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Reply to the reviewers

Reply to the reviewers

We thank the reviewers for your thoughtful assessment of our study and for recognizing its technical advance. We appreciate the reviewers’ comments and suggestions, all of which we have carefully addressed in the revised manuscript.

Reviewer #1

1. In the first section of results, a self-cleaving 2A peptide is inserted upstream of the selection marker to improve selection of correctly tagged genes, as reported in the cited literature. To demonstate this in their PCR-tagging method, the authors tag the HNRNPA1 gene with the mNG-2A-NeoR strategy and find a tagging efficiency of 70% and more, in contrast with the 32% efficiency found with the original method developed by Fueller et al. (2020) (page 5). In support of this conclusion, only a representative image of cells showing mNG and HOECHST signal is presented, with no quantification (Fig1b). As this is a central result of the manuscript that allowed the authors to maintain the 2A-NeoR selection strategy for further investigation of sequence-level data, it is advisable to perform a more thorough quantification of the tagging efficiency by counting (with the help of image analyis software such as Fiji) the mNG+ cells and the total number of cells (HOECHST+), and calculate the % of mNG+ cells across different biological replicates (ideally, cells transfected in different days). A direct comparison (statistical analysis) with the % of mNG+ cells obtained by the original methodology (Fueller et al) would be desirable. In this way, the robustness of the improved tagging efficiency with the optimized method could be also evaluated within one single gene.

Re____sponses

• We have now quantified the fraction of mNG+ cells across three biological replicates for three different genes, using cells transfected in independent experiments. The representative images and quantitative analysis have been added to the revised Figure 1b.
• We also revised the corresponding text in the revised manuscript on page 5 (lines 143-151) to avoid overinterpreting the comparison with the tagging efficiency previously reported by Fueller et al. (2020). The previous experiments were performed in parental HEK293T cells using Zeocin-based selection, whereas the present experiments were performed in HEK293T NeoR-KO cells and G418 selection. Since several experimental parameters were not fully matched, we agree that a direct statistical comparison would not be appropriate. The revised text is:” Using the 2A-linked selection cassette, we tagged HNRNPA1, DDX21, and SLC16A1 in HEK293T NeoR-KO cells (HEK293T cells in which the neomycin-resistance (NeoR) gene linked to the T-antigen has been inactivated), with three independent biological replicates for each gene. … (Figure 1b). Quantification across biological replicates confirmed the reproducibility of the 2A-linked tagging workflow and support its use in subsequent characterization and optimization.”
• In addition, we changed the title of this Results section to “2A-linked selection and characterization of integration outcomes of CRISPR-Cas12a-assisted PCR tagging” to avoid the claim of direct improvement relative to the previous method. Nevertheless, the high and reproducible tagging efficiencies observed here support the use of the 2A-linked selection strategy for subsequent experiments.

  1. In the following line (page 5), authors talk about "correctly localized" signals, although no clear criterium of "correct" signal localization is explained, nor it is indicated anywhere in the example image. While in the following section(s) it is mentioned that diffuse signal may come from unspecific mNG expression of concatenated PCR cassettes, it would be still important to quantify the "correct" vs "uncorrect" mNG signal (i.e: nuclear vs cytoplasmatic) via image analysis.

__Re____sponse: __Thank you for pointing out the lack of localization definitions. In the revised Figure 1b, examples of diffuse cytoplasmic fluorescence are indicated by white arrows, and the fractions of the two localization categories (“correct” vs “uncorrect”) are quantified. Accordingly, the Results text was revised as “Following G418 selection, fluorescence microscopy showed that most mNeonGreen-positive cells displayed signals consistent with the expected gene-specific subcellular localization, whereas only a small fraction exhibited diffuse mNeonGreen fluorescence (Figure 1b)” on page 5 (lines 146-149). And the criteria used for classification are now described in the Methods and figure legend.

1. Of particular significance would be to clarify whether there is a relationship between the % of concatemer product and the presence of diffuse cytoplasmic signal. In several instances, the authors mention their previous finding that diffuse cytoplasmic signal usually results from unspecific expression of the fluorescent reporter within a concatenated PCR cassette. However, from Fig1b there is no evident correlation between % of concatemer reads and % of diffuse cytoplasmic signal. Moreover, Fig2c is cited but no arrows are indicated in the figure in contrast with what mentioned in the text (page 10). Moreover, it is unclear what the authors would like to highlight in the following paragraph when talking about the percentage of diffuse signal (the discrepancy of the concatemers vs diffuse signal? Please make the paragraph more clear). Overall, I think that showing actual microscopy data and image quantification of diffuse vs localized signal would be ideal instead of only mentioning the result in the text. Moreover, a clearer and more detailed discussion about the authors' interpretation of the discrepancy observed between the % of concatemers and % of diffuse cytoplasmic signal is needed, and how it relates to previous findings by Fueller et al. (2020).

Re____sponses

• We apologize for the confusion. In the revised Figure 1b we included the example of diffuse signals and also quantified the fraction of cells with diffuse signal across three biological replicates. We also show example of diffuse signals in revised Fig. S2d. In addition, we revised the paragraphs on page 22 (lines 494-514) to make the description of concatemers and diffuse signals clearer: “Since these reads represent donor-donor junctions rather than intact alleles, their abundance cannot be interpreted directly as concatemer copy number or as the fraction of cells harboring concatemeric integrations.
• In our previous study (Fueller et al., 2020), we proposed that concatemer formation may contribute to diffuse cytoplasmic fluorescence (examples indicated by white arrows in Figure 1b and Figure S2d) through unintended expression of mNG from downstream cassette copies. Although an SV40 PolyA terminator sequence was included downstream of NeoR, the U6 Pol III promoter driving crRNA expression has been reported to mediate Pol II-driven transcription that can contribute to the expression of downstream mNG sequences (Gao et al., 2018; Rumi et al., 2006; Figure 4a). We therefore quantified the fraction of cells displaying diffuse signal at eight loci under control conditions with unmodified donors and compared with the corresponding fractions of concatemer reads, to examine the relationship between concatemer formation and diffuse fluorescence.
• We found that the frequency of diffuse signal varied substantially across loci and did not closely track the fraction of concatemer reads. No diffuse signal was observed at the CLTC, DDX21, and HNRNPA1 loci. Only a few cells (

  1. It is expectable that the efficiency of PCR-tagging might vary if different preparations of the PCR products are used. The authors should add technical details in the method section that are currently missing regarding kits and protocols used for PCR, PCR purification/extraction, verification of PCR by sequencing (within the "Generation of plasmids and PCR cassettes"paragraph). This includes kits, polymerase type (Q5? Phusion?), extraction protocols (was the PCR gel-extracted?), sequence verification (was the extracted band sent for sequencing prior to perform PCR-tagging?) and so on. In particular, sequence verification by Sanger sequencing would help understand whether some small nucleotide changes were generated by PCR prior to cell transfection and should be added to the discussion part as source of possible mutations.

Responses

• The PCR cassettes were amplified using Velocity DNA polymerase (Bioline), following our previously published protocol (Fueller et al., 2020). As described there, other commercia high-fidelity polymerases like Phusion (Thermo Fisher Scientific), as well as self-purified Pfu-Sso7d DNA polymerase, can also be used.
• Sanger sequencing of PCR cassettes before transfection was not performed, as the cassette sequence is defined by the known template plasmid and the primer sequences. Template plasmid was verified by sanger sequencing and the primers were synthesized and purified by cartridge to ensure high fidelity/purity. Although small nucleotide changes introduced by PCR cannot be excluded as a potential source of mutations, but their overall contribution is expected to be minor given the high-fidelity nature of the polymerases.
• We have now added the experimental details to the Methods on page 33 (lines 817-827):” The PCR cassettes were amplified from either pMaCTag-2A-N07 (mNeonGreen) or pMaCTag-2A-N11 (mScarlet-i) template plasmid based on our previously published protocol (Fueller et al., 2020). In brief, PCR cassettes were amplified using a Velocity polymerase (Bioline) in a reaction mixture containing self-made HiFi buffer (200 mM Tris-HCl pH 8.8, 100 mM (NH₄)₂SO₄, 500 mM KCl, 1% [vol/vol] Triton X-100, 1 mg/ml BSA, 20 mM MgCl₂), 10 mM dNTPs (Bioline), 5 M betaine (Sigma-Aldrich), 200 ng template plasmid, and 10 µM each of M1 and M2 tagging oligos. The following cycling conditions were used: 3 min at 95°C; 30 cycles of 20 s at 95°C, 30 s at 64°C, and 45 s per kb at 72°C; 5 min at 72°C; and 4°C hold. After PCR, 0.4 µl DpnI was added and the reaction was incubated for 1 h at 37°C to digest the plasmid template. PCR products were verified by agarose gel electrophoresis to confirm product size. As our PCR reactions consistently yielded a single specific band of the expected size, column-based purification (Macherey-Nagel, NucleoSpin Gel and PCR Clean-up) was performed without gel extraction.”

  1. [OPTIONAL] A significant improvement of the study in terms of reproducibility would be to analyze, via microscopy image analysis (NOT by sequencing), the % of tagging efficiency as suggested above (see point 1 under the microscopy section) for the same gene (i.e. HNRNPA1 or other) with biological replicates consisting of cells transfected with PCR reactions prepared in different days, or [OPTIONAL] even analyzing how the tagging efficiency varies with PCR reactions purified with different kits or protocols (example: gel extraction vs PCR elution). Image analysis should include signal quantification with estimation of the % of tagging efficiency and statistical analysis. These experiment, not particularly demanding in terms of reagents and time (~3 weeks in total due to puromycin selection according to the workflow in Fig2b) would greatly help the reader understanding the robustness of tagging efficiency within single genes.

Re____sponses

• As described in our response to the comment 1, we have now quantified tagging efficiency by microscopy for three different genes across three independent biological replicates. For each replicate, cells were transfected with independently prepared PCR products (generated on different days, in some cases by different lab members). Fraction of mNG+ cells was quantified using Fiji, and the statistical analysis has been added to the revised Fig. 1b.
• We agree that systematically comparing different PCR purification methods could provide additional technical information. However, our PCR reactions consistently yielded one specific band of the expected size, we therefore performed a simple column-based purification to minimize the processing time. We have nevertheless clarified the experimental procedures in the Methods on page 34 (lines 824-827): “PCR products were verified by agarose gel electrophoresis to confirm product size. As our PCR reactions consistently yielded a single specific band of the expected size, column-based purification (Macherey-Nagel, NucleoSpin Gel and PCR Clean-up) was performed without gel extraction. All the primers and oligos used for cloning, validation and PCR cassettes are listed in Table S1.”

  1. The concentrations of pharmacological inhibitors used (stated in the result section at page 8) should be included in the method section (in the "Transfection" section) and in FigS2, along with details of their use in cell culture. "If NHEJ inhibitors were applied, cell culture media containing small molecules (KU0060648, NU7441, VE-822, M3814) were added after 8 hours of transfection and cells were incubated for 16 hours. Two days after transfection, cells were selected with 500 μg/ml neomycin (Sigma-Aldrich)". Was the drug kept in the medium during neomycin selection?

Response: We have revised Fig. S2a to highlight the selected concentrations of inhibitors in red on x-axis. We have also added the concentrations to the Methods section and revised the text accordingly on page 34 (lines 834-837): “Briefly, cells at ~70% confluency in one well of a 24-well plate were transfected with 100 ng of Cas12a helper plasmid (either impLbCas12a (Addgene #137715) or impLbCas12a-hGEM) and 900 ng PCR cassette. After 8 h, the transfection medium was replaced with either fresh culture medium. Where indicated, NHEJ inhibitors (200nM KU0060648, 1μM NU7441, 1μM VE-822, and 500nM M3814) were added at this time, and cells were incubated for an additional 16 hours before the inhibitor-containing media was replaced with fresh culture medium. One day after transfection, cells were expanded to a 6-well plate. Two days after transfection, cells were selected with 500 µg/ml G418 (Sigma-Aldrich).”

1. While the authors mention the absence of technical/biological replication within single genes, some graphs are presented with error bars (Fig1F, Fig2d, FigS2b) although no details are given in the text. What replication has been done? What do the error bars represent? What is the sample size?

Re____sponse: Thank you for pointing out this ambiguity. For the samples shown in the original Fig. 1f and Fig. 2d, sequencing libraries were prepared independently in different batches from the same population of tagged cells (from the same transfection), and were sequenced on separate batches. We initially displayed the variation between these technical measurements as error bars. But since they do not represent independent biological replicates, we agree that the error bars could be misleading, so we now show the results from a single sequencing batch for each condition (revised Fig. 1f and revised Fig. 2e). For Fig. S2b, the results of 8h siRNA knockdown were generated from two biological replicate, we have also clarified this point in the revised figure legends.

1. (pages 9-10, Result section): "We quantified the ratio of the HDR band intensity to the total intensity of both bands, defining this as "HDR purity". At the HNRNPA1 locus, we observed that both inhibition of c-NHEJ and synchronization of Cas12a increased HDR purity (Figure 3a)." How were the bands quantified to obtain the reported HDR purity %? Which software was used for band intensity quantification? Similarly, the information about how HDR purity was calculated with the anchor-seq data is lacking. These pieces of information are not present in the Method section and should be added.

Response: This information has been included in the Method section on page 36 (lines 903-905): ” The PCR products were analyzed by gel electrophoresis on 1% agarose/TAE, where the upper band corresponds to junctions generated by integration via c-NHEJ and the lower via HR. The intensity of both bands was quantified using Fiji (ImageJ 2.14.0/1.54f). HDR purity was quantified as the ratio of the HDR band intensity to the total intensity of both bands.” and on page 38 (line 966): ” In addition, HDR purity was calculated as the ratio of the HDR / (HDR + Indel) reads. All custom scripts were integrated into a Snakemake workflow, allowing automated execution of the analysis pipeline.”

Minor comments:

1. A few typos are present throughout the text. Examples: "because the probability of perfect insertion at both ends of the reporter are very low" (page 2); "With this 'mammalian PCR tagging' method constitutes a" (page 3); "In this work we address these gaps and employ selection markers fused in-frame to the tag of choice (e.g. mNeonGreen) using a 2A peptide spacing the two protein domains ensures that" (page 4); "but increased the off-target frequency for TOMM20 by 0.6-fold? (page 9); "from the wide-type and tagged cells" (page 17); "Together, our improvements outline an robust strategy" (abstract). Some other might be present, please check carefully.

Re____sponse: We apologize for the typos. These have been fixed in the revised manuscript. We also checked to make sure other typos are corrected.

1. The Acknowledgement part seems incomplete, and the author contributions are not listed.

Re____sponse: The Acknowledgement part has been revised and author contributions have been added.

1. Can the authors explain the concept/meaning of "index hopping" in the text (page 6)?

Response: We have revised the text on page 6 (lines 207-213): “In Tn5-Anchor-Seq, the customized barcode strategy enables the pooling of a large number of samples immediately after Tn5 tagmentation, but this pre-PCR pooling can introduce index hopping — the misassignment of reads to an incorrect sample barcode through cross-amplification. To assess the extent of index hopping from pre-PCR pooling, we designed a dedicated experiment in which reads assigned to barcode-gene combinations not expected in the pool were counted as misassigned, and their fraction relative to total reads was calculated as the index hopping rate. The observed rates ranged from 0.05% to 6%.”

1. The FigS2g does not exist (cited at page 8). Did the authors mean f?

Re____sponse: We apologize for the incorrect figure citation. It has been corrected in the revised manuscript.

1. There is a discrepancy between Figures and labels regarding FigS3 at page 10: "The PS&Btn modifications on PCR cassettes reduced the frequency of concatemeric reads by 0.5- to 1.7-fold for most genes, while no effect was seen for CANX and SLC16A1 (Figure 4c and Figure S3d). As expected, inhibition of NHEJ with KU, NU, or M3814 decreased the concatemeric integration, while treatment with VE or the use of Cas12a-hGEM increased concatemer frequency at specific loci, such as CANX, DDX21, and SLC16A1 (Figure 4d, 4e, and Figure S3e). Inhibition of MMEJ by knocking down Polθ reduced concatemeric integration at the EMD and SLC16A1 loci but not at the LMNA locus (Figure S3e)." FigS3e does not exist, instead S3d seems to contain what S3e was supposed to show.

Re____sponse: We apologize for these mistakes. We have carefully reviewed the entire manuscript to ensure that all Figures and labels are consistent.

1. Figure 5b is never cited in the main text, nor elsewhere in the manuscript.

Re____sponse: We apologize for the typo. Fig 5b was mistakenly referred to as Fig 5a. This has now been fixed.

1. In the FigS2c caption, remove the sentence "All PCR cassettes used in this experiment were modified with PS and Btn." since both modified and unmodified PCR cassettes are shown in the panel.

Re____sponse: We apologize for this mistake. The Fig. S2c caption has been revised.

1. The scale bar in the microscopy images (Fig1b, Fig5c) is not clearly visible, please fix the thickness.

Re____sponse: Thanks for pointing this out. We have increased the thickness of the scale bars in the revised Figure 1b and Figure 5c.

1. In Fig5d, some lanes are highlighted in red although no explanation is given in the figure caption or in the text of what red color lanes represent.

Re____sponse: The red lanes indicate the clones that were subjected for sequencing. The Fig. 5d caption has been revised accordingly.

1. In FigS1, different graphs of different panels have the same legend, that is placed only within panel f. The same applies for FigS3. It would help readability to state where to find the legend in the figure caption or to rearrange the panels so that the legend appears next to each graph.

Re____sponse: Thank you for pointing this out. The plots in Fig. S1b, d, and f use the same symbols and colors for the integration outcome categories, with a shared legend next to panel f. We have clarified this in the revised Fig. S1b legend as well as the caption to improve the readability. We also make sure the other figure legends are clear in the revised manuscript.

11.Throughout the schematics used to exemplify the method workflow or cassette architecture there are several abbreviations that are not expanded in the relative figure caption. Examples: Figure 1a (HA, mNG, NeoR, U6, crRNA), Figure 1b (ONT, BC, Tn5) [...]. While some of them can be evinced in the main text, expanding each abbreviation in the respective figure caption can improve the figure readability.

Re____sponse: We have included the abbreviations in the respective figure captions throughout the revised manuscript.

1. In Fig1e, several symbols are present in the IGV snapshots whose meaning can only be guessed (what are purple vertical lines? What do numbers and letters indicate and what do the color indicate?). This information should be added as legend in the panel or explained in the figure caption. Similarly, it is not clear what the IGV snapshot indicates, it would be useful to add vertical lines in the IGV snapshot indicating, for example, the 5'-HA/3'-HA portion or something else that could help the reader understand what portion of the cassette is indicated.

Re____sponse: Thank you for the suggestions. We have added vertical lines to the IGV snapshots in the revised Fig. 1e to indicate the approximate positions of 5’-HA junctions. We have also expanded the figure caption to explain the IGV annotations: “(e) Schematics illustrating genomic integration scenarios following PCR tagging and corresponding IGV snapshots showing sequencing-read alignments: i. HDR-mediated integration; ii. NHEJ-mediated deletions and insertions; iii. Off-target integration; iv. Concatemeric integration. Black dashed lines connect each schematic to the genomic interval displayed in the corresponding IGV snapshot. In the IGV snapshots, grey bars represent aligned sequencing reads, whereas mismatches to the reference sequence are shown as colored vertical marks according to the standard IGV nucleotide color scheme (A, green; C, blue; G, brown; T, red). Purple vertical marks denote insertions, with numbers indicating the base-pair length of the insertion. Gaps or thin connecting lines within individual reads indicate deletions, with numbers indicating the size of deletion. Blue vertical dashed lines indicate the approximate positions of the 5’-HA junctions.”

1. Please specify that FACS was used only for the seamless tagging experiment, as it's unclear in the text. Were sorted cells seeded as one cell per well, or were they collected in one single tube and then separated? Why is Fig5b showing the sorting of mNG fluorescent cells while the result and method only mScarlet-i is mentioned (possibly wrong figure)?

Re____sponses

• FACS was only used for the seamless tagging experiment, and single cells were seeded as one cell per well. We have added this information to the Methods text on page 35 (lines 877-884): “During seamless PCR tagging, following G418 selection, cells were harvested, washed with PBS…… Single mScarlet-i-positive cells were sorted directly into separate wells of 96-well plates containing……”
• We have also revised Fig. 5b, in which the mScarlet-i was used as the fluorescent protein.

  1. In FigS2, panels e-f show the same variable (fraction of HDR reads). For EMD locus, however, there is a possible discrepancy on the fraction shown in e (yellow bar, PS&Btn) and f (grey bar, no treatment, modified oligos). Can the authors explain this apparent discrepancy?

Re____sponse: Thank you for pointing this out. Panels e and f (correspond to the revised Fig. 2d and S2e) were generated from different batches of transfection. The difference of EMD values is attributed to batch-to-batch transfection variability. Therefore, comparisons within each panel were performed within the same transfection batch. We have clarified this in Methods text on page 34 (lines 844-847): “Independent experiments shown in separate figure panels were performed in distinct transfection batches unless otherwise indicated. Because absolute editing efficiencies can vary between transfections, treatment effects were evaluated relative to the corresponding controls within each experimental batch. ”

1. Looking at some figures, such as Fig2, it is sometimes hard to relate the results to a "bigger picture". For example, Fig2d depicts "% of HDR integrations", while Fig2f shows "Fraction of HDR reads (%)". Besides possible confusion regarding the name of the variable analyzed, the caption of Fig2f explains that the relative panel contains the data in Fig2d. As Fig2d contains % of HDR-mediated integration of unmodified cassettes ranging 60-85%, one would expect to find the same percentages in Fig2f, under unmodified, control cassette; however, on average the fraction of HDR reads in these samples is only 10-20%. How is this possible? Is Fig2f including unmapped reads or reads mapped to off-target loci?

Re____sponse: We apologize for the confusion. We agree that the original description was not reader-friendly. We have restructured Results section 2 (pages 7-9). We now first describe the full spectrum of tagging outcomes across all gene loci and treatment conditions using the metrics “fraction of tagging outcomes”. Then we present in detail the “HDR efficiency” across conditions. In addition, we have clarified these metrics in Methods on page 37 (lines 961-966):” The total read count for tagging outcomes was defined as HDR + Indel + off-target + concatemer reads, whereas genomic integrations (Figure 1c) were defined as HDR + Indel + off-target reads, excluding concatemer reads. Thus, outcome fractions in the holistic analysis (Figure 2d) were normalized to all classified tagging outcomes, while event efficiencies/frequency (HDR, Indel, off-target) were calculated relative to genomic integrations only.”

1. The graph in Fig3d displays Log2FoldChange of indel frequencies. To have a better understanding of the data, it is advisable to show an additional graph with "raw" indel frequencies for each gene, as side-by-side bars (similar to the graph in Fig2c). The same applies for the fold change shown in Fig3g.

Re____sponse: Thank you for this suggestion. We have revised the figure to include the additional graphs showing the raw frequencies under the control conditions (revised Fig. 3d, 3g), and moved the Log2FoldChange graph to revised Fig. S3c, S3e. We have also included the side-by-side bars showing the raw frequencies under all conditions in the revised Fig. S3b, S3e.

1. [SUGGESTION TO IMPROVE CLARITY] Relative to the comments above (15-16), it would be advisable to add one or more graphs that summarize the read composition, similar to what has been done for Fig1f, for all genes analyzed in the different conditions. For example, it would be advisable to add a supplementary figure with one graph per gene analyzed (8 graphs in total) in the form of the one displayed in Fig2f, with stacked bars instead of boxplots as shown in Fig1f. This will help the reader understanding better and compare side-by-side the effect of the treatments applied in read composition for each gene.

Re____sponse: Thank you for this suggestion. We agree that a holistic overview of the outcome composition is important and helpful to illustrate the overall effects of different conditions. We have therefore showed the full spectrum of tagging outcomes across all gene loci and treatment conditions in the revised Fig. 2d and S2e. We have also revised the results text accordingly on pages 12-13 (lines 333-355).

Reviewer #____2

1. The most important shortcoming of this manuscript is the lack of biological replicates. The authors present results from multiple loci, but in this setting, variation will be largely driven by locus-specific effects rather than true experimental variation, which can be substantial for these types of methods. This makes it difficult for readers and potential users to evaluate how robust this pipeline is. The authors must present biological replicates for at least a small number of loci with their finalized method.

o Significant time and resources will be needed.

Re____sponse: Thank you for this valuable suggestion. We agree that biological replicates are critical for demonstrating the reproducibility and robustness of our workflow. We have therefore revised Fig. 1b, to include quantification of the fraction of mNG+ cells across three biological replicates for three different genes. These replicates were obtained from independent transfection experiments and were subjected to statistical analysis. The text on page 5 (lines 143-151) has also been revised accordingly.

1. The authors characterize clonal genotypes following seamless PCR tagging at two loci. They report that 2/6 isolated clones of HNRNPA1 have the desired edit, while 3/3 clones of SLC16A1 have the desired edit. However, the small number of amplicons sequenced makes it difficult to draw robust conclusions about clonal genotype outcomes. The authors should perform additional amplicon sequencing to strengthen these conclusions. In addition, they should sequence the incorrectly sized products generated from the junction-PCRs to gain further insight into alternative genotypes and incorrect editing that may occur with this method.

o Additional sequencing can easily be accomplished if cell lines are still available. An estimated time of about 1-2 weeks for cell thawing, genome extraction, amplicon sequencing, PCR purification, and outsourced Plasmidsaurus sequencing.

Re____sponse: Thank you for this important comment. We agree that sequencing more clones would robustly determine the frequencies of different genomic integration outcomes following seamless PCR tagging. However, our intention was not to quantitatively mapping full spectrum of editing outcomes, rather demonstrate that the two-cassette strategy can generate seamless integrations at different gene loci. We have therefore revised the Results text on pages 26 (lines 603-614) to avoid overclaiming regarding the genotype frequencies.In addition, we have revised the corresponding Discussion text on page 30 (lines 704-713) accordingly.

1. It is not obvious how the authors were able to accurately quantify concatemeric integrations with the Tn5-anchor-seq tool. Specifically, the schematic in Figure 4a makes it clear that concatemers have multiple binding sites for the PCR primer. If these binding sites give rise to multiple products from the same template, the quantification would be inaccurate. The authors should comment on their considerations in suppressing the formation of secondary products, such as the use of a non-strand displacing polymerase, and in ensuring that their quantifications are accurate, including any bioinformatic steps.

o The authors can clarify methods and adjust results presented in the manuscript in 1-2 days.

Re____sponse: Thank you for pointing this out. The scenario where a single template generates multiple PCR products would require amplification of an intact concatemer. However, in our Tn5-anchor-seq, Tn5 tagmentation precedes PCR so that concatemers are fragmented before PCR. Primer sites from a N-copy concatemer therefore reside on separate tagmented fragments, which are amplified independently. So, the concatemer-derived read counts scale with the amount of concatemeric sequence present in the library. Potential secondary products are further minimized by the nested two-round PCR design, biotin-streptavidin enrichment of cassette-primed amplicons, limited first-round PCR (15 cycles), hot-start polymerase, and size selection of products > 500bp. In bioinformatics analysis, each read is counted once after demultiplexing, mapping, filtering and removal of secondary and supplementary alignments. Importantly, this metric reports the fraction of concatemeric sequence, rather than the number of concatemeric integration events per allele. We have clarified the interpretation of concatemer reads in the revised manuscript on page 22 (lines 494-497).

1. The authors begin the results section by describing how their revised tagging cassette improves selection efficiency. It appears that they compare their newer data to data that were obtained for their previous manuscript, which were likely obtained at different points in time, potentially by different individuals, and using different sets of reagents, which makes direct comparisons impossible. It would be beneficial to include at least one side-by-side experiment to compare the authors' new method with their previous method to conclusively demonstrate any improvement.

Re____sponses

• We agree that our original text overinterpreted the comparison with the tagging efficiency previously reported by Fueller et al. (2020). The previous experiments were performed in parental HEK293T cells using Zeocin-based selection, whereas the present experiments were performed in HEK293T NeoR-KO cells using G418 selection. Since several experimental parameters were not fully matched, we recognize that a direct quantitative comparison is not be appropriate.
• We have therefore removed the sentence “compared to 32% when employing a cassette in which the selection marker was inserted as a separate gene (Fueller et al., 2020). ” in the revised Results text on page 5. Instead, we now report the quantification across biological replicates to show the reproducibility of the workflow using the new 2A-linked selection cassette, thereby supporting the use of the 2A-linked selection strategy for subsequent experiments.
• In addition, we changed the title of this Results section to “2A-linked selection and characterization of integration outcomes of CRISPR-Cas12a-assisted PCR tagging” to avoid the claim of direct improvement relative to the previous method.

  1. Data and method presentation: For much of the manuscript, the authors provide detailed descriptions of experiments and methods. However, the authors should provide more detail in the figure legends about the concentration and timing of chemical inhibitor treatments.

Re____sponse: Thank you for pointing this out. We have added the concentrations and treatment details to the Methods section and revised the text on page 34 (lines 834-837).

6.Replication and statistical analysis: While the authors mention their lack of replicates, and reason multiple loci and conditions compensate for this, replication of their experiments is still necessary in order to draw meaningful conclusions of their data (see comment above).

Re____sponse: As described in the response to the first comment, we have revised Fig. 1b, to include quantification of the fraction of mNG+ cells across three biological replicates for three different genes. The text on page 5 has also been revised accordingly.

Minor Comments:

1. The authors clearly identify and cite the prior work on which their method is based.

Re____sponse: We thank you for this kind comment.

1. The discussion focuses on the findings and limitations of the authors' specific study. Readers would benefit from a conceptual comparison of the strengths and weakness of their method to other similar technologies in this space, which would allow researchers to make better informed decisions about the appropriateness of this method for their own work.

Re____sponse: Thank you for this suggestion. We have added a paragraph in Discussion on page 31 (lines 718-727) to compare with similar technologies.

1. The text and line of the scale bar on all microscopy images needs to be enlarged for readability.

Re____sponse: All the scale bars of the microscopy images have been enlarged in the revised manuscript.

1. Text has inappropriate question mark in "... off-target frequency for TOMM20 by 0.6 fold?".

Re____sponse: The question mark has been removed.

1. Fold-changes in the text are described in an unconventional and unintuitive manner. For example, the authors note a 0.2 to 0.7-fold reduction in off target frequency contrasted against a 0.6-fold increase, which appear to be two different interpretations of fold-changes. These results might be more accurately represented by using a 1-fold change as the baseline for no change. Alternatively, the authors could provide this measure as percent decreases and increases.

Re____sponse: Thank you for pointing this out. We have revised the text to express decreases and increases as percent changes relative to the control condition, while retaining log2 fold-change values in the heatmaps. The revised text show on lines 436, 447, 448, and 517.

1. The authors mention that an example of diffuse cytoplasmic fluorescent signals observed in microscopy can be seen in Figure 2c, which are labeled with white arrows. A figure with this description is not present in the manuscript.

Re____sponse: We apologize for the confusion. In the revised Fig. 1b and S2d, examples of diffuse cytoplasmic fluorescence are indicated by white arrows. Accordingly, the Results text was revised on page 22 (lines 498-500).

1. Schematics in Figure 5 show mNeonGreen, however, Figure 5c is labeled as mScarlet. The Sauthors should clarify which fluorescence tag was used.

Re____sponse: We have revised Fig. 5a by replacing “mNG” with the generic word “tag”, as this panel is a general schematic to compare the two protein-tagging strategies. We also corrected Fig. 5b and 5d to indicate mScarlet-i, which is the fluorescent tag used in this part.

1. Figure S3e is mentioned in the text, however, the supplemental material does not contain a 3e.

Re____sponse: The typo has been corrected in the revised manuscript.

1. The authors have developed a fantastic pipeline to quantify tagging outcomes holistically, and in Figure 1f they visualize the results of the pipeline in an intuitive and informative manner. However, for the remainder of the manuscript, they proceed not to use this visualization and instead focus on the effects of their experimental parameters on individual outcomes or a ratio of two outcomes ("HDR purity"). This choice makes it difficult to clearly evaluate the effects of the parameters on all outcomes, and the "HDR purity" metric, although useful to compare against the gel-based readout, is difficult to interpret. We would recommend including the holistic visualization from Figure 1f for all experiments, in the supplement if necessary, for example as a large grid that depicts the frequency of all outcomes for each experimental condition by locus. This will make it much easier for readers to evaluate how a given experimental parameter affects the frequency of different editing outcomes.

Re____sponse: Thank you for this important suggestion. We agree that a holistic overview of the outcome composition is important to illustrate the overall effects of different conditions. We have therefore restructured the Results section 2 by first showing the full spectrum of tagging outcomes across all gene loci and treatment conditions in the revised Fig. 2d and S2e. We then described the HDR efficiency in the revised Fig. 2e, 2f, and S2g. The corresponding text has also been revised accordingly (pages 12-13, lines 333-355). We have also revised the description about HDR purity results on page 17 (lines 414-423) to make it clearer.

1. While the authors detail their rationale in selecting loci to tag in a previous publication, it is important to include the information in the current manuscript as well.

