims 1, 3, 4, 5 are well-supported by the presented data from electron and live cell microscopy, QCM-D and AFM. However, there is no convincing assay for caveolar endocytosis presented besides the "caveola duration" which although unclearly described seems to be the time it takes in imaging until a caveolae is not picked up by the tracking software anymore in TIRF microscopy. Since the main claim of the paper is a mechanism of caveolar endocytosis being blocked by Dyngo-4a, a true caveolar internalization assays is required to make this claim. This means either the intracellular detection of not surface connected caveolar cargo or the quantification of caveolar movement from TIRF into epifluorescence detection in the fluorescence microscope. Otherwise, the authors could remove the claim and just claim that caveolar mobility is influenced.

Significance

A number of small molecule inhibitors for the GTPase dynamics exist, that are commonly used tools in the investigation of endocytosis. This goes as far that the use of some of these inhibitors alone is considered in some publications as sufficient to declare a process to be dynamin-dependent. However, this is not correct, as there are considerable off-target effects, including the inhibition of caveolar internalization by a dynamin-independent mechanism. This is important, as for example the influence of dynamin small molecule inhibitors on chemotherapy resistance is currently investigated (see for example Tremblay et al., Nature Communications, 2020).

The investigation of the true effect of small molecules discovered as and used as specific inhibitors and their offside effects is extremely important and this reviewer applauds the effort. It is important that inhibitors are not used alone, but other means of targeting a mechanism are exploited as well in functional studies. The audience here thus is besides membrane biophysicists interested in the immediate effect of the small molecule Dyngo-4a also cell biologists and everyone using dynamic inhibitors to investigate cellular function.

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Reply to the reviewers

Reviewer #1 (Evidence, Reproducibility, and Clarity)

Reviewer comment: This is a very well conceived study of responses to plasma membrane stresses in yeast that signal through the conserved TORC2 complex. Physical stress through small molecular intercalators in the plasma membrane is shown to be independent of their biochemistry and then studies for its effect on plasma membrane morphology and the distribution of free ergosterol (the yeast equivalent of cholesterol), with free being the pool of cholesterol that is available to probes and/or sterol transfer proteins. Experiments nicely demonstrate a negative feedback loop consisting of: stress -> increased free sterol and TORC2 inhibition -> activation of LAM proteins (as demonstrated by Relents and co-workers previously) -> removal of free sterol -> return to unstressed state of PM and TORC2.

Author response: We thank the reviewer for their positive and encouraging feedback. We are pleased to submit our revised manuscript and have addressed all points raised below.

Comment: Fig 2A: Is detection of PIP/PIP2/PS linear for target, or possibly just showing availability that is increased due to local positive curvature?

Response: This is an excellent and fundamental question. While FLARE signal likely reflects lipid availability, its detection is indeed influenced by factors such as membrane curvature and lipid composition, due to varying insertion depths of the lipid-binding domains. For example, studies using NMR suggest that the PLCδ PH domain partially inserts into membranes, potentially conferring curvature sensitivity (Flesch et al., 2005; Uekama et al., 2009). Similarly, curvature influences lactadherin binding, though it's unclear if this extends to its isolated C2 domain (Otzen et al., 2012; Shao et al., 2008; Shi et al., 2004). We could not find direct evidence for curvature sensitivity of P4C(SidC), but assume some influence exists.

To avoid overinterpreting these limitations, we now describe our data based solely on the FLAREs used, rather than inferring enrichment of specific lipid species. We refer to these PM structures as "PI(4,5)P₂-containing", consistent with prior literature (Riggi et al., 2018) and have revised our manuscript accordingly.

Comment: Can any marker be identified for the D4H spots at 2 minutes? In particular, are they early endosomes (shown by brief pre-incubation with FM4-64)?

Response: We appreciate the reviewer's suggestion and have now added new data (Fig. S2E-H). We tested colocalization of D4H spots with FM4-64 (early endosomes), GFP-VPS21 (early endosome marker), and LipidSpot{trade mark, serif} 488 (lipid droplets), but found no overlap. This later observation was not unexpected given that D4H does not recognize Sterol esters. D4H foci also did not overlap with ER (dsRED-HDEL), though they were frequently adjacent to it. While their exact identity remains unknown, we agree this is an intriguing direction for future investigation.

Comment: Is there any functional (& direct) link between Arp inhibition (as in the Pombe study of LAMs by the lab of Sophie Martin) and PM disturbance by amphipathic molecules?

Response: We have explored this connection and now present new data (see final paragraph of Results). Briefly, we show that CK-666 induces internalization of PM sterols in a Lam2/4-dependent manner, and that TORC2 activity is more strongly reduced in lam2Δ lam4Δ cells compared to WT. These findings support the idea that, like PalmC, Arp2/3 inhibition triggers a PM stress that is counteracted by sterol internalization.

Minor Comment: Fig 2A: Labels not clear. Say for each part what FP is used for pip2.

Response: As noted above, we revised image labels to clarify which FLAREs were used, and refer to data accordingly throughout.

Minor Comment: Move fig s2d to main ms. The 1 min and 2 min data are integral to the story.

Response: We agree and have incorporated the 1-min and 2-min data into the main figures. Vehicle-treated controls were moved to Fig. S2.

Minor Comment: The role of Lam2 and Lam4 in retrograde sterol transport has in vivo only been linked to one of their two StART domains not both, as mentioned in the text.

Response: Thank you for pointing this out. We have corrected the text to:

"[...]Lam2 and Lam4[...] contain two START domains, of which at least one has been demonstrated to facilitate sterol transport between membranes (Gatta et al., 2015; Jentsch et al., 2018; Tong et al., 2018)."

Minor Comment: Throughout, images of tagged D4H should be labelled as such, not as "Ergosterol".

Response: We have updated all relevant figure labels and text to refer to "D4H" rather than "Ergosterol", in line with this recommendation.

Reviewer #1 (Significance):

These results in budding yeast are likely to be directly applicable to a wide range of eukaryotic cells, if not all of them. I expect this paper to be a significant guide of research in this area. The paper specifically points out that the current experiments do not distinguish the precise causation among the two outcomes of stress: increased free sterol and TORC2 inhibition. Of these two outcomes which causes which is not yet known. If data were added that shed light on this causation that would make this work much more signifiant, but I can understand 100% that this extra step lies beyond - for a later study for which the current one forms the bedrock.

Response:

We thank the reviewer for their generous assessment. We agree that understanding the causality between increased free sterol and TORC2 inhibition is a critical next step.

Based on our current data, we believe the increase in free ergosterol precedes TORC2 inhibition. For example, TORC2 inhibition alone (e.g., via pharmacological means) does not initially increase free sterol, while it does enhance Lam2/4 activity, promoting sterol internalization (Fig. 3A). Baseline TORC2 activity also inversely correlates with free PM sterol levels in lam2Δ lam4Δ versus LAM2T518A LAM4S401A cells (Figs. 2D, S2C).

Additionally, during sterol depletion, we observe an initial increase in TORC2 activity before growth inhibition occurs, after which activity declines-likely due to compromised PM integrity (Fig. S2M). We now also show that adaptation to several other stresses (e.g., osmotic shock, heat shock, CK-666) partially depends on sterol internalization, which correlates with TORC2 activation (Fig. 4, S4B).

While these findings strengthen the model that PM stress perturbs sterol availability and secondarily impacts TORC2, we cannot yet definitively demonstrate causality. As suggested by Reviewer 3, we tested cholesterol-producing yeast (Souza et al., 2011), but found their response to PalmC indistinguishable from WT, making it difficult to draw mechanistic conclusions (Rebuttal Fig. 2).

Taken together, we favour a model where sterols affect PM properties sensed by TORC2, probably lipid-packing, rather than acting as direct effectors. We hope our revised manuscript more clearly conveys this model and serves as a strong foundation for future mechanistic studies.

Reviewer #2 (Evidence, Reproducibility, and Clarity)

Reviewer comment: This manuscript describes multiple effects of positively-charged membrane-intercalating amphipaths (palmitoylcarnitine, PalmC, in particular) on TORC2 in yeast plasma membranes. It is a "next step" in the Loewith laboratory's characterization of the effect of this agent on this system. The study confirms the findings of Riggi et al.(2018) that PalmC inhibits TORC2 and drives the formation of membrane invaginations that contain phosphatidylinositol-bis-phosphate (PIP2) and other anionic phospholipids. It also demonstrates that PalmC intercalates into the membrane, acts directly (rather than through secondary metabolism) and is representative of a class of cationic amphipaths. The interesting finding here is that PalmC causes a rapid initial increase in the plasma membrane ergosterol accessible to the DH4 sterol probe followed by a decrease caused by its transfer to the cytoplasm through its transporter, LAM2/4. TORC2 is implicated in these processes. Loewith et al. have pioneered in this area and this study clearly shows their expertise. Several of the findings reported here are novel. However, I am concerned that PalmC may not be revealing the physiology of the system but rather adding tangential complexity. (This concern applies to the precursor studies using PalmC to probe the TORC2 system.) In particular, I am not confident that the data justify the authors' conclusions "...that TORC2 acts in a feedback loop to control active sterol levels at the PM and [the results] introduce sterols as possible TORC2 signalling modulators."

Author response:

We thank Reviewer #2 for the constructive and critical evaluation of our work. We appreciate the acknowledgment of the novelty and technical strength of several of our findings, and we understand the concern that PalmC could be eliciting non-physiological effects. Our study was designed precisely to use PalmC and similar membrane-active amphipaths as tools to strongly perturb the plasma membrane (PM) in a controlled and tractable way. We now state this intention explicitly in both the Introduction and Discussion sections. To address concerns about the specificity and physiological relevance of PalmC, we have expanded our dataset to include additional PM stressors (hyperosmotic shock, Arp2/3 inhibition, and heat shock), all of which reproduce key features observed with PalmC-namely, TORC2 inhibition, PM invaginations, and retrograde sterol transport (Fig. 4, S4).

We hope this more comprehensive dataset, along with revised discussion and clarified claims, addresses the reviewer's concerns regarding physiological interpretation and artifact.

Major issues 1 and 2: 1. The invaginations induced by PalmC may not be physiologic but simply the result of the well-known "bilayer couple" bending of the bilayer due to the accumulation of cationic amphipaths in the inner leaflet of the plasma membrane bilayer which is rich in anionic phospholipids. Such unphysiological effects make the observed correlation of invagination with TORC2 inhibition etc. hard to interpret.

Electrostatic/hydrophobic association of PIP2 with PalmC could sequester the anionic phospholipid(s). Such associations could also drive the accumulation of PIP2 in the invaginations. This could explain PalmC inhibition of TORC2 through a simple physical rather than biological process. So, it is difficult to draw any physiological conclusion about PIP2 from these experiments.

Response to major issues 1 and 2:

We agree that amphipath-induced bilayer stress, including via the bilayer-couple mechanism, may contribute to PM curvature changes. However, the reviewer's assumption that PalmC inserts preferentially into the inner leaflet appears inconsistent with both literature and our observations. PalmC is zwitterionic, not cationic, and is unlikely to electrostatically sequester anionic lipids such as PIP2. For clarification, we included a short summary of our proposed mechanism of PalmC in the context of the current literature in our Discussion:

"[...] study it was also demonstrated that addition of phospholipids to the outer PM leaflet causes an excess of free sterol at the inner PM leaflet, and its subsequent retrograde transport to lipid droplets (Doktorova et al., 2025). Although we cannot exclude that it is the substrate of a flippase or scramblase, PalmC is not a metabolite found in yeast, nor, given its charged headgroup, is it likely to spontaneously flip to the inner leaflet (Goñi, Requero and Alonso, 1996). Thus, we propose that PalmC accumulates in the outer leaflet, disrupts the lipid balance with the inner leaflet which is, similarly to the mammalian cell model (Doktorova et al., 2025), rectified by sterol mobilization, flipping and internalization (Fig. 5B)."