__Re____sponse: __We have included this information in the revised manuscript on page 11 (lines 305-311).

1. The authors present many figures that look similar but display different quantities. To improve readability, they should use more descriptive figure titles and axis labels so that the main findings and quantities are immediately clear. This is particularly needed in Fig.2d, where the variable plotted is not clear.

Re____sponse: We have restructured Figure 2 to provide a more holistic overview of the full spectrum of tagging outcomes. The original Fig. 2d has been revised as Fig. 2e with the y-axis labeled “HDR efficiency” and the condition indicated as “Unmodified, no treatment” on top. We have also revised the axis labels and results description on page 12 (lines 349-355) for greater clarity.

1. Two aspects of the final method may (or may not) represent limitations that would be helpful for the authors to discuss. First, the authors use a Cas12a with expanded PAM range, which has the advantage of increasing the number of available cut sites but also has the potential to lead to more off-target cutting, which can cause secondary mutations in the selected cell populations. Second, tagging the 3′ UTR may lead to differences in transcript and protein stability (especially due to the remainder of the 2A site). It would be helpful for the authors to include their perspectives on these issues and if they took efforts to address them.

Re____sponses

• Thank you for raising these two important points. Regarding the expanded-PAM Cas12a variant, we have added this point explicitly to the limitations paragraph in Discussion on page 32 (lines 757-759): “The use of an expanded-PAM Cas12a variant may also alter off-target activity relative to wild-type Cas12a (Kleinstiver et al., 2019). Thus, comprehensive off-target profiling is needed in applications where genomic integrity is critical. ” Systematic off-target characterization was beyond the scope of the current study, but we consider this an important direction for future work, particularly for therapeutic applications.
• Regarding the 2A site remainder and 3’-UTR effects, we partially address the concerns about protein stability/integrity by tagging mNG-FKBP degron at four loci and confirmed efficient inducible depletion of the tagged protein following degron induction (revised Fig. S4). This demonstrates that the integrated fusion proteins are expressed and that the degron domain remains structurally accessible. However, we acknowledge that direct measurement of endogenous protein activity will be important in future studies. We have therefore added discussion of this point in limitations paragraph on page 32 (lines 760-764).

  Reviewer #____3

1. All optimization experiments are performed in HEK293T-N cells, which are aneuploid/polyploid, permissive for genome editing and have atypical DNA repair dynamics. While acceptable for method development, this limits generalizability, especially given the strong locus and pathway dependent effects observed. DNA repair pathway balance (HDR vs NHEJ vs MMEJ, etc.) can be cell-type specific. The improvements reported here may not generalize to non-transformed cells, stem cells, cancer cell lines, or other therapeutically relevant cell types. Selecting a small, representative gene set (2-3 genes) and performing controlled tagging experiments across a panel including cancer cell lines, non-transformed cells (like hTERT immortalized RPE-1 cells), and embryonic stem cells (H1 or H9) could provide readers with a clearer view of integration and tagging efficiencies across diverse cellular contexts. Additionally, assessing the effects of pathway modulation in these cell types would help determine how broadly generalizable these strategies are increasing the impact of the method detailed herein.

Re____sponses

• Thank you for raising this important point. We fully agree that cell-type generalizability is very important. HEK293T NeoR-KO cells were selected for systematic optimization because their high editing permissiveness enables robust detection of differences across conditions and loci, rather than because they are representative of the broader range of cell types.
• To assess the portability of our workflow, we tested it in two additional cell lines. First, we applied the optimized standard PCR tagging protocol — using PS- and Btn- modified donors in combination with 200 nM KU0060648 — to HeLa cells. Tagging of HNRNPA1, DDX21, and TOMM20 was evaluated by fluorescence microscopy and flow cytometry. The fraction of mNG+ cells at expected localization were comparable to the observations in HEK293T-N cells. Second, we applied the seamless tagging strategy to HepG2 cells at HNRNPA1 locus and confirmed the comparable tagging efficiency via fluorescence microscopy. All these data are now summarized in Supplementary Note 1.
• We note that sequencing-based integration outcome characterization was not performed in either HeLa or HepG2 cells. We have clarified this in the revised Discussion on page 32 (754-757).

  1. While the manuscript presents a clear and well-supported optimization of CRISPR-Cas12a assisted PCR tagging, it would benefit from a more explicit contextual comparison to other contemporary endogenous tagging approaches, such as Cas9-mediated HDR with plasmid donors. Ideally, a single or small panel of genes could be compared to assess the benefits and drawbacks of each technique. Even a conceptual discussion outlining relative strengths, limitations, and use cases would help readers better position the proposed method within the broader genome-editing landscape. Such a comparison would clarify when PCR tagging is the most appropriate choice and where alternative strategies may offer advantages, thereby enhancing the interpretability and practical impact of the study.

Re____sponse: Thank you for this suggestion. We have revised the Discussion to include a dedicate paragraph for comparison with other similar technology on page 31 (lines 718-727).

1. Lack of functional validation beyond localization. Localization is used as the primary functional readout. Including limited functional validation (e.g., protein abundance, stability, or activity) for a representative target would strengthen the claim that optimized conditions preserve protein function, since donor modifications and DNA repair pathway inhibition could affect protein dosage or integrity. Alternatively, explicitly acknowledging this limitation would better frame the scope of the functional conclusions. At a minimum this needs to be discussed carefully.

Re____sponses:

• Thank you for this important suggestion. We agree that subcellular localization alone provides limited evidence for functional protein integrity. Thus, we applied mNG-degron tagging at HNRNPA1, DDX21, CANX, and KIF11 loci to confirm protein integrity beyond localization. Following degron induction, efficient depletion of the mNG-tagged proteins was confirmed by microscopy, flow cytometry, and western blot. The combination of correct subcellular localization and successful inducible degradation indicates that the tagged fusion proteins are expressed and structurally intact at the endogenous locus.
• The results are presented in revised Fig. S4, and a brief description has been added to the Results section on page 23 (lines 530-539).
• We noted that these results are not full functional validation, the degradation efficiency does not directly show whether native protein activity is preserved. We have revised the Discussion on page 32 (lines 764-767) to acknowledge this limitation.

  1. The effects of donor cassette size and sequence composition on integration efficiency and concatemer formation are not systematically explored. Because larger or more complex payloads may engage repair pathways differently, a brief discussion of how donor size might influence the reported improvements would help contextualize the results. If extra curious, a single reliably editable target gene could be used to assess and explore the effect of varying payload composition.

Response: Thank you for this suggestion. The mNG-degron cassette described in the revised Fig. S4 and also our response to Major point 3 is larger and compositionally more complex, as it contains an additional degron sequence and an HA epitope tag. With this degree of payload size expansion, we didn’t observe any obvious reduction in performance with respect to PCR amplification or tagging efficiency assessed via microscopy. However, we acknowledge that the effects on HDR efficiency and concatemer formation were not evaluated specifically. We have now discussed this limitation in the revised manuscript on page 31 (lines 728-735).

Minor ____Comments:

1. The frequency of concatemeric integrations is inferred from junction-centric Tn5-Anchor-Seq data rather than direct measurement of intact alleles, which limits the ability to determine concatemer copy number, allelic structure, or the presence of complex rearrangements within a single genomic locus. While this limitation is acknowledged, it should be more clearly emphasized when interpreting the magnitude of concatemer suppression and improvements in genomic homogeneity, particularly given the polyploid nature of HEK cells. Clarifying that junction counts do not directly equate to allele counts would help prevent overinterpretation of these results and better frame the conclusions drawn from the sequencing data.

__Response____: __Thank you for this suggestion. We have revised the corresponding text on page 22 (lines 495-497) to avoid overinterpretation of the concatemer results.

1. Inhibition of DNA-PKcs emerges as one of the most effective strategies for increasing HDR-mediated integration and suppressing undesired byproducts in this study. However, the broader practicality of this approach is not explored in depth. DNA-PKcs inhibitors can introduce cytotoxicity, alter cell-cycle progression, or induce stress responses that may be incompatible with certain experimental systems or long-term phenotypic analyses. A more explicit discussion of these limitations, including guidance on dosing, duration of treatment, and scenarios in which donor modification alone may be preferable, would help readers/researcher assess the applicability of this strategy across different cell types and use cases.

__Response____: __We have expanded the discussion of DNA-PKcs inhibitors in the revised manuscript on page 29 (lines 667-670).

1. The study focuses exclusively on C terminal tagging, and the applicability of the optimized workflow to N terminal or internal tagging configurations is not examined. Because tagging position can substantially influence repair outcomes and expression, a brief discussion of whether the observed improvements are expected to generalize beyond C terminal insertions would help clarify the scope of the method.

__Response____: __We have expanded the limitation paragraph in Discussion on page 31 (lines 736-743).

1. Clarify the rationale for inhibitor concentrations in the main text, not only in supplement.

__Response____: __We have revised the text on page 11 (lines 295-297).

1. Define all abbreviations at first use (e.g., c-NHEJ, MMEJ) for clarity.

__Response____: __The abbreviations have been defined in the revised manuscript.

1. Explicitly state sample sizes for microscopy-based quantifications.

__Response____: __This has been addressed.

7.Clarify how index hopping was quantified and controlled in pooled sequencing analysis.

__Response____: __We have clarified this in the revised manuscript on page 6 (lines 207-213).

1. Briefly describe computational resource requirements for the analysis pipeline.

__Response____: __Thank you for this suggestion. We have included this information in the Methods text on page 38 (lines 971-975).

1. State whether the "seamless" tagging method was tested with donor modifications and inhibitors (Assumption is no from your drawings in Figure 5).

__Response____: __We apologize for the missing information. Seamless tagging was performed using PS&Btn-modified donor in combination with KU treatment, as this was the best-performing condition identified in the standard PCR-tagging experiments. We have now clarified this in revised Fig. 5b and Results text on page 26 (lines 593-595).

1. Clarify whether donor-end modifications affect PCR yield or fidelity. Also, discuss cost implications of biotinylated/modified primers for scalability

__Response____: __We did not observe any obvious reduction in PCR performance when using modified primers, although PCR yield and fidelity were not quantified as separate endpoints. We have therefore clarified this as well as the primer cost in Discussion on page 29 (lines 660-664).

1. State whether sequencing depth was normalized across conditions.

__Response____: __Thank you for pointing this out. Sequencing depth was not explicitly normalized across conditions as all reported metrics are per-sample fractions. However, we ensured that sequencing depth was sufficient for all samples, such that fraction estimates were not biased by low coverage. This is now stated in the Methods on page 38 (lines 966-969).

1. Abstract: replace 'an robust strategy' with 'a robust strategy'.

__Response____: __This has been fixed.

1. Results section: ensure consistent use of 'Cas12a-hGEM' vs 'hGEM-Cas12a'.

__Response____: __It’s now consistently “Cas12a-hGEM” in the revised manuscript.

1. Figure 3g: remove stray question mark after '0.6-fold?'.

__Response____: __It has been removed.

1. Methods section: standardize units (µM vs uM) throughout.

__Response____: __We now use µM throughout the revised manuscript.

1. Figure references: inconsistent capitalization of figure labels (Figure vs Fig.).

__Response____: __We now use consistently “Figure” in the revised manuscript.

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Referee #3

Evidence, reproducibility and clarity

Improved cloning-free one-step CRISPR-Cas12a-assisted tagging of mammalian genes using PCR generated reagents (PCR tagging)

Peer Review Summary:

This manuscript presents a substantive and technically rigorous refinement of the previously published CRISPR-Cas12a assisted PCR tagging method for mammalian cells. Building on the original framework, Lou et al. introduce donor cassette engineering, repair pathway modulation, and an advanced long-read sequencing-based analysis pipeline to systematically improve tagging fidelity and to quantitatively characterize integration outcomes. The work is carefully executed, clearly written, and demonstrates a strong understanding of both the strengths and limitations of PCR-based genome editing strategies. A major strength of the study is its emphasis on measurement rather than inference. The use of Tn5-Anchor-Seq coupled with nanopore long-read sequencing provides a detailed and largely unbiased view of on-target HDR events, NHEJ-mediated insertions, concatemer formations, and off-target integrations. This addresses a known weakness of fluorescence- or selection-based readouts, which can overestimate true "precise" editing outcomes. The authors are appropriately cautious in interpreting their data and explicitly acknowledge the residual heterogeneity that persists even under optimized conditions.

Major Points:

1. All optimization experiments are performed in HEK293T-N cells, which are aneuploid/polyploid, permissive for genome editing and have atypical DNA repair dynamics. While acceptable for method development, this limits generalizability, especially given the strong locus and pathway dependent effects observed. DNA repair pathway balance (HDR vs NHEJ vs MMEJ, etc.) can be cell-type specific. The improvements reported here may not generalize to non-transformed cells, stem cells, cancer cell lines, or other therapeutically relevant cell types. Selecting a small, representative gene set (2-3 genes) and performing controlled tagging experiments across a panel including cancer cell lines, non-transformed cells (like hTERT immortalized RPE-1 cells), and embryonic stem cells (H1 or H9) could provide readers with a clearer view of integration and tagging efficiencies across diverse cellular contexts. Additionally, assessing the effects of pathway modulation in these cell types would help determine how broadly generalizable these strategies are increasing the impact of the method detailed herein.
2. While the manuscript presents a clear and well-supported optimization of CRISPR-Cas12a assisted PCR tagging, it would benefit from a more explicit contextual comparison to other contemporary endogenous tagging approaches, such as Cas9-mediated HDR with plasmid donors. Ideally, a single or small panel of genes could be compared to assess the benefits and drawbacks of each technique. Even a conceptual discussion outlining relative strengths, limitations, and use cases would help readers better position the proposed method within the broader genome-editing landscape. Such a comparison would clarify when PCR tagging is the most appropriate choice and where alternative strategies may offer advantages, thereby enhancing the interpretability and practical impact of the study.
3. Lack of functional validation beyond localization. Localization is used as the primary functional readout. Including limited functional validation (e.g., protein abundance, stability, or activity) for a representative target would strengthen the claim that optimized conditions preserve protein function, since donor modifications and DNA repair pathway inhibition could affect protein dosage or integrity. Alternatively, explicitly acknowledging this limitation would better frame the scope of the functional conclusions. At a minimum this needs to be discussed carefully.
4. The effects of donor cassette size and sequence composition on integration efficiency and concatemer formation are not systematically explored. Because larger or more complex payloads may engage repair pathways differently, a brief discussion of how donor size might influence the reported improvements would help contextualize the results. If extra curious, a single reliably editable target gene could be used to assess and explore the effect of varying payload composition.

Minor Points:

1. The frequency of concatemeric integrations is inferred from junction-centric Tn5-Anchor-Seq data rather than direct measurement of intact alleles, which limits the ability to determine concatemer copy number, allelic structure, or the presence of complex rearrangements within a single genomic locus. While this limitation is acknowledged, it should be more clearly emphasized when interpreting the magnitude of concatemer suppression and improvements in genomic homogeneity, particularly given the polyploid nature of HEK cells. Clarifying that junction counts do not directly equate to allele counts would help prevent overinterpretation of these results and better frame the conclusions drawn from the sequencing data.
2. Inhibition of DNA-PKcs emerges as one of the most effective strategies for increasing HDR-mediated integration and suppressing undesired byproducts in this study. However, the broader practicality of this approach is not explored in depth. DNA-PKcs inhibitors can introduce cytotoxicity, alter cell-cycle progression, or induce stress responses that may be incompatible with certain experimental systems or long-term phenotypic analyses. A more explicit discussion of these limitations, including guidance on dosing, duration of treatment, and scenarios in which donor modification alone may be preferable, would help readers/researcher assess the applicability of this strategy across different cell types and use cases.
3. The study focuses exclusively on C terminal tagging, and the applicability of the optimized workflow to N terminal or internal tagging configurations is not examined. Because tagging position can substantially influence repair outcomes and expression, a brief discussion of whether the observed improvements are expected to generalize beyond C terminal insertions would help clarify the scope of the method.
4. Clarify the rationale for inhibitor concentrations in the main text, not only in supplement.
5. Define all abbreviations at first use (e.g., c-NHEJ, MMEJ) for clarity.
6. Explicitly state sample sizes for microscopy-based quantifications.
7. Clarify how index hopping was quantified and controlled in pooled sequencing analysis.
8. Briefly describe computational resource requirements for the analysis pipeline.
9. State whether the "seamless" tagging method was tested with donor modifications and inhibitors (Assumption is no from your drawings in Figure 5).
10. Clarify whether donor-end modifications affect PCR yield or fidelity. Also, discuss cost implications of biotinylated/modified primers for scalability
11. State whether sequencing depth was normalized across conditions.

Spelling/Grammar/Other Errors:

1. Abstract: replace 'an robust strategy' with 'a robust strategy'.
2. Results section: ensure consistent use of 'Cas12a-hGEM' vs 'hGEM-Cas12a'.
3. Figure 3g: remove stray question mark after '0.6-fold?'.
4. Methods section: standardize units (µM vs uM) throughout.
5. Figure references: inconsistent capitalization of figure labels (Figure vs Fig.).

Significance

Overall, the manuscript represents an incremental, but meaningful advance rather than a conceptual reinvention of PCR tagging. The improvements described will be of clear practical value to users of the original method and to the broader genome editing community. Specific limitations of this study include the overreliance on a single cell line (HEK293T) as well as inherent methodological drawbacks, such as the toxicity associated with certain pathway modulation strategies and the likelihood of donor concatemerization. However, these limitations are clearly acknowledged by the authors and do not detract from the core contributions of the work.

I find this manuscript to be suitable for publication pending minor to moderate revisions. The technical advances are sound, the analysis is thorough, and the conclusions are well supported by the data. Addressing the major issues below, primarily related to scope, clarity, and contextualization, would further strengthen the manuscript and improve its accessibility.

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Referee #2

Evidence, reproducibility and clarity

Summary: In this study, Lou et al. provide an updated version of their previously established CRISPR/Cas12a-assisted PCR-tagging method for mammalian cells that supports large cassette integrations. They report improved fidelity and editing efficiency, introduce a strategy to quantify integration types using long read sequencing, and describe a one-step gene-tagging approach. The authors expand and improve upon their original protocol and analysis in the following ways: (1) The use of a tagging cassette that contains a tag-2A-marker fusion, allowing for easier selection of tagged clones. (2) The use of chemically modified PCR cassettes with phosphorothioate and biotin, which enhances the precision of integration. (3) Guiding cells towards HDR repair by chemical inhibition of NHEJ DNA-PKcs, particularly with inhibitor KU0060648. (4) Development of a Tn5-anchor-seq long-read sequencing platform coupled with a computational pipeline to classify knock-in outcomes such as HDR, NHEJ-mediated indels, concatemers, and off-target integrations. (5) A method for seamless tagging that better preserves endogenous 3'-UTRs by integrating tags immediately upstream of the target stop codon and removing the U6 cassette from the tag. Together, these developments have resulted in a method to incorporate large tags at endogenous loci with high efficiency. We expect this method will be a useful tool for researchers across many fields.

Major Comments:

• The most important shortcoming of this manuscript is the lack of biological replicates. The authors present results from multiple loci, but in this setting, variation will be largely driven by locus-specific effects rather than true experimental variation, which can be substantial for these types of methods. This makes it difficult for readers and potential users to evaluate how robust this pipeline is. The authors must present biological replicates for at least a small number of loci with their finalized method.
  • Significant time and resources will be needed.
• The authors characterize clonal genotypes following seamless PCR tagging at two loci. They report that 2/6 isolated clones of HNRNPA1 have the desired edit, while 3/3 clones of SLC16A1 have the desired edit. However, the small number of amplicons sequenced makes it difficult to draw robust conclusions about clonal genotype outcomes. The authors should perform additional amplicon sequencing to strengthen these conclusions. In addition, they should sequence the incorrectly sized products generated from the junction-PCRs to gain further insight into alternative genotypes and incorrect editing that may occur with this method.
  • Additional sequencing can easily be accomplished if cell lines are still available. An estimated time of about 1-2 weeks for cell thawing, genome extraction, amplicon sequencing, PCR purification, and outsourced Plasmidsaurus sequencing.
• It is not obvious how the authors were able to accurately quantify concatemeric integrations with the Tn5-anchor-seq tool. Specifically, the schematic in Figure 4a makes it clear that concatemers have multiple binding sites for the PCR primer. If these binding sites give rise to multiple products from the same template, the quantification would be inaccurate. The authors should comment on their considerations in suppressing the formation of secondary products, such as the use of a non-strand displacing polymerase, and in ensuring that their quantifications are accurate, including any bioinformatic steps.
  • The authors can clarify methods and adjust results presented in the manuscript in 1-2 days.
• The authors begin the results section by describing how their revised tagging cassette improves selection efficiency. It appears that they compare their newer data to data that were obtained for their previous manuscript, which were likely obtained at different points in time, potentially by different individuals, and using different sets of reagents, which makes direct comparisons impossible. It would be beneficial to include at least one side-by-side experiment to compare the authors' new method with their previous method to conclusively demonstrate any improvement.
• Data and method presentation: For much of the manuscript, the authors provide detailed descriptions of experiments and methods. However, the authors should provide more detail in the figure legends about the concentration and timing of chemical inhibitor treatments.
• Replication and statistical analysis: While the authors mention their lack of replicates, and reason multiple loci and conditions compensate for this, replication of their experiments is still necessary in order to draw meaningful conclusions of their data (see comment above).

Minor Comments:

References:

• The authors clearly identify and cite the prior work on which their method is based.
• The discussion focuses on the findings and limitations of the authors' specific study. Readers would benefit from a conceptual comparison of the strengths and weakness of their method to other similar technologies in this space, which would allow researchers to make better informed decisions about the appropriateness of this method for their own work.

Text and figures:

• The text and line of the scale bar on all microscopy images needs to be enlarged for readability.
• Text has inappropriate question mark in "... off-target frequency for TOMM20 by 0.6 fold?".
• Fold-changes in the text are described in an unconventional and unintuitive manner. For example, the authors note a 0.2 to 0.7-fold reduction in off target frequency contrasted against a 0.6-fold increase, which appear to be two different interpretations of fold-changes. These results might be more accurately represented by using a 1-fold change as the baseline for no change. Alternatively, the authors could provide this measure as percent decreases and increases.
• The authors mention that an example of diffuse cytoplasmic fluorescent signals observed in microscopy can be seen in Figure 2c, which are labeled with white arrows. A figure with this description is not present in the manuscript.
• Schematics in Figure 5 show mNeonGreen, however, Figure 5c is labeled as mScarlet. The authors should clarify which fluorescence tag was used.
• Figure S3e is mentioned in the text, however, the supplemental material does not contain a 3e.

Suggestions to improve presentation of data and conclusions:

• The authors have developed a fantastic pipeline to quantify tagging outcomes holistically, and in Figure 1f they visualize the results of the pipeline in an intuitive and informative manner. However, for the remainder of the manuscript, they proceed not to use this visualization and instead focus on the effects of their experimental parameters on individual outcomes or a ratio of two outcomes ("HDR purity"). This choice makes it difficult to clearly evaluate the effects of the parameters on all outcomes, and the "HDR purity" metric, although useful to compare against the gel-based readout, is difficult to interpret. We would recommend including the holistic visualization from Figure 1f for all experiments, in the supplement if necessary, for example as a large grid that depicts the frequency of all outcomes for each experimental condition by locus. This will make it much easier for readers to evaluate how a given experimental parameter affects the frequency of different editing outcomes.
• While the authors detail their rationale in selecting loci to tag in a previous publication, it is important to include the information in the current manuscript as well.
• The authors present many figures that look similar but display different quantities. To improve readability, they should use more descriptive figure titles and axis labels so that the main findings and quantities are immediately clear. This is particularly needed in Fig.2d, where the variable plotted is not clear.
• Two aspects of the final method may (or may not) represent limitations that would be helpful for the authors to discuss. First, the authors use a Cas12a with expanded PAM range, which has the advantage of increasing the number of available cut sites but also has the potential to lead to more off-target cutting, which can cause secondary mutations in the selected cell populations. Second, tagging the 3′ UTR may lead to differences in transcript and protein stability (especially due to the remainder of the 2A site). It would be helpful for the authors to include their perspectives on these issues and if they took efforts to address them.

Significance

Strengths/advance:

• This manuscript combines several established techniques into a single resource describing an updated PCR-tagging method for mammalian cells. In particular, the use of phosphorothioate and biotin-modified PCR cassettes together with the NHEJ inhibitor KU0060648 results in a pronounced increase in HDR while reducing indels, concatemers, and off-target integrations. This work takes CRISPR-assisted PCR-tagging from modest to strong editing outcomes and provides guidance and tools for others using this approach.
• Compared to other tagging methods in the field, this method allows for efficient integration of larger tags, such as an entire fluorescent protein, which is difficult to achieve using other methods.
• This study provides a useful method for cataloging and classifying integration outcomes with Tn5-Anchor-Seq plus a data processing pipeline.
• This study provides an updated online resource for designing primers for seamless PCR tagging.

Improvements:

• As the authors note in the discussion, demonstrating that this method is effective across cell models, especially physiologically relevant and/or therapeutically relevant models, would strengthen the impact of this work.

Audience:

• This study will be of interest to a broad audience, as improvements in mammalian CRISPR-mediated genome knock-ins are relevant to many fields.

Reviewer expertise:

• The PI and trainee together have expertise in genome engineering, synthetic biology, CRISPR technology development, and chemical screening.

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Referee #1

Evidence, reproducibility and clarity

Summary:

The manuscript by Lou et al. present a technological advancement of a previous technique developed by members of the same laboratory (Fueller et al., 2020) that allows gene tagging of mammalian cells (HEK293-T cells) with PCR-generated DNA fragments containing the tag of interest, a selection marker, and a functional crRNA gene driving the integration of the whole cassette at the target locus. Their work focuses on the optimization of the original PCR-tagging protocol, which displayed sub-optimal efficiency in correct gene tagging, by introducing (i) additional design and experimental modifications (such as 2A-linked selection marker, chemical modifications of the PCR cassette, and pharmacological treatment of cells with ATR, NHEJ, or MMEJ inhibitors) and (ii) a further development of the Tn5-Anchor-Seq sequencing protocol optimized for long-read sequencing. As a result, they observed an overall improvement of the gene tagging efficiency by using chemically modified cassettes and NHEJ inhibitors, particularly regarding HDR (which is the desired repair mechanism) efficiency, and a reduction in the frequency of indel generation/concatemers/off-target integration. In addition, they show how their optimized PCR-tagging method can be used to obtain seamless integration, thus preserving the endogenous 3'-UTR of the tagged gene.

Major comments:

Although most results support the authors' conclusions, additional analyses are required for some instances that do not seem fully convincing, particularly related to unclear microscopy image analysis and related supporting data that are underrepresented in the manuscript, yet often referred in the text. More clarity about reproducibility should be also implemented. Specific comments: EVIDENCE:

1. In the first section of results, a self-cleaving 2A peptide is inserted upstream of the selection marker to improve selection of correctly tagged genes, as reported in the cited literature. To demonstate this in their PCR-tagging method, the authors tag the HNRNPA1 gene with the mNG-2A-NeoR strategy and find a tagging efficiency of 70% and more, in contrast with the 32% efficiency found with the original method developed by Fueller et al. (2020) (page 5). In support of this conclusion, only a representative image of cells showing mNG and HOECHST signal is presented, with no quantification (Fig1b). As this is a central result of the manuscript that allowed the authors to maintain the 2A-NeoR selection strategy for further investigation of sequence-level data, it is advisable to perform a more thorough quantification of the tagging efficiency by counting (with the help of image analyis software such as Fiji) the mNG+ cells and the total number of cells (HOECHST+), and calculate the % of mNG+ cells across different biological replicates (ideally, cells transfected in different days). A direct comparison (statistical analysis) with the % of mNG+ cells obtained by the original methodology (Fueller et al) would be desirable. In this way, the robustness of the improved tagging efficiency with the optimized method could be also evaluated within one single gene.
2. In the following line (page 5), authors talk about "correctly localized" signals, although no clear criterium of "correct" signal localization is explained, nor it is indicated anywhere in the example image. While in the following section(s) it is mentioned that diffuse signal may come from unspecific mNG expression of concatenated PCR cassettes, it would be still important to quantify the "correct" vs "uncorrect" mNG signal (i.e: nuclear vs cytoplasmatic) via image analysis.
3. Of particular significance would be to clarify whether there is a relationship between the % of concatemer product and the presence of diffuse cytoplasmic signal. In several instances, the authors mention their previous finding that diffuse cytoplasmic signal usually results from unspecific expression of the fluorescent reporter within a concatenated PCR cassette. However, from Fig1b there is no evident correlation between % of concatemer reads and % of diffuse cytoplasmic signal. Moreover, Fig2c is cited but no arrows are indicated in the figure in contrast with what mentioned in the text (page 10). Moreover, it is unclear what the authors would like to highlight in the following paragraph when talking about the percentage of diffuse signal (the discrepancy of the concatemers vs diffuse signal? Please make the paragraph more clear). Overall, I think that showing actual microscopy data and image quantification of diffuse vs localized signal would be ideal instead of only mentioning the result in the text. Moreover, a clearer and more detailed discussion about the authors' interpretation of the discrepancy observed between the % of concatemers and % of diffuse cytoplasmic signal is needed, and how it relates to previous findings by Fueller et al. (2020).

REPRODUCIBILITY:

It is clearly stated in the discussion that the study "[...] prioritized breadth (multiple loci and conditions) over depth (replicates) [...]", convincingly demonstrating the robustness of the technique to generally improve the tagging efficiency across genes tagged. However, I think that estimating the reproducibility of the improved methodology in tagging genes is important, as the authors are presenting a method that should allow researcher to easily tag genes in mammalian cells. While this does not necessarily mean that the authors should include biological or technical replicates to estimate the robustness of tagging a single gene in this improved method through sequencing, some actions are required to give indications to the reader about expected outcomes and to improve reproducibility by adding the following information: 1. It is expectable that the efficiency of PCR-tagging might vary if different preparations of the PCR products are used. The authors should add technical details in the method section that are currently missing regarding kits and protocols used for PCR, PCR purification/extraction, verification of PCR by sequencing (within the "Generation of plasmids and PCR cassettes"paragraph). This includes kits, polymerase type (Q5? Phusion?), extraction protocols (was the PCR gel-extracted?), sequence verification (was the extracted band sent for sequencing prior to perform PCR-tagging?) and so on. In particular, sequence verification by Sanger sequencing would help understand whether some small nucleotide changes were generated by PCR prior to cell transfection and should be added to the discussion part as source of possible mutations. 2. [OPTIONAL] A significant improvement of the study in terms of reproducibility would be to analyze, via microscopy image analysis (NOT by sequencing), the % of tagging efficiency as suggested above (see point 1 under the microscopy section) for the same gene (i.e. HNRNPA1 or other) with biological replicates consisting of cells transfected with PCR reactions prepared in different days, or [OPTIONAL] even analyzing how the tagging efficiency varies with PCR reactions purified with different kits or protocols (example: gel extraction vs PCR elution). Image analysis should include signal quantification with estimation of the % of tagging efficiency and statistical analysis. These experiment, not particularly demanding in terms of reagents and time (~3 weeks in total due to puromycin selection according to the workflow in Fig2b) would greatly help the reader understanding the robustness of tagging efficiency within single genes. 3. The concentrations of pharmacological inhibitors used (stated in the result section at page 8) should be included in the method section (in the "Transfection" section) and in FigS2, along with details of their use in cell culture. "If NHEJ inhibitors were applied, cell culture media containing small molecules (KU0060648, NU7441, VE-822, M3814) were added after 8 hours of transfection and cells were incubated for 16 hours. Two days after transfection, cells were selected with 500 μg/ml neomycin (Sigma-Aldrich)". Was the drug kept in the medium during neomycin selection? 4. While the authors mention the absence of technical/biological replication within single genes, some graphs are presented with error bars (Fig1F, Fig2d, FigS2b) although no details are given in the text. What replication has been done? What do the error bars represent? What is the sample size? 5. (pages 9-10, Result section): "We quantified the ratio of the HDR band intensity to the total intensity of both bands, defining this as "HDR purity". At the HNRNPA1 locus, we observed that both inhibition of c-NHEJ and synchronization of Cas12a increased HDR purity (Figure 3a)." How were the bands quantified to obtain the reported HDR purity %? Which software was used for band intensity quantification? Similarly, the information about how HDR purity was calculated with the anchor-seq data is lacking. These pieces of information are not present in the Method section and should be added.