While we agree that PM invaginations per se are not the central focus of this study, they are indeed a reproducible and biologically intriguing phenomenon. We emphasize that similar invaginations occur not only during PalmC treatment but also in response to other physiological stresses, such as hyperosmotic shock and Arp2/3 inhibition (Fig. 4), and have been reported independently by others (Phan et al., 2025). Furthermore, related structures have been documented in yeast mutants with altered PIP2 metabolism or TORC2 hyperactivity (Rodríguez-Escudero et al., 2018; Sakata et al., 2022; Stefan et al., 2002), and even in mammalian neurons with SJ1 phosphatase mutations (Stefan et al., 2002). These observations support our interpretation that the observed invaginations represent an exaggerated manifestation of a physiologically relevant stress-adaptive process. In our previous study we indeed proposed that PI(4,5)P2 enrichment in PM invaginations was important for PalmC-induced TORC2 inactivation, using the heat sensitive PI(4,5)P2 kinase allele mss4ts - a rather blunt tool (Riggi et al., 2018). We have now come to the conclusion that different mechanisms other than, or in addition to, PIP2 changes drive TORC2 inhibition in our system. In this study, we use the 2xPH(PLC) FLARE exclusively as a generic PM marker, not as a readout of PIP2 biology. Rather, we propose that sterol redistribution and/or the biophysical impact that this has on the PM are central drivers, with TORC2 acting as a signaling node that senses and adjusts PM composition accordingly.

We now clarify these arguments in the revised Discussion and have reframed our use of PalmC as a probe to explore the capacity of the PM to adapt to acute stress via dynamic lipid rearrangements.

Major issue 3:

As the authors point out, a large number of intercalated amphipaths displace sterols from their association with bilayer phospholipids. This unphysiologic mechanism can explain how PalmC causes the transient increase in the availability of plasma membrane ergosterol to the D4H probe and its subsequent removal from the plasma membrane via LAM2/4. TORC2 regulation may not be involved. In fact, the authors say that "TORC2 inhibition, and thereby Lam2/4 activation, cannot be the only trigger for PalmC induced sterol removal." Furthermore, the subsequent recovery of plasma membrane ergosterol could simply reflect homeostatic responses independent of the components studied here.

Response:

We agree that increased free sterols in the inner leaflet likely initiate retrograde transport. Our results suggest that TORC2 inhibition facilitates this process by disinhibiting Lam2/4, allowing more efficient clearance of ergosterol from the PM (Fig. 3A, S2C). However, the process is not exclusively dependent on TORC2, and we state this explicitly.

We do not observe recovery of PM ergosterol on the timescales measured, while TORC2 activity recovers, suggesting that restoration likely occurs later via biosynthetic or anterograde trafficking pathways, which are outside the scope of this study. These points are clarified in the revised Discussion.

Major issue 3a:

The data suggest that LAM2/4 mediates the return of cytoplasmic ergosterol to the plasma membrane. To my knowledge, this is a nice finding that not been reported previously and is worth confirming more directly.

Response:

We thank the reviewer for this observation but would like to clarify a misunderstanding: our data do not suggest that Lam2/4 mediates anterograde sterol transport. Our results and prior work (Gatta et al., 2015; Roelants et al., 2018) show that Lam2/4 mediate retrograde transport from the PM to the ER, and TORC2 inhibits this process. We now clarify this point in the revised manuscript, stating:

"In vivo, Lam2/4 seem to predominantly transport sterols from the PM to the ER, following the concentration gradient (Gatta et al., 2015; Jentsch et al., 2018; Tong et al., 2018)."

Major issue 4:

I agree with the authors that "It is unclear if the excess of free sterols itself is part of the inhibitory signal to TORC2..." Instead, the inhibition of TORC2 by PalmC may simply result from its artifactual aggregation of the anionic phospholipids (especially, PIP2) needed for TORC2 activity. This would not be biologically meaningful. If the authors wish to show that accessible ergosterol inhibits TORC2 activity or vice versa, they should use more direct methods. For example, neutral amphipaths that do not cause the aforementioned PalmC perturbations should still increase plasma membrane ergosterol and send it through LAM2/4 to the ER.

Response:

We now provide evidence that three orthologous treatments (hyperosmotic shock, heat shock and Arp2/3 inhibition) similarly cause sterol mobilization and, in the absence of sterol clearance from the PM, prolonged TORC2 inhibition. These results do not support the reviewer's contention that the inhibition of TORC2 by PalmC is simply resulting from its artifactual aggregation of the anionic phospholipids. Furthermore, PalmC is zwitterionic, and its interaction with anionic lipids should be somewhat limited.

In our experimental setup, neutral amphipaths did not trigger TORC2 inhibition or D4H redistribution While this differs from prior in vitro work (Lange et al., 2009), we attribute this in part to a discrepancy to experimental setup differences, including flow chamber artifacts that we discuss in the methods section.

Importantly, only amphipaths with a charged headgroup, including zwitterionic (PalmC) and positively charged analogs, produced robust effects. A negatively charged derivative also seemed to have a minor effect on TORC2 activity and PM sterol internalization (Palmitoylglycine (Fig. 1D, Rebuttal Fig. 1). This suggests that in vivo, charge-based membrane perturbation is required to alter PM sterol distribution and TORC2 activity.

Major issue 5.:

The mechanistic relationship between TORC2 activity and ergosterol suggested in the title, abstract, and discussion is not secure. I agree with the concluding section of the manuscript called "Limitations of the study". It highlights the need for a better approach to the interplay between TORC2 and ergosterol.

Response:

This may have been true of the previous submission, but we now demonstrate that provoking PM stress in four orthogonal ways triggers mobilization of sterols, which left uncleared, prevents normal (re)activation of TORC2 activity. We thus conclude that free sterols, directly or more likely indirectly, inhibit TORC2. The role that TORC2 plays in sterol retrotranslocation has been demonstrated previously (Roelants et al., 2018). We believe our expanded data and clarified framework make a compelling case for a stress-adaptive role of sterol retrograde transport that is supervised and modulated-but not fully driven-by TORC2 activity.

Thus, we feel in the present version of this manuscript that the title is now justified.

Minor issue: Based on earlier work using the reporter fliptR, the authors claim that PalmC reduces membrane tension. They should consider that this intercalated dye senses many variables including membrane tension but also lipid packing. I suspect that, by intercalating into and thereby altering the bilayer, PalmC is affecting the latter rather than the former.

Response:

We thank the reviewer for this important point regarding the multifactorial sensitivity of intercalating dyes such as Flipper-TR®, including to membrane tension and lipid packing.

We respectfully note, however, that our current study does not include any new data generated using Flipper-TR®. We referred to earlier work (Riggi et al., 2018) for context, where Flipper-TR® was used as a membrane tension reporter.

We fully agree that the response of such "smart" membrane probes integrates multiple biophysical parameters-including tension, packing, and hydration-which are themselves interrelated as consequences of membrane composition (Colom et al., 2018; Ragaller et al., 2024; Torra et al., 2024). Indeed, this interconnectedness is central to our interpretation of PalmC's pleiotropic effects on the plasma membrane (PM). In our previous study, we observed that PalmC treatment not only reduced apparent PM tension (as measured by Flipper-TR®) but also increased membrane order ((Riggi et al., 2018); see laurdan GP, Fig. 6C), and here we show that it promotes the redistribution of free sterol away from the PM.

Furthermore, PalmC's effect on membrane tension was supported by orthogonal in vitro data: its addition to giant unilamellar vesicles (GUVs) led to a measurable increase in membrane surface area and decreased tension, as shown by pipette aspiration ((Riggi et al., 2018), Fig. 3F). This provides complementary evidence that the membrane tension reduction is not merely an artifact of Flipper-TR® reporting.

That said, we agree with the reviewer that in the case of TORC2 inhibition or hyperactivation, the observed changes in PM tension are based solely on Flipper-TR® data, without additional orthogonal validation. To address this concern, we have revised the relevant text in the manuscript to more cautiously reflect this complexity. The revised sentence now reads:

"Consistent with this role, data generated with the lipid packing reporter dye Flipper-TR® suggest that acute chemical inhibition of TORC2 increases PM tension, while Ypk1 hyperactivation decreases it."

This revised phrasing acknowledges both the utility and the limitations of Flipper-TR® as a probe of membrane biophysics.

Reviewer #2 Significance:

This is an interesting topic. However, use of the exogenous probe, palmitoylcarnitine, could be causing multiple changes that complicate the interpretation of the data.

Reviewers #1 and #3 were much more impressed by this study than I was. I am not a yeast expert and so I may have missed or confused something. I would therefore welcome their expert feedback regarding my comments (#2). Ted Steck

Response:

Thank you for your constructive feedback.

We believe that the manuscript is now much improved, and we hope to have convinced you that the mechanisms that we've elucidated using PalmC represent a general adaptation response to physiological PM stressors.

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

Reviewer comment: The authors describe the effects of surfactant-like molecules on the plasma membrane (PM) and its associated TORC2 complex. Addition of the surfactants with a positively-charged headgroup and a hydro-carbon tail of at least 16 caused the rapid clustering of PI-4,5P2 together with PI-4P and phosphatidylserine in large membrane invaginations. The authors convincingly demonstrate that this effect of the surfactants on the PM is likely caused by a direct disturbance of the PM organization and/or lipid composition. Interestingly, upon PalmC treatment, free ergosterol of the PM was found to first concentrate in the clusters, but within The kinetics of the changes in free ergosterol levels and the changes in TORC2 activity do not match. Ergosterol is rapidly depleted after PalmC treatment (The Lam2/4 data support the idea that ergosterol transport plays a role in the TORC2 recovery, but what role this is, is not clear to me. I think the data fit better with a model in which PalmC causes low tension of the PM which in turn disrupts normal lipid organization and thus causes TORC2 to shut down, maybe not by changes in free ergosterol but by changes, for instance, in lipid raft formation (which is in part effected by ergosterol levels). The transport of ergosterol is only one mechanism that is involved in restoring PM tension and TORC2 activity. However, sensing free ergosterol alone is most likely not the mechanism explaining how TORC2 senses PM tension.

Therefore, I recommend that the model is revised (or supported by more data), reflecting the fact that free ergosterol levels do not directly correlate with the TORC2 activity, but instead might be only one of the PM parameters that regulate TORC2.

Author response:

We thank the reviewer for their thoughtful assessment and constructive suggestions. As described in more detail above, we have included in our revised version of this manuscript a variety of new data, including the sterol-internalization dependent adaptation of the PM and regulation of TORC2 during additional stresses. We think that these data vastly improve on our previous manuscript version. We have addressed each point risen by the reviewer below and revised the manuscript accordingly, including a rewritten discussion and updated model to better reflect the limitations of our current understanding of how TORC2 senses changes in the plasma membrane (PM). It is true that the appearance of PM invaginations tracks well with TORC2 inhibition, but it is not clear to us if they are upstream of this inhibition or merely another symptom of the preceding PM perturbation (PalmC-induced free sterol increase can be observed after 10s (Fig. S2A), but PM invaginations become visible only after ~1 min - meanwhile we can observe near complete TORC2 inhibition after 30s). In this study, we are mostly interested in the role of PM sterol redistribution in stress response. Indeed we think that the role of free sterol clearance during stresses is to adapt the PM to these stresses - thus restoring PM parameters which in turn reactivates TORC2. This can be seen for hyperosmotic stress and the newly introduced PM stressors, Arp2/3 inhibition and heat shock response (Fig. 4). We have therefore softened our model and updated discussion and final figure (Fig. 5) to reflect that TORC2 likely responds to broader changes in PM organization or tension, with sterol redistribution representing one of several contributing factors rather than the sole signal.

Comment: - If TORC2 is indeed inhibited by free ergosterol, the addition of ergosterol to the growth medium should be able to trigger similar effects as PalmC. If this detection of free ergosterol is very specific (e.g. if TORC2 has a binding pocket for ergosterol) we would expect that addition of other sterols such a cholesterol or ergosterol precursors should not inhibit TORC2.

Response:

We appreciate this suggestion and agree that testing whether exogenous ergosterol can mimic PalmC effects would help assess specificity. However, yeast do not readily take up sterols under aerobic conditions, which renders artificial sterol enrichment at the yeast PM rather difficult. We have now included additional data characterizing our Lam2/4 mutants (see below), and pharmacological sterol synthesis inhibition, showing that a depletion of free sterols from the PM correlates with lower TORC2 activity (Fig. 2D, S2C). Additionally, as suggested, we tried to probe if ergosterol directly interacts with TORC2 through a specific binding pocket, by treating a yeast strain expressing cholesterol rather than ergosterol (Souza et al., 2011) with PalmC. However, the response of TORC2 activity in these cells was very similar to that of WT cells (Rebuttal Fig. 2). In conclusion, we agree that at present we do not know mechanistically how sterols affect TORC2 activity, although it does indeed seem more likely to be through an indirect mechanism linked to changes in PM parameters. The nature of such a mechanism will be subject to further studies. We hope that the introduced changes to the manuscript adequately reflect these considerations.

Rebuttal Fig. 2: WT yeast cells which produce ergosterol as main sterol, and mutant cells which produce cholesterol instead were treated with 5 µM PalmC, and TORC2 activity was assessed by relative phosphorylation of Ypk1 on WB. One representative experiment out of two replicates.