Minor comments:

1. A few typos are present throughout the text. Examples: "because the probability of perfect insertion at both ends of the reporter are very low" (page 2); "With this 'mammalian PCR tagging' method constitutes a" (page 3); "In this work we address these gaps and employ selection markers fused in-frame to the tag of choice (e.g. mNeonGreen) using a 2A peptide spacing the two protein domains ensures that" (page 4); "but increased the off-target frequency for TOMM20 by 0.6-fold? (page 9); "from the wide-type and tagged cells" (page 17); "Together, our improvements outline an robust strategy" (abstract). Some other might be present, please check carefully.
2. The Acknowledgement part seems incomplete, and the author contributions are not listed.
3. Can the authors explain the concept/meaning of "index hopping" in the text (page 6)?
4. The FigS2g does not exist (cited at page 8). Did the authors mean f?
5. There is a discrepancy between Figures and labels regarding FigS3 at page 10: "The PS&Btn modifications on PCR cassettes reduced the frequency of concatemeric reads by 0.5- to 1.7-fold for most genes, while no effect was seen for CANX and SLC16A1 (Figure 4c and Figure S3d). As expected, inhibition of NHEJ with KU, NU, or M3814 decreased the concatemeric integration, while treatment with VE or the use of Cas12a-hGEM increased concatemer frequency at specific loci, such as CANX, DDX21, and SLC16A1 (Figure 4d, 4e, and Figure S3e). Inhibition of MMEJ by knocking down Polθ reduced concatemeric integration at the EMD and SLC16A1 loci but not at the LMNA locus (Figure S3e)." FigS3e does not exist, instead S3d seems to contain what S3e was supposed to show.
6. Figure 5b is never cited in the main text, nor elsewhere in the manuscript.
7. In the FigS2c caption, remove the sentence "All PCR cassettes used in this experiment were modified with PS and Btn." since both modified and unmodified PCR cassettes are shown in the panel.
8. The scale bar in the microscopy images (Fig1b, Fig5c) is not clearly visible, please fix the thickness.
9. In Fig5d, some lanes are highlighted in red although no explanation is given in the figure caption or in the text of what red color lanes represent.
10. In FigS1, different graphs of different panels have the same legend, that is placed only within panel f. The same applies for FigS3. It would help readability to state where to find the legend in the figure caption or to rearrange the panels so that the legend appears next to each graph.
11. Throughout the schematics used to exemplify the method workflow or cassette architecture there are several abbreviations that are not expanded in the relative figure caption. Examples: Figure 1a (HA, mNG, NeoR, U6, crRNA), Figure 1b (ONT, BC, Tn5) [...]. While some of them can be evinced in the main text, expanding each abbreviation in the respective figure caption can improve the figure readability.
12. In Fig1e, several symbols are present in the IGV snapshots whose meaning can only be guessed (what are purple vertical lines? What do numbers and letters indicate and what do the color indicate?). This information should be added as legend in the panel or explained in the figure caption. Similarly, it is not clear what the IGV snapshot indicates, it would be useful to add vertical lines in the IGV snapshot indicating, for example, the 5'-HA/3'-HA portion or something else that could help the reader understand what portion of the cassette is indicated.
13. Please specify that FACS was used only for the seamless tagging experiment, as it's unclear in the text. Were sorted cells seeded as one cell per well, or were they collected in one single tube and then separated? Why is Fig5b showing the sorting of mNG fluorescent cells while the result and method only mScarlet-i is mentioned (possibly wrong figure)?
14. In FigS2, panels e-f show the same variable (fraction of HDR reads). For EMD locus, however, there is a possible discrepancy on the fraction shown in e (yellow bar, PS&Btn) and f (grey bar, no treatment, modified oligos). Can the authors explain this apparent discrepancy?
15. Looking at some figures, such as Fig2, it is sometimes hard to relate the results to a "bigger picture". For example, Fig2d depicts "% of HDR integrations", while Fig2f shows "Fraction of HDR reads (%)". Besides possible confusion regarding the name of the variable analyzed, the caption of Fig2f explains that the relative panel contains the data in Fig2d. As Fig2d contains % of HDR-mediated integration of unmodified cassettes ranging 60-85%, one would expect to find the same percentages in Fig2f, under unmodified, control cassette; however, on average the fraction of HDR reads in these samples is only 10-20%. How is this possible? Is Fig2f including unmapped reads or reads mapped to off-target loci?
16. The graph in Fig3d displays Log2FoldChange of indel frequencies. To have a better understanding of the data, it is advisable to show an additional graph with "raw" indel frequencies for each gene, as side-by-side bars (similar to the graph in Fig2c). The same applies for the fold change shown in Fig3g.
17. [SUGGESTION TO IMPROVE CLARITY] Relative to the comments above (15-16), it would be advisable to add one or more graphs that summarize the read composition, similar to what has been done for Fig1f, for all genes analyzed in the different conditions. For example, it would be advisable to add a supplementary figure with one graph per gene analyzed (8 graphs in total) in the form of the one displayed in Fig2f, with stacked bars instead of boxplots as shown in Fig1f. This will help the reader understanding better and compare side-by-side the effect of the treatments applied in read composition for each gene.

Significance

The study provides an advancement in terms of tagging efficiency of genes in mammalian cells with design and protocol optimization of the PCR-tagging technique developed previously by the same lab, which suffered of low tagging efficiency. The study appears to bring a degree of novelty to the community interested in endogenous gene tagging of mammalian genes towards the goal of gaining a high efficiency in mammalian gene tagging, although representing a protocol optimization of a previously developed methodology. In particular, novelty is mainly technical, represented by the use of chemically modified PCR cassette, the introduction of P2A-linked selection marker, and the use of pharmacological inhibitors to suppress undesired repair mechanism in conjunction with improved computational pipeline.

GENERAL ASSESSMENT: The strength of the study is the thorough characterization of PCR-tagging and the step-wise protocol optimization analyzed with great detail at the sequencing level, particularly regarding the classification of possible outcomes. Following identification of the tagging outcomes exemplified in Fig1e, the authors introduce step-wise protocol optimization and characterize, for each integration outcome, if the added variables provide an improvement to the integration quality. Another strength resides in the analysis of multiple gene loci, indicating that the optimized tagging method can be used broadly. The matters described above about microscopy image display and analysis need to be improved, as several conclusions are drawn from such experiments throughout the manuscript. Moreover, a detailed explanation of some procedures central to the manuscript must be implemented, in order to improve reproducibility of the technique described.

ADVANCE: The study represents a technical advace of the previously developed PCR-tagging method. I had no prior knowledge of the PCR-tagging method or other similar methods used to tag endogenous genes in mammalian cells, so my evaluation of the advancement in the field is very limited, as well as whether the cited literature is comprehensive. Nevertheless, I was surprised to see that the Discussion section does not contain any reference (besides Fueller et al. 2020 in the first line), particularly regarding how the optimized method compares with other similar studies (for example Philip et al., 2025 and others cited in the introduction). While the authors do a great job in mentioning the possible limitations of the study and how to further improve the technique, most of the discussion focuses on general aspects of their study, failing (in my opinion) to contextualize the findings in the literature. Here, are only some examples of sentenced that can be contextualized a bit more: - "Likewise, transient suppression of Polθ (MMEJ) produced modest or gene-contingent improvements in our context, in line with emerging evidence that the relative contributions of c-NHEJ, MMEJ, and HDR vary with sequence architecture, chromatin environment, and cell state." - "This resolves a known ambiguity of selection based readouts: a cell can be drug-resistant and fluorescent for reasons other than a perfect on-target HDR event." - "Finally, selection based on a 2A-linked marker improves the fraction of functional fusions but could, in principle, bias against edits that affect translation or protein stability"

AUDIENCE: The study does not investigate the tagging efficiency robustness of single genes. Although this is a clearly stated choice by the authors, it results in being a resource mainly for labs interested in high-throughput gene tagging where the number of genes tagged are maybe more important than focusing on robustly tagging a single gene (the "breadth over depth" matter).

To conclude, I mostly enjoyed reading the work by Lou et al. As an experienced molecular and cell biology researcher currently working in genetic engineering and synthetic biology, I focused my attention in suggesting how to strenghten microscopy analysis and image display to support the author claims and help the reader understanding what changes in signal localization mean, as well as PCR-related methodologies. I also have prior experience in the production and analysis of sequencing libraries (RNA-seq in particular) and could evaluate that the presented analyses are well done and adequately detailed. I don't have sufficient expertise in editing mammalian cells to evaluate possible pit-falls of using pharmacological suppression of repair mechanism.

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-2026-03640

Corresponding author(s): Deborah Walter, Gebhard Schertler

1. Point-by-point description of the revisions

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

Summary: Walter et al. present an interesting series of experiments establishing new optogenetic tools for light regulation of cellular signaling processes downstream of GPCRs. These tools are based on the previously characterised, UV light-sensitive "bistable" jumping spider rhodopsin 1 (JSR1), in some instances carrying the single point mutant S199F (which appears -but I may be wrong here- to also have been characterised previously). Signaling profile analysis of WT JSR1 and JSR1 S199F is followed by the engineering of chimeric GPCRs, an approach commonly termed OptoXRs. With the exception of chimeras constructed around the dopamine receptor 1 the generated OptoXRs were non-functional. The OptoDRD1 receptor however performed well and was further optimised and then applied in multiple cell types.

We are grateful for the appreciation of our study and the constructive criticism, as well as the opportunity to further improve our work by addressing the specific points below. The JSR1 single point mutant S199F has indeed been described the first time by Nagata et al. 2019.

Major comments:

-1-The advantages of using a bistable scaffold for OptoXRs are clear (e.g., less photobleaching and more repeatable activation) but I am not sure that this manuscript actually contains data demonstrating this? My apologies if I am not reading the methods section right but retinal seems to have been added to all assay solutions, which limits interpretation of the presented results in the context of one of the main advantages for the proposed system?

We thank the reviewer for this important point and agree that the original data did not directly demonstrate the advantages of a bistable scaffold. Retinal was indeed present in the assay buffer (original Methods, l. 611-613), which could mask differences between bistable and monostable opsins by continuous chromophore regeneration.

To address this, we performed a long-term repeated-stimulation experiment in which cells were supplemented with 2 µM 9-cis-retinal overnight only, and no retinal was added to the assay buffer. OptoDRD1 was activated with violet light and deactivated with green light six times over 6 h. A single activation maintained elevated cAMP for the full 6 h, whereas repeated 5-min activation periods produced reproducible cAMP spikes. The sixth spike still reached ~73% of the first spike (new Fig. 4f; new text, l. 383–390).

We also directly compared optoDRD1 and the Gs-coupled opsin JellyOp, with and without retinal in the assay buffer (new Fig. S14). Retinal in the buffer did not significantly change the signal amplitude of optoDRD1 peaks [Anova, n = 6, p-adj. between 0.22 and 0.051]. Furthermore, removing retinal from the assay buffer gave a more stable baseline and more complete deactivation, to a level below the pre-activation baseline. JellyOp showed a marked amplitude decrease after the first stimulus without retinal in the assay buffer, which was less present in the conditions with retinal in the assay buffer. All five cAMP peaks of JellyOp without retinal, except the first one, were significantly lower than the cAMP peaks in the conditions with retinal (p-adj. These data support repeatable activation of optoDRD1 independent of continuous retinal supply, and we have revised the Abstract and Discussion accordingly. We note that the signal declines moderately over the six cycles and have phrased our claims accordingly. Cells were still exposed to retinal overnight, as it is required for pigment formation.

-2- In the abstract and elsewhere the authors claim that OptoDRD1c5 kinetics match those of WT DRD1 receptors and indeed the data shown in Fig. 4a and c follow similar time courses. But would we actually expect the kinetics to be similar given that this are two entirely different receptors with entirely different reaction chemistries. Could it be that the time course are simply limited by assay kinetics rather than receptor kinetics? E.g., I have overlayed the Jellyfish opsin off trace of Fig. 5c onto Fig. 5b and the kinetics look very similar, at first glance. So, is it the assay or the receptors that shape time course; asked differently: Wouldn't a good agreement between OptoDRD1 and DRD1 indicate that Gs binding and only Gs binding determines GPCR in activation rates?

We thank the reviewer for this insightful comment and agree that the time courses measured in the GloSensor cAMP assay do not report receptor kinetics alone. The signal integrates several steps: receptor activation, Gs coupling and nucleotide exchange, adenylyl cyclase activity, cAMP degradation by phosphodiesterases (PDEs), and the response time of the biosensor. The similar time courses of optoDRD1 c5, DRD1 and JellyOp deactivation (Fig. 5a-c) therefore likely reflect, at least in part, the rate-limiting properties of the downstream signalling cascade and of the assay components. This is particularly relevant for deactivation: switching off the receptor only stops new Gs activation, whereas the decay of the cAMP signal is set mainly by PDE-mediated degradation1. By deactivating the receptor we only control that no new G protein is stimulating cAMP formation, but not how fast it is degraded. To prevent misinterpretation, we have revised the text to clearly distinguish between receptor kinetics and the downstream signaling effects. We have therefore (i) replaced "signaling kinetics" with "cAMP signaling kinetics" throughout, including the Abstract (l. 15-17) and Discussion (l. 533-535); (ii) added a paragraph to the Results (l. 398-402) explaining that the cAMP assay reports pathway kinetics, not purely receptor kinetics, and a new paragraph (l. 408-423) describing the comparison to JellyOp; (iii) amended the legends of Fig. 5, Fig. S9 and Table S5 to state this limitation.

New text l. 398-402: The cAMP signal integrates several steps: receptor activation, Gs coupling, adenylyl cyclase activity, cAMP degradation by phosphodiesterases (PDEs) and the response time of the biosensor. The apparent kinetics therefore reflect this integrated signal rather than the intrinsic kinetics of receptor activation, which occur on much faster (sub-second to second) timescales50.

New text l. 408-423: JellyOp produced a robust but transient response, rising and then spontaneously decaying with a peak at ~ 11 minutes without reaching a sustained plateau consistent with previous reports that JellyOp does not require a deactivating light stimulus (Fig. 5a). This contrasts with the light-controlled bistability of optoDRD1, which remains in a stable active state until deliberately deactivated by green light. The extracted rate constants for conditions where receptor was only activated once without any deactivation indicate a much faster deactivation rate for JellyOp (0.09 min⁻¹) than for DRD1 (0.001 min⁻¹) and optoDRD1 (0.003 min⁻¹), which both decay very slowly. In the 6h measurement optoDRD1 has a half-life (t1/2) of about 5h (Fig. 4f). The spontaneous decay of JellyOp (0.09 min⁻¹) is in the same order of magnitude to the light-induced deactivation of optoDRD1 (0.05 min⁻¹; Fig. 5c, Table S5). Because both receptors share the same reporter system, this suggests comparable cAMP clearance kinetics once deactivation begins, whether spontaneous (JellyOp) or light-triggered (optoDRD1). Together, these results indicate that the chimeric design of optoDRD1 enables sustained, light-controlled activation similar to DRD1 cAMP responses, when continuously exposed to the agonist. JellyOp may be the preferred choice for applications requiring short pulses of activation without requiring control over the length of the signalling active state.

Minor comments:

-1- The inclusion of alphafold in the design of OptoXRs is exciting, as mentioned below! To me, this is more important than analysis of JSR1 and its apparently already known colour-shifting mutant. It may be in the interest of the authors to think how to best balance these aspects in the revised manuscript.

We thank the reviewer for the positive assessment of our AlphaFold-guided approach. We have reduced the details in the analysis of the colour-shifting mutant and reformatted the first section. We however think it is still important to introduce the JSR1-S199F scaffold and it’s signalling characterization between JSR1-WT and JSR1-S199F in our assay system. We added a sentence on the AlphaFold design approach in the abstract (new l. 7-8) and extended explanations in results and added additional spearman correlation analysis of the extracted AF interface parameters to our signalling data (Fig. 2c, S6b-c, S8). We also added a section to our methods (l. 865-896) and qualified the claim about predicting function in the discussion (l. 616-622).

New text l. 616-622: Consistent with this, AF analysis predicted that optoDRD1 has higher confidence scores at the receptor-G protein interface than the other chimeras. These scores correlated significantly with experimental signalling efficiency when all chimeras described in the manuscript were included (Fig. S6), but not for the initial screening chimeras alone. Given the small number of constructs and the dominance of a few high-signalling complexes, we regard these metrics as a useful tool for guiding GPCR chimera design, checking structural plausibility and prioritizing candidates for experimental validation and not as quantitative predictors of efficacy.

-2- It was interesting to see that JSR1 based receptor respond differently to the various available retinal isoforms (e.g. Figure S4 or S11)? Could the authors speculate what the mechanism for this might be?

We thank the reviewer for this question and have extended the hypothesis of possible mechanisms (Results, l. 334–346). Our data indicate that the isomer-dependent behaviour has at least two components. First, we propose that optoDRD1 preferentially incorporates all-trans-retinal. This is supported by the dark time-courses in Fig. S12b, c-e, in which all-trans-retinal supplementation gives the highest activity over time, and by the decrease of the signal after both 385 nm and 525 nm illumination in cells supplemented with 11- or all-trans-retinal, consistent with deactivation of a pre-existing all-trans-retinal-bound active state. Although 11-cis-retinal was supplemented, it is plausible that all-trans-retinal is formed by spontaneous thermal isomerisation of 11-cis-retinal in aqueous solution at 37°C.

Second, the retinal pocket is allosterically coupled to the G-protein binding region. Recent MD simulations of JSR1-WT with 9-cis-, 11-cis- and all-trans-retinal (Costa et al. 2025) show isomer-dependent interaction networks in the pocket and differences in communication via helix 6 to the intracellular side, which might explain our observations. The chimera-specific differences in Fig. S4 support reciprocal allosteric coupling, where intracellular domains modulate the retinal-binding site. We label these explanations as hypotheses in the text, since we did not test them directly with our own simulations.

-4- Similarly, how might introduction of the S-F substitution alter signaling profiles (p3)?

We thank the reviewer for this question and have added a paragraph to the Discussion (new l. 597–611). We did not perform molecular dynamics simulations ourselves; the paragraph draws on published simulations. These show that Ser199 is part of the hydrogen-bond network linking the protonated retinal Schiff base to the E194 counterion, and that the S199F substitution perturbs this network and the associated interactions with Tyr126 and Tyr293 (Church et al., 2022; Bertalan et al. 2026). Further simulations show that retinal configuration influences communication between this region, Trp290, TM6 and the intracellular transducer-binding surface (Costa et al., 2025; DiPrima et al., 2025). We therefore propose that S199F shifts the conformational equilibrium towards states that couple more efficiently to Gq. JSR1-WT shows only a minor Gq response in the GRK3-BRET assay but a Gi response that is only modestly lower to JSR1-S199F. Because this assay reports Gβγ release, this could reflect either weaker Gq coupling or reduced G protein turnover (for example, stable, slowly dissociating complexes), and the present data cannot distinguish between these possibilities. We have stated explicitly in the text that this is a hypothesis: the simulations did not include G proteins or arrestins and therefore do not establish transducer-specific selectivity. Testing it would require simulations of the receptor-transducer complexes.

-5- Along the same lines, the significant basal activation of the system upon incorporation with all-trans retinal is a concern as this would require green light stimulation of the cells or tissue right after gene delivery, unless of course the specific cell type tolerates Gs signaling: is this the case in the beta-cells - do these or other cells homeostatically adapt to elevanted Galphas?

We thank the reviewer for raising this important point. We agree that reconstitution with all-trans-retinal results in basal Gs activity before light stimulation (Fig. S12) and that this could be problematic when cells are stressed by high Gs activity and light cannot be applied immediately after gene delivery. In EndoC-βH5 cells, overnight incubation with all-trans-retinal increased insulin release without light to a similar extent as light-activated, 9-cis-retinal-reconstituted optoDRD1 (Fig. 6b), and the cells remained responsive during the experiment. We have not measured cAMP, receptor expression or desensitisation in these cells, so we cannot conclude that beta-cells adapt to the elevated Gs activity. β-cells are exposed to sustained Gs signalling through GLP-1R and GIPR and possess cAMP-buffering mechanisms such as phosphodiesterases2. While this may make them more tolerant to sustained activation than other cell types, investigating this was beyond the scope of the current study. Prolonged activity may also lead to receptor desensitisation or loss, which would have to be tested in vivo. We have added this limitation to the Discussion (l. 561-576).

New text l. 561-576: These results confirm that all-trans-retinal supplementation is sufficient to activate optoDRD1. This is beneficial for tissues lacking 11-cis-retinal, but it comes at a cost: all-trans-retinal reconstitution produces a receptor population with basal Gs activity before any light stimulation (Fig. S12). This activity can be reduced by a brief green-light pre-illumination that returns the receptor to its inactive ground state, or by reconstituting with 9-cis-retinal. Prolonged high Gs activity might induce stress responses in some cells65,66, other cells might be able to adapt or even benefit from it67,68. In EndoC-βH5 cells, overnight incubation with all-trans-retinal increased insulin release to a similar extent as light-activated 9-cis-retinal-reconstituted optoDRD1 (Fig. 6b), indicating that these cells remained responsive after prolonged exposure to all-trans-retinal. However, we did not measure intracellular cAMP or receptor surface levels in these cells, and we cannot exclude adaptation, desensitisation or altered expression. Two points need to be tested for each new cell type or tissue. First, it must be determined whether endogenous retinal is sufficient to reconstitute optoDRD1 or whether it must be supplemented. Second, it must be determined whether optoDRD1 raises Gs activity in the dark and whether cells tolerate this. If basal activity is a problem, it can be reduced by using 9-cis-retinal or green-light illumination. However, optoDRD1 may still be unsuitable for applications that require a very low dark-state signal.

-6- There are a few sentences and figures here and there that could need a polish... e.g. "Activation of GPCRs typically results in the activation of 33 heterotrimeric G proteins" or the axis scales of Fig 4c vs e. I am not sure what the purpose of Figure 1c is as more functional data follows.

The sentence (original l. 32-33) is written as “Activation of GPCRs typically results in the activation of heterotrimeric G proteins” “33” might have slipped in as the line numbering, we could not identify any other issues. The axis scale was updated to be the same between original Fig. 4c-f (new Fig 4a-d). Original Fig. 1c depicts the BRET assay data of JSR1-S199F, which is our starting construct. We additionally added the G protein selectivity of JSR1-S199F compared to JSR1-WT to the main figure (new Fig. 1a). We moved original Fig 1c to new Fig. 1b. This figure was chosen to demonstrate that the starting construct is a bistable photoswitchable receptor that activates Gq and Gi and can be deactivated in cells. Although, this mutant has been characterized before in (Nagata et al. 2019, Hagio et al. 2023)3,4. To our knowledge it was previously not characterized for both Gi and Gq activity and no cell assay was reported that showed activation and deactivation in cells.

Reviewer #1 (Significance (Required)):

This is robust work that will significantly expand the growing repertoire of specialised optogenetic tools for light control of GPCR associated pathways. The main advance is the use of the bistable JSR1 scaffold and coupling it to GalphaS. At the same, for me the most exciting element of this work was the alphafold modeling as this represents a significant step forward from pervious structure-based approaches! In particular the use of alphafold to rationalise and select chimeras is highly innovative.

We thank the reviewer for this encouraging assessment. In response, we have given the AlphaFold-guided design more prominence in the revised manuscript. We additionally included a spearman correlation analysis with the signalling data. At the same time, we want to be clear about what the approach can and cannot do. Given the small number of constructs and the dominance of a few high-signalling complexes, we regard these metrics as a useful tool for guiding GPCR chimera design, checking structural plausibility and prioritizing candidates for experimental validation and not as quantitative predictors of signalling efficacy.

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

The paper "Photoswitchable optoGPCRs for Reversible Control of Gs and Arrestin Signalling," by Deborah Walter, Richard McDowell, Polina Isaikina, Andreea Pantiru, Hiruttika Ravimohan, Xavier Deupi, Robert J. Lucas, and Gebhard F. X. Schertler, presents a comprehensive characterization of a chimeric optoGPCR engineered from a mutated bistable visual pigment. The construct's spectral properties allow it to be reversibly switched on and off with light, enabling controlled activation of Gs signaling pathways. The starting visual pigment used in this study was a mutant of jumping spider rhodopsin 1 (JSR1) carrying the S199F mutation, which shifts the dark-state λmax from 535 nm to 380 nm., The λmax of the light-activated pigment remains 535 nm in both the wild-type and mutant pigments. This large separation between the dark- and light-activated λmax values allows researchers to reversibly activate and inactivate the optoGPCR at will. Unmodified JSR1 activates Gq and Gi G proteins, whereas many of the signaling pathways researchers wish to study are Gs-mediated. Using structural knowledge together with AlphaFold-based modeling, the researchers designed, constructed, and tested an optoGPCR construct capable of activating Gs pathways.

This is a comprehensive study, comprising 5 main figures, 13 supplemental figures, and 6 tables.

We thank Reviewer 2 for supporting our manuscript and for providing constructive and critical feedback, which has helped us improve clarity and convey a stronger message.

Many of the paper's claims are well supported by experimental data; however, a few statements lack direct experimental evidence. In the first paragraph of the Results section, the authors claim that JSR1 reconstituted with 9-cis-retinal is blue-shifted relative to the pigment reconstituted with 11-cis-retinal. The researchers could easily have shown this spectrum, even if they ultimately chose to use 9-cis-retinal for the remainder of the experiments. They also claim that the photo reversed chromophore is 11-cis-retinal; this claim could be verified experimentally through chromophore extraction and HPLC analysis.

We thank Reviewer 2 for this comment. We agree that both statements should be supported by experimental evidence, and we have the corresponding data for JSR1-S199F: (i) UV-vis spectra of the 11-cis- and 9-cis-retinal-reconstituted pigments, and (ii) hydroxylamine extraction and HPLC analysis of the chromophore of the 9-cis-reconstituted pigment in the dark, after activation and after photoreversal, following the procedure described in Ehrenberg et al. (2019). We show these data in Response Figure R1 below. The 9-cis pigment is blue-shifted relative to the 11-cis pigment (λmax 365 nm vs. 385 nm), and after photoreversal the main retinal isomer is 11-cis-retinal (58%). These results agree with Nagata et al. (2019), who reported both the UV-vis spectrum of 11-cis-reconstituted JSR1-S199F and the retinal extraction analysis of 11-cis-reconstituted JSR1-S199F. Varma et al. (2019) and Ehrenberg et al. (2019), both report on the photochemistry of JSR1-WT reconstituted with 9-cis-retinal, which also blue-shift the λmax (505 nm) compared to the 11-cis retinal (535 nm). Because these measurements belong to a more detailed spectroscopic and photochemical characterization of the JSR1 variants that we are preparing as a separate manuscript, we prefer not to include them in the present paper, which focuses on the engineering and cellular characterization of optoDRD1. Following a comment of Reviewer 1, we also removed some details on the photochemical properties (original l.87-98), since they are not essential for the application of the tool. To make sure that no claim in the manuscript depends on unpublished data, we reworded the statement on the photoreversed chromophore (new l. 105-110) and added the references to Nagata et al. (2019), Ehrenberg et al. (2019) and Varma et al. (2019) at l. 110.

The experiments depicted in Figure 5d and 5e are misleading and inconsistent with the data shown in Figure 5f and 5g. The BRET experiments directly test G protein activation and demonstrate the utility of the engineered construct, whereas the experiments in 5d and 5e rely on cAMP measurements and do not demonstrate the selectivity of the optoGPCR.

We appreciate the critical comment on the Gsx assay and agree that it does not provide an absolute measure of G protein selectivity but reports the comparative preference of the Gα C-terminus within a Gs backbone. We have therefore restructured the Results (l. 442-460) so that the BRET assay with native heterotrimeric G proteins (Fig. 5d-e) is presented first as the primary test of selectivity. The Gsx assay (Fig. 5f-g) now follows as a complementary readout, and we state its limitation explicitly. We also removed the claim that the Gsx assay "confirms" selectivity, so that the conclusion rests on the BRET data. We revised the Figure 5 legend and panel order accordingly. We further discuss that the partial responses of non-Gs chimeras may reflect additional receptor-Gα core contacts, based on an analysis of the 27 available DRD1-Gs structures (Table S6).

Reviewer #2 (Significance (Required)):

This is a significant study describing the engineering of a highly useful optogenetic tool for activating Gs pathways. Its utility is illustrated here in Neuro-2a cells, validating its usefulness in tissue culture systems. It will be interesting to see this tool validated in an in vivo animal model.

We are very grateful for support of our manuscript and the considerate comments. We agree that the next step should be in-vivo validation and we have started collaborations in that direction.

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

__Summary __ This manuscript presents optoDRD1, a bistable optoGPCR generated by combining the photoswitchable JSR1-S199F scaffold with intracellular regions of the human dopamine D1 receptor. The authors combine UV-visible spectroscopy, cAMP and Ca2+ assays, BRET-based G-protein measurements, an indirect arrestin recruitment assay, AlphaFold-guided chimera design, and experiments in HEK293T, Neuro-2a, and human EndoC-betaH5 cells.

The study provides a technically strong and potentially valuable Gs-coupled optogenetic tool that can be activated with violet light and deactivated with green light. The systematic chimera series, broad G-protein profiling, and testing in physiologically relevant cell models are important strengths. The data support the central conclusion that the JSR1-S199F scaffold can be redirected toward light-dependent Gs/cAMP activation while retaining bidirectional optical control.

The manuscript would nevertheless benefit from more rigorous and consistent reporting of biological replication, a matched comparison with JellyOp, clearer justification of the selected lead construct and the AlphaFold-guided design claims, and more cautious interpretation of arrestin, retinal, kinetic, and in vivo applicability claims.

We thank the Reviewer for the thorough and analytical inspection of our manuscript. The comments helped us refine important details in the text and figures and improve our statistical reporting.

Major comment

1. Clarify biological replication and perform kinetic analyses across independent experiments

Several central time-resolved experiments are presented as representative datasets with technical replicates, including __Figs. 1c, 3b-d, 5a-c and 5f, and 6c. __In addition, Tables S5 and S6 report fitted rate constants with confidence intervals and R2 values, but it is not clear whether these parameters were obtained from one averaged trace, one representative experiment, or independently from multiple biological experiments. Fit confidence intervals quantify uncertainty within a fitted trace; they do not substitute for variability across biological replicates.

For the main kinetic comparisons, the authors should fit each independent biological experiment separately and report the distribution of the resulting parameters. At minimum, this should include peak response or response amplitude, apparent activation and deactivation rate constants, residual signal after green-light deactivation, and the magnitude of reactivation. Individual biological data points should be displayed, and at least three independent experiments should be used for central claims. The n = 2 datasets, particularly Fig. 3b and Fig. 6c, are not sufficient for quantitative conclusions.

The text should also distinguish the kinetics of the measured cAMP reporter response from intrinsic receptor conformational or G-protein activation kinetics. The minute-scale rate constants in Tables S5 and S6 reflect the integrated receptor/G-protein/adenylyl-cyclase/cAMP/reporter system and should be described as apparent cAMP-response kinetics. Please compare this slow response kinetics with the very fast responses of Gs coupled receptors in vivo including JellyOp.

We thank the reviewer for this important point and agree that fit confidence intervals do not substitute for biological variability. We have made the following changes:

1. Replicate-level fitting. For time resolved cAMP assay data each independent biological experiment (n = 3-7 per construct) was fitted separately. The new Table S5, contains for every construct and experiment, basal activity, raw response amplitude, residual signal after green-light deactivation, the magnitude of reactivation, and apparent activation and deactivation rate constants, together with mean ± SEM of biological replicates. Additionally, Fig. S9 shows a matched comparison between the DRD1 chimeras with individual biological replicates far all the parameters mentioned before. Individual data points are now shown in Figs. 3b-d, 5d, 6b, 6c, S9 and S10c, and exact p-values are added (Fig. 6b) and mentioned in the text; a complete list can be found in the summary data file and supplementary excel sheets (parameters_stats.xlsx) on Zenodo: 5281/zenodo.24013508.
2. Number of experiments. The Fig. 6c Neuro-2a dataset now comprises three independent biological experiments (previously n = 2). We decided to keep Fig. 3e-g as a representative dataset with the raw measurement data as illustrative panels, but all quantitative claims are based on the detailed replicate-level analysis of at least n = 3 biological replicates in Fig. 3b-d, S9 and Table S5.
3. Apparent kinetics. We now describe all rate constants as apparent cAMP-response kinetics and specifically mention that the cAMP signal integrates several steps in the signalling cascade, and state that intrinsic receptor conformational and G protein-activation steps occur on much faster timescales (l.398-402).
4. Comparison with JellyOp. JellyOp shows a transient response with spontaneous decay, whereas optoDRD1 shows a sustained, light-controlled plateau that is terminated by green light. We compared the decay phase and found faster spontaneous deactivation rate for JellyOp (0.09 min⁻¹) than for optoDRD1 (0.003 min⁻¹). The spontaneous decay of JellyOp (0.09 min⁻¹) is in a similar range to the light-induced deactivation rate constant of optoDRD1 (0.05 min⁻¹), which might be an indication that this phase is dominated by shared downstream components of the reporter system.

   1. Ensure that the comparison with JellyOp is performed under matched conditions The comparison with JellyOp is central to the claims that optoDRD1 has a larger response, more sustained signalling, and superior reversibility. However, the presentation of the assay conditions is not fully consistent. In particular, Fig. S5 states that forskolin was added to the 9-cis-retinal conditions except JellyOp, whereas the Methods state that forskolin was used when measuring Gi-mediated inhibition. Forskolin changes basal cAMP, reporter dynamic range, and potentially the apparent amplitude and decay of the response.