Comment: - The experiment in Figure 1C is not controlled for differences in membrane intercalation of the different compounds. For instance, does C16 choline and C16 glycine accumulate at the same rate in the PM (measure similar to experiment in Figure 1B). Maybe the positive charge at the headgroup of the surfactants increases the local concentration at the PM and therefore can explain the difference in effect on the PM.

Response:

We agree with the reviewer that the effects of the various PalmC derivatives are not directly controlled for differences in membrane intercalation. Our structure-activity screen was intended to demonstrate the general biophysical mode of action of PalmC-like compounds and to define minimal structural requirements for activity.

We now note in the manuscript that differential membrane insertion could contribute to the observed variation in efficacy, particularly in relation to tail length. While we considered this additional suggested experiment, it was ultimately judged to be outside the scope of this study due to its complexity and limited impact on the central conclusions.

A clarifying sentence has been added to the relevant results section to explicitly acknowledge this limitation:

"We did not control for differences in PM intercalation efficiency."

We also include a discussion here to further clarify our interpretation. Prior in vitro studies have shown that while intercalation is necessary, it is not sufficient for PM perturbation. For example, palmitoyl-CoA intercalates into membranes but does not induce the same biophysical effects as PalmC (Goñi et al., 1996; Ho et al., 2002). Thus, we believe that intercalation is only part of the story, and that the intrinsic propensity of different headgroups to perturb the PM plays a key role in the disruption of PM lipid organization.

Comment: - Are the intracellular ergosterol structures associated (or in close proximity) with lipid droplets (ergosterol being modified and delivered into a lipid droplet)?

Response:

We thank the reviewer for raising this point. We now include additional data (Fig. S2H) showing that intracellular D4H-positive structures do not reside near or colocalize with lipid droplets. The latter is not entirely unexpected as D4H does not recognize esterified sterols. However, we do observe an increase in overall LD volume following PalmC treatment, consistent with the idea that internalized PM sterols may be stored in LDs as sterol esters over time - although we did not test if this increase in LD volume is Lam2/4 dependent. This increase is mentioned in the revised results text. An increase in cellular LDs has also been recently reported during hyperosmotic shock (Phan et al., 2025).

For more attempts to identify a marker for intracellular D4H foci, see reply to reviewer 1.

Comment:

• How does the AA and DD mutations in Lam2/4 change the localization of the ergosterol sensor (before and after PalmC treatment).

Response:

We thank the reviewer for this question, as in the course of generating these data we realized that our "inhibited" DD mutant was in fact not phosphomimetic but displayed the same D4H distribution as the "hyperactive" AA mutant, i.e. a marked inwards shift of D4H signal away from the PM to internal structures due to increased PM-ER retrograde transport of sterols (Fig. S2C). This led us to critically re-evaluate and ultimately repeat our TORC2 activity WB experiments for PalmC treatment in LAM2/4 mutants. In this new set of experiments, the faster TORC2 recovery after PalmC treatment in the LAM2T518A LAM4S401A mutant did unfortunately not repeat robustly. It is possible that such differences can be observed under specific conditions. Nevertheless, the improved overall quality of the Western blot data allowed us to make the observation that baseline activity was already slightly different in these strains. The Lam2/4 centered part of the results section has subsequently been updated in the manuscript:

"Using a phosphospecific antibody, we did not observe an increase in baseline TORC2 activity in lam2Δ lam4Δ cells, which had been previously reported by electrophoretic mobility shift (Murley et al., 2017). Instead, baseline TORC2 activity was consistently slightly decreased in these cells (Fig. 2D). Ypk1, activated directly by TORC2, inhibits Lam2 and Lam4 through phosphorylation on Thr518 and Ser401, respectively (Roelants et al., 2018; Topolska et al., 2020). We substituted these residues with alanine, generating a strain in which Lam2/4 were no longer inhibited by phosphorylation (Roelants et al., 2018). In these cells, yeGFP-D4H showed that free sterols were constitutively shifted away from the PM to intracellular structures (Fig. S2C, bottom panel). Intriguingly, in opposition to lam2Δ lam4Δ cells, basal TORC2 activity was increased in LAM2T518A LAM4S401A cells (Fig. 2D). This suggests that a decrease in free PM sterols stimulates TORC2 activity [...]"

"In LAM2T518A LAM4S401A cells, TORC2 activity recovers with similar kinetics as the WT (Fig. 2D, bottom blot), suggesting that Lam2/4 release from TORC2 dependent inhibition during PalmC treatment is a fast and efficient process in WT cells, not further expedited by these constitutively active Lams."

As suggested, we also observed D4H localization in LAM2T518A LAM4S401A after PalmC treatment, and implemented these data to further demonstrate that PalmC causes an increase in the fraction of free ergosterol at the PM, which is subsequently removed:

"PalmC addition to LAM2T518A LAM4S401A cells likewise resulted first in a transient increase and then a further decrease in PM yeGFP-D4H signal (Fig. 3C, S3D)."

Comment: - Does Lam2/4 localize to ER-PM contact sites near the large PM invaginations, which could allow for efficient transport of the free ergosterol that accumulates in these structures.

Response:

We were curious about this too, and have now added the requested data in our supplementary material and added a sentence in our results:

"Indeed, in cells expressing GFP-Lam2 we observed that PalmC induced PM invaginations often formed at sites with preexisting GFP-Lam2 foci (Fig. S2K, cyan arrow), although GFP-Lam2 foci did not always colocalize with invaginations (Fig. S2K, yellow arrow) and vice versa. "

Additionally, in the effort to characterize intracellular D4H foci during PalmC as requested by reviewer 1, we also looked at the localization of these foci relative to ER, and found that

"During early timepoints, intracellular foci are usually in close vicinity to ER (Fig. S2E)"

Reviewer #3 (Significance (Required)): The manuscript describes the effects of small molecule surfactants on the PM organization and on TORC2 activity. This is an important set of observation that helps understanding the response of cells to environmental stressors that affect the PM. This field of study is very challenging because of the limited tools available to directly observe lipids and their movements. I consider the data and most of its interpretations of high importance, but I am not convinced of the larger model that tries to link the ergosterol data with TORC2 activity. With adjustments of the model or additional experimental support, this manuscript will be of general interest for cell biologists, especially for researchers studying membrane stress response pathways.

Response:

We thank the reviewer for highlighting the importance of studying PM stress responses and acknowledging the technical challenges involved. We hope the applied changes and additional data succeed in softening our claims about TORC2 regulation while convincing the reviewer that free sterol levels at the PM are one of several contributing factors that correlate with changes in TORC2 activity.

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Referee #3

Evidence, reproducibility and clarity

The authors describe the effects of surfactant-like molecules on the plasma membrane (PM) and its associated TORC2 complex. Addition of the surfactants with a positively-charged headgroup and a hydro-carbon tail of at least 16 caused the rapid clustering of PI-4,5P2 together with PI-4P and phosphatidylserine in large membrane invaginations. The authors convincingly demonstrate that this effect of the surfactants on the PM is likely caused by a direct disturbance of the PM organization and/or lipid composition. Interestingly, upon PalmC treatment, free ergosterol of the PM was found to first concentrate in the clusters, but within <5min this ergosterol seemed to be transported into intracellular structures, causing an overall loss in free ergosterol of the PM. The authors speculate that the initial spike in free ergosterol might be the trigger for the shutdown of TORC2 signaling. The PalmC-triggered transport of free ergosterol from the PM to intracellular structures required the lipid transport proteins Lam2/4. Loss of these transporters caused a delay in TORC2 reactivation, supporting the idea that ergosterol transport out of the PM plays a role in the recovery of normal PM organization. Hyperosmotic shock mimics some of the effects observed with PamlC, but unlike PalmC treatment, TORC2 recovery after hyperosmotic shock is not dependent on Lam2/4.

The presented data are of high quality and most conclusions are well supported. However, based on the presented data the model that a PalmC-triggered increase in free ergosterol is the cause of TORC2 inactivation is not obvious to me. The kinetics of the changes in free ergosterol levels and the changes in TORC2 activity do not match. Ergosterol is rapidly depleted after PalmC treatment (<5min) whereas TORC2 activity requires 30min to recover. Also, the hyperosmotic data on free ergosterol levels and TORC2 activity do not match. In fact, the presence of the large PM invaginations is a better predictor of TORC2 activity. The Lam2/4 data support the idea that ergosterol transport plays a role in the TORC2 recovery, but what role this is, is not clear to me. I think the data fit better with a model in which PalmC causes low tension of the PM which in turn disrupts normal lipid organization and thus causes TORC2 to shut down, maybe not by changes in free ergosterol but by changes, for instance, in lipid raft formation (which is in part effected by ergosterol levels). The transport of ergosterol is only one mechanism that is involved in restoring PM tension and TORC2 activity. However, sensing free ergosterol alone is most likely not the mechanism explaining how TORC2 senses PM tension. Therefore, I recommend that the model is revised (or supported by more data), reflecting the fact that free ergosterol levels do not directly correlate with the TORC2 activity, but instead might be only one of the PM parameters that regulate TORC2.

Further comments:

• If TORC2 is indeed inhibited by free ergosterol, the addition of ergosterol to the growth medium should be able to trigger similar effects as PalmC. If this detection of free ergosterol is very specific (e.g. if TORC2 has a binding pocket for ergosterol) we would expect that addition of other sterols such a cholesterol or ergosterol precursors should not inhibit TORC2.
• The experiment in Figure 1C is not controlled for differences in membrane intercalation of the different compounds. For instance, does C16 choline and C16 glycine accumulate at the same rate in the PM (measure similar to experiment in Figure 1B). Maybe the positive charge at the headgroup of the surfactants increases the local concentration at the PM and therefore can explain the difference in effect on the PM.
• Are the intracellular ergosterol structures associated (or in close proximity) with lipid droplets (ergosterol being modified and delivered into a lipid droplet)?
• How does the AA and DD mutations in Lam2/4 change the localization of the ergosterol sensor (before and after PalmC treatment).
• Does Lam2/4 localize to ER-PM contact sites near the large PM invaginations, which could allow for efficient transport of the free ergosterol that accumulates in these structures.

Significance

The manuscript describes the effects of small molecule surfactants on the PM organization and on TORC2 activity. This is an important set of observation that helps understanding the response of cells to environmental stressors that affect the PM. This field of study is very challenging because of the limited tools available to directly observe lipids and their movements. I consider the data and most of its interpretations of high importance, but I am not convinced of the larger model that tries to link the ergosterol data with TORC2 activity. With adjustments of the model or additional experimental support, this manuscript will be of general interest for cell biologists, especially for researchers studying membrane stress response pathways.

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Referee #2

Evidence, reproducibility and clarity

This manuscript describes multiple effects of positively-charged membrane-intercalating amphipaths (palmitoylcarnitine, PalmC, in particular) on TORC2 in yeast plasma membranes. It is a "next step" in the Loewith laboratory's characterization of the effect of this agent on this system. The study confirms the findings of Riggi et al.(2018) that PalmC inhibits TORC2 and drives the formation of membrane invaginations that contain phosphatidylinositol-bis-phosphate (PIP2) and other anionic phospholipids. It also demonstrates that PalmC intercalates into the membrane, acts directly (rather than through secondary metabolism) and is representative of a class of cationic amphipaths. The interesting finding here is that PalmC causes a rapid initial increase in the plasma membrane ergosterol accessible to the DH4 sterol probe followed by a decrease caused by its transfer to the cytoplasm through its transporter, LAM2/4. TORC2 is implicated in these processes.

Loewith et al. have pioneered in this area and this study clearly shows their expertise. Several of the findings reported here are novel. However, I am concerned that PalmC may not be revealing the physiology of the system but rather adding tangential complexity. (This concern applies to the precursor studies using PalmC to probe the TORC2 system.) In particular, I am not confident that the data justify the authors' conclusions "...that TORC2 acts in a feedback loop to control active sterol levels at the PM and [the results] introduce sterols as possible TORC2 signalling modulators."

Major issues

1. The invaginations induced by PalmC may not be physiologic but simply the result of the well-known "bilayer couple" bending of the bilayer due to the accumulation of cationic amphipaths in the inner leaflet of the plasma membrane bilayer which is rich in anionic phospholipids. Such unphysiological effects make the observed correlation of invagination with TORC2 inhibition etc. hard to interpret.
2. Electrostatic/hydrophobic association of PIP2 with PalmC could sequester the anionic phospholipid(s). Such associations could also drive the accumulation of PIP2 in the invaginations. This could explain PalmC inhibition of TORC2 through a simple physical rather than biological process. So, it is difficult to draw any physiological conclusion about PIP2 from these experiments.
3. As the authors point out, a large number of intercalated amphipaths displace sterols from their association with bilayer phospholipids. This unphysiologic mechanism can explain how PalmC causes the transient increase in the availability of plasma membrane ergosterol to the D4H probe and its subsequent removal from the plasma membrane via LAM2/4. TORC2 regulation may not be involved. In fact,the authors say that "TORC2 inhibition, and thereby Lam2/4 activation, cannot be the only trigger for PalmC induced sterol removal." Furthermore, the subsequent recovery of plasma membrane ergosterol could simply reflect homeostatic responses independent of the components studied here.

3a. The data suggest that LAM2/4 mediates the return of cytoplasmic ergosterol to the plasma membrane. To my knowledge, this is a nice finding that not been reported previously and is worth confirming more directly. 4. I agree with the authors that "It is unclear if the excess of free sterols itself is part of the inhibitory signal to TORC2..." Instead, the inhibition of TORC2 by PalmC may simply result from its artifactual aggregation of the anionic phospholipids (especially, PIP2) needed for TORC2 activity. This would not be biologically meaningful. If the authors wish to show that accessible ergosterol inhibits TORC2 activity or vice versa, they should use more direct methods. For example, neutral amphipaths that do not cause the aforementioned PalmC perturbations should still increase plasma membrane ergosterol and send it through LAM2/4 to the ER. 5. The mechanistic relationship between TORC2 activity and ergosterol suggested in the the title, abstract and discussion is not secure. I agree with the concluding section of the manuscript called "Limitations of the study". It highlights the need for a better approach to the interplay between TORC2 and ergosterol.

Minor issue

Based on earlier work using the reporter fliptR, the authors claim that PalmC reduces membrane tension. They should consider that this intercalated dye senses many variables including membrane tension but also lipid packing. I suspect that, by intercalating into and thereby altering the bilayer, PalmC is affecting the latter rather than the former.

Referees cross-commenting

Reviewers #1 and #3 were much more impressed by this study than I was. I am not a yeast expert and so I may have missed or confused something. I would therefore welcome their expert feedback regarding my comments (#2). Ted Steck

Significance

This is an interesting topic. However, use of the exogenous probe, palmitoylcarnitine, could be causing multiple changes that complicate the interpretation of the data.

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Referee #1

Evidence, reproducibility and clarity

This is a very well conceived study of responses to plasma membrane stresses in yeast that signal through the conserved TORC2 complex.

Physical stress through small molecular intercalators in the plasma membrane is shown to be independent of their biochemistry and then studies for its effect on plasma membrane morphology and the distribution of free ergosterol (the yeast equivalent of cholesterol), with free being the pool of cholesterol that is available to probes and/or sterol transfer proteins. Experiments nicely demonstrate a negative feedback loop consisting of: stress -> increased free sterol and TORC2 inhibition -> activation of LAM proteins (as demonstrated by Relents and co-workers previously) -> removal of free sterol -> return to unstressed state of PM and TORC2.

Comments

Fig 2A: Is detection of PIP/PIP2/PS linear for target, or possibly just showing availability that is increased due to local positive curvature?

Can any marker be identified for the D4H spots at 2 minutes? In particular, are they early endosomes (shown by brief pre-incubation with FM4-64)?

Is there any functional (& direct) link between Arp inhibition (as in the Pombe study of LAMs by the lab of Sophie Martin) and PM disturbance by amphipathic molecules ?

Minor

Fig 2A: Labels not clear. Say for each part what FP is used for pip2. Move fig s2d to main ms. The 1 min and 2 min data are integral to the story

The role of Lam2 and Lam4 in retrograde sterol transport has in vivo only been linked to one of their two StART domains not both, as mentioned in the text.

Throughout, images of tagged D4H should be labelled as such, not as "Ergosterol".

Significance

These results in budding yeast are likely to be directly applicable to a wide range of eukaryotic cells, if not all of them. I expect this paper to be a significant guid elf research in this area.

The paper specifically points out that the current experiments do not distinguish the precise causation among the two outcomes of stress: increased free sterol and TORC2 inhibition. Of these two outcomes which causes which is not yet known. If data were added that shed light on this causation that would make this work much more signifiant, but I can understand 100% that this extra step lies beyond - for a later study for which the current one forms the bedrock.

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Reply to the reviewers

We thank all the reviewers for their helpful and constructive comments and for their time.

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

Summary: Dady et al have developed fluorescent reporters to enable live imaging of cell behaviour and morphology in human pluripotent stem cell lines (PSCs). These reporters target 3 main features, the plasma membrane, nucleus and cytoskeleton. Reporter PSCs have been generated using a piggyBac transposon-mediated stable integration strategy, using a hyperactive piggyBac transposase (HyPBase). The same constructs were also used for mosaic labelling of cells within 2D cultures using lipofectamine transfection.

The reporters used are tagged with either eGFP or mKate2 (far red) and tag the plasma membrane (pm) via the addition of a 20 amino-acid sequence from rat GAP-43 to the N-terminus of the fluorescent protein, the nucleus via Histone 2B with a laser-mediated photo-conversion option (H2B-mEos3.2), and the cytoskeleton via F-Tractin. In total, the authors produced lines with the following:

• pm-mKate2 (far red) • pm-eGFP (green) • H2B-mEos3.2 (green to red) • F-tractin-mKate2 (far red) • H2B-mEos3.2 and pm-mKate2 (green to red, plus far red)

The cell lines used to generate these were the human embryonic stem cell line H9 and human induced pluripotent cell line ChiPS4. The constructs were also used to label cells in a mosaic fashion, using lipofectamine transfection of the original cell lines once they had formed neural rosettes.

Using these cells, Dady et al then performed live imaging in vitro of human spinal cord rosettes and assessed cell behaviour. In particular they analysed mitotic cleavage planes and apical positioning of neural progenitor cells (NPCs), and assessed actin dynamics within these cells. They showed a slowing of the cell cycle length after the initial expansion phase, an increase in the rate of asymmetric division of these NPCs, and abscission of the apical membrane during these divisions. The F-tractin reporter showed enrichment at the basal nuclear membrane during these cell divisions, suggested to help prevent basal chromosome displacement during mitosis.

Major comments: The data presented are convincing and could be strengthened by the following additions and clarifications:*

2. How long do the fluorescent reports take to be visible when transfected via lipofectamine? How efficiently are they expressed? And what concentrations were tested to enable the mosaic expression presented? * We followed the manufacturer’s instructions for Lipofectamine 3000 transfection, using the protocol recommended for set up for a 6 wells plate. We detected fluorescence the following morning ~16h. We did not assess earlier time points or optimise efficiency as we observed the mosaic pattern of expression we set out to achieve, with small groups of labelled cells and single cells as shown in Figure 3 and movies 2 and 3. This information and the detailed protocol provided below are now included in the Methods section “Labelling individual cells in human spinal cord rosettes by lipofection”.

Manufacturer’s instructions for Lipofectamine 3000 transfection (6 well plate):

• 1 tube containing 125 ul of Opti-MEM and 7.5 ul of Lipofectamine 3000
• 1 tube containing 250 ul of Opti-MEM with 5 ug of DNA (total mix DNAs of 2 ug/ul) and P3000 Reagent
• Add diluted DNA to diluted Lipofectamine 3000 (Ratio 1:1) and incubate for 10 to 15 min at Room Temperature.
• 20 ul of DNA-Lipid complex was added to neural rosettes growing in 8 well IBIDI dishes (20 ul/well).
• The ratio of DNA (PiggyBac plasmid) and HypBase transposase was kept at 5:1 (for a final concentration of 2ug/ul).

• Cells in IBIDI dishes were left to develop in a sterile incubator overnight and mosaic fluorescence was observed the following morning (~16h post-lipofection).

• Will these cell lines and constructs be made publicly available after publication?*

The cell lines can be made available: for those reporters made in the H9 WiCell line an MTA will first have to be signed between the requesting PI and WiCell and permission for us to share the line(s) confirmed by WiCell; similarly, for reporters in ChiPS4 line an MTA will first need to be signed between the requesting PI and Cellartis/TakaraBio Europe. We will need to make a charge to cover costs. Constructs will be deposited with Addgene.

• Were the H9 and ChiPS4 lines characterised after the reporters were added to show they still proliferate/differentiate as they did prior to the reporter integration*?

In the Results we make clear that all lines created are polyclonal, with exception of a pm-eGFP ChiPS4 line, which is a monoclonal line (lines 145-150). We do not have direct data measuring cell proliferation but collected cell passaging data for all the reporter lines. This showed that they grow to similar densities at each passage compared to the parental line (this metadata is now provided as Supplementary data 1 and is cited in the Methods, line 348).

As a proof of principle for this approach, we created one monoclonal line from a polyclonal line ChIPS4-pm-eGFP. The latter was made by selecting an individual clone and this was then expanded and characterised for expression of pluripotency markers (immunocytochemistry data Figure S4), and the ability to differentiate into 3 germ layers (qPCR Supplementary data 1). This information is already cited in the Methods (Lines 358-362).

• Can the novel actin dynamics described be quantified? How many cells imaged show these novel dynamics?* Some of this quantification data was already reported in the paper (in figure 4 legend and in the Methods); we have now updated this and provide the detailed metadata in an Excel spread sheet, Supplementary data 4 (cited in the Methods, line 489)

Minor comments: 1. Some images in the figures and supplemental movies are low in resolution, for example the DAPI in Fig 4B, making it hard to distinguish individual cells. Please increase this.

We consider the DAPI labelling in Figure 4b to be clear, however, we wonder whether the reviewer was expecting to also see this combined with the other markers. We have therefore now provided these merged additional images in a revised Figure 4.

• Please show a merge of Phalloidin and F-Tractin in Fig4, this will help the colocalization to be fully appreciated.*

This has now been provided in revised Figure 4B.

• Some additional annotation on the supplemental movies would be useful to indicate to the **reader exactly what cell to follow. *

We have added indicative arrows to the movies, and note that more detailed labelling of the series of still images from these movies are provided in the main figures (Figures 3D and 4E & F).

*Reviewer #1 (Significance (Required)):

Human neurogenesis is currently poorly understood compared to many model systems used, yet key differences have already been identified between the human and the mouse, prompting the need for further investigation of human neural development. A major reason that human neurogenesis has been difficult to study is a lack of tools to enable cell morphology and behaviours to be analysed in real time.

The reporters and reporter PSC lines generated by Dady et al will allow many of these cell characteristics to be observed using live imaging. For example, the morphology of neural progenitors during and after cell divisions, how the apical and basal processes and membranes are divided, and how the actin cytoskeleton helps to regulate these processes.

*Importantly, PSC lines can be very heterogeneous, making generating reporter lines costly and time intensive. The use of these reporters with lipofectamine transfection, for a mosaic labelling, allows the visualisation of the plasma membrane, nucleus and cytoskeleton in any human PSC/NPC line, or even in human tissue cultures, without the need to generate each specific reporter line, making it a valuable tool for many labs in the field.

We strongly agree with this final point; this is a major reason for our study.

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

The manuscript describes the generation of novel lines of human pluripotent stem cells bearing fluorescent reporters, engineered through piggyBac transposon-mediated integration. The cells are differentiated into neuronal organoids, allowing to capture cellular behaviors associated to cell division. A replating protocol allows the observation of aging neurons by reducing the thickness of the tissue thereby facilitating live imaging. The authors also leverage the transposon technology to create mosaically-labelled organoids which allows visualizing aspects of neuronal delamination, notably cytoskeleton dynamics. They discover an undescribed pattern of F-actin enrichment at the basal nuclear membrane prior to nuclear envelope breakdown.

L104-109: "Moreover, the transposon system obviates drawbacks of directly engineering endogenous proteins...". Despite the risk of endogenous protein dysfunction, directly tagging allows the full regulation of gene expression (including the promoter, the enhancers and other regulatory regions rather than a strong constitutive promoter such as CAG). In addition, the number of copies integrated and the genomic regions are variable with PB, which does not reflect the endogenous expression. This could be rephrased by nuancing the advantages and drawbacks of each approach. The PiggyBac method is easier and faster, but it results in overexpression of a tagged protein that will be expressed since the hESC state and might not reflect the expression dynamics of the endogenous protein.* We agree and have now revised this in the Introduction L109-118.

*L124-126: "To monitor cell shape and dynamics we used a plasma membrane (pm) localized protein tagged with eGFP or mKate2 (pm-eGFP or pm-mKate2)." Could the authors provide more details and a reference on the palmitoylated rat peptide use to force membrane expression? *

This information, including the peptide sequence, is provided in the Methods (L330-331), we have now added a reference addressing its role in membrane localisation PMID: 2918027.