A focused head-to-head comparison of optoDRD1 and JellyOp should therefore be performed or re-presented using identical cell type and batch, retinal condition, receptor DNA amount, reporter amount, illumination wavelength-specific photon exposure, forskolin treatment (ideally none), timing, and normalization. Raw baselines and expression or surface-expression controls should be shown. The analysis should distinguish absolute response amplitude, fold induction over baseline, area under the curve or persistence, spontaneous decay, and the ability to undergo repeated switching. Until such a matched comparison is provided, statements that optoDRD1 produces a higher-amplitude response than JellyOp should be qualified.

We thank the Reviewer for this important point and agree that the comparison needs to be performed under matched conditions. There was already a matched comparison in Fig. 5a, but to further compare optoDRD1 to JellyOp we added a new long-term experiment that measured activity over 6 h.

1. Matched experiments. optoDRD1 and JellyOp were transfected from the same cell batch, plated side by side on the same 96-well plate and measured with identical retinal (2 µM 9-cis-retinal), 250 ng receptor and 250 ng GloSensor plasmid per well, no forskolin, one 1 s light pulse of equal photon exposure, and identical normalization to highest value of the 96-well plate (Fig. 4f and S14; l. 347-354). Raw luminescence traces of matched experiments and same plate measurements are also shown in Fig. 5a.
2. Forskolin was used only for the initial screening of Gs optoGPCRs to observe any potential Gi induced decreases of cAMP (Fig. 2b, S5). We now state this explicitly and no longer base any comparison with JellyOp on forskolin-treated cells. All other comparison of JellyOp and optoDRD1 do not contain forskolin (Fig. 4f, 5a, S14).
3. Fig. S14a displays persistence over repeated stimulations for the long-term measurement. Table S5 displays absolute amplitude, fold induction over baseline, and induced decay for optoDRD1 as well as spontaneous decay for JellyOp and optoDRD1, as mean ± SEM of n = 3 independent experiments.
4. We have qualified the statement on amplitude (lines 211–214): the ~30% higher amplitude is now explicitly described as a screening result obtained with forskolin for the chimeras but not for JellyOp, and we refer to the matched comparison (Fig. 4f, 5a, S14), in which both receptors reach a similar amplitude. We have removed the statement that it yields a higher amplitude (Abstract/Discussion). We now emphasise that optoDRD1 differs in sustained, light-terminable signalling and in repeated switching (l. 403-423, Fig. S14). We have revised the Discussion (l. 526-528) to present JellyOp more neutrally, highlighting its fast, repeatable activation and its intrinsic spontaneous deactivation, which may be advantageous for pulse-like Gs signalling. We describe optoDRD1 as complementary to JellyOp, with sustained, light-terminable signalling.
5. We acknowledge that surface expression could not be matched between optoDRD1 and JellyOp. We now state this limitation explicitly where the matched comparison is presented (Results, lines 405-407) and discuss it in the Discussion (new l. 541-544). We also note that our main conclusions concern signal persistence, light-dependent termination and repeated switching, which do not depend on absolute expression level.

   1. Justify the selection of c5 as the lead construct and explain the relevant trade-offs The c1-c5 series is informative, and c5 produces the largest absolute cAMP response in Fig. 3e. However, Fig. S8a indicates that c4 and c5 have similar fold induction, Table S5 indicates somewhat faster apparent deactivation for c4, and Fig. 3f-g shows elevated basal arrestin association for c5. Thus, c5 appears optimal for absolute signal amplitude, but not necessarily for dynamic range, basal activity, or temporal shut-off.

Please provide a concise side-by-side comparison of c4 and c5 using matched biological replicates. This comparison should include basal cAMP, absolute amplitude, fold induction, activation and deactivation, residual signal after deactivation, repeated switching, basal and light-induced arrestin recruitment, and receptor expression or surface abundance. The apparent difference between the large c5 advantage in Fig. 3e and the similar fold induction in Fig. S8a should be explained explicitly. The authors do not necessarily need to change the selected lead construct, but "optimal" should be defined according to the property being optimized. The trade-off between high absolute output and higher basal activity should be transparent.

We thank the reviewer for this helpful comment. We agree that c5 was selected on the basis of its highest absolute light-induced cAMP amplitude, which approaches that of ligand-activated DRD1-WT, and not because it is superior in every parameter. We retained c5 as the lead construct and have revised the text accordingly:

1. The term "optimal" has been removed and the selection criterion is now stated explicitly (l. 11).
2. We now explain the apparent discrepancy between Fig. 3e and Fig. S8a. c5 yields ~2-fold higher absolute amplitude than c4, but both show ~30-fold induction over their respective baselines, because c5 also has a higher baseline (l. 256-259; Fig. S9 and Table S5).
3. We have added a side-by-side comparison of all JSR1-S199F-DRD1 chimeras c1-c5 (Fig. S9 and Table S5), listing basal cAMP, absolute amplitude, fold induction, apparent activation and deactivation rate constants, residual signal 30 min. after green light deactivation, and response to repeated stimulation (Fig. S9).
4. We now state the trade-offs explicitly: c5 offers the highest absolute output but has higher basal activity, higher basal arrestin association and slightly slower apparent deactivation (k2050 vs 0.054 min⁻¹; Table S5). c4 may be preferable where low basal activity, faster shut-off or dynamic range is the priority (l. 322-323).
5. We note that basal activity of optoDRD1 depends on the retinal concentration in the assay buffer and incubation with retinal in the assay buffer leads to a rising baseline over time (Fig. S14c).
6. Surface abundance was not quantified separately. Total expression was comparable across variants (Fig. S10; c5 lowest), and we now mention the lack of surface quantification as a limitation (l. 256-257).

   1. Clarify the AlphaFold-guided design logic and the novelty relative to earlier Gs chimeras The manuscript presents the design as structure-guided, but the connection between the interface analysis in Fig. S2 and the selected grafts is not yet sufficiently clear. In particular, Fig. S2 maps receptor-Gs contacts, whereas the design replaces ICL2, ICL3, adjacent parts of TM5 and TM6, helix 8, and the C-terminus. The rationale for extending the grafts into transmembrane segments and for including the C-terminus, which is generally unresolved in the structural interface dataset, should be explained explicitly in the main text and in an expanded Fig. S2 legend (especially legend to S2b is insufficient). The meanings and limitations of pLDDT, PAE, contact probability, and ipTM should be explained at first use, together with any thresholds or decision rules used to select constructs. Fig. 2c shows only the JSR1-DRD1-miniGs model. The supplementary tables contain data for the other designs, but the manuscript would be strengthened by a quantitative analysis of whether the structural confidence metrics predict functional cAMP output. A scatter plot and an appropriate rank correlation across the initial receptor chimeras and, separately, across c1-c5 would be informative. If the relationship is weak outside the c1-c5 series, the predictive claim should be qualified and the models presented primarily as evidence of structural plausibility rather than as functional predictors.

The manuscript also notes that the JellyOp ICL3 had previously been used to generate Gs-coupled chimeras with bistable opsins. Please explain more clearly what limited those earlier constructs and define the specific advance here. The strongest novelty appears to be the combination of the JSR1-S199F spectral switch, systematic multi-domain optimization, robust Gs output, and repeatable bidirectional control, rather than Gs redirection by an intracellular-loop swap alone.

We thank the reviewer for these constructive suggestions. We have revised the manuscript as follows:

1. Design logic. We now explain in the main text (l. 157-159) how the GPCRdb interface map (Fig. S2) supported the selection of grafting positions, why the grafts extend into the cytoplasmic ends of TM5 and TM6, and why the flexible part of the C-terminus was included although it is unresolved in the structures (l. 151-157). The Fig. S2 legend has been expanded; S2b now specifies the residues shown, their source and the meaning of the colour scheme and consensus table.
2. AF metrics. pLDDT, PAE, contact probability and ipTM are now defined at first use (l. 189-202), including the contact threshold and the selection criteria.
3. Predictive value. We analysed whether interface confidence parameters extracted from AF predict cAMP output (new Fig. 2c). For the initial screening chimeras, the signalling data did not significantly correlate to the AF predicted complexes with spearman correlation (n = 7). The analysis for c1-c5 chimeras and DRD1 (n = 6) yielded significant spearman correlations for average receptor PAE, contact probability, pLDDT at the interface and ipTM. AF3 interface confidence ranked the c1-c5 designs in the same order as their measured cAMP output, and including all receptor chimeras it correlated with signalling (Fig. S6b-c), whereas global pTM and the number of contacts did not. Given the small number of constructs and the dominance of a few high-signalling complexes, we regard these metrics as a useful filter for structural plausibility and not as quantitative predictors of efficacy. We have therefore qualified the claim in the Discussion (original l. 479-483, new l. 599-605) and present the AF models primarily as evidence of structural plausibility.
4. We now state more clearly what limited earlier JellyOp-ICL3 chimeras and define the advance of optoDRD1 as the combination of the JSR1-S199F spectral switch, multi-domain optimisation, robust Gs output and repeatable bidirectional control. New text (l. 628-634):Earlier chimeras carrying the JellyOp ICL3 established Gs coupling in bistable opsins and were mainly used to study opsin light sensitivities via a cAMP assay, but they gave modest responses and did not combine sustained Gs output with repeatable switching35. The advance of optoDRD1 is therefore not the redirection to Gs by an intracellular loop swap alone, but the combination of the JSR1-S199F spectral switch, systematic multi-domain optimisation, robust and prolonged Gs output, and repeatable bidirectional light control (Fig. 5, S14).

1. Refine the interpretation of arrestin recruitment and retinal-dependent activity The assay used here measures split-luciferase complementation between a membrane-anchored fragment and arrestin-tagged fragment. It therefore reports membrane-proximal arrestin recruitment indirectly; it does not establish direct receptor-arrestin binding or arrestin-dependent downstream signalling. The title and text should use "arrestin recruitment" rather than "arrestin signalling" unless a downstream functional endpoint is added. Likewise, replacing ICL3 may abolish assay-detectable recruitment, but this alone does not prove that ICL3 is the dominant physical arrestin-binding interface, because the substitution may also alter receptor conformation, phosphorylation, or membrane abundance.

There are two acceptable ways to resolve this issue. The most direct is to revise the title and claims throughout and limit the conclusions to reversible arrestin recruitment. Alternatively, if "arrestin signalling" is retained as a central claim, the authors should add two major arrestin-dependent functional readouts, such as receptor internalization or ERK phosphorylation, ideally with a control that establishes arrestin dependence.

The proposed preferential incorporation of all-trans-retinal is plausible but remains indirect. The data demonstrate retinal-isomer-dependent basal activity and light responses, but do not directly establish the bound retinal species. The binding mechanism and suggested in vivo advantage should therefore be framed as hypotheses. The substantial basal activity observed with 11-cis- and all-trans-retinal should also be discussed as a potential limitation for applications that require a low dark-state signal. Estimated effort: textual qualification is immediate; retaining a downstream "arrestin signalling" claim would likely require approximately 3-6 weeks for a focused functional assay.

We thank the reviewer for these helpful points and chose the first option, restricting the claims to reversible arrestin recruitment. Moreover, we state explicitly that the split-luciferase assay reports membrane-proximal recruitment indirectly (Results: l. 294-298; Fig. 3 legend). In the discussion of arrestin recruitment, we explicitly acknowledge that the absence of a detectable agonist-induced signal does not exclude low-level or transient arrestin engagement (l. 550-552).

New text results l. 294-298: Since arrestins play a crucial role in GPCR desensitization, internalization and the initiation of arrestin-mediated signalling cascades, we assessed the recruitment of arrestin 2 and arrestin 3 to the cell membrane upon activation of JSR1, JSR1-S199F, the JSR1-DRD1-chimera variants c1-c5 and DRD1. JSR1 indirectly recruits both arrestin 2 and arrestin 3 to the membrane upon light activation (Fig. 3c-d).

New text discussion l. 550-552: Since our arrestin readout is an indirect assay, we cannot exclude low level or transient recruitment, and the absence of a detectable signal should not be interpreted as an absence of arrestin engagement.

We no longer claim that ICL3 is the dominant arrestin-binding interface but also provide other hypothesis as possible explanations.

New text results l. 302-307: Replacing the C-terminus alone (c1) reduces arrestin 2 recruitment while minimally affecting arrestin 3, suggesting isoform-selective interactions at the C-terminus. Replacing ICL3 (c2) almost completely abolished arrestin recruitment of both arrestin isoforms (Fig. S11b). This may indicate that ICL3 is either the dominant arrestin recruitment site of JSR1 or induces conformational changes, phosphorylation, or altered membrane abundance that could affect arrestin recruitment.

New text discussion l. 580-588: Analysis of the chimeras showed that ICL3 of JSR1 is required for arrestin 3 recruitment, whereas replacing the C-terminus had only a minimal effect. This could mean that ICL3, rather than the C-terminus, is the primary arrestin-interacting site in JSR1, or that the DRD1 C-terminus can compensate for the JSR1 C-terminus because it serves a similar function. Within the flexible ICL3, a sequence motif (SxxSxED) containing two serines, a glutamate and an aspartate may contribute to the high arrestin recruitment, since arrestin-binding interfaces are typically enriched in negative charges, such as those provided by phosphoserines. However, replacing ICL3 could also alter receptor conformation, phosphorylation or membrane abundance, any of which could affect arrestin recruitment independently of this motif.

The preferential incorporation of all-trans-retinal and any in vivo advantage are now presented as hypotheses, since the data show isomer-dependent basal activity and light responses but do not identify the bound chromophore. Additionally, we added the substantial basal activity with 11-cis- and all-trans-retinal as a limitation for applications requiring a low dark-state signal (l. 561-576).

In addition, we have recently purified optoDRD1 and reconstituted the cell pellet before solubilization with all-trans-retinal. We could obtain a UV-vis spectra of purified optoDRD1 and get absorbance at 535 nm, which is characteristic for the active all-trans-retinal state. This is for us a further hint that all-trans-retinal can be taken up directly by optoDRD1. We will further follow up on this characterization, and it will become part of another manuscript.

1. Temper the physiological and in vivo applicability claims

Photon flux, total photon exposure, pulse duration, and optical power density should be reported consistently and distinguished throughout. The underlying data points should be shown for the fitted action spectra in Fig. 4a.

The EndoC-betaH5 and Neuro-2a experiments are useful proof-of-principle demonstrations, but they do not yet establish reversible physiological control or in vivo readiness. For the beta-cell experiment, "biological replicate" should be defined clearly, particularly because the Methods indicate that the procedure was repeated one week later. Individual values should be shown. Green-light treatment did not reverse the insulin-secretion phenotype, so the conclusion should be restricted to light-triggered potentiation of insulin secretion under the tested conditions. Also provide data for violet light with ATR and green with 9-cis or better explain the rationale of selection in Fig 6b. The Neuro-2a experiment is presented as a representative n = 2 dataset and should be repeated in at least three independent experiments. The Fig. 6c legend should identify the cAMP assay used. More generally, claims of in vivo applicability should remain prospective because the activation wavelength, potential phototoxicity and tissue penetration, retinal-dependent basal activity, and cell-type-dependent retinal behaviour have not been tested in vivo.

We thank the reviewer and have limited the conclusions of Fig. 6 to proof-of-principle in cell lines and qualified in vivo applicability claims. Specifically, we revised the text and the figures as follows:

1. Light dosimetry. Optical power density, photon flux, pulse duration and total photon exposure are now reported for every condition and in the Methods (l. 733-744) and figure legends.
2. __ 4.__ We have updated the figure legend to explain that the data points underlying the action spectra are shown in Fig. 4a-d, and the fitted spectra are in Fig. 4e.
3. EndoC-βH5. We now display wells remeasured a week later in Fig. 6b in a different color and describe it in the figure legend and in the methods (l. 819-832). Individual values and exact p-values are now shown (Fig. 6b). We limited the conclusion to light-triggered potentiation of insulin secretion under the tested conditions, as green light did not reverse the phenotype.
4. Choice of conditions in Fig. 6b. We did not include violet light stimulation with all-trans-retinal incubated cells or green light with 9-cis-retinal incubated cells. From our experiments in HEK293T cells we experienced that violet light (activation stimulus) does not further increase cAMP activity of all-trans-retinal supplemented optoDRD1 and the use of green light (deactivation) is more effective to deactivate the receptor and decrease cAMP levels. Therefore, we choose to use green light for deactivating all-trans-retinal incubated conditions assuming they will be mainly in an active state. On the other hand, we used violet light (activation) to stimulate 9-cis-retinal incubated cells, since in HEK293T cells violet light leads to activation of the receptor and an increase in cAMP, while green light has a minimal effect on a receptor that is already mainly in the inactive state. The 24 h starvation before glucose stimulation prevents sequential activation, and deactivation with collection of released insulin after each step. We therefore chose to start from the active state by adding all-trans-retinal, and we explain this rationale in the text. New text (l. 471-475): Since the experimental conditions did not allow to extract released insulin from the same well for activation and deactivation, we started from an active receptor by supplementing all-trans-retinal and to observe the effect of deactivation with green light.

Neuro-2a. 6c now shows replicates from 3 independent experiments, with individual traces normalised to the percent of the maximum response. The analysis of all biological replicates can be found in Table S5. The legend names the GloSensor cAMP assay. In vivo claims. These are now prospective, and a limitations paragraph (l. 557-565) lists what must be tested in vivo: activation wavelength, phototoxicity and tissue penetration, retinal-dependent basal activity, and cell-type-dependent retinal behaviour.

New text (l. 519-524): The shorter wavelengths required for optoDRD1 activation penetrate tissue less effectively than red light and may carry greater phototoxicity risks, representing a practical limitation for deep-tissue applications. Recent advances in two-photon activation have demonstrated that deep tissue stimulation of UV-sensitive opsins is feasible6,59. OptoDRD1 may therefore be suitable for two-photon activation, offering deeper tissue penetration and single-cell spatial resolution within living organisms60.

(l. 571-576) Two points need to be tested for each new cell type or tissue. First, it must be determined whether endogenous retinal is sufficient to reconstitute optoDRD1 or whether it must be supplemented. Second, it must be determined whether optoDRD1 raises Gs activity in the dark and whether cells tolerate this. If basal activity is a problem, it can be reduced by using 9-cis-retinal or green-light illumination. However, optoDRD1 may still be unsuitable for applications that require a low dark-state signal.

Minor comment

1. Use "arrestin recruitment" consistently in the title, Abstract, Results, Discussion, and figure legends unless a downstream arrestin-dependent response is measured.

We agree with this comment and revised the manuscript, referring to it as “arrestin recruitment”.

1. In the Abstract, qualify "precise signal termination" to distinguish receptor photodeactivation from the slower decay of downstream cAMP and physiological outputs.

We thank the reviewer and agree. 'Precise signal termination' could imply immediate cessation of all downstream signalling and we have adapted the sentence to specify that the receptor is deactivated. The Abstract (l. 14-15) now reads: '…, while green light rapidly deactivates the receptor at any chosen timepoint'.

1. For Fig. 1c and Fig. S1e-f, show individual biological data points and statistical comparisons. Please move the quantified G-protein selectivity summary (Fig S1E) into the main figure (to Fig. 1c) so that the representative trace is supported directly.

Fig S1e was moved to Fig. 1a and individual biological data points and statistical comparison of the rate constants was added to Fig. S1. Additionally, all parameters for the individually fitted curves to each replicate were added in the summary_data.xlsx.

1. State the number of independent protein preparations used for the UV-visible spectra and quantify the fraction of incomplete photoconversion in Fig. 1b, or describe it explicitly as a limitation.

In the new Fig. 1c, the spectra from a single purification were plotted. To address the raised concern, we now show values from three purifications in supplementary Fig. S1f. We additionally quantified the absorbance at 365 nm and 535 nm for each purification and illumination, which can be found in the summary excel table (given as percentage to the absorbance at 365 nm before illumination). There is some variability in the chromophore peak (365 nm) after retinal reconstitution, which is dependent on protein purity (if the sample is not fully pure, other proteins or receptors without a retinal can contribute to the 280 nm signal). Differences in the light activated UV-vis spectra, are coming from the use of different illumination systems. The first time the optowell was used for 60s at 368 nm and 519 nm (0.5pt), the 2nd time we illuminated 5s (1pt, dotted) with the coolLED (385 nm and 525 nm), the third time 10s activation and 100s deactivation (2p) with the coolLED (385 nm and 525 nm). Overall, we observed a very small remaining absorbance at 535 nm (

1. Fig. S3 demonstrates receptor immunoreactivity and cellular localization, but permeabilized-cell staining does not quantitatively establish plasma-membrane trafficking. Please revise the wording or add a surface-expression assay for the lead constructs.

We thank the reviewer for bringing this important point to our attention. We agree that immunocytochemistry performed on permeabilized cells (Fig. S3) cannot distinguish total receptor expression from plasma-membrane-resident receptor. We have revised the text (Results, line l. 204–206 to reflect this limitation accurately.

Revised text: Immunocytochemistry assays in HEK293T cells confirmed that all chimeric proteins were expressed (Fig. S3). As these assays were performed on permeabilized cells, they report on total cellular immunoreactivity and localization pattern rather than quantitative plasma-membrane trafficking.

1. For Fig. S9, explain the multiple Western blot bands, indicate the expected molecular mass, describe the band(s) included in quantification, show the normalization or loading control, and display the individual values from the three experiments.

We appreciate the reviewer’s careful reading of our manuscript. The updated legend of Fig. S9 (now S10) explains the multiple bands (monomeric receptors at 35-50 kDa, with size differences due to the length of ICL3 and the DRD1 C-terminus; bands at about 75-100 kDa likely represent glycosylated or palmitoylated receptors or dimers,) and states that all bands were included in the quantification. We now also plot the individual values of the three independent experiments in Fig. S10c.

1. Fig. S4 appears to refer to curves in Fig. S6, although the corresponding cAMP traces are in Fig. S5. Please correct the cross-reference.

We corrected the cross-reference. The legend of Fig. S4 now refers to Fig. S5 (cAMP traces).

1. Table S6 refers to curves in Fig. 4a-c, whereas the relevant kinetic curves are in Fig. 5a-c. Please correct this reference. Overall perform a careful reading before submission as a respect to the reviewer.

We corrected the reference in the legend of Table S5, which now refers to Fig. 5a-c and Fig. 6c.

1. For Fig. S13, explain more quantitatively how the violet-light aequorin artifact in sensor-only cells was distinguished from a receptor-dependent Ca2+ response. The n = 2 dataset should be strengthened or the conclusion qualified.

Thanks for the comment. We have increased the replicates to n = 4 and quantified the distinction in the figure legend (new S15).

Part of the figure legend: At high intensities, a transient increase in luminescence was observed in a single measurement point (2+ response, which is defined as luminescence remaining elevated over several consecutive measurement points (~30 s), as seen in c.

1. Show individual biological data points in Figs. 3e-g, 4a, 5g, 6b, S8a, and S9c where possible, and report exact P values for the main statistical comparisons rather than threshold notation alone.

We thank the reviewer. Individual values of the independent experiments are now shown as symbols in Figs. 3e-g (new Fig. 3b-d), 5g (new Fig. 5d), 6b, S8a (new Fig. S9c), S9c (new Fig. S10c). The individual biological data points underlying the fitting to the Govardovskii nomogram Fig. 4a (new Fig. 4e) are shown in Fig. 4a-d. The p-values are given in the figure legends for all main comparisons. The exact p-values together with the statistical test, the correction for multiple comparisons and the number of independent experiments are in the Summary_Data excel file and in the supplemented files on Zenodo: 10.5281/zenodo.24013508.

1. Fig. 4b could be moved to the Supplementary Information. The axis labels in Fig. 5g should be enlarged, and the underlying replicate values should be shown.

Fig. 4b has been moved to the Supplementary Information (new Fig. S13d) and the main text and legends were updated accordingly. The axis labels in Fig. 5g were enlarged and the individual replicate values are now displayed (new Fig. 5d).

1. The Fig. 6c legend should state explicitly that the GloSensor cAMP assay was used, if this is correct.

The legend of Fig. 6c now states that cAMP was measured with the GloSensor assay in Neuro-2a cells.

1. Use HEK293T, HEK293S DeltaGs, and Neuro-2a designations consistently throughout the manuscript.

We thank the reviewer for pointing this out. We have checked the main text, figures, figure legends, Methods and Supplementary Information and now use the designations HEK293T, HEK293S ΔGs and Neuro-2a consistently throughout. The general term "HEK293 cells" is used only where a statement applies to both HEK293 lines (HEK293T and HEK293S ΔGs), for example in the general description of the cell culture conditions.

E.g. l. 462: To evaluate the broader applicability of optoDRD1 beyond HEK293 cells,

1. Standardize spacing and units throughout, for example "2 µM," "385 nm," "1 s," "photons cm-2," and "photons cm-2 s-1," and distinguish photon exposure from photon flux.

We thank the reviewer for pointing out these inconsistencies. We have revised the Methods (line 733-744) and all relevant figure legends (Fig. S8, Fig. 6b, Fig. 6c) to clearly distinguish photon flux (photons cm⁻² s⁻¹), which describes the irradiance of our light sources, from total photon exposure (photons cm⁻²), which describes the integrated dose over the stated illumination time. We have replaced ambiguous terms such as 'light intensity' with the correct quantity and unit throughout.

1. Correct typographical and formatting errors in the Methods and supplementary legends, including the heading for the indirect arrestin recruitment assay.

We thank the reviewer. We have carefully proofread the Methods and the Supplementary legends and corrected typographical and formatting errors. The heading of the indirect arrestin recruitment assay was corrected to "Indirect arrestin recruitment assay". We also standardized the names of the constructs and methods across the main text and the Supplementary Information.

Reviewer #3 (Significance (Required)):

__Nature and significance of the advance __

The principal advance is technical: the authors generate a bistable, bidirectionally controlled Gs-coupled optoGPCR with substantial spectral separation between activation and deactivation. This addresses an important gap in the optoGPCR toolbox, in which well-characterized Gs actuators are less common than Gi/o- and Gq-coupled tools. The work also provides useful information about JSR1-S199F itself, including its coupling to human Gi and Gq proteins and its reversible arrestin recruitment. The systematic c1-c5 construct series is potentially valuable beyond the specific tool because it provides design information on the contributions of ICL2, ICL3, helix 8, and the C-terminus to G-protein redirection, signal amplitude, persistence, and arrestin recruitment. The current physiological experiments are proof-of-principle rather than evidence of established in vivo utility. __ Context within the existing literature __

Previous optoXR strategies have redirected opsin scaffolds toward Gs signalling, and the manuscript itself notes earlier use of the JellyOp ICL3 to generate Gs-coupled chimeras with bistable opsins. JellyOp also provides a native Gs-preferring comparator. The novelty should therefore be framed carefully. The most compelling distinction of optoDRD1 is not loop exchange alone or response amplitude alone, but the proposed combination of a bistable JSR1-S199F scaffold, large spectral separation, sustained Gs/cAMP output, and externally timed deactivation and reactivation. The claim that this is the first bistable Gs-selective optoGPCR should be phrased as "to our knowledge" and supported by a careful literature survey. Its advantage over JellyOp will be most convincing after a quantitatively matched comparison.

__Audience __ The manuscript will be of interest to researchers working in optogenetics, GPCR signalling, receptor engineering, synthetic biology, neuroscience, and metabolic or pancreatic beta-cell research.

We thank Reviewer 3 for the positive and thoughtful assessment of our work and for recognizing the significance of optoDRD1 as a bistable, bidirectionally controlled Gs-coupled optoGPCR, as well as the value of the systematic c1–c5 construct series as design information beyond this specific tool. We also appreciate the reviewer's balanced view of the physiological experiments as proof-of-principle, which is how we intend them to be understood. We have taken the comments on novelty and on the comparison with JellyOp into account in the revised manuscript, as detailed in our responses to the specific points above.

1. Lohse, M. J. et al. Kinetics of G‐protein‐coupled receptor signals in intact cells. Br. J. Pharmacol. 153, (2008).
2. Tengholm, A. Cyclic AMP dynamics in the pancreatic β-cell. Ups. J. Med. Sci. 117, 355–369 (2012).
3. Nagata, T. et al. The counterion–retinylidene Schiff base interaction of an invertebrate rhodopsin rearranges upon light activation. Commun. Biol. 2, 180 (2019).
4. Hagio, H. et al. Optogenetic manipulation of Gq- and Gi/o-coupled receptor signaling in neurons and heart muscle cells. eLife 12, e83974 (2023).
5. Ehrenberg, D. et al. The Two-Photon Reversible Reaction of the Bistable Jumping Spider Rhodopsin-1. Biophys. J. 116, 1248–1258 (2019).

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Referee #3

Evidence, reproducibility and clarity

Summary

This manuscript presents optoDRD1, a bistable optoGPCR generated by combining the photoswitchable JSR1-S199F scaffold with intracellular regions of the human dopamine D1 receptor. The authors combine UV-visible spectroscopy, cAMP and Ca2+ assays, BRET-based G-protein measurements, an indirect arrestin recruitment assay, AlphaFold-guided chimera design, and experiments in HEK293T, Neuro-2a, and human EndoC-betaH5 cells. The study provides a technically strong and potentially valuable Gs-coupled optogenetic tool that can be activated with violet light and deactivated with green light. The systematic chimera series, broad G-protein profiling, and testing in physiologically relevant cell models are important strengths. The data support the central conclusion that the JSR1-S199F scaffold can be redirected toward light-dependent Gs/cAMP activation while retaining bidirectional optical control. The manuscript would nevertheless benefit from more rigorous and consistent reporting of biological replication, a matched comparison with JellyOp, clearer justification of the selected lead construct and the AlphaFold-guided design claims, and more cautious interpretation of arrestin, retinal, kinetic, and in vivo applicability claims.

Major comments

1. Clarify biological replication and perform kinetic analyses across independent experiments Several central time-resolved experiments are presented as representative datasets with technical replicates, including Figs. 1c, 3b-d, 5a-c and 5f, and 6c. In addition, Tables S5 and S6 report fitted rate constants with confidence intervals and R2 values, but it is not clear whether these parameters were obtained from one averaged trace, one representative experiment, or independently from multiple biological experiments. Fit confidence intervals quantify uncertainty within a fitted trace; they do not substitute for variability across biological replicates. For the main kinetic comparisons, the authors should fit each independent biological experiment separately and report the distribution of the resulting parameters. At minimum, this should include peak response or response amplitude, apparent activation and deactivation rate constants, residual signal after green-light deactivation, and the magnitude of reactivation. Individual biological data points should be displayed, and at least three independent experiments should be used for central claims. The n = 2 datasets, particularly Fig. 3b and Fig. 6c, are not sufficient for quantitative conclusions. The text should also distinguish the kinetics of the measured cAMP reporter response from intrinsic receptor conformational or G-protein activation kinetics. The minute-scale rate constants in Tables S5 and S6 reflect the integrated receptor/G-protein/adenylyl-cyclase/cAMP/reporter system and should be described as apparent cAMP-response kinetics. Please compare this slow response kinetics with the very fast responses of Gs coupled receptors in vivo including JellyOp.

2. Ensure that the comparison with JellyOp is performed under matched conditions The comparison with JellyOp is central to the claims that optoDRD1 has a larger response, more sustained signalling, and superior reversibility. However, the presentation of the assay conditions is not fully consistent. In particular, Fig. S5 states that forskolin was added to the 9-cis-retinal conditions except JellyOp, whereas the Methods state that forskolin was used when measuring Gi-mediated inhibition. Forskolin changes basal cAMP, reporter dynamic range, and potentially the apparent amplitude and decay of the response. A focused head-to-head comparison of optoDRD1 and JellyOp should therefore be performed or re-presented using identical cell type and batch, retinal condition, receptor DNA amount, reporter amount, illumination wavelength-specific photon exposure, forskolin treatment (ideally none), timing, and normalization. Raw baselines and expression or surface-expression controls should be shown. The analysis should distinguish absolute response amplitude, fold induction over baseline, area under the curve or persistence, spontaneous decay, and the ability to undergo repeated switching. Until such a matched comparison is provided, statements that optoDRD1 produces a higher-amplitude response than JellyOp should be qualified.

3. Justify the selection of c5 as the lead construct and explain the relevant trade-offs The c1-c5 series is informative, and c5 produces the largest absolute cAMP response in Fig. 3e. However, Fig. S8a indicates that c4 and c5 have similar fold induction, Table S5 indicates somewhat faster apparent deactivation for c4, and Fig. 3f-g shows elevated basal arrestin association for c5. Thus, c5 appears optimal for absolute signal amplitude, but not necessarily for dynamic range, basal activity, or temporal shut-off. Please provide a concise side-by-side comparison of c4 and c5 using matched biological replicates. This comparison should include basal cAMP, absolute amplitude, fold induction, activation and deactivation, residual signal after deactivation, repeated switching, basal and light-induced arrestin recruitment, and receptor expression or surface abundance. The apparent difference between the large c5 advantage in Fig. 3e and the similar fold induction in Fig. S8a should be explained explicitly. The authors do not necessarily need to change the selected lead construct, but "optimal" should be defined according to the property being optimized. The trade-off between high absolute output and higher basal activity should be transparent.