L132-133: " Finally, to observe actin cytoskeletal dynamics we selected F-tractin, for its minimal impact on cytoskeletal homeostasis".

A recent JCB paper (https://doi.org/10.1083/jcb.202409192) suggests that "F-tractin alters actin organization and impairs cell migration when expressed at high levels". Whether the overexpression of F-tractin in hESC using a CAG promoter reflects the physiological F-actin dynamics and/or if the high levels could lead to an alteration of cell behavior should be addressed or at least discussed. The paper we cite in this sentence (Belin et al 2014) evaluates F-tractin expression against other approaches to labelling and monitoring the actin cytoskeleton and concludes that in comparison F-tractin has minimal impact.

We do appreciate that expression above the endogenous level has the potential to alter cell behaviour and have revised the paper to more explicitly acknowledge this: in the Introduction (L109-112), and in the Discussion/conclusion (L289-293) where we now note the recent advances reported in Shatskiy et al. 2025 PMID: 39928047.

“A further potential limitation of this approach is that over-expression driven by the CAG promoter might not reflect physiological protein dynamics and/or alter cell behaviour; for example, high levels of F-Tractin can impair cell migration and induce actin bundling, interestingly, this can now be minimised by removing the N-terminal region (Shatskiy et al 2025)”.

L146-147: "...to generate polyclonal cell lines selected for expression of easily detectable (medium level) fluorescence for live imaging studies". What are the criteria used to define medium level? Number of copies integrated into the genome? Or levels by FACS during clone selection?

To clarify, all the lines presented here are polyclonal, except for one clonal line, pm-eGFP in ChiPS4. The numbers of copies integrated may vary from cell to cell in polyclonal lines. In this study, we selected cells for all lines with a FACS gate and this data is presented in Figure S1 (see line 147).

L260-263: "Efficient stable integration and moderate expression levels were achieved by optimising, i) the quantity and ratio of piggyBac plasmids and transposase and ii) subsequent FACS to exclude high expressing cells, as well as iii) transfection methods, including temporally defined lipofection in hiPSC-derived tissues." The ration 5:1 is classically used for PB Transposase delivery, however there is still high variability in the number of copies integration. Lipofection in derived tissues has been shown to be challenging. Could the authors should provide quantitative data regarding the efficiency of their approaches, notably the level of mosaicism one could expect?

We provide quantitative data for the efficiency of transfection using nucleoporation assays (FACS data presented in Supplementary figure S1), which shows more than 80-90% efficiency for eGFP in 82.82% of cells, mKate2 in 92.74% of cells, and H2B-mEos3 22.75% of cells, while 13.79% of cells co-expressed pm-Kate and H2B-mEos3.2. No comparative data regarding the efficiency of the tissue Lipofection assay was collected: our goal was to label single/small numbers of cells in order to monitor individual cell behaviours, and this “inefficient labelling” was readily achieved following the manufacturer’s instructions (please see response to Review 1 point 1), further details are now provided in the Methods.

L191-194: "We further wished to monitor sub-cellular behaviour within the developing neuroepithelium. To achieve this, we devised a strategy to target a mosaic of cells in established neural rosettes using lipofection. PiggyBac constructs and HyPBase transposase were transfected into D8/D9 human spinal cord neural progenitors using lipofectamine (Felgner, et al., 1987)(Fig. 3A)." The mosaicism is not an all or nothing in this method but also leads to variations in expression levels among the positive cells. The protocol for lipofection could be better detailed to allow easy reproduction by other teams, and its expected efficiency should be discussed. It would be interesting to explore the relationship between individual cells phenotype and expression levels. Please see response to Reviewer 1 point 1 above for more detailed lipofection protocol which generated mosaic expression, this is now also included in the Methods. We agree that investigating the relationship between individual cell phenotypes and expression levels would be interesting, but we think this is beyond the scope of this paper.

Additional comments: -Did the authors perform karyotyping of the hPSCs prior to use in the differentiation protocol?

As these are polyclonal lines, we did not undertake karyotyping. This could be done for the one monoclonal line described here (pm-eGFP ChiPS4 line): we lack funds for commercial options, but we are exploring other possibilities.

-Were pluripotency assays performed after reporter lines generation?

These were carried out for the clonal pm-eGFP ChiPS4 line (lines 145-150). The latter was made by selecting an individual clone and this was then expanded and characterised for expression of pluripotency markers by IF (Figure S4), and the ability to differentiate into 3 germ layers by qPCR (Supplementary data 2). This information is provided in the Methods (Lines 358-362).

*-Did the authors measure the cell proliferation rate in H2B-overexpressing cells and controls? Since H2B plays an important role in cytokinesis, it could interfere in cell division when H2B is overexpressed (see doi: 10.3390/cells8111391). *

We did not directly measure cell division when H2B is over-expressed. However, we assessed cell -passaging time of all the transfected cell lines. This showed that they grow to similar densities at each passage compared to the parental line (this is now provided as Supplementary data 1 and is cited in the Methods, line 348). We also found no difference between apical visiting time of progenitors in spinal cord rosettes expressing pm-eGFP or H2B-mEoS3.2, further supporting the conclusion that levels of H2B-mEoS3.2 expression achieved in this line did not interfere with cell division (metadata provided in Supplementary data 3).

The authors should provide data concerning the efficiency of expression of the distinct markers after electroporation. This is provided in Supplementary Figure S1 (FACS data) and detailed above for this reviewer.

*At Fig 1C, the schematic representation describes clone selection, however in the methods it is stated (L348-349): "Sorted cells expressing medium levels of fluorescence were expanded and frozen then representative lots of each polyclonal cell line...". There is some confusion regarding which experiments were performed using polyclonal medium-level mixed populations or monoclonal populations. *

We apologise for any confusion and have revised the Figure 1C schematic to indicate that cells can be selected to either make polyclonal lines or clonal lines.

*Reviewer #2 (Significance (Required)):

The study provides novel tools, as well as elements regarding neuroepithelium biology. It is well conducted and written, and the quality of images is excellent. It reads more as a resource paper in its current version, since the observation regarding neural cell division and delamination are interesting but not deeply explored, so this review will focus on those technical aspects rather than the novelty of the biological findings.

This study would be of interests for researchers in stem cells and organoids, developmental biology, and neurosciences.

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

In the manuscript, "Engineering fluorescent reporters in human pluripotent cells and strategies for live imaging human neurogenesis" the authors Dady et al. describe the adaptation of a recent advancement in transposase technology (HyPBase) as a method to integrate live reporters in human pluripotent stem cells. They show that these florescent reporters paired with new imaging strategies can be used to confirm the existence cellular behaviour described in other species such as the interkinetic nuclear migration (IKNM) of dividing progenitors in neural tube development. Finally, they demonstrate that this live imaging system is also able to discover novel biology by identifying previously undescribed actin polymerization at the basal nuclear surface of cortical progenitors undergoing cell division. Overall, the study presents two examples in which this adapted tool will aid in live-imaging studies of cellular biology.

Major Concerns: 1. This work needs more controls to properly demonstrate claims that their engineering strategy provides an advancement to current Piggyback methods. Their HyPBase strategy needs to be compared and quantified in terms of efficiency with other methods to support their claims (increased detection and reduced phototoxicity).*

We do not make specific claims for our experiments with respect to the superiority of HyPBase strategy. Our comments on this approach referred to by the reviewer here are in the Introduction (L 94-103), are supported by the literature (e.g. more stable gene expression than native piggyBac or the Tc1/mariner transposase Sleeping Beauty (Doherty, et al., 2012, Yusa, et al., 2011) and serve to explain our selection of HyPBase for our experiments. We make a case for using HyPBase as opposed to another transposase and although it would be interesting to compare efficiencies, this comment does not specify what “other methods” might be informative.

2.Throughout the manuscript more quantification is needed of the results. How many rosettes were examined? Were all the reported cells within one rosette? Were there differences between rosettes? This should be done for both the spinal and cortical differentiations.

The reviewer appears to have missed this information – we placed detailed quantifications in the figure legends (numbers of independent experiments and rosettes) and in the Methods in a specific section on Quantification of cell behaviour (L465-486), rather than in the main text. These has since been further updated and we now also provide additional metadata in the form of Excel spreadsheets for quantifications and analyses made for both spinal cord and cortical rosettes (Supplementary data 3 and 4 respectively).

Minor Comments: 1. Line 246 needs quantification shown in figures of the statements made. Specifically, how many cells were measured to get this number?

This information was provided in the figure 4 legend and we have since added numbers to these data; we were able to monitor 169 divisions in 21 rosettes; 154/166 divisions had vertical cleavage planes (symmetric) and 12/166 had horizontal cleavage planes (asymmetric).

These detailed observations were made in two independent experiments, along with observations of basal nuclear membrane F-Tractin localisation. This is noted in figure 4 legend, Methods and detailed metadata is provided in Supplementary data 4.

2.How many cells in the cortical rosettes had the enriched actin at the basal nuclear surface?

We confidently observed basal nuclear membrane F-Tractin enrichment in 141/146 divisions, for the remaining 20 cases (166-146), we could not tell whether F-Tractin is enriched or not at the basal nuclear membrane either because of low expression levels or because the basal nuclear membrane was out of focus at NEB. In 5 cases, we did not see the basal nuclear enrichment despite sufficient F-Tractin expression levels and the nucleus being in focus. We have updated the Fig4 legend excluding the non-analysable cases and see detailed metadata is provided in Supplementary data 4.

*Reviewer #3 (Significance (Required)):

General Assessment: This manuscript makes a very minor advancement in the field of stem cell engineering and developmental biology, but one that is worthy of publication with a few edits.

Advance: While PiggyBac reporters are widely used in stem cell engineering, Dady et al. demonstrate a new workflow using HyPBase which would be beneficial to the field. However, to increase this benefit, much more description and quantification of the methods would be needed. The biological advances of this manuscript are also very minor, but interesting as most of them confirm that human neural rosettes mimic many of the observed cell behaviours seen in animal models. Along these lines is the actin dynamics observation in cortical rosettes is interesting, but a preliminary observation and in need of follow up experiments.

Audience: Regardless, this technique would be of interest to the wider field of stem cell engineering.

My Expertise: Human Stem Cell Engineering, Neural Tube Development*

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Referee #3

Evidence, reproducibility and clarity

In the manuscript, "Engineering fluorescent reporters in human pluripotent cells and strategies for live imaging human neurogenesis" the authors Dady et al. describe the adaptation of a recent advancement in transposase technology (HyPBase) as a method to integrate live reporters in human pluripotent stem cells. They show that these florescent reporters paired with new imaging strategies can be used to confirm the existence cellular behaviour described in other species such as the interkinetic nuclear migration (IKNM) of dividing progenitors in neural tube development. Finally, they demonstrate that this live imaging system is also able to discover novel biology by identifying previously undescribed actin polymerization at the basal nuclear surface of cortical progenitors undergoing cell division. Overall, the study presents two examples in which this adapted tool will aid in live-imaging studies of cellular biology.

Major Concerns:

1.This work needs more controls to properly demonstrate claims that their engineering strategy provides an advancement to current Piggyback methods. Their HyPBase strategy needs to be compared and quantified in terms of efficiency with other methods to support their claims (increased detection and reduced phototoxicity). 2.Throughout the manuscript more quantification is needed of the results. How many rosettes were examined? Were all the reported cells within one rosette? Were there differences between rosettes? This should be done for both the spinal and cortical differentiations

Minor Comments:

1.Line 246 needs quantification shown in figures of the statements made. Specifically how many cells were measured to get this number? 2.How many cells in the cortical rosettes had the enriched actin at the basal nuclear surface?

Significance

General Assessment: This manuscript makes a very minor advancement in the field of stem cell engineering and developmental biology, but one that is worthy of publication with a few edits.

Advance: While PiggyBac reporters are widely used in stem cell engineering, Dady et al. demonstrate a new workflow using HyPBase which would be beneficial to the field. However, to increase this benefit, much more description and quantification of the methods would be needed. The biological advances of this manuscript are also very minor, but interesting as most of them confirm that human neural rosettes mimic many of the observed cell behaviours seen in animal models. Along these lines is the actin dynamics observation in cortical rosettes is interesting, but a preliminary observation and in need of follow up experiments.

Audience: Regardless, this technique would be of interest to the wider field of stem cell engineering.