4. Clarify the AlphaFold-guided design logic and the novelty relative to earlier Gs chimeras The manuscript presents the design as structure-guided, but the connection between the interface analysis in Fig. S2 and the selected grafts is not yet sufficiently clear. In particular, Fig. S2 maps receptor-Gs contacts, whereas the design replaces ICL2, ICL3, adjacent parts of TM5 and TM6, helix 8, and the C-terminus. The rationale for extending the grafts into transmembrane segments and for including the C-terminus, which is generally unresolved in the structural interface dataset, should be explained explicitly in the main text and in an expanded Fig. S2 legend (especially legend to S2b is insufficient). The meanings and limitations of pLDDT, PAE, contact probability, and ipTM should be explained at first use, together with any thresholds or decision rules used to select constructs. Fig. 2c shows only the JSR1-DRD1-miniGs model. The supplementary tables contain data for the other designs, but the manuscript would be strengthened by a quantitative analysis of whether the structural confidence metrics predict functional cAMP output. A scatter plot and an appropriate rank correlation across the initial receptor chimeras and, separately, across c1-c5 would be informative. If the relationship is weak outside the c1-c5 series, the predictive claim should be qualified and the models presented primarily as evidence of structural plausibility rather than as functional predictors. The manuscript also notes that the JellyOp ICL3 had previously been used to generate Gs-coupled chimeras with bistable opsins. Please explain more clearly what limited those earlier constructs and define the specific advance here. The strongest novelty appears to be the combination of the JSR1-S199F spectral switch, systematic multi-domain optimization, robust Gs output, and repeatable bidirectional control, rather than Gs redirection by an intracellular-loop swap alone.

5. Refine the interpretation of arrestin recruitment and retinal-dependent activity The assay used here measures split-luciferase complementation between a membrane-anchored fragment and arrestin-tagged fragment. It therefore reports membrane-proximal arrestin recruitment indirectly; it does not establish direct receptor-arrestin binding or arrestin-dependent downstream signalling. The title and text should use "arrestin recruitment" rather than "arrestin signalling" unless a downstream functional endpoint is added. Likewise, replacing ICL3 may abolish assay-detectable recruitment, but this alone does not prove that ICL3 is the dominant physical arrestin-binding interface, because the substitution may also alter receptor conformation, phosphorylation, or membrane abundance. There are two acceptable ways to resolve this issue. The most direct is to revise the title and claims throughout and limit the conclusions to reversible arrestin recruitment. Alternatively, if "arrestin signalling" is retained as a central claim, the authors should add two major arrestin-dependent functional readouts, such as receptor internalization or ERK phosphorylation, ideally with a control that establishes arrestin dependence. The proposed preferential incorporation of all-trans-retinal is plausible but remains indirect. The data demonstrate retinal-isomer-dependent basal activity and light responses, but do not directly establish the bound retinal species. The binding mechanism and suggested in vivo advantage should therefore be framed as hypotheses. The substantial basal activity observed with 11-cis- and all-trans-retinal should also be discussed as a potential limitation for applications that require a low dark-state signal. Estimated effort: textual qualification is immediate; retaining a downstream "arrestin signalling" claim would likely require approximately 3-6 weeks for a focused functional assay.

6. Temper the physiological and in vivo applicability claims Photon flux, total photon exposure, pulse duration, and optical power density should be reported consistently and distinguished throughout. The underlying data points should be shown for the fitted action spectra in Fig. 4a. The EndoC-betaH5 and Neuro-2a experiments are useful proof-of-principle demonstrations, but they do not yet establish reversible physiological control or in vivo readiness. For the beta-cell experiment, "biological replicate" should be defined clearly, particularly because the Methods indicate that the procedure was repeated one week later. Individual values should be shown. Green-light treatment did not reverse the insulin-secretion phenotype, so the conclusion should be restricted to light-triggered potentiation of insulin secretion under the tested conditions. Also provide data for violet light with ATR and green with 9-cis or better explain the rationale of selection in Fig 6b. The Neuro-2a experiment is presented as a representative n = 2 dataset and should be repeated in at least three independent experiments. The Fig. 6c legend should identify the cAMP assay used. More generally, claims of in vivo applicability should remain prospective because the activation wavelength, potential phototoxicity and tissue penetration, retinal-dependent basal activity, and cell-type-dependent retinal behaviour have not been tested in vivo.

Minor comments

1. Use "arrestin recruitment" consistently in the title, Abstract, Results, Discussion, and figure legends unless a downstream arrestin-dependent response is measured.

2. In the Abstract, qualify "precise signal termination" to distinguish receptor photodeactivation from the slower decay of downstream cAMP and physiological outputs.

3. For Fig. 1c and Fig. S1e-f, show individual biological data points and statistical comparisons. Please move the quantified G-protein selectivity summary (Fig S1E) into the main figure (to Fig. 1c) so that the representative trace is supported directly.

4. State the number of independent protein preparations used for the UV-visible spectra and quantify the fraction of incomplete photoconversion in Fig. 1b, or describe it explicitly as a limitation.

5. Fig. S3 demonstrates receptor immunoreactivity and cellular localization, but permeabilized-cell staining does not quantitatively establish plasma-membrane trafficking. Please revise the wording or add a surface-expression assay for the lead constructs.

6. For Fig. S9, explain the multiple Western blot bands, indicate the expected molecular mass, describe the band(s) included in quantification, show the normalization or loading control, and display the individual values from the three experiments.

7. Fig. S4 appears to refer to curves in Fig. S6, although the corresponding cAMP traces are in Fig. S5. Please correct the cross-reference.

8. Table S6 refers to curves in Fig. 4a-c, whereas the relevant kinetic curves are in Fig. 5a-c. Please correct this reference. Overall perform a careful reading before submission as a respect to the reviewer.

9. For Fig. S13, explain more quantitatively how the violet-light aequorin artifact in sensor-only cells was distinguished from a receptor-dependent Ca2+ response. The n = 2 dataset should be strengthened or the conclusion qualified.

10. Show individual biological data points in Figs. 3e-g, 4a, 5g, 6b, S8a, and S9c where possible, and report exact P values for the main statistical comparisons rather than threshold notation alone.

11. Fig. 4b could be moved to the Supplementary Information. The axis labels in Fig. 5g should be enlarged, and the underlying replicate values should be shown.

12. The Fig. 6c legend should state explicitly that the GloSensor cAMP assay was used, if this is correct.

13. Use HEK293T, HEK293S DeltaGs, and Neuro-2a designations consistently throughout the manuscript.

14. Standardize spacing and units throughout, for example "2 µM," "385 nm," "1 s," "photons cm-2," and "photons cm-2 s-1," and distinguish photon exposure from photon flux.

15. Correct typographical and formatting errors in the Methods and supplementary legends, including the heading for the indirect arrestin recruitment assay.

Significance

Nature and significance of the advance

The principal advance is technical: the authors generate a bistable, bidirectionally controlled Gs-coupled optoGPCR with substantial spectral separation between activation and deactivation. This addresses an important gap in the optoGPCR toolbox, in which well-characterized Gs actuators are less common than Gi/o- and Gq-coupled tools. The work also provides useful information about JSR1-S199F itself, including its coupling to human Gi and Gq proteins and its reversible arrestin recruitment. The systematic c1-c5 construct series is potentially valuable beyond the specific tool because it provides design information on the contributions of ICL2, ICL3, helix 8, and the C-terminus to G-protein redirection, signal amplitude, persistence, and arrestin recruitment. The current physiological experiments are proof-of-principle rather than evidence of established in vivo utility.

Context within the existing literature

Previous optoXR strategies have redirected opsin scaffolds toward Gs signalling, and the manuscript itself notes earlier use of the JellyOp ICL3 to generate Gs-coupled chimeras with bistable opsins. JellyOp also provides a native Gs-preferring comparator. The novelty should therefore be framed carefully. The most compelling distinction of optoDRD1 is not loop exchange alone or response amplitude alone, but the proposed combination of a bistable JSR1-S199F scaffold, large spectral separation, sustained Gs/cAMP output, and externally timed deactivation and reactivation. The claim that this is the first bistable Gs-selective optoGPCR should be phrased as "to our knowledge" and supported by a careful literature survey. Its advantage over JellyOp will be most convincing after a quantitatively matched comparison.

Audience

The manuscript will be of interest to researchers working in optogenetics, GPCR signalling, receptor engineering, synthetic biology, neuroscience, and metabolic or pancreatic beta-cell research.

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Referee #2

Evidence, reproducibility and clarity

• The paper "Photoswitchable optoGPCRs for Reversible Control of Gs and Arrestin Signalling," by Deborah Walter, Richard McDowell, Polina Isaikina, Andreea Pantiru, Hiruttika Ravimohan, Xavier Deupi, Robert J. Lucas, and Gebhard F. X. Schertler, presents a comprehensive characterization of a chimeric optoGPCR engineered from a mutated bistable visual pigment. The construct's spectral properties allow it to be reversibly switched on and off with light, enabling controlled activation of Gs signaling pathways.The starting visual pigment used in this study was a mutant of jumping spider rhodopsin 1 (JSR1) carrying the S199F mutation, which shifts the dark-state λmax from 535 nm to 380 nm., The λmax of the light-activated pigment remains 535 nm in both the wild-type and mutant pigments. This large separation between the dark- and light-activated λmax values allows researchers to reversibly activate and inactivate the optoGPCR at will. Unmodified JSR1 activates Gq and Gi G proteins, whereas many of the signaling pathways researchers wish to study are Gs-mediated. Using structural knowledge together with AlphaFold-based modeling, the researchers designed, constructed, and tested an optoGPCR construct capable of activating Gs pathways.

• This is a comprehensive study, comprising 5 main figures, 13 supplemental figures, and 6 tables. Many of the paper's claims are well supported by experimental data; however, a few statements lack direct experimental evidence. In the first paragraph of the Results section, the authors claim that JSR1 reconstituted with 9-cis-retinal is blue-shifted relative to the pigment reconstituted with 11-cis-retinal. The researchers could easily have shown this spectrum, even if they ultimately chose to use 9-cis-retinal for the remainder of the experiments. They also claim that the photo reversed chromophore is 11-cis-retinal; this claim could be verified experimentally through chromophore extraction and HPLC analysis. The experiments depicted in Figure 5d and 5e are misleading and inconsistent with the data shown in Figure 5f and 5g. The BRET experiments directly test G protein activation and demonstrate the utility of the engineered construct, whereas the experiments in 5d and 5e rely on cAMP measurements and do not demonstrate the selectivity of the optoGPCR.

Significance

This is a significant study describing the engineering of a highly useful optogenetic tool for activating Gs pathways. Its utility is illustrated here in Neuro-2a cells, validating its usefulness in tissue culture systems. It will be interesting to see this tool validated in an in vivo animal model.

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Referee #1

Evidence, reproducibility and clarity

Summary:

Walter et al. present an interesting series of experiments establishing new optogenetic tools for light regulation of cellular signaling processes downstream of GPCRs. These tools are based on the previously characterised, UV light-sensitive "bistable" jumping spider rhodopsin 1 (JSR1), in some instances carrying the single point mutant S199F (which appears -but I may be wrong here- to also have been characterised previously). Signaling profile analysis of WT JSR1 and JSR1 S199F is followed by the engineering of chimeric GPCRs, an approach commonly termed OptoXRs. With the exception of chimeras constructed around the dopamine receptor 1 the generated OptoXRs were non-functional. The OptoDRD1 receptor however performed well and was further optimised and then applied in multiple cell types.

Major comments:

1- The advantages of using a bistable scaffold for OptoXRs are clear (e.g., less photobleaching and more repeatable activation) but I am not sure that this manuscript actually contains data demonstrating this? My apologies if I am not reading the methods section right but retinal seems to have been added to all assay solutions, which limits interpretation of the presented results in the context of one of the main advantages for the proposed system?

2- In the abstract and elsewhere the authors claim that OptoDRD1c5 kinetics match those of WT DRD1 receptors and indeed the data shown in Fig. 4a and c follow similar time courses. But would we actually expect the kinetics to be similar given that this are two entirely different receptors with entirely different reaction chemistryies Could it be that the time course are simply limited by assay kinetics rather than receptor kinetics? E.g., I have overlayed the Jellyfish opsin off trace of Fig. 5c onto Fig. 5b and the kinetics look very similar, at first glance. So, is it the assay or the receptors that shape time course; asked differently: Wouldn't a good agreement between OptoDRD1 and DRD1 indicate that Gs binding and only Gs binding determines GPCR in activation rates?

Minor comments:

1- The inclusion of alphafold in the design of OptoXRs is exciting, as mentioned below! To me, this is more important than analysis of JSR1 and its apparently already known colour-shifting mutant. It may be in the interest of the authors to think how to best balance these aspects in the revised manuscript.

2- It was interesting to see that JSR1 based receptor respond differently to the various available retinal isoforms (e.g. Figure S4 or S11)? Could the authors speculate what the mechanism for this might be?

3- Similarly, how might introduction of the S-F substitution alter signaling profiles (p3)?

4- Along the same lines, the significant basal activation of the system upon incorporation with all-trans retinal is a concern as this would require green light stimulation of the cells or tissue right after gene delivery, unless of course the specific cell type tolerates Gs signaling: is this the case in the beta-cells - do these or other cells homeostatically adapt to elevanted Galphas?

5- There are a few sentences and figures here and there that could need a polish... e.g. "Activation of GPCRs typically results in the activation of 33 heterotrimeric G proteins" or the axis scales of Fig 4c vs e. I am not sure what the purpose of Figure 1c is as more functional data follows.

Significance

This is robust work that will significantly expand the growing repertoire of specialised optogenetic tools for light control of GPCR associated pathways. The main advance is the use of the bistable JSR1 scaffold and coupling it to GalphaS. At the same, for me the most exciting element of this work was the alphafold modeling as this represents a significant step forward from pervious structure-based approaches! In particular the use of alphafold to rationalise and select chimeras is highly innovative.

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Reply to the reviewers

1. General Statements [optional]

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

2. Point-by-point description of the revisions

Reviewer #1:

Major comments

1. It is rather difficult to conclude whether the observed nipple phenotype reflects an early embryonic/prepubertal defect in establishing the nipple stroma, is caused by a constitutive response to ongoing cell death, or a response to continuous DTA expression (or a combination of some of these). The data raise a couple of additional questions: Is there a nipple phenotype at 3 wk of age? It would not be totally unsurprising if ablation of a major fraction of dermal fibroblasts in the nipple area would lead to an early embryonic/prepubertal phenotype but there is no data on this. Hence, is there a "congenital" nipple deformity, as concluded by the authors (line 191)?

We appreciate the reviewer’s insightful comments. We have now included data on embryonic nipple development. These data demonstrate abundant S100A4-lineage cells in E15.5 and E18.5 skin of S100a4-Cre;mT/mG embryos (Figure for Reviewers 1a, corresponding to Figure S4a in the revised manuscript) and normal appearance of nipple sheath in S100a4-Cre;DTA embryos at E18.5 (Figure for Reviewers 1b, corresponding to Figure S4b in the revised manuscript), suggesting no embryonic defect.

Unfortunately, we cannot provide data on 3-weeks old mice (we have not collected this timepoint previously and currently we do not have this mouse line alive). Instead, however, we provide in situ pictures of DTA and S100a4-Cre;DTA nipples at 7 weeks of age (Figure for Reviewers 1c; Figure S4c in the revised manuscript), which demonstrate that the phenotype of defective nipple is fully established at this timepoint. Because the late embryonic data did not support the “congenital” establishment of the nipple deformity and we could not provide any more data from early postnatal development, we have corrected the statement “we describe a congenital nipple deformity” in the discussion (line 202) to “depletion…results in nipple deformity”.

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

The S100A4+ cells are present in the nipple area of S100a4-Cre;DTA mice, suggesting a continuous supply of new S100A4+ cells (Figure for Reviewers 1b, corresponding to Figure S4b in the revised manuscript; and Figure for Reviewers 5a,b, corresponding to Figure S8a,b in the revised manuscript). In the revised manuscript, we comment on this in Discussion (lines 263–268): “Notably, we observed incomplete depletion of S100A4+ cells in the mammary gland and nipple. Interestingly, the same S100a4-Cre;DTA mouse model resulted in complete depletion of S100A4+ cells in the superficial layer of the mandibular condyle46. This suggests that incomplete depletion of S100A4+ cells in the nipple and mammary gland is due to tissue-specific dynamics, rather than lack of depletion efficiency, indicating a compensatory mechanism that can balance the cell loss.”

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

We apologize for the section title confusion. We have analyzed branching frequency in 7-weeks-old females and observed reduced total number of branching points in S100a4-Cre;DTA mice (Figure for Reviewers 2a, corresponding to Figure 2f in the revised manuscript). A significant difference in number of branching points remained also after their normalization to body weight, (Figure for Reviewers 2c, corresponding to Figure 2h in the revised manuscript). We have now added the new quantifications to the revised manuscript with accompanying descriptions in the main text (lines 63-68) “Analysis of mammary epithelial development using whole-mount carmine staining revealed no significant differences in the prenatal establishment of the mammary epithelial tree but it did reveal significantly delayed epithelial outgrowth and reduced branching in pubertal (7 weeks old) S100a4-Cre;DTA mice (Figure 2d-f). Normalization of epithelial outgrowth and branching to body weight indicates that the observed defect represents a mammary-specific impairment rather than a consequence of reduced body growth (Figure 2g,h).”

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

Picrosirius red staining viewed under polarized light is a classic way to assess collagen organization, thickness, and packing. Red/orange/yellow color typically marks thicker, more mature, and more tightly packed collagen fibers (often associated with type I collagen), while green color usually marks thinner, less organized, or less densely packed fibers (often associated with type III collagen or immature collagen). We had included this explanation in the Figure 4 legend of the submitted manuscript already: “Typically, thicker collagen fibers exhibit stronger birefringence and appear red or orange, while thinner fibers exhibit weaker birefringence and appear green or yellow.” To help with the quantification, we have extracted the red channel and quantified color intensity. The results are shown in Figure for Reviewers 3a,b, corresponding to Figure S5 in the revised manuscript. To investigate the morphology of collagen fibers in more detail, we performed collagen fiber analysis CT-FIRE1 (Figure for Reviewers 3c). The analysis suggests that the fibers in S100a4-Cre;DTA nipples might be longer and less straight (Figure for Reviewers 3d,e); however, the result is statistically nonsignificant.

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

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

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

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

Thank you for your comment. We have addressed the issues in the Abstract and in the Discussion. We revisited the cited studies more carefully, clearly distinguishing the different approaches and particular findings. In our literature review, we also considered studies that used S100a4-Cre mouse model to manipulate gene expression within S100A4+ cells. We argue that these studies bring indirect evidence of involvement of S100A4-expressing cells (and the particular targeted gene in them) in development and/or homeostasis of a tissue, such as mammary gland. Please, find the rephrased part of Abstract in the text, and below:

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

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

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

• Ref 37 used S100a4-Cre to delete sharpin

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

• Likewise ref 39 deleted another gene using S100a4-Cre

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

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

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

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

Please find the rephrased part of Discussion in the text (lines 242-262), and below:

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

Studies using S100a4-Cre to manipulate specific signaling pathways (e.g. Wnt or Hedgehog signaling via gene deletion) in S100A4-expressing cells have reported diverse phenotypes, including effects on fertility and endocrine function28,44. However, these phenotypes primarily reflect the consequences of pathway perturbations within S100A4-expressing cells rather than the role of S100A4⁺ cells themselves. This is fundamentally different from the ablation approach used here, which removes the S100A4⁺ cell population.

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

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

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

Minor comments:

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

To fulfil the suggestion, we have performed a new round of immunostaining followed by high-resolution confocal imaging. We have now updated Figure 5 in the revised manuscript.

**Referee cross-comenting**

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

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

Reviewer #1 (Significance (Required)):

General assessment:

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

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

Reviewer #2

Major comments:

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

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

Here are few examples:

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

We have rephrased the paragraph and removed repeated information. The new text can be found in lines 200-205 in the revised manuscript.

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

We apologize for the confusion; we have now rephrased our claims (lines 242-262):

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

Studies using S100a4-Cre to manipulate specific signaling pathways (e.g. Wnt or Hedgehog signaling via gene deletion) in S100A4-expressing cells have reported diverse phenotypes, including effects on fertility and endocrine function28,44. However, these phenotypes primarily reflect the consequences of pathway perturbations within S100A4-expressing cells rather than the role of S100A4⁺ cells themselves. This is fundamentally different from the ablation approach used here, which removes the S100A4⁺ cell population.

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

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

We have revised our claim. We have now included, also in response to other Reviewers’ comments, data on S100A4 expression in the S100A4-Cre;DTA model (Figure for Reviewers 5, corresponding to Figure S8 in the revised manuscript), and commented on these results in lines 263-268: “Notably, we observed incomplete depletion of S100A4+ cells in the mammary gland and nipple. Interestingly, the same S100a4-Cre;DTA mouse model resulted in complete depletion of S100A4+ cells in the superficial layer of the mandibular condyle46. This suggests that incomplete depletion of S100A4+ cells in the nipple and mammary gland is due to tissue-specific dynamics, rather than lack of depletion efficiency, indicating a compensatory mechanism that can balance the cell loss.”

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

We have now added quantification of GFP+ lineage cell’s contribution to immune cell and fibroblasts populations (Figure 5 in the revised manuscript). Moreover, we have now included data on the presence of S100A4+ cells in S100a4-Cre;DTA mice (Figure for Reviewers 5a,b; Figure S8a,b in the revised manuscript), which demonstrate incomplete depletion of the S100A4+ cells in the nipple and the mammary gland. This is likely due to ongoing tissue remodeling and continuous S100A4+ replenishment/ supply. Another study using the same S100a4-Cre;DTA mouse model reported an efficient S100A4+ cell depletion in mandibular condyle2, which suggests that the presence of S100A4+ cells in the S100a4-Cre;DTA mammary gland and nipple is due to tissue-specific dynamics rather than lack of depletion efficiency.

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

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

Thank you for this insightful observation. It is well established that metabolic and nutritional condition directly affect female reproductive functions. Adult S100A4-Cre;DTA mice are generally smaller compared to their litter counterparts, potentially because of lower body fat content or other anatomic/metabolic condition that might negatively influence fecundity, for instance, lowering ovulation rate and/or embryonic survival. In support of this, earlier studies have reported a positive correlation between growth rate/body condition and litter size3. Unfortunately, in the case of S100A4-Cre;DTA mice, we can only speculate about the possible explanations, as we do not have supporting data which could confirm it.

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

To address this comment, we performed a new round of immunostaining and high-resolution confocal imaging and quantifications (Figure 5 and Figure S7 in the revised manuscript). In the nipple, GFP+ cells were found among both immune cells and fibroblasts, with prevalent expression by fibroblasts (Figure 5e). In the mammary gland, the S100a4-lineage cells comprised mostly immune cells and only very few GFP+ fibroblasts (Figure S7).

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

We performed a co-staining of GFP and AIF1, a macrophage marker expressed by Langerhans cells, and found GFP+ AIF1+ cells localized in the epidermis (Figure 5f in the revised manuscript). This result confirmed that the cells are Langerhans cells.

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

Thank you for this comment. Indeed, there are no GO terms explicitly labeled as “inflammation” and “repair”; however, several GO terms are functionally related to these processes. Our interpretation was based on broader biological context rather the explicit annotation. To clarify this, we revisited the text and included GO terms that reflect the tissue response (lines 192-196).

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

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

Thank you for raising this point. Indeed, in this line, we refer to ongoing tissue inflammation and repair. We also considered the hypothesis that ejection incapability (and consecutive milk stasis) triggers involution. However, tissues were collected within a few hours after parturition, when only very early signs of involution, if any, would be detectable; therefore, we expect minimal influence of involution. To reflect this comment, we added new text to the Discussion (lines 278- 283). “The observed tissue response can be also associated with hallmarks of mammary involution, the process which is triggered by the milk stasis. However, the tissues were collected within few hours after parturition, when the effect of involution should be minimal51. Rather, we hypothesize that immune cell recruitment, and the upregulation of the lipid skin barrier might be caused in response to the continuous apoptosis of S100A4+ cells and their replacement.”

Minor comments:

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

Yes, we had checked the S100A4-lineage cells in the pituitary gland and ovary and have now included the results in the manuscript (Figure for Reviewers 4a,b corresponding to Figure S2a,b in the revised manuscript), along with relevant text description (lines 97-98 in the revised manuscript). “We observed S100A4-lineage/traced cells in the pituitary gland and ovaries of S100a4-Cre;mT/mG mice (Figure S2a,b).” The presence of S100A4+ cells in these organs was also reported previously5.

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

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

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

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

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

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

Line 150. Figure S4 should be Figure S4a.

(Please note that by adding new Supplementary figures, this comment is referring to Figure S7 in the new version of manuscript.) Thank you for this comment. In the text (lines 155-156), we state “GFP+ cells were spread throughout the fat pad but were also localized in the periepithelial stroma and infiltrated the epithelium”. This we show in Figure S7a and in S7b; therefore, we now changed the reference accordingly, as it might be more accurate.

**Referee cross-comenting**

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

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

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

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

Reviewer #3

Major comments:

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

Thank you for this comment. The role of S100A4+ cells in adipose tissue was previously reported6. Authors reported significantly lower weight of fat pads/ inguinal white adipose tissue (I-WAT) in S100a4-Cre;DTA mice (both males and females), as well as smaller size of I-WATs and smaller adipocytes in I-WATs from S100a4-Cre;DTA mice. In our work, we measured the area of the fat pad, and adipocyte size in distal fat pad and found no significant differences between the DTA and S100a4-Cre;DTA mice. The discrepancy in absence vs. presence of the altered adiposity phenotype between our study and the published study6 might be due to different background of the experimental mice. Our mice were on C57BL/6 background, while the mice in the published study were backcrossed to FVB/N background. There is quite strong evidence that mouse genetic background affects adiposity, adipose-tissue expansion, and where/how excess lipid is stored, and there are several direct comparisons of FVB/N vs. C57BL/6 (PMID: 22964790; PMID: 19325873; PMID: 23423668; PMID: 28483861; PMID: 28605665 etc.).

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

S100A4-expressing cells are present during embryonic mammary development, too. Please note the embryonic lineage-tracing time-points incorporated in the first version of the manuscript already (Figure 5a and Figure S7a). Now, we have added Figure for Reviewers 1, corresponding to Figure S4 in the revised manuscript, which focuses on the embryonic nipple phenotype but also provides information on the presence of S100A4+ cells.

On top, we examined available data from previously published work7–10 to investigate S100a4 expression in early and late development of the mammary gland and the nipple (Figure for Reviewers 5). S100a4 was detected in the epithelium and fibroblasts in early postnatal (P0) mammary gland. At later stages (pubertal mammary gland development), its expression was shifted predominantly to leukocytes, with reduced levels in fibroblasts. In contrast, scRNA seq data from embryonic skin revealed broad expression of S100a4 within the fibroblast cluster, along with a small, distinct immune cells population expressing S100a4. In adult skin, S100a4 expression was observed in epidermal cells, immune cells, and fibroblasts.

We agree that the use of inducible S100a4-CreERT model could potentially bring new insights into developmental stage-specific roles of S100A4+ cells. However, such experiments are beyond our capacity. Therefore, we have included a new subsection on Limitations of the study, where we comment (lines 292-296):

“A limitation of this study is that the timing of DTA-mediated cell depletion cannot be precisely defined in the constitutive mouse model employing S100a4-Cre because recombination may occur continuously following the initial expression of S100a4 (E8.518). This limitation could be overcome by usage of inducible S100a4-CreERT instead, which could help determine if the nipple phenotype is established embryonically or during postnatal morphogenesis.”

3) Although the authors attribute lactation failure primarily to defects in nipple architecture, the RNA seq data reveal downregulation of key milk production genes and luminal differentiation keratins, strongly suggesting impaired secretory activation. The authors should more explicitly discuss the relative contributions of epithelial functional maturation defects versus nipple structural abnormalities to the lactation failure observed upon S100A4+ cell depletion.

Thank you for this suggestion. We agree that secretory activation might be impaired in S100a4-Cre;DTA mice; more specifically the suckling/milk removal-dependent maintenance and amplification of mammary secretory function and postpartum alveolar remodeling (Wagner et al., 1997, PMID: 9678900). In this regard, we have included new text in Discussion (lines 283-286):

“The transcriptomic signature also revealed downregulation of genes essential for milk production and luminal epithelial differentiation. This potentially reflects the lack of suckling/milk removal-dependent post-partum alveolar maturation and maintenance of secretory activation52.” To a small extent, the results may be also influenced by differences in tissue composition between samples. In control mice, more fully developed nipples and an extended ductal network likely contribute to a greater representation of differentiated luminal epithelial cells, thereby increasing the abundance of expression of these markers.

Minor comments:

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

We have now included Figure for Reviewers 6 that corresponds to Figure S8 in the revised manuscript and comment on the results in sections Results (lines 175-176) and Discussion (lines 263-268). In Results: “Interestingly, S100A4 antibody labeling revealed presence of S100A4+ cells in S100a4-Cre;DTA tissues (Figure S4b, Figure S8a,b).” In Discussion: “Notably, we observed incomplete depletion of S100A4+ cells in the mammary gland and nipple. Interestingly, the same S100a4-Cre;DTA mouse model resulted in complete depletion of S100A4+ cells in the superficial layer of the mandibular condyle46. This suggests that incomplete depletion of S100A4+ cells in the nipple and mammary gland is due to tissue-specific dynamics, rather than lack of depletion efficiency, indicating a compensatory mechanism that can balance the cell loss.”

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

We have now included Figure for Reviewers 7 that corresponds to Figure 2d in the revised manuscript. We performed immunostaining for keratin 5 (KRT5, basal – myoepithelial cells), keratin 8 (KRT8, luminal cells) and α smooth muscle actin (αSMA, basal – myoepithelial cells) on adult (16 weeks of age) mammary gland sections. The epithelial architecture in S100a4-Cre;DTA was preserved, with no detectable abnormalities. Accordingly, we comment on this in the Results section (lines 61-62): “Immunofluorescent examination of epithelial organization also showed no detectable abnormalities in S100a4-Cre;DTA mammary glands.”

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

Thank you for this comment. As explained in the response to your major comment 3, we believe our results show that the secretory activation is conserved in S100a4-Cre;DTA lactating mice. We understand that “lactation failure” might be misleading terminology, as the production of the milk is conserved as well. We therefore change the phrasing into “nursing defect” (line 51, 75, 85, 210), as this could reflect the phenotype most precisely.

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

We have now included Figure for Reviewers 8 that corresponds to Figure S6 in revised manuscript. We performed immunostaining for keratin 5 (KRT5), keratin 8 (KRT8), keratin 10 (KRT10) and α smooth muscle actin (αSMA) on lactating nipple sections. The epithelial organization is well preserved in S100a4-Cre;DTA nipples.

We comment on this in Results section (lines 133-135): “There were no abnormalities in epithelial organization, smooth muscle or sebaceous glands along the lactiferous duct in the S100a4-Cre;DTA L1 nipple (Figure S6a-c).”

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

We performed the requested co-labeling of GFP and CD31 (Figure for Reviewers 9 and Figure 5c in the revised manuscript). Our result confirms the contact between GFP+ cells and endothelial cells, as GFP+ cells were present within the vasculature.

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

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

**Referee cross-comenting**

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

Reviewer #3 (Significance (Required)):

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

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

Thank you for appreciation of our work.

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

Reviewer #1

Major Comment 1.

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

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

Reviewer #2

Major Comment 3.

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

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

Reviewer #3

Major comment 1.

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

We thank the Reviewer for this insightful suggestion. We agree that genetic approaches targeting S100A4 function (e.g., knockout or knockdown) could, in principle, help disentangle cell-autonomous effects of S100A4 from those resulting from the loss of S100A4-expressing cell populations. However, the primary objective of our study was to investigate the functional contribution of S100A4+ stromal cells at the population level, rather than to dissect the molecular function of S100A4. In this context, the S100A4-Cre;DTA model provides a well-established and appropriate strategy to ablate this cell population and assess its role in tissue development. Importantly, S100A4 is not only a functional protein but also a widely used marker of a heterogeneous stromal cell population. Genetic ablation of S100a4 itself would not eliminate these cells, and may result in relatively subtle or compensable phenotypes due to functional redundancy within the S100 protein family or context-dependent roles of S100A4. Therefore, such approaches would address a distinct biological question and may not directly recapitulate the phenotypes observed upon cell ablation.

References

1. Bredfeldt, J.S., Liu, Y., Pehlke, C.A., Conklin, M.W., Szulczewski, J.M., Inman, D.R., Keely, P.J., Nowak, R.D., Mackie, T.R., and Eliceiri, K.W. (2014). Computational segmentation of collagen fibers from second-harmonic generation images of breast cancer. J. Biomed. Opt. 19, 016007. https://doi.org/10.1117/1.JBO.19.1.016007.
2. Tuwatnawanit, T., Wessman, W., Belisova, D., Sumbalova Koledova, Z., Tucker, A.S., and Anthwal, N. (2025). FSP1/S100A4-Expressing Stem/Progenitor Cells Are Essential for Temporomandibular Joint Growth and Homeostasis. J. Dent. Res. 104, 551–560. https://doi.org/10.1177/00220345251313795.
3. Eisen, E.J., and Durrant, B.S. (1980). Genetic and Maternal Environmental Factors Influencing Litter Size and Reproductive Efficiency in Mice. J. Anim. Sci. 50, 428–441. https://doi.org/10.2527/jas1980.503428x.
4. Friedman, G., Levi-Galibov, O., David, E., Bornstein, C., Giladi, A., Dadiani, M., Mayo, A., Halperin, C., Pevsner-Fischer, M., Lavon, H., et al. (2020). Cancer-associated fibroblast compositions change with breast cancer progression linking the ratio of S100A4+ and PDPN+ CAFs to clinical outcome. Nat. Cancer 1, 692–708. https://doi.org/10.1038/s43018-020-0082-y.
5. Ren, Y.A., Monkkonen, T., Lewis, M.T., Bernard, D.J., Christian, H.C., Jorgez, C.J., Moore, J.A., Landua, J.D., Chin, H.M., Chen, W., et al. (2019). S100a4-Cre–mediated deletion of Ptch1 causes hypogonadotropic hypogonadism: Role of pituitary hematopoietic cells in endocrine regulation. JCI Insight 4. https://doi.org/10.1172/jci.insight.126325.
6. Zhang, R., Gao, Y., Zhao, X., Gao, M., Wu, Y., Han, Y., Qiao, Y., Luo, Z., Yang, L., Chen, J., et al. (2018). FSP1-positive fibroblasts are adipogenic niche and regulate adipose homeostasis. PLoS Biol. 16. https://doi.org/10.1371/journal.pbio.2001493.
7. Carabaña, C., Sun, W., Veludo Ramos, C., Huyghe, M., Perkins, M., Maillot, A., Journot, R., Hartani, F., Faraldo, M.M., Lloyd-Lewis, B., et al. (2024). Spatially distinct epithelial and mesenchymal cell subsets along progressive lineage restriction in the branching embryonic mammary gland. EMBO Journal 43, 2308–2336. https://doi.org/10.1038/s44318-024-00115-3.
8. Sumbal, J., Journot, R.P., Attri, K., Danek, V., Merle, C., Faraldo, M.M., Sumbalova Koledova, Z., and Fre, S. (2025). Contractile fibroblasts form a transient niche for the branching mammary epithelium. Nature Communications 16. https://doi.org/10.1038/s41467-025-63612-x.
9. Jacob, T., Annusver, K., Czarnewski, P., Dalessandri, T., Kalk, C., Levra Levron, C., Campamà Sanz, N., Kastriti, M.E., Mikkola, M.L., Rendl, M., et al. (2023). Molecular and spatial landmarks of early mouse skin development. Dev. Cell 58, 2140-2162.e5. https://doi.org/10.1016/j.devcel.2023.07.015.
10. Joost, S., Annusver, K., Jacob, T., Sun, X., Dalessandri, T., Sivan, U., Sequeira, I., Sandberg, R., and Kasper, M. (2020). The Molecular Anatomy of Mouse Skin during Hair Growth and Rest. Cell Stem Cell 26, 441-457.e7. https://doi.org/10.1016/j.stem.2020.01.012.
11. Wagner, K., Young, W., Liu, X., Ginns, E., Li, M., Furth, P., and Hennighausen, L. (1997). Oxytocin and milk removal are required for post‐partum mammary‐gland development. Genes Funct. 1, 233–244. https://doi.org/10.1046/j.1365-4624.1997.00024.x.

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Referee #3

Evidence, reproducibility and clarity

Summary:

In this pre-print, Belisova et al. investigate the under-explored mechanisms regulating nipple development and its essential role in offspring nourishment, focusing on the contribution of S100A4‑expressing cells in the mouse mammary gland. The authors use an elegant combination of Cre::DTA-mediated cell depletion, lineage tracing, imaging, RNA-seq, and functional assays to reveal roles for S100A4‑expressing fibroblasts and immune cells in nipple morphogenesis and lactation. The manuscript is generally well written, and the experimental design is strong, with appropriate controls supporting the overall conclusions. However, I have several comments and suggestions to improve this initial manuscript.

Major comments:

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

2) The differential systemic versus mammary-specific effects of DTA-mediated S100A4 cell ablation are intriguing. The authors should address why the mammary fat pad appears unaffected. Are S100A4 expressing cells present during embryonic mammary development, or are they mainly postnatal? Would an inducible S100A4CreERT model lead to similar phenotypes, or might the timing of depletion influence the outcome? Discussing these points would reinforce the conclusions regarding the contribution of S100A4-expressing cells to mammary and nipple development and could also clarify the transient nature of the ductal branching phenotype.

3) Although the authors attribute lactation failure primarily to defects in nipple architecture, the RNA seq data reveal downregulation of key milk production genes and luminal differentiation keratins, strongly suggesting impaired secretory activation. The authors should more explicitly discuss the relative contributions of epithelial functional maturation defects versus nipple structural abnormalities to the lactation failure observed upon S100A4+ cell depletion.

Minor comments:

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

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

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

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

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

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

Referee cross-comenting

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

Significance

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

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

I have expertise in mammary epithelial biology.

I estimate that revisions would require 3-6 months if new experiments are performed, and 1-3 months if revisions focus on clarifying claims and strengthening the discussion.

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Referee #2

Evidence, reproducibility and clarity

Summary:

In this study, Jaros Belisova et al. systematically investigated the composition and roles of S100A4+ cells during mammary gland development and identified a novel role for S100A4 for nipple development. Depletion of S100A4+ lineage using the S100a1-Cre;DTA model resulted in delayed pubertal mammary gland development but with normal morphology and milk production capacity during lactation. The authors further investigated the milk-ejection function of the alveoli using an ex vivo culture method combined with live imaging. This revealed that depletion of S100A4+ cells does not interfere with the normal function of alveoli. However, the abnormal development of the nipple, characterised by smaller size, shorter length, lacking protrusion, increased collagen composition and decreased cell proliferation at the onset of lactation, results in milk delivery failure which is responsible for the lethality of the pups. To further understand the consequences of S100A4+ cell depletion, the author utilised the S100a4-Cre;mTmG model to trace the cell types depleted in the DTA model across various developmental stages. Immunofluorescent staining revealed that S100A4 lineage cells comprised both fibroblasts and immune cells, consistent with previous studies. Interestingly, some S100A4 lineage (GFP+) retain the expression of S100A4. In addition, the RNAseq data comparing the nipple cells from S100a4-Cre;DTA and DTA lactation mice confirmed their observations in transcription level. Overall, the experiments are well designed and the key findings are valid, especially about the role of S100A4 during nipple development is novel and interesting.

Major comments:

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

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

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

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

d. The authors tried to attribute the minor phenotype to the incomplete depletion of S100A4+ cells. However, it is possible that if the S100A4+ cells only represented a minor population, their function may be compensated by other populations. This might be confirmed by quantification of S100A4+ cells or S100A4-Cre; GFP+ cells in fibroblast or CD45 populations from images showed in Figure 5. 2. In Fig. 1, the authors described the impaired nursing capacity of S100A4-Cre;DTA dam. However, it seems the little size is also smaller (Fig 1a). Do authors have any explanation or hypothesis? 3. In Fig S1c, d and lines 93-96, the authors investigated the estrus cycles to determine the potential cause of lactation failure. The data was presented as the number of mice in each stage. A more intuitive approach would be to follow the same mice for two to three cycles and observe the duration of each stage. 4. The images in Figure 5 and Figure S4 are difficult to confirm colocalization. A higher magnification image would be required for each panel. Furthermore, a precise quantification based on the current images would be more supportive of the conclusion regarding the discrepancy of the composition of S100A4 lineage between epidermis and mammary gland (lines 163-165). 5. Line 163, the author hypothesis the Langerhans cells due to morphology. Those cells should be able to be confirmed by a co-staining with F4/80 in addition to the current form of Fig 5h. 6. In lines 181-184, the authors states "the results showed that the tissue reacted to a foreign chemical or an endogenous compound....." , which results are referring here? I could not find any inflammation related GO terms in figure 6b. It would be more accurate to specify them in lines 179-181, which appears to be a technical statement rather than a result in current form. 7. The lines 182-184 was not clear. Does the author refer the "nipple tissue response" in general as malfunction of development or inflammation and tissue repair as mentioned in the previous sentence? If the later cases, the authors should consider the failure of lactation might mimic the involution, which may cause the apoptosis and inflammation as well. This might be independent of the DTA expression.

Minor comments:

1. The authors demonstrated in Figure S1 and lines 92-96 that no significant differences were observed in pituitary glands and ovaries in S100a4-Cre:DTA and DTA mice. Have the authors checked the S100A4 expression or lineage cells in these organs, or have been reported by others?
2. The authors have performed live imaging to evaluate the contraction of alveoli. It would be better to include a video together with the snapshots showed in Figure S2.
3. Since the study is mainly using S100a4, it would be better to avoid using FSP1 in the results, for example Fig 5h.
4. What does L1 stand for? Lactation Day 1? It should be spelt out in the first instance.
5. Line 150. Figure S4 should be Figure S4a.

Referee cross-comenting

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

Significance

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

My expertise:

mammary gland development and breast cancer

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Referee #1

Evidence, reproducibility and clarity

Summary

In this study, Belisova et al. investigate the function of S100a4+ (a.k.a. Fsp1) cells in the mammary gland. S100a4 expressing cells were constitutively ablated using the DTA system by crossing S100a4-Cre mice with ROSA26-eGFP-DTA mice. Female mice exhibited a severe nursing defect, leading to whole-litter mortality within 1-2 days postpartum. However, no abnormalities were detected in the morphology of the mammary ductal tree, milk production, or alveolar contractility of S100a4-Cre;DTA mice. Instead, nipples were malformed, likely prevent normal suckling. Analysis of the lineage of S100a4 expressing cells in the mammary gland using the S100a4-Cre mouse in combination with a fluorescent Cre reporter identified S100a4+ cells as fibroblasts and immune cells in the nipple region, while only immune cells were labelled in the mammary gland stroma, findings that agree with previous studies.

Major comments:

1. It is rather difficult to conclude whether the observed nipple phenotype reflects an early embryonic/prepubertal defect in establishing the nipple stroma, is caused by a constitutive response to ongoing cell death, or a response to continuous DTA expression (or a combination of some of these). The data raise a couple of additional questions: Is there a nipple phenotype at 3 wk of age? It would not be totally unsurprising if ablation of a major fraction of dermal fibroblasts in the nipple area would lead to an early embryonic/prepubertal phenotype but there is no data on this. Hence, is there a "congenital" nipple deformity, as concluded by the authors (line 191)? Are there S100a4+ cells in the nipple area of pubertal S100a4-Cre/DTA mice? I.e. is there a continuous supply of new S100a4+ cells and thereby continuous cell death and DTA expression as one might expect based on the RNA-seq data?
2. The subtitle on line 54 implies that that S100a4-Cre/DTA mice display a branching phenotype. However, it looks to me as if there is a pubertal outgrowth defect (as is also written in the body text, line 64) rather than a branching phenotype, potentially reflecting the much smaller size of S100a4-Cre/DTA mice (Fig. 2a). Unless there is a change in branch point frequency, I suggest rephrasing the title and discussion. Instead, I suggest the authors discuss the observed outgrowth delay considering the gross overall growth defect (Fig. 2a). If ductal outgrowth was normalized to the overall growth defect, would one still observe 'a delay in branching morphogenesis'?
3. Fig. 4e shows Masson's Trichrome and Picrosirius Red staining and the authors report the findings as follows (lines 120-124): "collagen fibers were loosened in the DTA nipples and more densely packed in the S100a4-Cre;DTA nipples". Perhaps the authors could help non-specialists to observe the loosened fibers and if they wish to make quantitative statements ("more densely packed"), such statements should be backed-up by quantifications.
4. I found the Discussion on the various mouse models somewhat problematic. Overall, the paper is written is a way that it often remains unclear whether it refers to studies addressing the role of S100a4 itself, studies addressing the function of S100a4+ cells via ablation approaches (S100a4-Cre or S100a4-CreERT2 crossed with floxed DTA), or those where S100a4-Cre has been used to delete gene X/Y/Z. These are all very different experimental approaches where one approach is not necessarily informative when trying to understand the results from another one. The authors should make these points clear and consider whether all their discussion points are relevant. The abstract states S100a4 (fibroblast-specific protein 1) is "expressed by mesenchymal cells and has been implicated in the development of eccrine glands, hair follicles, and mammary branching morphogenesis". However, the study on eccrine glands (ref. 19) shows that S100A4+ cells play a role in eccrine gland development but it does not address the role of S100a4 itself, while the study on hair follicles (ref.20) in turn reports the expression pattern of S100a4 in hair follicles but does not address its function, nor the role of S100a4+ cells. Finally, I failed to find references in the paper to studies addressing the role of S100a4, or S100a4+ cells in the mammary gland. Instead, the paper had references to studies where S100A4-Cre had been used to delete different genes and these mice had various mammary phenotypes - which, as indicated above, is a very different approach compared to deleting S100a4 or ablating S100a4+ cells.

In Discussion (lines 197-200), the authors write: "We described significant delay in mammary branching morphogenesis in puberty, confirming an important role for S100A4+ cells in mammary development, as it was previously described (refs 37-39)." It should be noted that none of these studies addressed the role of S100A4+ cells:

• Ref 37 used S100a4-Cre to delete sharpin
• Ref 38 used the same Cre line to delete Ptch1, did not address the role of S100a4 or S100a4 expressing cells
• Likewise ref 39 deleted another gene using S100a4-Cre

Later on in Discussion, the authors compare the reported phenotype to previous studies (lines 248-255): "...targeting S100A4+ cells through knockout experiments can result in severe phenotypes, such as a reduction in adipose tissue (ref 26), skin phenotypes, a disrupted estrous cycle, reduced fertility (ref. 38), and complete infertility, hypogonadism and defects in pituitary endocrine function (ref. 28). Of these, Ref. 26 used the same approach as the current study (S100a4-Cre; DTA) (Fig. 7A in the paper) - these mice were significantly lean, with markedly reduced fat compared with the control mice - also the mice in the current study are very small, so perhaps they could also be described as 'lean'. Yet ref. 26 reports that female mice had comparable food uptake, respiratory exchange ratio and physical activity, and slightly increased energy expenditure

Ref. 38 (as mentioned above) reports deletion of Ptch1 using S100a4-Cre lines and these mice "displayed a disrupted estrous cycle and dramatically reduced fertility over 6.5 weeks". However, this has nothing to do with the approaches where Fsp1/S100a4+ cells are depleted with DTA. Likewise, reference 28 analyzed the phenotype of S00a4-Cre;Ptch1fl/fl mice. Obviously, deleting Ptch1 using S100a4-Cre mice is quite a different approach than "targeting S100A4+ cells" through knockout experiments". Ptch1 deletion leads to a combination of gain-of-function (of Hedgehog activation) and loss-of-function (loss of Hh-independent functions of Ptch1) and hence comparisons with these phenotypes is rather challenging. I suggest the authors focus their phenotype comparisons to ref. 26 where S100a4/Fsp1+ cells were ablated with DTA, i.e. the same approach as in the current study. 5. I find the Discussion is somewhat off the topic by starting with WHO recommendations on breastfeeding and linking this to observed mouse phenotype. Overall, the discussion is rather long and from time-to-time more like a literature review. I would recommend keeping the Discussion more succinct and focused.

Minor comments:

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

Referee cross-comenting

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

Significance

General assessment:

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

Advance:

This study provides novel information on nipple morphogenesis, with potential (though with reservation) relevance to the congenital human inverted nipple condition affecting 3-5% of women.

Audience:

This work should appeal to mammary gland biologists interested in mammary gland development and nipple formation; those with interest on fibroblasts biology given that S100a4 was once thought to be a broad marker of fibroblasts, as well as those with interest in the inverted nipple condition.

My expertise:

Mammary gland morphogenesis, developmental biology, cell signaling

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Reply to the reviewers

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

Summary: The manuscript by Obaji et al investigates the role of TFIIIC and RNA Pol III in the recruitment of SMC protein containing complexes (condensin IDC, condensin I, and cohesion), as well as their role in remodeling the 3D genome in C. elegans. Connection between TFIIIC, condensin, and 3D genome organization have been seen in other organisms, several cited by the authors. This works extends the idea to C. elegans. The authors perform a series of ChIP-seq and Hi-C experiments after depletion of TFIIIC or a subunit of RNA Pol III. The observed impacts are relatively minor, but TFIIIC does appear to play a role in recruiting condensin and cohesin to a subset of their binding sites, and it also plays a role in shaping the 3D genome. However, there does not seem to be the same level cooperation between SMC complexes and TFIIIC at tRNA genes as was previously described in yeast (Hausler et al 2006, Genes and Development). The paper is written in a very short format, and as a result some details, at times essential information (such as the antibodies used in the experiment) are missing. So some aspects of the work were hard to evaluate. Overall, the study describes some interesting findings, but the significance of the work is limited by the relatively minor effects observed.

The experiments were well done. My expertise is not in Hi-C data analysis, so I cannot comment on the quality of those aspects of the paper. Most of my concerns relate the how the experiments were described and how conclusions were drawn. Some of the conclusions should be qualified, but I am not sure if additional experiments would make the conclusions any stronger.*

* Major comments: 1. The information on what antibodies were used in the ChIP-seq experiments are missing. tftc-3 and rpc-1 were tagged with degron::GFP. Did the authors use anti-GFP antibodies? For other proteins analyzed, such as TFTC-5 and TBP-1, what antibodies were used? Are these antibodies validated/high quality?*

• *The antibodies used for each data set is provided in the column labeled “Antibody” in the Supplemental File 1, ChIP tab. The anti-GFP antibody is ab290 from Abcam. TFTC-5, TBP-1 antibodies are from modENCODE used in PMID: 31918747 and PMID: 24011592. We added this information in the Methods section.

* To show that the tag did not interfere with gene function, the authors assessed lethality in the tagged strains. The data shown on Supplemental Figure 2 shows unusually high level of lethality in the no tag control. Only 20-40 eggs were counted for each data point. I would recommend counting more, and if the lethality remains in the no tag control, I would worry about the starting wild type strain having some background mutations.*

• *We thank the reviewer for pointing this out. The lethality shown in the plot is likely due to technical variability, miscounting embryos and worms crawling to the edge of the plate. Students include the control strain every time, and perform the counting for at least three biological replicates to account for the technical variability within the experimenter. As we do not observe dead embryos on our maintenance plates of no tag control, we think the issue is likely technical, rather than background mutations.

* After validating the strains and determining depletion conditions, the authors first analyze 3D genome organization. Compartmentalization weakens a bit, more obvious after 22 hours of TFTC-3 depletion, at which point they see increased interactions between the arms and the center of chromosomes. Additionally, a small increase in insulation is observed at TAD boundaries on the X chromosome. These data are described on Fig 3, and in general support the conclusions. In the legend, the authors mention to B-B, A-A, A-B. It was unclear what they refer to.*

• The A and B refer to the two compartments that the principal component analysis assigns each genomic bin to. At the scale of chromosomal domains, A compartments are designated to be the chromosome centers, and B compartments correspond to the two arms. The C. elegans* genome also compartmentalizes at a smaller scale, which is apparent when the compartment analysis is performed using Hi-C data from the arms and centers separately. This smaller scale compartmentalization correlates with transcription and is antagonized by DNA loop extrusion (PMID: 36331876). At the smaller scale, A compartments correspond to active chromatin based on overlap with histone modifications that mark active chromatin. B compartments are inactive/repressed. For both large and small scale compartmentalization, A-A means the interactions between the genomic bins both assigned to the A compartment. A-B means interactions between a pair of genomic bins with one assigned to A and the other to B. We edited the Figure legend to read “PCA analysis segregates the genome into large-scale A and B compartments. A compartments are located mostly towards chromosome centers and B the arms.”

* Next, the authors investigate impacts on condensin IDC binding. After 1 hour of TFTC-3 depletion, condensin IDC binding is reduced at a subset of sites that overlap with TFTC-3 sites (Fig 4). The authors refer to these as tRNA genes. While many of them are likely tRNA genes, not necessarily all. Either check whether they are all tRNA genes, or refer to them as TFTC-3 binding sites.*

• *Thank you for pointing out the mismatch between the text and figure. We edited the subheading to read “TFIIIC regulates condensin I-DC binding to TFIIIC sites including tRNA genes”. We indeed analyzed all TFIIIC peaks. In the revised figure, we splitted the TFIIIC peaks that are tRNA genes, which confirms the effect on tRNA genes (Supplemental Figure 4).

* For one of these sites, the authors scramble the box A/B DNA sequence. Please explain how this experiment was done. Was it by replacing the endogenous sequence using crispr? In any case, in this mutant, TFTC-3, RPC-1 and DPY-27 binding all decreased. *

• *The sequence of the box A and B motifs were mutated using CRISPR/Cas9 and homologous recombination. The resulting mutant sequence with highlighted changes are provided in the Supplemental File 1 “strains” tab.

On Fig 4 B, binding seems to be decreased at many additional sites as well. Why is binding decreased at additional sites?

• *Thank you for pointing to these additional sites. We found out that while constructing the mutant genome, we mistakenly used a genome sequence with an unrelated insertion (400 bp at chromosome X 16215493) which is ~14.4 Mb downstream of the scramble mutation site. This shifted the coordinates starting from ~16.2 to the 17.7 Mb, which is the end of the chromosome, thus systematically reducing ChIP average signal for the TFIIIC sites in this region. The genome version is corrected and the data is re-plotted in Figure 4B.

* While not necessarily easy to answer, what I am most curious about is whether the change in condensin IDC binding at a subset of sites is actually biologically relevant. Is there an impact on dosage compensation?*

We have been curious about this question as well. We performed mRNA-seq upon TFTC-3 depletion. mRNA-seq detects upregulation of X chromosomes due to subtle defects in dosage compensation (example TOP-1 and TOP-1 depletion from our lab PMID: 36302374). We asked if TFTC-3 depletion causes derepression of the X chromosomes. To answer, we test if the change in X chromosomal gene expression is within or outside the variation observed for autosomes. The new Figure 3G and the associated supplemental panels show that while TFIIIC depletion does cause differential mRNA expression, the effect is not specific to the X chromosome, thus we cannot claim a role on dosage compensation. We think that TFIIIC binding at the rex sites is a consequence of condensin I-DC bridging tRNA genes to the rex sites as two anchors of a condensin I-DC mediated DNA loop (the cartoon in Figure 3D and the revised model figure in Figure 7C tries to make this point).

* While the experiments concerning condensin IDC binding were done after 1 hour of depletion (after 1 hr of TFTC-3 depletion RPC-1 is still bound), the experiments with cohesin were done after 22 hours of depletion (when RPC-1 binding is impacted). Therefore, the authors can conclude that condensin IDC binding is impacted by TFTC-3, but not RPC-1, but the same cannot be said for cohesin (Fig 5). The authors seem to imply that only TFCT-3 is involved and not RPC-1. In fact, data for 1 hr of TFTC-3 depletion is not shown. *

• *Our data show that TFIIIC regulates SMC-3 but does not definitely rule out RPC-1 role and we removed claims of such. However, at tRNA genes, where both RPC-1 and TFTC-3 bind highly, the effect size of RPC-1 depletion on SMC-3 binding is lower than that of TFTC-3 (Figure 5B), thus our original conclusion is likely to be correct. We have revised the text to read:

“We should note that 22 hr TFTC-3 depletion reduces RNA Pol III. However the magnitude of SMC reduction upon TFTC-3 depletion is greater than that of RPC-1 (Figure 5B), thus supporting a specific role for TFIIIC in cohesin regulation. In addition, SMC-3 binding at RNA Pol III only sites (without TFIIIC) is significantly lower compared to TFIIIC+, PolIII+ sites and ETCs (Figure 5F), supporting the interpretation that TFIIIC is required for cohesin localization.”

Addiotionally, the title of the section and the title of figure refer to these sites as tRNA genes, but tRNAs are not even mentioned in the text of this section. Are these in fact exclusively tRNA genes, or are they TFTC-3 binding sites.

• *Please see our response to comment 4 as we marked the tRNA genes in example regions and split the classes of TFIIIC binding sites as being tRNA genes and not.

* In a very brief section, the authors describe the final finding, clustering of tRNA genes, which seems to depend on TFTC-3, but not RPC-1 or condensin or cohesin. While the rest of the paper investigates how TFTC-3 impacts condensin and cohesin, this data shows that condensin and cohesin are not working with TFIIIC in this process. The data is data, and I am not arguing with it, but the story does seem more disconnected than the title implies.*

• *Yes, it is fair to point out the disconnect. We do not want to imply a connection in the title, but we want to state the two main functions of TFIIIC: regulating SMC binding and regulating 3D contacts of tRNA genes. I think we do a reasonable job explaining that these two observations may be connected but, we cannot find a direct support for or rule out SMCs mediating tRNA genes clustering. Redundancy may be the reason, because TFIIIC regulates multiple SMC complexes. To deplete all SMCs simultaneously is not trivial, because the efficiency of auxin mediated depletion differs between different targets due to rate of protein turnover, and the level of depletion need to be characterized individually and combinatorially.

*

Minor comments: 1. TFTC-3 depletion seems quite effective, RPC-1 depletion a little less so. It should be mentioned in the text. Also, on Fig 1C, please explain the signal that remains after depletion. (The explanation is in the legend for Figure 2-it should be explained earlier.)*

• Auxin inducible depletion was done in a tissue-specific manner, using eft-3* promoter to drive TIR1 expression in soma. In early-stage L3 worms, most cells are postmitotic and there are a handful of germ cells (~10-30) that start to proliferate and do not express TIR1. This corresponds to ~2-4% of total cells, and is observed as remaining GFP signal in the belly of the worm upon 1 hr auxin depletion. Even if 100% depletion is achieved in the soma, some protein is expected to remain in the western blot and ChIP-seq.

Thus, to compare TFTC-3 and RPC-1 depletion, we quantified the level of GFP signal reduction in the head of worms. The baseline GFP signal is lower for TFTC-3 compared to RPC-1, thus making comparison difficult, but normalizing the signals to the average of the initial condition (no auxin control) showed roughly similar level of depletion (Supplemental Figure 2B).

The following sentences describes the tissue specific depletion: “By choosing eft-3 driven TIR1 expression, depletion is limited to the somatic cells in L3 larvae while the few germ cells are not affected.”.... “Soma-specific depletion was validated by the reduction of the GFP signal across the body except the few mitotic germ cells in early L3 larvae (Figure 1C).”

* Supplemental Figure 3 legend refers to distribution of peak categories and cartoon interpretation that are not shown on the figure.*

• *Supplemental Figure 3 legend is corrected by removing text referring to a cartoon. The peak distributions are plotted on the lower left of each chromosome.

* Figure 7 shows some new analysis described in the discussion. It should be in the results section.

*

We added a final paragraph to the results section titled: TFIIIC promotes 3D DNA contacts between tRNA genes located on different chromosomes.

“Although subtle, we also detected an enrichment of Hi-C contacts between TFIIIC bound tRNA genes on different chromosomes, which did not reduce upon single depletion of cohesin or condensin (Figure 7A). We reasoned that the TFIIIC dependent trans contacts between tRNA genes reflect interphase organization of the genome in postmitotic somatic cells. Indeed, Hi-C data derived from mixed developmental stage C. elegans embryos lacked the enrichment of trans contacts between TFIIIC bound tRNA genes (Figure 7B).”

*

Reviewer #1 (Significance (Required)):

Significance: My enthusiasm is a bit limited due to the minor impacts observed. Condensin and cohesin binding is only impacted at a subset of binding sites and it is unclear whether the changes affects condensin and cohesin function. Similarly, 3D genome organization did not change that much, and condensin and cohesin are not even involved in tRNA clustering. As a result, the study does not advance the knowledge in the field by a lot.*

*

Audience: the study will be interesting to scientists in the 3D genome organization field, especially as a point of comparison to other systems.

My expertise is in chromosome structure and organization and condensin biology.*

• *

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

General Writing Comments • Given that the strongest and most novel finding is TFIIIC's role in condensin/cohesin recruitment and boundary formation, the Introduction and Abstract would benefit from earlier framing around why SMC complexes localize where they do (i.e., boundary-element biology), rather than leading primarily with the transcriptional background of TFIIIC.*

• Thank you for the suggestion and we agree that the introduction can be written by leading with SMCs. However, by explaining that TFIIIC is a recruiter of RNA Pol III first, we emphasize the need for a robust evaluation of TFIIIC function in SMC regulation in multicellular organisms. Much of the field has accepted correlations from genomic experiments in humans, drosophila and worm, as strong evidence for TFIIIC role in metazoan genome organization. However, a direct test to distinguish TFIIIC function from RNA Pol III had not been done. Our study used the auxin inducible system in C. elegans* to accomplish this.

• * In the Discussion, consider leading with the strongest, most novel results (SMC recruitment, tRNA gene 3D contacts) before moving to the more incremental arm/center compartmentalization findings.*

* Science Comments HOT-site behavior vs. direct regulatory function. Because TFIIIC/ETC sites can behave as generically hyper-occupied regions in other organisms, the authors should more explicitly distinguish the possibility that TFIIIC directly regulates SMC recruitment from the alternative that TFIIIC and SMC complexes are both independently drawn to a shared class of highly accessible chromatin. Or that TFIIIC is generating a HOT site. A discussion of HOT sites vs TFIIIC sites would be helpful.*

• Although TFIIIC/ETC sites are hyper occupied in yeast, a vast majority of TFIIIC/ETC sites are not hyper occupied in C. elegans; 71 out of 914 TFIIIC peaks overlap with a HOT site and 70/422 HOT sites overlap with a TFIIIC peak. The reviewer’s question is: whether TFIIIC and SMC complexes are independently drawn to a class of highly accessible chromatin. We answered this question by focusing on condensin I-DC, which is restricted to the X chromosome, thus autosomal HOT sites serve as a control. We show that TFTC-3 binding at the X chromosomal condensin I-DC binding sites, including the strong rex* sites, are greater than that of HOT sites across other chromosomes (Supplemental figure 3E). Thus, our data is consistent for a specific interaction of TFIIIC with condensin I-DC rather than each independently being attracted to HOT sites. We added the following text to the result section: “We reasoned that if TFIIIC binds to rex sites due their properties as a HOT site, the level of TFIIIC enrichment at the rex sites should be comparable to other HOT sites across the genome. This was not the case (Supplemental figure 3E), thus further supporting the specific interaction between TFIIIC binding and condensin I-DC.”

* Possible chromatin-opening role for TFIIIC at the 1 hr timepoint. Along the same lines. At 1 hr TFTC-3 depletion, condensin binding is lost specifically at sites where TFIIIC and DPY-27 binding overlap, while DPY-27 is retained at other, non-overlapping sites. This raises the possibility that TFIIIC helps maintain locally accessible chromatin that permits condensin binding, rather than (or in addition to) direct recruitment via protein-protein interaction. ATAC-seq under the same depletion conditions could help distinguish these possibilities.*

• It is possible that TFIIIC mediates nucleosome removal from tRNA genes and this helps with SMC complex binding. However, our data argues that accessibility is not sufficient*. While RNA Pol III+/TFIIIC- sites are more accessible than RNA Pol III -/TFIIIC+ sites, SMC binding is higher at RNA Pol III -/TFIIIC+ sites, as shown in new Figure 5F and added the text:

“Next, we considered the possibility that TFIIIC bound sites are more accessible thus show greater ChIP-seq signal. Instead, we found that ATAC-seq coverage was higher for RNA Pol III-only sites compared to TFIIIC-only sites, which is opposite of the pattern observed for SMC-3 (Figure 5F). Together, our results in Figure 4 and 5 are consistent with a specific function for TFIIIC in mediating SMC complex localization.”

* More minor comments: 1. Quantify depletion efficiency. The claim of GFP signal loss (Fig. 1C) is currently supported only by representative images - please quantify mean GFP intensity per worm (auxin vs. no-auxin) across a sample of animals. Similarly, please quantify Western blot band intensity (Fig. 1B, normalized to tubulin, across replicates) rather than relying on visual inspection of a single blot.*

Please note that the depletion is accomplished by driving the expression of TIR1 by using eft-3 promoter, thus expressing in somatic cells. Please see our response to the reviewer 1 minor comments #1. We quantified the level of GFP signal reduction in the head of worms. The baseline GFP signal is lower for TFTC-3 compared to RPC-1, thus making comparison difficult, but normalized signals with and without auxin showed roughly similar levels of depletion (Supplemental Figure 2B).

* Genome-wide confirmation that RPC-1 depletion leaves TFIIIC binding intact. Figure 4C shows TFTC-3 signal is retained at one representative locus after 1 hr RPC-1 depletion, but this is not shown genome-wide. Since the claim of an RNA Pol III-independent function for TFIIIC rests on RPC-1 depletion not affecting TFIIIC binding, please provide a genome-wide comparison (e.g., a heatmap or violin plot analogous to Fig. 1D) confirming this.*

The claim of an RNA Pol III independent role for TFIIIC is supported by 1) TFIIIC does not require RNA Pol III for binding in vitro (PMID: 23063749). In vivo, RNA Pol III and TFIIIC each have independent localization sites, thus their binding does not require each other (Supplemental Figure 1). 2) RNA Pol III only sites show lower SMC binding compared to sites where TFIIIC binds (Figure 5F), thus RNA Pol III cannot be the major regulator of SMCs. 3) 1 hr RPC-1 depletion substantially affecting TFIIIC is inconsistent with our results that TFTC-3 but not RPC-1 depletion regulates condensin I-DC binding and tRNA gene clustering.