My Expertise: Human Stem Cell Engineering, Neural Tube Development

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

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Referee #2

Evidence, reproducibility and clarity

The manuscript describes the generation of novel lines of human pluripotent stem cells bearing fluorescent reporters, engineered through piggyBac transposon-mediated integration. The cells are differentiated into neuronal organoids, allowing to capture cellular behaviors associated to cell division. A replating protocol allows the observation of aging neurons by reducing the thickness of the tissue thereby facilitating live imaging. The authors also leverage the transposon technology to create mosaically-labelled organoids which allows visualizing aspects of neuronal delamination, notably cytoskeleton dynamics. They discover an undescribed pattern of F-actin enrichment at the basal nuclear membrane prior to nuclear envelope breakdown.

L104-109: "Moreover, the transposon system obviates drawbacks of directly engineering endogenous proteins...". Despite the risk of endogenous protein dysfunction, directly tagging allows the full regulation of gene expression (including the promoter, the enhancers and other regulatory regions rather than a strong constitutive promoter such as CAG). In addition, the number of copies integrated and the genomic regions are variable with PB, which does not reflect the endogenous expression. This could be rephrased by nuancing the advantages and drawbacks of each approach. The PiggyBac method is easier and faster, but it results in overexpression of a tagged protein that will be expressed since the hESC state and might not reflect the expression dynamics of the endogenous protein.

L124-126: "To monitor cell shape and dynamics we used a plasma membrane (pm) localized protein tagged with eGFP or mKate2 (pm-eGFP or pm-mKate2)." Could the authors provide more details and a reference on the palmitoylated rat peptide use to force membrane expression?

L132-133: " Finally, to observe actin cytoskeletal dynamics we selected F-tractin, for its minimal impact on cytoskeletal homeostasis..". A recent JCB paper (https://doi.org/10.1083/jcb.202409192) suggests that "F-tractin alters actin organization and impairs cell migration when expressed at high levels". Whether the overexpression of F-tractin in hESC using a CAG promoter reflects the physiological F-actin dynamics and/or if the high levels could lead to an alteration of cell behavior should be addressed or at least discussed.

L146-147: "...to generate polyclonal cell lines selected for expression of easily detectable (medium level) fluorescence for live imaging studies". What are the criteria used to define medium level? Number of copies integrated into the genome? Or levels by FACS during clone selection?

L260-263: "Efficient stable integration and moderate expression levels were achieved by optimising, i) the quantity and ratio of piggyBac plasmids and transposase and ii) subsequent FACS to exclude high expressing cells, as well as iii) transfection methods, including temporally defined lipofection in hiPSC-derived tissues." The ration 5:1 is classically used for PB Transposase delivery, however there is still high variability in the number of copies integration. Lipofection in derived tissues has been shown to be challenging. Could the authors should provide quantitative data regarding the efficiency of their approaches, notably the level of mosaicism one could expect?

L191-194: "We further wished to monitor sub-cellular behaviour within the developing neuroepithelium. To achieve this, we devised a strategy to target a mosaic of cells in established neural rosettes using lipofection. PiggyBac constructs and HyPBase transposase were transfected into D8/D9 human spinal cord neural progenitors using lipofectamine (Felgner, et al., 1987)(Fig. 3A)." The mosaicism is not an all or nothing in this method but also leads to variations in expression levels among the positive cells. The protocol for lipofection could be better detailed to allow easy reproduction by other teams, and its expected efficiency should be discussed. It would be interesting to explore the relationship between individual cells phenotype and expression levels.

Additional comments:

• Did the authors perform karyotyping of the hPSCs prior to use in the differentiation protocol?
• Were pluripotency assays performed after reporter lines generation?
• Did the authors measure the cell proliferation rate in H2B-overexpressing cells and controls? Since H2B plays an important role in cytokinesis, it could interfere in cell division when H2B is overexpressed (see doi: 10.3390/cells8111391). The authors should provide data concerning the efficiency of expression of the distinct markers after electroporation. At Fig 1C, the schematic representation describes clone selection, however in the methods it is stated (L348-349): "Sorted cells expressing medium levels of fluorescence were expanded and frozen then representative lots of each polyclonal cell line...". There is some confusion regarding which experiments were performed using polyclonal medium-level mixed populations or monoclonal populations.

Significance

The study provides novel tools, as well as elements regarding neuroepithelium biology. It is well conducted and written, and the quality of images is excellent. It reads more as a resource paper in its current version, since the observation regarding neural cell division and delamination are interesting but not deeply explored, so this review will focus on those technical aspects rather than the novelty of the biological findings.

This study would be of interests for researchers in stem cells and organoids, developmental biology, and neurosciences.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

---

Referee #1

Evidence, reproducibility and clarity

Summary:

Dady et al have developed fluorescent reporters to enable live imaging of cell behaviour and morphology in human pluripotent stem cell lines (PSCs). These reporters target 3 main features, the plasma membrane, nucleus and cytoskeleton. Reporter PSCs have been generated using a piggyBac transposon-mediated stable integration strategy, using a hyperactive piggyBac transposase (HyPBase). The same constructs were also used for mosaic labelling of cells within 2D cultures using lipofectamine transfection.

The reporters used are tagged with either eGFP or mKate2 (far red) and tag the plasma membrane (pm) via the addition of a 20 amino-acid sequence from rat GAP-43 to the N-terminus of the fluorescent protein, the nucleus via Histone 2B with a laser-mediated photo-conversion option (H2B-mEos3.2), and the cytoskeleton via F-Tractin. In total, the authors produced lines with the following:

• pm-mKate2 (far red)
• pm-eGFP (green)
• H2B-mEos3.2 (green to red)
• F-tractin-mKate2 (far red)
• H2B-mEos3.2 and pm-mKate2 (green to red, plus far red)

The cell lines used to generate these were the human embryonic stem cell line H9 and human induced pluripotent cell line ChiPS4. The constructs were also used to label cells in a mosaic fashion, using lipofectamine transfection of the original cell lines once they had formed neural rosettes.

Using these cells, Dady et al then performed live imaging in vitro of human spinal cord rosettes and assessed cell behaviour. In particular they analysed mitotic cleavage planes and apical positioning of neural progenitor cells (NPCs), and assessed actin dynamics within these cells. They showed a slowing of the cell cycle length after the initial expansion phase, an increase in the rate of asymmetric division of these NPCs, and abscission of the apical membrane during these divisions. The F-tractin reporter showed enrichment at the basal nuclear membrane during these cell divisions, suggested to help prevent basal chromosome displacement during mitosis.

Major comments:

The data presented are convincing and could be strengthened by the following additions and clarifications: 1. How long do the fluorescent reports take to be visible when transfected via lipofectamine? How efficiently are they expressed? And what concentrations were tested to enable the mosaic expression presented? 2. Will these cell lines and constructs be made publicly available after publication? 3. Were the H9 and ChiPS4 lines characterised after the reporters were added to show they still proliferate/differentiate as they did prior to the reporter integration? 4. Can the novel actin dynamics described be quantified? How many cells imaged show these novel dynamics?

Minor comments:

1. Some images in the figures and supplemental movies are low in resolution, for example the DAPI in Fig 4B, making it hard to distinguish individual cells. Please increase this.
2. Please show a merge of Phallodin and F-Tractin in Fig4, this will help the colocalization to be fully appreciated.
3. Some additional annotation on the supplemental movies would be useful to indicate to the reader exactly what cell to follow.

Significance

Human neurogenesis is currently poorly understood compared to many model systems used, yet key differences have already been identified between the human and the mouse, prompting the need for further investigation of human neural development. A major reason that human neurogenesis has been difficult to study is a lack of tools to enable cell morphology and behaviours to be analysed in real time.

The reporters and reporter PSC lines generated by Dady et al will allow many of these cell characteristics to be observed using live imaging. For example, the morphology of neural progenitors during and after cell divisions, how the apical and basal processes and membranes are divided, and how the actin cytoskeleton helps to regulate these processes.

Importantly, PSC lines can be very heterogeneous, making generating reporter lines costly and time intensive. The use of these reporters with lipofectamine transfection, for a mosaic labelling, allows the visualisation of the plasma membrane, nucleus and cytoskeleton in any human PSC/NPC line, or even in human tissue cultures, without the need to generate each specific reporter line, making it a valuable tool for many labs in the field.

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Reply to the reviewers

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

Comments for the authors of Review Commons Manuscript RC-2024-02804:

The author of the Review Commons manuscript "Antigen flexibility supports the avidity of hemagglutinin-specific antibodies at low antigen densities", present their recent work evaluating hemagglutinin interactions with cellular receptors and antibodies. This manuscript focuses specifically on the avidity of the hemagglutinin using a fluorescence-based assay to measure dissociation kinetics and steady-state binding of antibodies to virions. Their findings confirm that bivalent interactions can offset weak monovalent affinity and that HA ectodomain flexibility is an additional determinant of antibody avidity. These findings are key for our understanding of neutralizing antibodies. Below are some comments that I would like the authors to address as they revise the manuscript.

Comments:

1. Can the authors provide justification for the two influenza viruses that they used.

We selected the lab-adapted IAV strains A/WSN/1933 (H1N1) and A/Hong Kong/1968 (H3N2) for this work because they are well-studied, including in the context of the antibodies used here, S139/1 and C05. While both antibodies bind to more contemporary H3N2 strains, they no not bind to HA from pandemic H1N1. Another feature of these strains is that their HAs have high enough affinity to both antibodies to enable strong signal in our imaging assays. This context for our strain selection has been added in lines 85-88.

1. The use of filamentous particles is a strength, but authors should detail the role of filamentous vs. spherical in nature and lab settings. This will help researchers that plan to repeat these assays.

We have revised the text (lines 336-339) to include more context on the biology of filamentous and spherical influenza viruses. In our experiments, HK68 naturally produces filaments in cell culture whereas WSN33 does not. To produce filaments artificially, we replace the M1 sequence from WSN33 with that of M1 from A/Udorn/1972, an H3N2 strain that is closely related to HK68.

1. Did the authors add the Udorn M1 to the HK68 as well?

Since HK68 naturally forms filaments, we did not introduce Udorn M1 into this strain. We note that the amino acid sequences of Udorn M1 and HK68 M1 differ only at position 167 (Alanine in Udorn, Threonine in HK68), and that this residue has previously been found to not correlate with virus morphology (10.1016/j.virol.2003.12.009).

Reviewer #1 (Significance (Required)):

This manuscript focuses specifically on the avidity of the hemagglutinin using a fluorescence-based assay to measure dissociation kinetics and steady-state binding of antibodies to virions. Thie findings confirm that bivalent interactions can offset weak monovalent affinity and that HA ectodomain flexibility is an additional determinant of antibody avidity. These findings are key for our understanding of neutralizing antibodies.

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

Summary

In this study, Benegal et al. investigate the binding kinetics of HA-head-specific antibodies (S139/1 and C05) to intact influenza virus particles using a fluorescence microscopy-based technique to measure the dissociation rate (koff) of the antibodies. By applying their proposed equilibrium model for bivalent antibody binding to HA, the authors calculated the crosslinking rate (kx), which represents the rate at which a single-bound antibody crosslinks to an additional HA molecule. Their experiments revealed that antigen crosslinking significantly slows koff, reducing it by up to two orders of magnitude. The authors further utilized streptavidin-coated beads conjugated with biotinylated HA or biotinylated BSA at varying concentrations to control HA surface density. Their results demonstrated that the two tested HA-head-specific antibodies retained the ability to crosslink HAs even at ~10-fold lower HA surface densities. In a complementary experiment, they employed an HA-anchor-specific antibody to restrict HA flexibility, which led to reduced binding of S139/1 and C05 IgGs but not their Fab fragments. This finding suggests that HA flexibility, rather than density, is the primary determinant of antibody crosslinking and avidity. Overall, the authors present an innovative approach to elucidating the dissociation and crosslinking kinetics of antibodies targeting intact virions or nanoparticles. The study is well-designed, with alternative interpretations of the results carefully considered and addressed throughout. I have only a few minor comments and suggestions for clarification.

Minor comments:

1. In Figure 1, does the grey color of each IgG in panel C indicate the Fc domain? If so, please add the description of the colors to the figure legend. In fact, it may be better to explain all the colors used here (for HA1, HA2, Fab heavy chain, light chain, etc.).

We have included this information in panel C and the caption for Figure 1.

1. Under the section," Bivalent binding of S139/1 and C05 persists after ~10-fold reductions in HA surface densities", the beginning of the second paragraph writes, "For both S139/1 and C05 Fab, binding increases linearly with HA density, as expected for a monovalent interaction dictated by absolute HA availability rather than density (Fig. 3D). Interestingly, the same relationship is observed for S139/1 IgG."

Visually, I think the same relationship also seems to hold for C05 IgG. Would it be better to perform some linear regression and report the R2 value for the fitting so that this assessment can be quantitative?

We agree with the reviewer's point. In Figure 3 of the revised manuscript, we include the results from a linear regression analysis to make this assessment more quantitative.

1. At the end of the same page, in the same paragraph, the authors mentioned, "In contrast to the IgG, Fab binding measured at twice the molar concentration of the IgG is nearly undetectable under these conditions, confirming the IgG binding is not occurring through monovalent interactions (Fig. S2E)." What are the conditions you are referring to? In Fig. S2E, there is only the Ab intensity for the Ab binding at 100% HA (and not the other percentages). For the Ab intensity of S139/1 Fab, what is the concentration of the Fab used in Figure 3D? Why could the intensity in this experiment for S139/1 Fab reach ~100,000, whereas that of the 8 nM in Fig. S2E can only reach ~20,000?

To clarify this point, we have updated Figure 3 to include the antibody concentration used for each experiment. The experiments in Fig 3 are conducted approximately around the respective KD of each IgG or Fab to ensure both consistency and strong signal-to-noise. For S139/1, we use 4nM of IgG, and 25nM of Fab. In Fig S2E, we use a concentration of Fab fragments double to that of the IgG, to reach an equivalent concentration of binding sites and confirm that the IgG binding we see is indeed due to bivalent binding. In this case, we use 4nM of IgG and 8nM of Fab.

1. Under the section, "Tilting of HA about its membrane anchor contributes to C05 and S139/1 avidity", in the second paragraph, the authors wrote, "If this is correct, we reasoned that avidity could be reduced by constraining tilting of the HA ectodomain. To test this hypothesis, we used FISW84, an antibody that binds to the HA anchor epitope and biases the ectodomain into a tilted conformation (Fig. 4B)."

Can you use some computational models (maybe the same one you used for Figure 4A) to show that when an HA trimer is bounded by FISW84 Fabs, the tilting of HA is constrained? I think this will help substantiate the assertion above.

This is an important point. The model that we employ in Figure 4A is suited to predicting the angles sampled by HAs when they are bound by an IgG antibody, but it does not take into consideration clashes with the viral membrane. It is these clashes that we predict based on published structures (reference 35 in the revised manuscript) will constrain HA tilting when FISW84 binds to the HA anchor. We have revised the text (Lines 247-249) to clarify these points.

1. It would be good if you could mention the strain of HA used in the experiments in Figure 4 in the actual Figure as well (as supposed to just in the figure legend).

We have added this information to Figure 4 in the revised manuscript.

1. I do not see a method section for the structure-based model you used in Figure 4. In the text, you cited your previous study (ref 28) for the model, but it would be good to write about this briefly (and how you specifically apply the model in this study) in this current manuscript.

We have updated the methods to include a subsection ("Geometric Model for Preferred Crosslinking Geometry") on how the structure-based model was set up, along with a corresponding visual in Fig S3 of the angles of freedom given.

1. In Figure S1 panel D, what is the unit of the antibody concentration? Could you please add it to the graph legend?

We have updated the figure (S1E in the revised manuscript) to include this information.

Reviewer #2 (Significance (Required)):

Previously, this group utilized the same fluorescence-based method to investigate the potency of anti-HA IgG1 antibodies in preventing viral entry versus egress, as well as the tendency of antibodies targeting different HA epitopes to crosslink two HA trimers in cis or in trans (He et al., J Virol, 2024). In this study, they extend their work by evaluating, in-depth, how the density and flexibility of hemagglutinin (HA) on the viral surface influence the binding avidity of anti-HA antibodies. Using two human IgG1 antibodies targeting the HA head, the authors demonstrate that these antibodies can crosslink two HA trimers in cis, even when the trimers are further apart than adjacent HAs. Notably, the study reveals that HA flexibility, rather than density, is the key determinant modulating antibody crosslinking. Even at a 10-fold reduced HA density compared to the original, the antibodies retained their ability to crosslink trimers.

This study provides critical insights into the relationship between HA density, flexibility, and antibody function, adding to the broader understanding of antibody crosslinking-a topic frequently discussed in the field of influenza research. These findings could have significant implications for vaccine design, particularly for strategies involving the display of the HA ectodomain on nanoparticles, potentially guiding the development of more effective influenza vaccines. Furthermore, the broader relevance of these findings may extend to other viruses with similar structural and immunological properties.

My expertise lies in the structural determination of antibody-antigen complexes in influenza and other pathogens. While I may not have sufficient expertise to evaluate specific technical details of the fluorescence-based methods employed, the authors have convincingly demonstrated the robustness of their experimental design and interpretation, supported by appropriate controls.

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

SUMMARY In "Antigen flexibility supports the avidity of hemagglutinin-specific antibodies at low antigen densities", Benegal et al. develop a microscopy-based assay to measure dissociation of HA head-binding antibodies from intact virions. This assay allows the authors to explore the contribution of IgG bivalent avidity to antibody interaction with native virions, which is not accessible using other methods such as BLI. Using this assay, the authors further explore the effect of HA density on IgG avidity with engineered low-HA virions and then with artificial HA-coated microspheres. In addition to measuring antibody dissociation, the authors perform structural analyses to predict the conformational preferences of many HA IgGs from published structures. The authors conclude that low HA densities (down to ~10%) still support high avidity binding for the 2 IgGs tested, and thus there would be little evolutionary pressure for IAV to reduce the HA density as a strategy to evade immune recognition.

MAJOR COMMENTS

The data presented are generally convincing for the two antibodies tested, with some caveats listed below. I believe the microscopy technique is valuable and provides a significant contribution to the field, and I believe that the finding that avidity persists at low densities for IAV is compelling and worth communicating to other virologists. Overall, with the incorporation of the suggested major revisions, this manuscript represents a significant advancement in the field.

A major limitation of the current study is the small number of antibodies tested. Two antibodies are quite few, particularly since this work attempts to generalize these observations with structural predictions of dozens or hundreds of HA antibodies. While I believe that the resilience of IgG binding to lower epitope densities is likely common to many HA antibodies (or antibodies in general), this work alone does not support this. To this end, the authors should acknowledge their limited sample size in the text or discussion and that the generalization to other antibodies is speculative. Alternatively, the authors could demonstrate with additional antibodies (such as F045-092 which is pointed out in Fig S3A and perhaps group 'i' antibodies according to Fig S3A).

This is an important point, and we more explicitly acknowledge this limitation in lines 277-278.

It seems to me lateral diffusion of HA in the viral membrane is an important discussion point that was missed in this manuscript. The authors should comment on what is known about the lateral mobility of HA on virions, and how this could impact the ability of an IgG to crosslink. The authors should comment about whether long range diffusion and/or short range "shuffling" of glycoproteins could contribute to crosslinking preferences of antibodies in addition to the tilt, which is the only movement discussed. As appropriate, the authors should then comment on how this may affect their interpretation of experiments using beads. In experiments on beads, there is certainly no lateral mobility of the HA trimers; what are the consequences of this on the analysis?

We agree that this is an important consideration, and we have revised the manuscript (lines 296-298) to address these points. Briefly, we have previously performed fluorescence recovery after photobleaching of covalently labeled HA and NA on the surface of filamentous influenza particles (10.7554/eLife.43764; see Figure 1B of this reference for a representative example). This data indicates that long range diffusion does not seem to be occurring on the virion surface. Short range diffusion, or shuffling, has not been observed, but cannot be ruled out, and may increase conformations favorable to bivalent binding.

Should the authors qualify the limitations in the scope of their experimental results and the system of choice (beads vs. virions) as described in my previous comments, I suggest three experiments that I believe are essential to support the authors' claims. Alternative to qualifying the limitations, two optional experiments are also listed that could support the authors' claims as they are - those require a more extensive experimental undertaking and are thus labeled [OPTIONAL].

1) The photobleaching experiment shown in Figure S1A. I am concerned that measuring photobleaching in steady state conditions does not properly control for the experimental conditions. In steady state, bleached antibody could unbind and be replaced by fluorescent antibody that has diffused into the field of view. This should be more thoroughly controlled by irreversibly capturing antibody (such as with biotin) and imaging after excess antibody is washed away, or by some other method such as capturing and imaging virus that has been directly labeled with AF555. This should be possible using reagents and techniques already demonstrated by the authors.

We have updated the supplemental information with a more rigorous control for photobleaching; the revised figures are shown in Fig S1A. In this experiment, fluorescent S139/1 IgG was bound to HK68 virions. The antibody was washed away, and the loss of fluorescence signal was imaged separately under two conditions: 1) Dissociation only; an image was collected at 0s and one at 60s. 2) Dissociation and photobleaching; an image was collected at a rate of 1 frame per second for 60 seconds. The difference between the endpoint intensities from both conditions is not statistically significant. This supports our conclusion that, in the absence of antibodies in solution that can exchange with those bound to virions, photobleaching does not make a detectable contribution to the loss of signal we observe in our antibody dissociation experiments.

2) In imaging, the authors analyzed only filamentous virions because they exhibit the best signal to noise ratio, which is a reasonable technical simplification. However, this relies on the assumption that glycoprotein presentation is relatively constant between virions of different sizes. It would be helpful to perform some analysis of small virions in any movie where there is sufficient signal. This would support the assumption that rates for small virions are comparable to those of filaments in the same experiment. This should be possible by performing additional analysis on existing data, without requiring additional experiments.

Thank you for calling our attention to a point that needs clarification. The analysis that was restricted to filaments was for the SEP-HA binding experiments (shown in Fig 3A&B). This was done in order to select only those particles that were not diffraction-limited, so that we could control for any systematic differences in size between the two populations by measuring HA signal per unit particle length. For the dissociation experiments (Fig 2), data was taken from all virions in the fields of view. For this analysis, the normalized dissociation curves were averaged in two ways to account for the potential discrepancy that the reviewer points out. In the first method, the average was taken with each virion equally weighted, while in the second method, the entire field of view was masked and normalized together. Both curves look very similar, suggesting that any potential differences between smaller virions and filaments are not enough to make a quantifiable difference in dissociation rate. A representative dissociation curve with both analyses shown side-by-side has been added in Figure S1B.

3) In figure 3, C05 fab binding is used to assay HA content of the SEP HA virions. An additional method of confirming HA content that is more independent from the imaging assay would be beneficial, such as a Western blot to quantify HA relative to NP, NA, or M1 etc.

We have used western blotting to quantify the amount of HA contained relative to M1 in each population. This new data is discussed in lines 163-168 of the revised manuscript and shown in Figure S2C. As noted in the revised text, western blot analysis suggests that the density of native HA is decreased to ~31% its normal level in SEP-HA virions, lower than the ~75% value determined via fluorescence microscopy. One possible reason for this disparity is the presence of virus-like particles in the SEP-HA sample that completely lack wildtype HA. These would be excluded from our imaging analysis but captured by the western blot.

4) [OPTIONAL] In figure 4, it is depicted that FISW84 biases HA in a tilted conformation, and the authors reasonably propose the reduced flexibility discourages crosslinking by IgGs. From the modeling summarized in Figure S3A, are there any antibodies predicted to prefer crosslinking HA at the same angle FISW84 tilts the ectodomain? Would FISW84 enhance crosslinking by such an antibody?

This is an interesting suggestion, and we have revised the manuscript (lines 247-249) to clarify our thinking on this point. Based on the structure of the FISW84 Fab (PDB ID 6HJQ), we conclude that binding of a single Fab fragment does not necessarily actively tilt the HA ectodomain in a specific direction. Rather, it restricts tilting in the direction that would cause a steric clash between the Fab and the membrane. As a result, HA can still sample a range of angles, but this range is no longer symmetrical about the ectodomain axis. By reducing the likelihood that two HA ectodomains would tilt towards each other at a favorable angle, we would expect all antibodies to be disadvantaged to some degree. A possible exception could be if three FISW84 Fab fragments manage to bind to a single HA trimer. In this case, the HA ectodomain would be forced to remain perpendicular to the membrane to accommodate them all. This would favor antibodies that prefer binding to HAs where the ectodomains are parallel to each other. In our analysis in Figure S3A, this includes primarily antibodies that bind to the HA central stalk, such as 31.b.09. However, we note that these antibodies may encounter barriers to bivalent binding that we do not consider here, including proximity to the FISW84 epitope and the high density of HA in the membrane.

5) [OPTIONAL] In figure S3A, the authors display theoretical tilt and spacing preferences for many HA antibodies based on published structures. Interestingly, their group iii antibody is predicted to prefer greater spacing and tilt, and likewise the authors observe increased binding at lower densities (in figure 3E). It would be beneficial to the work to test group i antibodies (base binding) in the dissociation experiments. The behavior of a base binding antibody, particularly at low densities could reinforce the modeling performed for this work.