* Reconcile genome-wide vs. locus-specific contact-frequency effects. The claim of "minimal impact on average contact frequency" (Supp. Fig. 3A) rests on a genome-wide P(s)/slope plot, which by construction averages over all loci and distances and could mask spatially localized effects. This appears to be in some tension with Fig. 3B/C and Supp. Fig. 3B, which show a visibly stronger arm-center mixing signal specifically at 22 hr TFTC-3 depletion. A quantitative summary distinguishing a modest genome-wide shift from a strong, spatially restricted effect diluted by averaging would strengthen this section.*

• *Hi-C measures relative contact frequencies, a quantitative summary must be accomplished by fitting a model to the data. While models are useful, they also make a lot of assumptions. As a result, the field has presented distinct models that fit HiC data (e.g. both loop extrusion and non loop extrusion models produce SMC mediated loops).

Our lab would like to take a genetic approach to address the mechanisms by which arm-center organization is changed upon RPC-1/TFTC-3 depletion. For example, do nuclear pores which interact with both TFIIIC/RNA Pol III explain their common role in chromosome arm/center organization?

* o Related: please provide statistics on the apparent partial rebound in B-compartment strength after 22 hr auxin treatment (Fig. 3B, bottom-right saddle values) even as A-compartment strength remains reduced.*

• *Thank you for bringing our attention to this partial rebound. This was a product of the first eigen vector not correctly assigning the arm/center compartments to A and B for in the TFTC-3 22 hour depletion data. In the revised version, we standardized the compartment designation, by using the no-tag control EV1 to define the A and B compartments in all samples. This showed that there is no partial rebound in B compartment strength. The Figure 3B is updated and data from replicates are provided in Supplemental Figure 3B. We also provide a statistical test of the compartmentalization in Supplemental Figure 3D.

* Direct comparison between the scramble and depletion experiments (Figure 4). The Box A/B scramble experiment (Fig. 4A-B) and the TFTC-3 auxin depletion experiment (Fig. 4C-D) are presented as parallel lines of evidence but are never directly compared quantitatively. Is the reduction in DPY-27 binding at the scrambled locus comparable in magnitude to the reduction at TFTC-3-depletion-affected peaks genome-wide? A side-by-side comparison, or at least a statement about this, would strengthen the claim that both perturbations report on the same mechanism.*

• *The ChIP-seq scores from depletion and the scramble mutation cannot be compared to each other directly, because ChIP-seq measures relative binding, rather than absolute (unless very careful spike-in corrections are done (PMID: 39271835). Immunoprecipitation enriches DNA, thus in knockdown conditions, it may inflate the level of binding. This is why we refrain from making statements about absolute changes, and instead limit our definitive conclusions based on relative comparisons.

For instance, we can definitively state that TFTC-3 depletion specifically reduces SMC binding at sites that overlap with TFIIIC relative to sites that do not overlap with TFIIIC (Figure 4D and 5B). Similarly, scramble mutation specifically reduces binding, relative to the other sites that are not mutated (Figure 4B).

* Single-locus scope of the scramble experiment. The Box A/B scramble was performed at only one tRNA gene (F56C3.t1). Please discuss whether this result is expected to generalize across tRNA genes broadly, or consider testing a second, independent locus to rule out gene-specific effects.*

• The scramble experiment at one locus supports the observation from tens of other loci in the wild type condition, where SMC complexes do not bind to unexpressed tRNA genes *(Supplemental Figure 4A). Thus, the conclusion that TFIIIC regulates SMC binding comes from 1) endogenous condition - where TFIIIC presence is a requirement for observing SMC localization, 2) scramble experiment - where boxA/B mutation eliminate binding of TFIIIC and SMC 3) depletion experiment - where TFTC-3 depletion reduce SMC specifically at TFIIIC binding sites compared to non-TFIIIC dependent SMC binding sites.

* Figure/text mismatch for autosomal DPY-26 binding (Figure 5). The statement "DPY-26 binding to autosomes was weak" (p. 11) is illustrated by Fig. 5C, which shows an X-chromosomal region, not an autosome (autosomal DPY-26/SMC-3 tracks appear only in Fig. 5A). Please point the reader to the correct panel, or add a clearly labeled autosomal example alongside the X-chromosomal one so both are shown side by side.*

• *Thank you for pointing out the disconnect. The quantification for the autosomal data is shown in Figure 5D. We edited the sentence as follows: “As expected, DPY-26 binding to autosomes was weak in largely interphase cells of L3 larvae, thus resulting in fewer peaks compared to the X chromosome (Figure 5D).“

* Replicate-level concordance for Hi-C. All Hi-C data are presented as merged replicates; replicate-level correlation is not shown. A supplementary figure comparing the two biological replicates (e.g., stratum-adjusted correlation or scatterplots of key metrics such as insulation score or compartment strength) would let readers judge how robust the reported effects are across replicates.*

• *We provide the key figures in the paper plotted separately for the biological replicates in Supplemental Figure 3B and Supplemental Figure 5, and present statistical tests with the replicates included in Supplemental Figure 3D, Figure 3E, Figure 7A.

* Derepression as a potential mechanism. Neither the tRNA promoter scramble nor TFTC-3 depletion is accompanied by expression data. Since transcriptional derepression of genes near the scrambled motif or near TFIIIC-bound sites could confound the interpretation of reduced condensin/cohesin binding, even limited expression data (qRT-PCR at a few loci, or RNA-seq) would help rule this out. Otherwise, please discuss this caveat in the results.*

We performed mRNA-seq analysis upon 1 hr and 22 hr TFTC-3 depletion. If TFIIIC locally regulated RNA Pol II transcription, there should be a correlation between differential gene expression and distance to a TFIIIC binding site. Although there were some differentially expressed genes close to TFIIIC peaks, the correlation was not statistically significant (Figure 5E). Indeed, acute depletion of TFTC-3 had limited effect on mRNA expression (Supplemental Figure 3F). Thus, the TFTC-3 effect on SMC binding and tRNA gene clustering is unlikely to be through RNA Pol II transcription. We added the following text:

“To rule out the local control of SMC binding by TFIIIC across the genome is indirect through regulation of the neighboring genes, we analyzed mRNA-seq changes upon 1 hr and 22 hr depletion of TFTC-3 as a function of distance to the nearest TFIIIC binding sites. We did not observe a statistically significant correlation (Figure 5E). There were genes close to TFIIIC binding sites that were affected by TFTC-3 or RPC-1 depletion (Supplemental Figure 4C, Supplemental File 1 DESeq tab). However, this effect was not widespread and thus the local effect of TFIIIC and RNA Pol III on RNA Pol II transcription is limited and does not explain the observations presented in Figure 4D and Figure 5B.”

* Quantification of interchromosomal tRNA gene contacts. The intrachromosomal tRNA-tRNA contact enrichment is quantified with paired statistics (Fig. 6B), but the interchromosomal (trans) pileups shown in Fig. 7A are presented only qualitatively. Since the trans-chromosomal contacts are central to the argument against a pure loop-extrusion model, a matching quantification and statistical test would substantially strengthen this claim.*

• For trans contacts, we merged TFIIIC-bound tRNA genes into 1kb clusters to match the HiC resolution. We then extracted Hi-C contacts for every inter-chromosomal pair of clusters. A majority of these pairwise contacts were 0, thus for each tRNA gene/cluster containing bin, we calculated the average of all its trans *pairwise contacts with other tRNA gene/cluster containing bins. Differences between conditions were assessed with a nested ANOVA testing whether the variation between conditions exceeded variation between replicates followed by a post hoc t-test against the control using the ANOVA error term with Bonferroni correction. The effect of TFIIIC depletion was statistically significant, while SMC depletions were not. The results are presented in revised Figure 7A with replicates separated.

* Basis for attributing reduced Hi-C fountains to "indirect effects." Supp. Fig. 4B attributes the loss of cohesin-mediated fountain signal after 22 hr TFTC-3 depletion to indirect effects of prolonged depletion, but no data directly distinguishes direct from indirect causes. Please either soften this interpretive claim or provide supporting evidence (e.g., a comparison against the 1 hr TFTC-3 depletion timepoint, which does not show this loss).*

• *The data for the 1hr depletion of TFTC-3 is shown in the same Figure panel (Supplemental Figure 4B). To help readers assess the intensity of the Hi-C contact frequency, we averaged contact frequency within a 60 degree cone centered at the fountain origins, and plotted as a line for individual replicates of relevant data sets in Supplemental Figure 4B.

* Reliance on an external dataset for condensin I/II clustering. The individual contributions of condensin I (DPY-26 TEV) and condensin II (KLE-2 TEV) to tRNA gene clustering (Fig. 6D-E) are assessed using a previously published dataset (Das et al., 2024) rather than the authors' own degron system. Please confirm that depletion timing/developmental stage are comparable enough to the rest of the study for direct comparison.*

• The time at which the Hi-C are performed is L3 larvae for both studies. Das et al 2024 depletes target protein by heat shock activation of TEV mediated cleavage, which starts at the L1 stage, ~24 hours before the Hi-C is performed. In Das et al. 2024, COH-1 degradation showed reduced Hi-C contacts forming fountains, which was also the case for our 1 hr auxin induced SMC-3 degradation (Kim et al 2025). Similarly, DPY-26 degradation produced the expected X chromosomal 3D organization changes in Das et al. 2024, which is the case using an sdc-2* mutant+RNAi in Crane et al. 2015. Thus we believe the data are comparable to a reasonable extent.

In addition, the higher than average contact frequencies between TFIIIC bound tRNA genes in our Hi-C experiments and the Meister lab data, confirm the replicability of the observation that TFIIIC bound tRNA genes have higher than expected contacts in 3D.

* Additional Points Requiring Clarification • Viability and developmental timing of depletion. The strains remain viable without auxin, with depletion restricted to the soma; some GFP signal and germ cell division are still observed at the 2-cell stage under auxin. Please clarify what this residual signal implies for interpreting phenotypes at the earliest depletion timepoints - could early developmental effects be underestimated if depletion is incomplete at this stage?*

• *The lack of depletion in the germline and early embryogenesis is by design, because we did not want to potentially affect the germline and early development, as TFIIIC and RNA Pol III are needed for tRNA expression. Rather, we aimed to directly test the interphase functions in 3D genome regulation. Thus we expressed TIR1 under the control of the eft3 promoter, which is a strong somatic promoter that is not expressed in the germline. We clarified the text as follows: “We endogenously tagged tftc-3 and rpc-1 at the C terminus with degron-GFP and crossed to obtain homozygous strains expressing the auxin receptor TIR1 under the control of a soma-specific promoter peft-3 (Zhang et al., 2015) (Figure 1A). By choosing eft-3 driven TIR1 expression, depletion is limited to the somatic cells in L3 larvae while the few germ cells that are present are not affected.”

• * Nature of the rex site overlapping a tRNA gene cluster (Figure 3D). One strong rex site sits near a cluster of four tRNA genes with higher TFTC-3 than RPC-1 binding. Since tRNA genes and rex sites are both classic examples of highly-occupied regions, the authors should discuss whether this overlap reflects a specific functional relationship between condensin I-DC recruitment and TFIIIC, or a more generic co-occurrence at hyper-bound loci - and whether this particular locus is representative of the other 16 strong rex sites analyzed in Fig. 3E.*

• We show TFIIIC ChIP-seq signal at 17 strong rex and non-rex HOT sites in Supplemental Figure 3E, which supports the specific enrichment of TFIIIC at the rex sites above other HOT sites, including those on the X chromosomes. This supports the conclusion that the binding reflects a specific binding relationship *between condensin I-DC and TFIIIC and is unlikely to be a generic co-occurance at hyper-bound loci. The following text is added:

“In previous work, we noted that rex elements coincide with high occupancy target (HOT) sites defined by a high number of transcription factors localizing to a subset of genomic sites by ChIP (Albritton et al., 2017). We reasoned that if TFIIIC binds to rex sites due their properties as a HOT site, the level of TFIIIC enrichment at the rex sites should be comparable to other HOT sites across the genome. This was not the case (Supplemental figure 3E), thus further supporting the specific interaction between TFIIIC binding and condensin I-DC.”

• * Strength of the DPY-27/TFTC-3 correlation. The correlation between DPY-27 and TFTC-3 ChIP enrichment across the X chromosome (r = 0.82, Fig. 3F) is notably strong relative to the RPC-1 correlation (r = 0.45) and, in our view, deserves more prominent discussion in the main text as one of the more compelling quantitative links supporting the model.*

We thank the reviewer for their suggestion and added the following text to highlight the finding. “In S. pombe, the TFIIIB subunit TBP physically interacts with condensin and localizes it to tRNA genes (Iwasaki et al., 2015). In human cell extracts, condensin II physically interacts with the TFIIIC subunits (Yuen et al., 2017). Our analysis of the X-specific condensin I-DC provides strong evidence for a specific interaction between an SMC complex with TFIIIC and not RNA Pol III. First, the correlation between DPY-27 and TFTC-3 ChIP enrichment across the X chromosome (r = 0.82) is stronger than that of the RPC-1 (r = 0.45), thus quantitatively linking TFIIIC binding to that of condensin I-DC. Second, unlike TFIIIC, RNA Pol III depletion does not reduce condensin I-DC localization at the X chromosomal tRNA genes (Figure 4D). Together, these observations support an evolutionary conserved function for the general initiation factors, rather than RNA Polymerase III, in regulating SMC complex binding to tRNA genes.”

• * Normalization for insulation score comparisons. Figure 3E reports Wilcoxon rank-sum p-values comparing insulation scores across conditions, but it is not stated whether a spike-in or other cross-condition normalization was used for the underlying Hi-C/ChIP data, and no per-site error bars or replicate spread are shown. Please clarify the normalization approach and, if possible, show replicate-level variability underlying these scores.*

Hi-C data was normalized using the ICE (iterative correction and eigenvector decomposition) method from Imakaev et al. Nature Methods from Mirny lab. Raw observed counts are generated in Juicer and Cooltools add ICE balancing. Broadly, the contacts of each genomic bin are balanced, meaning Hi-C matrices reflect the “relative” contact frequency of each genomic region with the rest of the genome, and is not a measure of “absolute” contact frequency. Spike in approaches are not a validated normalization technique in Hi-C. There is indeed variability in the insulation scores between replicates. A linear mixed-effects model with strain/depletion conditions as a fixed effect and rex sites as shared conditions, did not show statistical significance for an effect of TFTC-3 depletion on average insulation score across all rex sites (figure 3E). We edited the text accordingly and edited the section subheading to read “TFIIIC binding positively correlates with condensin I-DC on the X chromosomes”

• * Reference line for Figure 4B. A diagonal line with slope 1 would help readers visually assess the degree of deviation from a 1:1 relationship between wild-type and scramble-mutant ChIP enrichment, and should be added to this panel.*

• *We added the line to Figure 4B.

• * tRNA gene positions relative to ChIP signal (Figure 4C). Please mark the positions of tRNA genes directly on this genome browser panel, since the spatial relationship between the TFTC-3/RPC-1/DPY-27 tracks and the underlying tRNA genes is central to the interpretation of this representative locus.*

• *Thank you for pointing this out. We updated Figure 4C, Figure 5 A&C marking the tRNA genes.

• * Loop vs. compartment-level nature of tRNA gene interactions. It remains unclear whether the reported tRNA gene contacts (Fig. 6, 7) reflect discrete, loop-like interactions or a broader compartment-level clustering phenomenon. Given that these possibilities imply different underlying mechanisms, the authors should state explicitly which interpretation their data best support, or acknowledge that both may contribute.*

• *Our data is best explained with a model combining both, and we tried to clarify in the revised Figure 7C model panel legend:

“(C) Since both TFIIIC and RNA Pol III mediate interaction of tRNA genes with the nuclear pore (Ikegami & Lieb, 2013) and reduce contacts between chromosome arm and centers, nuclear pore tethering may contribute to the 3D compartmentalization of chromosome arm and centers. Our data showed that TFIIIC is required for localization of cohesin and condensin complexes to tRNA genes. TFIIIC is also required for 3D contacts between TFIIIC bound tRNA genes. The lack of prominent Hi-C loops between tRNA genes argue that the contacts must be infrequent, thus heterogeneous within the population of cells. We propose that (i) TFIIIC acts as a dynamic barrier to loop extrusion, thus localizing SMC complexes at a fraction of tRNA genes in a given cell. This conclusion is supported by TFTC-3 mediating condensin and cohesin binding to TFIIIC sites, and the specific enrichment of TFTC-3 at rex sites, as a result of TFIIIC being at one of the two anchors of a condensin I-DC mediated DNA loop. We also propose that (ii) TFIIIC promotes 3D contacts between tRNA genes by protein-protein interactions through compartmentalization of the interphase genome. This conclusion is supported by the presence of tRNA gene contacts between different chromosomes and DPY-26 depletion not reducing tRNA contact frequency on the X chromosomes. “

• *

• * Explicit mechanistic model for TFIIIC-SMC recruitment. The manuscript would benefit from a clearer statement of which mechanistic model is favored: (i) TFIIIC acts as a loop-extrusion barrier/anchor, with tRNA gene interactions arising in cis (proximal or distal) or in trans as extrusion products; or (ii) TFIIIC recruits SMC complexes to sites independent of loop extrusion. The current data (weak but genome-wide insulation effects, plus trans contacts and DPY-26 TEV results that argue against extrusion alone) suggest a hybrid model - making this explicit would help readers evaluate the proposed self-organization model in Figure 7C.*

• Our study supports a hybrid model including two mechanisms for TFIIIC mediated promotion of 3D contacts between tRNA genes: (i) TFIIIC is a weak barrier to DNA loop extrusion by multiple SMC complexes. Thus, TFIIIC mediates 3D contacts in cis by positioning tRNA genes at the anchor of SMC mediated DNA loops. We do not favor the recruitment model, because of two reasons. First, TFIIIC likely ChIPs to the rex sites because condensin I-DC mediated DNA loop anchors TFIIIC next to the rex sites. Thus loop extrusion is consistent with the strong positive correlation between TFIIIC binding and condensin I-DC. Second, if TFIIIC recruited condensin I-DC, we expected the X chromosome expression to increase significantly upon TFTC-3 depletion, which was not the case (Figure 3G). (ii) TFIIIC mediates compartmentalization of tRNA genes in trans*. Our analysis shows that DPY-26 cleavage does not reduce contacts between tRNA genes on the X chromosomes. Thus loop extrusion alone fails to explain TFIIIC function in 3D clustering of tRNA genes. Thus we also have to include a loop extrusion independent mechanism. We tried to clarify this model in Figure 7 and its legend (see previous response).

• * Statistical comparison of RNA Pol III recycling correlations. The claim that snoRNA genes show less efficient Pol III recycling than tRNA/ncRNA genes rests on comparing three Pearson correlation coefficients (0.36 tRNA, 0.38 ncRNA, 0.52 snoRNA; Supp. Fig. 2C) without a formal statistical test for whether these correlations differ significantly from one another.*

We performed an Analysis of Covariance (ANCOVA) with an interaction test to ask whether the relationship (slope) between RPC-1 binding and TFTC-3 depletion differed between the three groups of genes. Less RNA Pol III recycling at the snoRNA genes was statistically significant; snoRNA vs tRNA p=0.0062 , snoRNA vs ncRNA p=0.0347, tRNA vs ncRNA= 0.9095. The supplemental figure is updated to contain the slope of the correlations, and figure legend contains the results of the statistical test. *

Reviewer #2 (Significance (Required)):

This manuscript investigates whether TFIIIC regulates SMC complex (cohesin, condensin I, condensin I-DC) binding and 3D genome organization independent of its canonical role in recruiting RNA Pol III. Using auxin-inducible degradation of TFTC-3 (TFIIIC subunit) and RPC-1 (Pol III catalytic subunit) in C. elegans, the authors show that TFIIIC, but not Pol III, is required for cohesin and condensin binding at tRNA genes, and that TFIIIC specifically promotes long-range 3D contacts between distant tRNA genes. Depletion of individual SMC complexes does not eliminate these tRNA gene contacts, suggesting either redundancy among SMC complexes or an SMC-independent mechanism. The work is a well-designed and largely convincing dissection of a long-standing correlative hypothesis, separating the transcriptional and structural roles of TFIIIC.

The findings are exciting, since little is known about positioning SMC complexes in C. elegans, and more broadly, the relationship between TFIIIC and SMC in other systems. While correlations have been seen, I know only one paper showing reliance of condensin (II) and TFIIIC by the Gerton lab, but this was a broad knock down, not the elegant scramble experiments shown here. In addition, this paper broadens the relationship to other SMC complexes. I do have some questions/clarifications.

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

The manuscript by Obaji et al entitled "TFIIIC regulates SMC complex binding and 3D contacts between tRNA genes" is a detailed molecular genetic characterization of the role of tRNA genes in the organization of the C. elegans genome. The manuscript builds on data from numerous organisms. The data show that tRNA genes function as chromosome organizing hubs in worms. The strength of this manuscript is the thoroughness of the experiments and the careful and accurate description of the results without any hyperbole. The authors use auxin to induce depletion of essential protein subunits of TFIIIC, polIII and SMC. They follow the effect using western blots. They show significant depletion of these proteins within 1h. However, the western blots are not quantitative. They should titrate known quantities of purified proteins as standards in order to quantify depletion.*

• *The depletion is performed by a somatic promoter driven TIR-1 in full L3 larvae, with ~1-3% germ cells. We quantified the level of depletion in somatic cells using GFP expression in nuclei at the head. Please see our response to the reviewer 1 minor comments #1. We quantified the level of GFP signal reduction in the head of worms. The baseline GFP signal is lower for TFTC-3 compared to RPC-1, thus making comparison difficult, but normalized signals with and without auxin showed roughly similar levels of depletion (Supplemental Figure 2B).

* Following depletion, the authors use ChIP Seq to map binding of these proteins at sites in the genome. The authors may wish to analyze the DNA sequence motifs that remain bound by TFIIIC following depletion for 1 hour compared to sequences that lose TFIIIC binding upon depletion. The same analysis should be performed for sites that remain bound after 22h. What are the chromatin signatures at these sites (from previous ChIP-Seq data). This analysis could highlight high-affinity sites for TFIIIC or specific chromatin signatures that aid in TFIIIC binding and residence time in chromatin.*

• *While we achieve effective depletion of target proteins by driving TIR-1 under eft-3 promoter, the level of depletion is a function of the amount of p-eft3 driven TIR1 in each cell cell type. Thus the proposed analysis is more suited to a single cell organism or a tissue culture system. Nevertheless, we were able to capture interpretable differences between broad classes of TFIIIC targets, as shown in Supplemental Figure 2D where snoRNA promoters have a higher RPC-1 turnover (less efficient recycling) compared to the tRNA genes.

* In Figure3 the authors analyze 3D contacts using HiC. Depletion of TFIIIC had minimal effects on average contact frequency. This is to be expected given that most contact sites are unlikely to be influenced by TFIIIC. There were subtle differences in separation on arms and centers upon depletion that appear to have a greater effect on smaller chromosomes. Is the density of TFIIIC sites greater on smaller chromosomes? This result is similar to data in yeast that show that tRNA genes have local effects on chromosome function rather than global effects.*

• *There was no obvious correlation between the density of TFIIIC sites (see different classes of peaks marked for each chromosome on the left) and the chromosome-domain level as shown in Supplemental Figure 3.

* In Fig3D they analyze "insulation" on the X chromosome at a specific rex site and show that there are subtle changes. *

It is unclear if these are statistically significant and/or functionally important.

Indeed, the effect on the insulation score was limited to the rex site near the tRNA gene cluster in Figure 3D, and there was no statistical difference between average insulation score across all other rex sites (Figure 3E). We asked if the TFIIIC function at the rex sites is to recruit condensin I-DC to the X chromosome. Subtle changes in condensin I-DC binding results in derepression of X chromosome expression as measured by mRNA-seq (PMID: 36302374). We did not detect an X chromosome specific effect in TFTC-3 knockdown (Figure 3G). Thus we conclude that TFIIIC contributes to insulation at the example rex site by being the anchor of a local DNA loop that connects a TFIIIC site to the rex site (Cartoon in Figure 3D). We reason that the insulation score, calculated from local contacts, increases as a result of fewer DNA loops on the left side of the rex site, rather than TFIIIC functioning directly as an insulator at the rex site. We added the following text:

“To understand if TFIIIC binding at the rex sites contribute to condensin I-DC recruitment, we performed mRNA-seq upon TFTC-3 depletion (Supplemental figure 3F). Depletion of proteins that regulate condensin I-DC binding results in derepression of the X chromosomes within one hour of auxin incubation (Morao et al., 2022). We compared 1 hr depletion of TFTC-3 to no auxin control, and 22 hr depletion of TFTC-3 to 22 hr auxin no tag control, which reports on the combined effect of the degron tag and auxin inducible depletion of TFTC-3. The statistically significant differences on average mRNA abundance from different chromosomes was not X chromosome specific (Figure 3G), supporting our conclusion that TFIIIC binding at rex sites is a consequence of condensin I-DC activity on the X chromosomes.”

* In Figure4A and 4B, the authors mutate the TFIIIC binding site at a specific tRNA gene on the X chromosome. This mutation eliminated TFIIIC binding but only reduced Dpy27 binding. Furthermore, the authors also investigated Dpy27 binding upon TFIIIC depletion and determined that depletion reduced Dpy27 binding at TFIIIC sites. These data suggest that TFIIIC may not be involved in "recruiting" Dpy27 but in stabilizing the binding at specific sites after it has been recruited.*

• *We agree with this interpretation. As for the mechanism of “stabilization”, in the model we propose that TFIIIC is a weak barrier to DNA loop extrusion, thus condensin/cohesin “pauses” at the TFIIIC occupied sites.

* In figure6 the authors deplete TFIIIC or SMC3 or Dpy26 and analyze tRNA contacts via HiC. They show that TFIIIC plays a role in the long-range contacts but are not cohesion/condensin dependent. This is interesting and needs to be highlighted. Is it possible that they utilize other proteins such as nuclear pore proteins.*

• *While both TFIIIC and RNA Pol III subunits physically interact with the nuclear pore proteins, only TFIIIC regulates SMC complex binding. Therefore, we do not favor the nuclear pore idea for SMC regulation. However, we do agree that the mechanism of TFIIIC being a barrier may be through changing DNA topology or anchoring the DNA at another nuclear structure that prevents the loop extruding SMC complexes to bypass the TFIIIC bound locus.

* One weakness of this manuscript is a lack of discussion on the conserved mechanisms that tRNA genes use in 3D organization of genomes across species from yeast to flies to worms to mammals. The discussion needs expanding highlighting commonalities in mechanism across species.

*

We summarized mechanisms of tRNA gene clustering in different species in the final section of the revised discussion. To our knowledge, tRNA gene clustering was not shown outside yeast species.

* Reviewer #3 (Significance (Required)):

The manuscript builds on data from numerous organisms. The data show that tRNA genes function as chromosome organizing hubs in worms. The strength of this manuscript is the thoroughness of the experiments and the careful and accurate description of the results without any hyperbole. The weakness of this manuscript is a lack of discussion on the conserved mechanisms that tRNA genes use in 3D organization of genomes across species from budding yeast to fission yeast to flies to worms to mammals. The discussion needs expanding highlighting commonalities in mechanism across species.*

• *

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Referee #3

Evidence, reproducibility and clarity

The manuscript by Obaji et al entitled "TFIIIC regulates SMC complex binding and 3D contacts between tRNA genes" is a detailed molecular genetic characterization of the role of tRNA genes in the organization of the C. elegans genome. The manuscript builds on data from numerous organisms. The data show that tRNA genes function as chromosome organizing hubs in worms. The strength of this manuscript is the thoroughness of the experiments and the careful and accurate description of the results without any hyperbole.

The authors use auxin to induce depletion of essential protein subunits of TFIIIC, polIII and SMC. They follow the effect using western blots. They show significant depletion of these proteins within 1h. However, the western blots are not quantitative. They should titrate known quantities of purified proteins as standards in order to quantify depletion. Following depletion, the authors use ChIP Seq to map binding of these proteins at sites in the genome. The authors may wish to analyze the DNA sequence motifs that remain bound by TFIIIC following depletion for 1 hour compared to sequences that lose TFIIIC binding upon depletion. The same analysis should be performed for sites that remain bound after 22h. What are the chromatin signatures at these sites (from previous ChIP-Seq data). This analysis could highlight high-affinity sites for TFIIIC or specific chromatin signatures that aid in TFIIIC binding and residence time in chromatin. In Figure3 the authors analyze 3D contacts using HiC. Depletion of TFIIIC had minimal effects on average contact frequency. This is to be expected given that most contact sites are unlikely to be influenced by TFIIIC. There were subtle differences in separation on arms and centers upon depletion that appear to have a greater effect on smaller chromosomes. Is the density of TFIIIC sites greater on smaller chromosomes? This result is similar to data in yeast that show that tRNA genes have local effects on chromosome function rather than global effects. In Fig3D they analyze "insulation" on the X chromosome at a specific rex site and show that there are subtle changes. It is unclear if these are statistically significant and/or functionally important.

In Figure4A and 4B, the authors mutate the TFIIIC binding site at a specific tRNA gene on the X chromosome. This mutation eliminated TFIIIC binding but only reduced Dpy27 binding. Furthermore, the authors also investigated Dpy27 binding upon TFIIIC depletion and determined that depletion reduced Dpy27 binding at TFIIIC sites. These data suggest that TFIIIC may not be involved in "recruiting" Dpy27 but in stabilizing the binding at specific sites after it has been recruited.

In figure6 the authors deplete TFIIIC or SMC3 or Dpy26 and analyze tRNA contacts via HiC. They show that TFIIIC plays a role in the long-range contacts but are not cohesion/condensin dependent. This is interesting and needs to be highlighted. Is it possible that they utilize other proteins such as nuclear pore proteins. One weakness of this manuscript is a lack of discussion on the conserved mechanisms that tRNA genes use in 3D organization of genomes across species from yeast to flies to worms to mammals. The discussion needs expanding highlighting commonalities in mechanism across species.

Significance

The manuscript builds on data from numerous organisms. The data show that tRNA genes function as chromosome organizing hubs in worms. The strength of this manuscript is the thoroughness of the experiments and the careful and accurate description of the results without any hyperbole. The weakness of this manuscript is a lack of discussion on the conserved mechanisms that tRNA genes use in 3D organization of genomes across species from budding yeast to fission yeast to flies to worms to mammals. The discussion needs expanding highlighting commonalities in mechanism across species.

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Referee #2

Evidence, reproducibility and clarity

General Writing Comments

• Given that the strongest and most novel finding is TFIIIC's role in condensin/cohesin recruitment and boundary formation, the Introduction and Abstract would benefit from earlier framing around why SMC complexes localize where they do (i.e., boundary-element biology), rather than leading primarily with the transcriptional background of TFIIIC.
• In the Discussion, consider leading with the strongest, most novel results (SMC recruitment, tRNA gene 3D contacts) before moving to the more incremental arm/center compartmentalization findings.

Science Comments

HOT-site behavior vs. direct regulatory function. Because TFIIIC/ETC sites can behave as generically hyper-occupied regions in other organisms, the authors should more explicitly distinguish the possibility that TFIIIC directly regulates SMC recruitment from the alternative that TFIIIC and SMC complexes are both independently drawn to a shared class of highly accessible chromatin. Or that TFIIIC is generating a HOT site. A discussion of HOT sites vs TFIIIC sites would be helpful. Possible chromatin-opening role for TFIIIC at the 1 hr timepoint. Along the same lines. At 1 hr TFTC-3 depletion, condensin binding is lost specifically at sites where TFIIIC and DPY-27 binding overlap, while DPY-27 is retained at other, non-overlapping sites. This raises the possibility that TFIIIC helps maintain locally accessible chromatin that permits condensin binding, rather than (or in addition to) direct recruitment via protein-protein interaction. ATAC-seq under the same depletion conditions could help distinguish these possibilities.