This is an excellent suggestion which we are not currently able to pursue for technical reasons. In particular, it would be difficult to distinguish between increased binding of these antibodies at low antigen densities that is due to bivalent attachment (and thus reduced dissociation) versus increased accessibility of the epitope, which may be occluded at higher HA densities.

The experiments are well explained and supported by methods that would enable reproducibility.

The authors state "The statistical tests and the number of replicates used in specific cases are described in the figure legends" yet in many cases this information is absent. For the k values in fig 2D, some indication of error or confidence interval would be helpful.

We have ensured that this information is included in each of the captions. Regarding the k values, formal error propagation is challenging due to the way the k values were derived. Specifically, these values were calculated by fitting the average of the three initial dissociation traces, rather than fitting each replicate individually and then averaging the rate constants. As a result, the usual methods for estimating confidence intervals or standard error of the mean are not directly applicable.

MINOR COMMENTS

o Some of the small details in fig 1A and fig S1 are lost due to small figure size - such as the sialic acid residues and lipid bilayer.

We have resized the figure components.

o Although described in the text, it could be helpful to incorporate into figure 2 why the BLI data is shown for S129 fab. Perhaps indicate in 2C that that curve is "too fast to accurately measure" and perhaps near the table in 2D indicate the blue data is from Lee et al. It may be fine to simply remove the BLI results from the figure and refer to them only in the discussion of the experiments. Even with the measured data, the difference between fab and IgG is striking enough to support the paper, and the BLI data may be more confusing in the figure than it adds.

We have updated the caption for Figure 2D to clarify that binding between the S139/1 Fab and A/WSN/1933 HA is approaching the limit of detection in our assay, and that the additional rates are from Lee et al. We have also updated the table to make the presentation of the kinetic parameters more clear.

o In figure 3A, better describe the fluorescent components in the fluorescent images in the legend.

We have updated the caption for Figure 3A to describe the fluorescent components shown in the image. Specifically, the panel labeled 'HA' shows signal from a fluorescent FI6v3 scFv, while the panel labeled 'decoy' shows signal from the SEP-HA construct.

o From personal experience, the flexibility of HA ectodomain can be significantly affected by how much of the membrane proximal linker region is retained or removed. Could the authors comment on how they chose the cutoff for their HA ectodomain used in the bead experiments and their rationale?

This is an important point, and while the precise impact of the linker on HA flexibility remains uncertain, we agree that it may increase the freedom of motion of the ectodomain relative to the HA membrane anchor. We mention this caveat in the revised text (lines 188-191) and we have added an AlphaFold2 prediction of how our recombinant HA might look to Figure S2D.

o In Figure S1B, if I understand correctly: black dashed line "IgG equivalent dissociation rate" is the experimental data, magenta "Crosslinking model fit" is the theoretically total antibody bound as described by the mathematical model. Then the gray lines "Double- /singly- bound antibodies plot the theoretical amount of antibody bound once and bound twice. If this is correct, I believe it would be clearer if the singly- and doubly- bound were plotted in separate colors, and that this is explained more clearly in the legend.

We have revised the figure to show doubly- and singly-bound curves using different line styles.

o Related to an earlier comment, if lateral diffusion may play a role, how might this differ between different types of antibodies?

As mentioned in our previous response, we do not anticipate that lateral diffusion makes a significant contribution to antibody binding to the surface of virions, although it may be important on the cell surface.

o Could the authors comment in the discussion on how their results on virions may translate to the surface of the infected cell, which is also decorated in viral glycoproteins? Early time points of infection could be an in vivo example of low-density HA. What extent may antibody binding and crosslinking affect viral proteins on the cell surface or the immune response?

This is a very interesting point. Antibody binding to the infected cell surface has been shown to alter viral release and morphology, presumably at lower HA densities than those observed the viral surface. We have added a brief discussion of this point (lines 291-295) to the revised manuscript.

o The github link in the methods is incorrect or not yet available.

Thank you for noting this. We have updated the link.

o Reference 1 has an incorrect or expired link.

These references have been updated.

Reviewer #3 (Significance (Required)):

• This work represents a conceptual advance in our understanding of antibody action on viral pathogens. The authors adapt existing microscopy methodologies to measure antibody avidity in a new way that is better representative of in vivo conditions.

• To my knowledge, this is the first instance of direct measurement of antibody off-rates from intact virus particles, instead of immobilized protein as in BLI, SPR, or interferometry.

• This work should be of interest to virologist and biophysicists interested in the cooperative binding of antibodies and the relation of virus structural organization to antibody recognition. Immunologist may also be influenced by this work. This work may be followed up by other researchers similarly measuring the association and dissociation rates of antibodies with single virions, or otherwise comparing fab to IgG binding to gain insight into when crosslinking is or is not occurring.

• Reviewer expertise: Single-virion imaging, protein complexes, biochemistry, influenza A.

• I do not have sufficient expertise to evaluate the mathematical models and differential equations for modeling the k-on and k-off rates.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

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Referee #3

Evidence, reproducibility and clarity

Summary

In "Antigen flexibility supports the avidity of hemagglutinin-specific antibodies at low antigen densities", Benegal et al. develop a microscopy-based assay to measure dissociation of HA head-binding antibodies from intact virions. This assay allows the authors to explore the contribution of IgG bivalent avidity to antibody interaction with native virions, which is not accessible using other methods such as BLI. Using this assay, the authors further explore the effect of HA density on IgG avidity with engineered low-HA virions and then with artificial HA-coated microspheres. In addition to measuring antibody dissociation, the authors perform structural analyses to predict the conformational preferences of many HA IgGs from published structures. The authors conclude that low HA densities (down to ~10%) still support high avidity binding for the 2 IgGs tested, and thus there would be little evolutionary pressure for IAV to reduce the HA density as a strategy to evade immune recognition.

Major comments

The data presented are generally convincing for the two antibodies tested, with some caveats listed below. I believe the microscopy technique is valuable and provides a significant contribution to the field, and I believe that the finding that avidity persists at low densities for IAV is compelling and worth communicating to other virologists. Overall, with the incorporation of the suggested major revisions, this manuscript represents a significant advancement in the field.

A major limitation of the current study is the small number of antibodies tested. Two antibodies are quite few, particularly since this work attempts to generalize these observations with structural predictions of dozens or hundreds of HA antibodies. While I believe that the resilience of IgG binding to lower epitope densities is likely common to many HA antibodies (or antibodies in general), this work alone does not support this. To this end, the authors should acknowledge their limited sample size in the text or discussion and that the generalization to other antibodies is speculative.

Alternatively, the authors could demonstrate with additional antibodies (such as F045-092 which is pointed out in Fig S3A and perhaps group 'i' antibodies according to Fig S3A).

It seems to me lateral diffusion of HA in the viral membrane is an important discussion point that was missed in this manuscript. The authors should comment on what is known about the lateral mobility of HA on virions, and how this could impact the ability of an IgG to crosslink. The authors should comment about whether long range diffusion and/or short range "shuffling" of glycoproteins could contribute to crosslinking preferences of antibodies in addition to the tilt, which is the only movement discussed. As appropriate, the authors should then comment on how this may affect their interpretation of experiments using beads. In experiments on beads, there is certainly no lateral mobility of the HA trimers; what are the consequences of this on the analysis?

Should the authors qualify the limitations in the scope of their experimental results and the system of choice (beads vs. virions) as described in my previous comments, I suggest three experiments that I believe are essential to support the authors' claims. Alternative to qualifying the limitations, two optional experiments are also listed that could support the authors' claims as they are - those require a more extensive experimental undertaking and are thus labeled [OPTIONAL].

1. The photobleaching experiment shown in Figure S1A. I am concerned that measuring photobleaching in steady state conditions does not properly control for the experimental conditions. In steady state, bleached antibody could unbind and be replaced by fluorescent antibody that has diffused into the field of view. This should be more thoroughly controlled by irreversibly capturing antibody (such as with biotin) and imaging after excess antibody is washed away, or by some other method such as capturing and imaging virus that has been directly labeled with AF555. This should be possible using reagents and techniques already demonstrated by the authors.
2. In imaging, the authors analyzed only filamentous virions because they exhibit the best signal to noise ratio, which is a reasonable technical simplification. However, this relies on the assumption that glycoprotein presentation is relatively constant between virions of different sizes. It would be helpful to perform some analysis of small virions in any movie where there is sufficient signal. This would support the assumption that rates for small virions are comparable to those of filaments in the same experiment. This should be possible by performing additional analysis on existing data, without requiring additional experiments.
3. In figure 3, C05 fab binding is used to assay HA content of the SEP HA virions. An additional method of confirming HA content that is more independent from the imaging assay would be beneficial, such as a Western blot to quantify HA relative to NP, NA, or M1 etc.
4. [OPTIONAL] In figure 4, it is depicted that FISW84 biases HA in a tilted conformation, and the authors reasonably propose the reduced flexibility discourages crosslinking by IgGs. From the modeling summarized in Figure S3A, are there any antibodies predicted to prefer crosslinking HA at the same angle FISW84 tilts the ectodomain? Would FISW84 enhance crosslinking by such an antibody?
5. [OPTIONAL] In figure S3A, the authors display theoretical tilt and spacing preferences for many HA antibodies based on published structures. Interestingly, their group iii antibody is predicted to prefer greater spacing and tilt, and likewise the authors observe increased binding at lower densities (in figure 3E). It would be beneficial to the work to test group i antibodies (base binding) in the dissociation experiments. The behavior of a base binding antibody, particularly at low densities could reinforce the modeling performed for this work.

The experiments are well explained and supported by methods that would enable reproducibility.

The authors state "The statistical tests and the number of replicates used in specific cases are described in the figure legends" yet in many cases this information is absent. For the k values in fig 2D, some indication of error or confidence interval would be helpful.

Minor Comments

• Some of the small details in fig 1A and fig S1 are lost due to small figure size - such as the sialic acid residues and lipid bilayer.
• Although described in the text, it could be helpful to incorporate into figure 2 why the BLI data is shown for S129 fab. Perhaps indicate in 2C that that curve is "too fast to accurately measure" and perhaps near the table in 2D indicate the blue data is from Lee et al. It may be fine to simply remove the BLI results from the figure and refer to them only in the discussion of the experiments. Even with the measured data, the difference between fab and IgG is striking enough to support the paper, and the BLI data may be more confusing in the figure than it adds.
• In figure 3A, better describe the fluorescent components in the fluorescent images in the legend.
• From personal experience, the flexibility of HA ectodomain can be significantly affected by how much of the membrane proximal linker region is retained or removed. Could the authors comment on how they chose the cutoff for their HA ectodomain used in the bead experiments and their rationale?
• In Figure S1B, if I understand correctly: black dashed line "IgG equivalent dissociation rate" is the experimental data, magenta "Crosslinking model fit" is the theoretically total antibody bound as described by the mathematical model. Then the gray lines "Double-/singly- bound antibodies plot the theoretical amount of antibody bound once and bound twice. If this is correct, I believe it would be clearer if the singly- and doubly-bound were plotted in separate colors, and that this is explained more clearly in the legend.
• Related to an earlier comment, if lateral diffusion may play a role, how might this differ between different types of antibodies?
• Could the authors comment in the discussion on how their results on virions may translate to the surface of the infected cell, which is also decorated in viral glycoproteins? Early time points of infection could be an in vivo example of low-density HA. What extent may antibody binding and crosslinking affect viral proteins on the cell surface or the immune response?
• The github link in the methods is incorrect or not yet available.
• Reference 1 has an incorrect or expired link.

Significance

• This work represents a conceptual advance in our understanding of antibody action on viral pathogens. The authors adapt existing microscopy methodologies to measure antibody avidity in a new way that is better representative of in vivo conditions.
• To my knowledge, this is the first instance of direct measurement of antibody off-rates from intact virus particles, instead of immobilized protein as in BLI, SPR, or interferometry.
• This work should be of interest to virologist and biophysicists interested in the cooperative binding of antibodies and the relation of virus structural organization to antibody recognition. Immunologist may also be influenced by this work. This work may be followed up by other researchers similarly measuring the association and dissociation rates of antibodies with single virions, or otherwise comparing fab to IgG binding to gain insight into when crosslinking is or is not occurring.
• Reviewer expertise: Single-virion imaging, protein complexes, biochemistry, influenza A.
• I do not have sufficient expertise to evaluate the mathematical models and differential equations for modeling the k-on and k-off rates.