More minor comments:

1. Quantify depletion efficiency. The claim of GFP signal loss (Fig. 1C) is currently supported only by representative images - please quantify mean GFP intensity per worm (auxin vs. no-auxin) across a sample of animals. Similarly, please quantify Western blot band intensity (Fig. 1B, normalized to tubulin, across replicates) rather than relying on visual inspection of a single blot.
2. Genome-wide confirmation that RPC-1 depletion leaves TFIIIC binding intact. Figure 4C shows TFTC-3 signal is retained at one representative locus after 1 hr RPC-1 depletion, but this is not shown genome-wide. Since the claim of an RNA Pol III-independent function for TFIIIC rests on RPC-1 depletion not affecting TFIIIC binding, please provide a genome-wide comparison (e.g., a heatmap or violin plot analogous to Fig. 1D) confirming this.
3. Reconcile genome-wide vs. locus-specific contact-frequency effects. The claim of "minimal impact on average contact frequency" (Supp. Fig. 3A) rests on a genome-wide P(s)/slope plot, which by construction averages over all loci and distances and could mask spatially localized effects. This appears to be in some tension with Fig. 3B/C and Supp. Fig. 3B, which show a visibly stronger arm-center mixing signal specifically at 22 hr TFTC-3 depletion. A quantitative summary distinguishing a modest genome-wide shift from a strong, spatially restricted effect diluted by averaging would strengthen this section. o Related: please provide statistics on the apparent partial rebound in B-compartment strength after 22 hr auxin treatment (Fig. 3B, bottom-right saddle values) even as A-compartment strength remains reduced.
4. Direct comparison between the scramble and depletion experiments (Figure 4). The Box A/B scramble experiment (Fig. 4A-B) and the TFTC-3 auxin depletion experiment (Fig. 4C-D) are presented as parallel lines of evidence but are never directly compared quantitatively. Is the reduction in DPY-27 binding at the scrambled locus comparable in magnitude to the reduction at TFTC-3-depletion-affected peaks genome-wide? A side-by-side comparison, or at least a statement about this, would strengthen the claim that both perturbations report on the same mechanism.
5. Single-locus scope of the scramble experiment. The Box A/B scramble was performed at only one tRNA gene (F56C3.t1). Please discuss whether this result is expected to generalize across tRNA genes broadly, or consider testing a second, independent locus to rule out gene-specific effects.
6. Figure/text mismatch for autosomal DPY-26 binding (Figure 5). The statement "DPY-26 binding to autosomes was weak" (p. 11) is illustrated by Fig. 5C, which shows an X-chromosomal region, not an autosome (autosomal DPY-26/SMC-3 tracks appear only in Fig. 5A). Please point the reader to the correct panel, or add a clearly labeled autosomal example alongside the X-chromosomal one so both are shown side by side.
7. Replicate-level concordance for Hi-C. All Hi-C data are presented as merged replicates; replicate-level correlation is not shown. A supplementary figure comparing the two biological replicates (e.g., stratum-adjusted correlation or scatterplots of key metrics such as insulation score or compartment strength) would let readers judge how robust the reported effects are across replicates.
8. Derepression as a potential mechanism. Neither the tRNA promoter scramble nor TFTC-3 depletion is accompanied by expression data. Since transcriptional derepression of genes near the scrambled motif or near TFIIIC-bound sites could confound the interpretation of reduced condensin/cohesin binding, even limited expression data (qRT-PCR at a few loci, or RNA-seq) would help rule this out. Otherwise, please discuss this caveat in the results.
9. Quantification of interchromosomal tRNA gene contacts. The intrachromosomal tRNA-tRNA contact enrichment is quantified with paired statistics (Fig. 6B), but the interchromosomal (trans) pileups shown in Fig. 7A are presented only qualitatively. Since the trans-chromosomal contacts are central to the argument against a pure loop-extrusion model, a matching quantification and statistical test would substantially strengthen this claim.
10. Basis for attributing reduced Hi-C fountains to "indirect effects." Supp. Fig. 4B attributes the loss of cohesin-mediated fountain signal after 22 hr TFTC-3 depletion to indirect effects of prolonged depletion, but no data directly distinguishes direct from indirect causes. Please either soften this interpretive claim or provide supporting evidence (e.g., a comparison against the 1 hr TFTC-3 depletion timepoint, which does not show this loss).
11. Reliance on an external dataset for condensin I/II clustering. The individual contributions of condensin I (DPY-26 TEV) and condensin II (KLE-2 TEV) to tRNA gene clustering (Fig. 6D-E) are assessed using a previously published dataset (Das et al., 2024) rather than the authors' own degron system. Please confirm that depletion timing/developmental stage are comparable enough to the rest of the study for direct comparison.

Additional Points Requiring Clarification

• Viability and developmental timing of depletion. The strains remain viable without auxin, with depletion restricted to the soma; some GFP signal and germ cell division are still observed at the 2-cell stage under auxin. Please clarify what this residual signal implies for interpreting phenotypes at the earliest depletion timepoints - could early developmental effects be underestimated if depletion is incomplete at this stage?
• Nature of the rex site overlapping a tRNA gene cluster (Figure 3D). One strong rex site sits near a cluster of four tRNA genes with higher TFTC-3 than RPC-1 binding. Since tRNA genes and rex sites are both classic examples of highly-occupied regions, the authors should discuss whether this overlap reflects a specific functional relationship between condensin I-DC recruitment and TFIIIC, or a more generic co-occurrence at hyper-bound loci - and whether this particular locus is representative of the other 16 strong rex sites analyzed in Fig. 3E.
• Strength of the DPY-27/TFTC-3 correlation. The correlation between DPY-27 and TFTC-3 ChIP enrichment across the X chromosome (r = 0.82, Fig. 3F) is notably strong relative to the RPC-1 correlation (r = 0.45) and, in our view, deserves more prominent discussion in the main text as one of the more compelling quantitative links supporting the model.
• Normalization for insulation score comparisons. Figure 3E reports Wilcoxon rank-sum p-values comparing insulation scores across conditions, but it is not stated whether a spike-in or other cross-condition normalization was used for the underlying Hi-C/ChIP data, and no per-site error bars or replicate spread are shown. Please clarify the normalization approach and, if possible, show replicate-level variability underlying these scores.
• Reference line for Figure 4B. A diagonal line with slope 1 would help readers visually assess the degree of deviation from a 1:1 relationship between wild-type and scramble-mutant ChIP enrichment, and should be added to this panel.
• tRNA gene positions relative to ChIP signal (Figure 4C). Please mark the positions of tRNA genes directly on this genome browser panel, since the spatial relationship between the TFTC-3/RPC-1/DPY-27 tracks and the underlying tRNA genes is central to the interpretation of this representative locus.
• Loop vs. compartment-level nature of tRNA gene interactions. It remains unclear whether the reported tRNA gene contacts (Fig. 6, 7) reflect discrete, loop-like interactions or a broader compartment-level clustering phenomenon. Given that these possibilities imply different underlying mechanisms, the authors should state explicitly which interpretation their data best support, or acknowledge that both may contribute.
• Explicit mechanistic model for TFIIIC-SMC recruitment. The manuscript would benefit from a clearer statement of which mechanistic model is favored: (i) TFIIIC acts as a loop-extrusion barrier/anchor, with tRNA gene interactions arising in cis (proximal or distal) or in trans as extrusion products; or (ii) TFIIIC recruits SMC complexes to sites independent of loop extrusion. The current data (weak but genome-wide insulation effects, plus trans contacts and DPY-26 TEV results that argue against extrusion alone) suggest a hybrid model - making this explicit would help readers evaluate the proposed self-organization model in Figure 7C.
• Statistical comparison of RNA Pol III recycling correlations. The claim that snoRNA genes show less efficient Pol III recycling than tRNA/ncRNA genes rests on comparing three Pearson correlation coefficients (0.36 tRNA, 0.38 ncRNA, 0.52 snoRNA; Supp. Fig. 2C) without a formal statistical test for whether these correlations differ significantly from one another.

Significance

This manuscript investigates whether TFIIIC regulates SMC complex (cohesin, condensin I, condensin I-DC) binding and 3D genome organization independent of its canonical role in recruiting RNA Pol III. Using auxin-inducible degradation of TFTC-3 (TFIIIC subunit) and RPC-1 (Pol III catalytic subunit) in C. elegans, the authors show that TFIIIC, but not Pol III, is required for cohesin and condensin binding at tRNA genes, and that TFIIIC specifically promotes long-range 3D contacts between distant tRNA genes. Depletion of individual SMC complexes does not eliminate these tRNA gene contacts, suggesting either redundancy among SMC complexes or an SMC-independent mechanism. The work is a well-designed and largely convincing dissection of a long-standing correlative hypothesis, separating the transcriptional and structural roles of TFIIIC.

The findings are exciting, since little is known about positioning SMC complexes in C. elegans, and more broadly, the relationship between TFIIIC and SMC in other systems. While correlations have been seen, I know only one paper showing reliance of condensin (II) and TFIIIC by the Gerton lab, but this was a broad knock down, not the elegant scramble experiments shown here. In addition, this paper broadens the relationship to other SMC complexes. I do have some questions/clarifications.

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Referee #1

Evidence, reproducibility and clarity

Summary: The manuscript by Obaji et al investigates the role of TFIIIC and RNA Pol III in the recruitment of SMC protein containing complexes (condensin IDC, condensin I, and cohesion), as well as their role in remodeling the 3D genome in C. elegans. Connection between TFIIIC, condensin, and 3D genome organization have been seen in other organisms, several cited by the authors. This works extends the idea to C. elegans. The authors perform a series of ChIP-seq and Hi-C experiments after depletion of TFIIIC or a subunit of RNA Pol III. The observed impacts are relatively minor, but TFIIIC does appear to play a role in recruiting condensin and cohesin to a subset of their binding sites, and it also plays a role in shaping the 3D genome. However, there does not seem to be the same level cooperation between SMC complexes and TFIIIC at tRNA genes as was previously described in yeast (Hausler et al 2006, Genes and Development). The paper is written in a very short format, and as a result some details, at times essential information (such as the antibodies used in the experiment) are missing. So some aspects of the work were hard to evaluate. Overall, the study describes some interesting findings, but the significance of the work is limited by the relatively minor effects observed.

The experiments were well done. My expertise is not in Hi-C data analysis, so I cannot comment on the quality of those aspects of the paper. Most of my concerns relate the how the experiments were described and how conclusions were drawn. Some of the conclusions should be qualified, but I am not sure if additional experiments would make the conclusions any stronger.

Major comments:

1. The information on what antibodies were used in the ChIP-seq experiments are missing. tftc-3 and rpc-1 were tagged with degron::GFP. Did the authors use anti-GFP antibodies? For other proteins analyzed, such as TFTC-5 and TBP-1, what antibodies were used? Are these antibodies validated/high quality?
2. To show that the tag did not interfere with gene function, the authors assessed lethality in the tagged strains. The data shown on Supplemental Figure 2 shows unusually high level of lethality in the no tag control. Only 20-40 eggs were counted for each data point. I would recommend counting more, and if the lethality remains in the no tag control, I would worry about the starting wild type strain having some background mutations.
3. After validating the strains and determining depletion conditions, the authors first analyze 3D genome organization. Compartmentalization weakens a bit, more obvious after 22 hours of TFTC-3 depletion, at which point they see increased interactions between the arms and the center of chromosomes. Additionally, a small increase in insulation is observed at TAD boundaries on the X chromosome. These data are described on Fig 3, and in general support the conclusions. In the legend, the authors mention to B-B, A-A, A-B. It was unclear what they refer to.
4. Next, the authors investigate impacts on condensin IDC binding. After 1 hour of TFTC-3 depletion, condensin IDC binding is reduced at a subset of sites that overlap with TFTC-3 sites (Fig 4). The authors refer to these as tRNA genes. While many of them are likely tRNA genes, not necessarily all. Either check whether they are all tRNA genes, or refer to them as TFTC-3 binding sites.
5. For one of these sites, the authors scramble the box A/B DNA sequence. Please explain how this experiment was done. Was it by replacing the endogenous sequence using crispr? In any case, in this mutant, TFTC-3, RPC-1 and DPY-27 binding all decreased. On Fig 4 B, binding seems to be decreased at many additional sites as well. Why is binding decreased at additional sites?
6. While not necessarily easy to answer, what I am most curious about is whether the change in condensin IDC binding at a subset of sites is actually biologically relevant. Is there an impact on dosage compensation?
7. While the experiments concerning condensin IDC binding were done after 1 hour of depletion (after 1 hr of TFTC-3 depletion RPC-1 is still bound), the experiments with cohesin were done after 22 hours of depletion (when RPC-1 binding is impacted). Therefore, the authors can conclude that condensin IDC binding is impacted by TFTC-3, but not RPC-1, but the same cannot be said for cohesin (Fig 5). The authors seem to imply that only TFCT-3 is involved and not RPC-1. In fact, data for 1 hr of TFTC-3 depletion is not shown. Addiotionally, the title of the section and the title of figure refer to these sites as tRNA genes, but tRNAs are not even mentioned in the text of this section. Are these in fact exclusively tRNA genes, or are they TFTC-3 binding sites.
8. In a very brief section, the authors describe the final finding, clustering of tRNA genes, which seems to depend on TFTC-3, but not RPC-1 or condensin or cohesin. While the rest of the paper investigates how TFTC-3 impacts condensin and cohesin, this data shows that condensin and cohesin are not working with TFIIIC in this process. The data is data, and I am not arguing with it, but the story does seem more disconnected than the title implies.

Minor comments:

1. TFTC-3 depletion seems quite effective, RPC-1 depletion a little less so. It should be mentioned in the text. Also, on Fig 1C, please explain the signal that remains after depletion. (The explanation is in the legend for Figure 2-it should be explained earlier.)
2. Supplemental Figure 3 legend refers to distribution of peak categories and cartoon interpretation that are not shown on the figure.
3. Figure 7 shows some new analysis described in the discussion. It should be in the results section.

Significance

My enthusiasm is a bit limited due to the minor impacts observed. Condensin and cohesin binding is only impacted at a subset of binding sites and it is unclear whether the changes affects condensin and cohesin function. Similarly, 3D genome organization did not change that much, and condensin and cohesin are not even involved in tRNA clustering. As a result, the study does not advance the knowledge in the field by a lot.

Audience: the study will be interesting to scientists in the 3D genome organization field, especially as a point of comparison to other systems.

My expertise is in chromosome structure and organization and condensin biology.

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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 manuscript identifies a previously uncharacterized mode of neuronal remodeling in dopamine neurons (DANs) of Drosophila melanogaster, which operates independently of canonical ecdysone signaling but relies on AKT-GSK3β signaling, cytoskeletal remodeling, and glial engulfment and elimination. While the study presents a novel developmental process with detailed analyses, several critical issues regarding mechanistic depth, significance, experimental design, and organization need to be addressed to strengthen the impact of the work.

Major Concerns

The mechanistic exploration heavily relies on pathways (e.g., glial involvement, cytoskeletal dynamics) previously validated in other models, limiting the novelty of the findings. The study would benefit from deeper investigation into how these pathways uniquely contribute to the described remodeling process. For instance, the observation that MP1 neurons target the MV1/junction region of mushroom body (MB) suggests a potential role in regulating γ neuron pruning and regrowth. However, this link remains unexplored. A deeper investigation into this connection is essential to establish the broader relevance of the proposed remodeling mode.

The authors note that PPL1 DANs consistently undergo neurodegeneration in Parkinson's disease (PD) models and propose a connection to AKT-GSK3β signaling. Yet, no experimental evidence is provided to link the described remodeling process to pathological neurodegeneration. This represents a missed opportunity to establish physiological or disease relevance.

The manuscript contains redundant descriptions and would benefit from concise restructuring. The language requires streamlining and improve clarity. For example: The Introduction lists multiple unresolved questions (paragraphs 2-4) without clearly defining the central scientific problem. In lines 211-218, references to Figures 1, 3, and 4F,H are disjointed and disrupt narrative flow. Consider integrating background details into the results for Figure 4 instead of presenting them prematurely.

A notable inconsistency is observed in the morphological appearances of neurons across different figures (e.g., GFP signals in Figure 4A vs. 4C at 24h and 30h APF; and vs. controls in Figure 7A and 7C). Uniform time points and representative images from biologically replicated experiments performed under identical conditions are required.

The analysis of EcR-B1 protein expression is insufficient. Protein level validation should precede genetic manipulation experiments. The use of "other brain regions" as a control is vague-specificity, antibody validation, and rationale for region selection must be clarified.

Minor Points

Figure 5A, Figure S5A, C-G lack necessary controls.

The relevance of AKT-GSK3β signaling in other neuronal types appears tangential to the core findings and may be better suited as supplementary material.

References for fly strains (e.g., EcR-B1-DN, GSK3β-DN, AKT-CA) are missing and should be cited appropriately.

Figure S7 presents statistical analyses without representative images, limiting interpretability.

Figure S3D should be rescaled to match the dimensions of Figure S3C for visual consistency.

Language should be polished throughout to improve clarity and conciseness.

Significance

This study systematically reveals an atypical "overgrowth pruning" mode of developmental remodeling in Drosophila PPL1 dopamine neurons during pupal stages. This process is independent of canonical ecdysone signaling but relies on neuron intrinsic AKT GSK3β pathway regulating microtubule stability and requires glial phagocytic activity for axonal debris clearance. The overall logic of the work is clear, the experimental system is complete, and the narrative is well structured.

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Referee #1

Evidence, reproducibility and clarity

In this manuscript, Zhang et al., describe the unique pruning and regrowth program of a specific set of dopaminergic neurons (DANs) in the third instar larvae of Drosophila CNS that share commonalities with the mammalian SNc dopaminergic neurons affected in PD. The authors convincingly show that during metamorphosis, unlike the known "pruning followed by regrowth' developmental remodeling program followed by gabaergic APL neurons and da sensory neurons, the MP1 dopaminergic neurons show a distinct and atypical pattern of initial overgrowth followed by pruning. The authors use elegant photoactivation in MP1 axon/soma to show that of the 3 DAN neurons in the region, only one undergoes developmental remodeling. Then they find that glial cells infiltrate the region and mediate endosomal engulfment of the axonal debris. Pruning of these neurons was found to be surprisingly not mediated by ecdysone signaling which led the authors to look into other signaling mechanisms. Screening around 60 genes involved in neuronal remodeling, the authors found a profound block in pruning with expression of DN GSK3b and CA AKT. Given that AKT negatively regulates GSK3b, the effect of DN GSK3b and CA AKT are in the same direction leading to inhibition of GSK3 activity, which the authors show leads to increase MT stability hence disrupting pruning. This is an important and well executed study that uncovers a new pruning paradigm with distinct cellular, signaling and molecular signatures relevant to a disease associated neuronal population. I strongly recommend publication of this important study with few minor revisions to improve readability.

Minor comments:

• All experimental data figures should indicate what n refers to? Is n the number of experiments? If so number of animals observed for each experiment should be indicated. example: n=10 larvae were quantified from three independent experiments.
• Figure 1A schematic will benefit from annotating the neuron populations (similar to Figure S1A). Can the MP1/ MP1o branch be marked on the schematic as well to make the projections easier to understand. Also, the soma's of DANs should be depicted in the schematic. The projection that overgrows in the later time point should be indicated by arrow in Figure 1A schematic.
• In the description of results (for Figure 3) please detail how the GRASP reconstitution experiment was performed. What crosses/markers were used for the MB and MP1o.
• Please show zoomed in images of Fig.4E, it is hard to see the colocalization of lysotracker with the debris.
• Please provide quantification of effect seen on pruning in Figure 6A-D.
• In Figure 7, it appears that staining with marker for stable MT (acetylated/detyrosinated tubulin)would be more helpful in discerning whether inhibiting GSK3beta is impacting MT stability rather than GFP-tubulin. If possible to stain these neurons, this data would improve interpretation.
• Figure S8 which shows the overgrowth and pruning paradigm for MP1 DANs would be useful to be in the main figures for ease of reading the manuscript.

Significance

This is an important study with several conceptual advances uncovering a new neuronal pruning paradigm that exhibits distinct cellular, signaling and molecular signatures relevant to a disease associated neuronal population.

These findings would be of high interest to audience in fields of neuronal degeneration and regeneration, signaling mediating neuronal homeostasis, Parkinson's Disease, and neuro-glial interactions.

My own expertise is in the field of kinase signaling in neuronal development and disease.

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Reply to the reviewers

We thank the reviewers for their time and their helpful comments and suggestions. In this updated version of the manuscript, we addressed the main concerns regarding autoactivity, carried out ion leakage assays of the tested NLR combinations and added the recommended negative controls. Additionally, we performed new confocal imaging experiments with a plasma membrane marker instead of FDA and carried out additional membrane fractionation replicates to strengthen our finding that the Pik complex accumulates at the plasma membrane. We replaced the previous data that included FDA and the autoactive constructs C-terminally tagged with mNeonGreen with this new experiment (updated Figure 3 and Figure S4). We replaced the previous membrane fractionation replicates with 2 new replicates showing that the H+ATPase does not show differential enrichment between samples. On these new replicates, we observed that Pikm-2 only accumulates in the membrane fraction, similar to that of the H+ ATPase control. These new data are now presented in Figure 3 and Figure S3.

Please find below a detailed response to each comment.

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

In this manuscript, Pai et al show that the NLR pair Pikm-1/Pikm-2 is putatively present as an hetero-oligomer at the plasma membrane in the inactive state. This report could show that the mechanisms of NLR inhibition are diverse and could potentially inform strategies to engineer synthetic NLRs. As such, it could be an interesting study. However, there are major issues in this study.

Major comments:

One major comment comes from the use of modified Pik receptors. In this study, the fact that GFP is seen in the Pikm-1 enhancer / Pikm-2 active complex in fig 4 may not represent the normal active state of the NLR pair. It is interesting that such a complex can exist, but the author should clarify figure 5 and precise that the complex represented is not an NLR-effector complex but an artificial NLR-GFP complex. It is claimed that the NLR pair oligomerizes at the plasma membrane in the inactive state. It cannot be ruled out that the pair is partially active when overexpressed. Activity of NLRs does not always result in cell death. In figure 2C, a mild chlorosis phenotype is clearly seen in the mcherry co-expression side. This experiment needs more controls (empty vector, use EV + Pikm-1, EV + Pikm-2) and some other proxy for NLR activation should be used to claim that the complex is inactive (gene expression or else as appropriate).

Answer: We carried out ion leakage assays in all previously tested combinations and added the suggested combinations of co-expressing Pikm-1 variants and Pikm-2 with Rx as negative controls. Rx provides a superior baseline for non-specific NLR overexpression effects compared to an empty vector control. The updated hypersensitive response assays can be found on Figure 1B, 2C and 4A with the corresponding ion leakage measurements at 24 hpi on Figure S1B and Figure S2.

This experiment demonstrates that only the functional combinations (Pikm-1 + Pikm-2 + AVR-PikD and Pikm-1Enhancer+ Pikm-2 + GFP) lead to significant increase of ion leakage compared to all other tested combinations, including the Rx controls.

While we observe mild chlorosis in some overexpression contexts (such as Figure 2C), our quantitative ion leakage data confirm that this does not amount to full cell death activation. We acknowledge the reviewer's suggestion to use gene expression proxies, however, this would require setting up an RNAseq experiment across multiple combinations (Pikm-1 + Rx, Pikm-2 + Rx, Pikm-1 + Pikm-2) that is beyond the scope of this project. Additionally, it has been shown in multiple studies that cell death serves as reliable readouts for Pik pair activation by effectors (https://doi.org/10.1038/s41477-018-0194-x; https://doi.org/10.1371/journal.pone.0238616).

I am not convinced by the confocal microscopy data presented in figure 3 and by the Co-IP data in figure 1.

Figure 3: The confocal microscopy presented in figure 3 needs some refining. This experiment may not be suitable to estimate the change in receptor localization as the difference is quantitative. We can always see some signal in the cytoplasm and putatively in the plasma membrane and it is difficult to evaluate what is signal and what is noise. A plasma membrane marker should be used in this experiment to conclude on the localization of the receptors.

Upper panels: It is claimed that Pikm-1 fully co-localized with fluoresceine when co-expressed with Rx. On the figure, I can see purple signal and blue signal that do not co-localize. Co-localization of Pikm-1 when co-expressed with Rx or Pikm-2 is not clearly different.

Most importantly, the images were not taken using the same magnification which prevents a clear comparison. Define FDA in the caption.

Answer: the aim of this experiment was not to measure the change in receptor localization, as this is not the correct setup for such an experiment. Indeed, as the reviewer pointed out, we expect to see signal in both cytosol and plasma membrane in all tested combinations based on the membrane fractionation experiment.

The aim was to identify in which membrane compartment Pik1 and Pik2 accumulate based on the membrane fractionation assays. The confocal imaging experiment suggests that Pikm-1 and Pikm-2 accumulate is the plasma membrane since they do not localize to any other membrane compartment. We updated the text and changed the order of Figure 2A,B and 2 C,D to emphasize this. Additionally, we conducted a new confocal experiment with N-terminally tagged LTI6b from Arabidopsis as plasma membrane marker.

Figure 1: Co-IP experiment shows many bands that may or may not be considered as background noise.

In the first lane, Pikm1-v5 is expressed with Rx-HA. On the v5 blot of the input, we can see a band at approximately 130kDa that is supposedly Pikm1-v5. On the HA blot, we can also see a band at 130kDa that is supposed to be Rx-Ha. However, on the third lane of the v5 input blot, Rx-v5 is much lower. Thus, it is not clear what this 130kDa band is. Size of Pik1 and 2 are said to be around 110kDa. In the IPv5 blot v5 part, lane 1 where Pikm-1-v5 is co-expressed with Rx-HA, we cannot see a clear Pikm-1 band at around 130kDa. Both Pikm1 and 2 bands are supposed to be around 130kDa on this gel, as indicated by the red arrows, but this size is very close to this non-specific band. Overall, there are too many non-specific bands to draw conclusions from this experiment.

Answer: We re-examined the blots and realigned the IP blots as we noticed a slight difference in migration between the input and IP gels.

Rx-2xv5 is 4.5 kDa smaller than Rx-6xHA (see below) so a slight difference in band migration is expected. Additionally, the Pikm-1 and Pikm-1Enhancer bands on the IP blot are visible at the top (close to the 130 kDa mark), although the signal was too strong to see a complete band. We added an arrow to clarify this. The space between the lower non-specific bands and the Pik band is wide enough to differentiate these.

We listed below the weight of each tagged construct for reference:

Pikm-2-6xHA: 122.04 kDa

Pikm-1-v5: 129.88 kDa

Pikm-1Enhancer-v5: 135.28 kDa

Rx-2xv5 110.51 kDa

Rx-6xHA 115.01 kDa

Minor comments:

I would like to ask the author to be careful about the use of jargon and to always define terms at first use. In the abstract, Pikm is not defined; in the introduction, ID is not defined, ZAR1, Sr35, WAI3 etc... The term Pikm1 "enhancer" is confusing, it seems that this protein is just a hyperactive version of Pikm-1. Please try to be more accessible to students and non-specialists, this field is becoming increasingly opaque for non-specialists.

Answer: we made the suggested adjustments. Enhancer is the published name of the nanobody that was integrated into the Pik chassis, so we clarified this in the introduction.

Figure 3:

A: Labels are not aligned with the lanes.

Page 7 "To determine whether treatment with the ligand would alter the Pik hetero-complex" this statement is confusing, this is not what you test.

Answer: we made the suggested adjustments.

Reviewer #1 (Significance (Required)):

This study is potentially interesting but the novelty is limited. The interaction of these NLRs was shown before. Here the authors do not show the nature of the complex, its stoichiometry. The presence of effector in the complex is shown using an artificial NLR and GFP that may not represent the normal complex. If the NLRs were forming oligomers and were present at the plasma membrane (and this is still not clearly demonstrated), the question is: How is the complex inhibited? If the authors were to describe this putative inhibition mechanism, this would be highly interesting.

Answer: while interaction between Pik-1 and Pik-2 was indeed demonstrated, their oligomeric state in the resting state has not been described. Identifying the stoichiometry of the complex and how it is maintained in an inactive state would require extensive structural biology work that proved difficult to conduct and is beyond the scope of this study.

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

Summary This manuscript investigates the resting-state organisation of the rice NLR pair Pikm-1/Pikm-2 and reports that these receptors form a ~1 MDa hetero-oligomeric complex that accumulates at the plasma membrane prior to activation. Using a combination of experiments (coIP, Blue Native-PAGE, subcellular fractionation and confocal microscopy) the authors provide evidence that both native and engineered Pikm-1 associate with Pikm-2 in a pre-activation.

The study addresses an important and timely question in plant immunity on how paired sensor-helper NLRs are organised before activation and offers some conceptual advances relevant to NLR mechanistic. The work is technically ambitious and generally well executed (proper controls, loading samples). However, some data presentation, interpretation and experiments, especially regarding membrane localisation, and proposed functional implications would benefit with further clarification.

Major comments

• Clarity and focus of the Introduction: Some paragraphs in the Introduction are very dense and read more like a review article than a research manuscript. While the background is comprehensive, streamlining several sections would improve focus and help guide the reader more directly toward the specific questions addressed in this study.

We shortened (-300 words) and restructured the introduction for better clarity.

• Interpretation of intermediate oligomeric status: Intermediate oligomeric bands are observed along the manuscript when Pikm-1 or Pikm-1Enhancer is expressed without Pikm-2. While mentioned, their possible significance is not fully discussed. Would this intermediates be functionally relevant, assembly precursors or artefacts of overexpression? A clearer discussion would help contextualise the ~1 MDa complex.In same lines, the statement "Overall, the biochemical nature of these puncta remains elusive, as they might consist of resistosome foci or clusters of inactive NLR complexes." would benefit from further clarification.

We added a couple of sentences to the “The Pik pair forms a hetero-oligomer in its resting state” discussion section to elaborate on the intermediate complexes. Regarding the observation of punctate, we do not have the proper system to study their dynamics in the Pik pair since the Pikm-2 constructs C-terminally tagged with fluorescent proteins are autoactive.

• The organisation of Figure 1C is somewhat confusing. I suggest rearranging the blot so that the Ponceau S staining is placed directly under the corresponding input lanes, as both should originate from the same membrane. The immunoprecipitated (IP v5) samples could then be shown below.

The suggested adjustments were made.

Given the central role of membrane localisation in the proposed model, the membrane fractionation data raise concerns. In Figure 3A, the decrease in soluble Pikm-1 upon co-expression with Pikm-2 is not clearly accompanied by a corresponding increase in the membrane fraction, whereas Figure S3 suggests a more pronounced enrichment. Similar inconsistencies appear for Pikm-2. In addition, the plasma membrane ATPase control shows variable enrichment between Figure 3A and Figure S3. Because these experiments underpin key conclusions about pre-assembly and membrane recruitment, I strongly suggest repeating and consolidating these fractionation experiments with clearer quantification.

We performed two additional replicates of the membrane fractionation experiment that shows consistent accumulation of the ATPase control in the total and membrane fractions. This now allows us to conclude that 1) Pik-2 accumulates in the membrane fraction and 2) Pik-1 is always present in both soluble and membrane fractions, but shows higher accumulation at the membrane in presence of Pik-2 compared to Rx. We added these new replicates to the main Figure 3D and Figure S3 and updated the text accordingly.

• The reference to Fig. 4"We detected a GFP signal (using anti-FLAG antibodies) at ~1 MDa only when GFP was co-expressed with Pikm-1Enhancer and Pikm-2EE. " is misleading as GFP is also detected in Pikm1 homo-oligomers at 480 kDa in Fig.4B anti FLAG lane 1. Please clarify, explain or acknowledge.

We clarified the statement to illustrate that a signal was observed at 1 MDa in the FLAG blot only where GFP was co-expressed in the Pik pair and not mCherry.

The confocal imaging data are not fully convincing as presented. The use of FDA as a cytosolic marker is acceptable, but the fluorescence intensity profiles differ substantially between samples (peaks vs slopes in fg3.B), and scale bars does not appear consistent, text cannot be read. Not all the presented images show the epidermal cell periphery. To strengthen the conclusions, the authors could consider use a plasma membrane marker (FM4-64 or PI) and/or plasmolysis assays to more definitively demonstrate plasma membrane localisation. Intensity plots should span comparable distances across conditions.

We attempted to image with a FM dye compatible with mCherry but the signal was always leaking into the cytosol, probably due to the fact that most constructs show auto activity. Alternatively, we identified that mTFP1 is not recognized by the nanobody Enhancer and thus Pikm-1Enhancer does not induce strong HR in presence of the N-terminally tagged mTFP1-AtLTI6b plasma membrane marker. We have thus repeated the confocal imaging experiments with this construct (Figure 3A).

• Several figures contain very small text, making them difficult to read (e.g. Fig. 1A, 1C, plots in Fig. 2B, and Fig. S4). Panel sizes in Fig. S4 are particularly small and should be enlarged.

We made the suggested adjustments.

• The authors state the use of Pikm2 EE to abolish downstream cell death but conclusive results from this experiments did not show any major difference in NLR pair association Pikm1Enh and Pikm2EE biochemichaly. A more explicit discussion on alternative activation models (e.g. conformational changes within a pre-assembled complex, changes in membrane topology or altered interactions with additional components) and how to address this issue would strengthen discussion section.

At this stage, we cannot rule out that Pikm2EE is a nonfunctional version of Pikm2 that cannot be activated. Hence we cannot conclude whether the Pikm-1/ Pikm2EE/GFP complex is truly activated and this is why we did not expand this discussion point. We edited this part of the discussion to better reflect this.

• OPTIONAL experimental suggestion: it would be informative to examine the dynamics of puncta formation using fluorescently tagged, non-autoactive versions of the NLRs during activation by GFP-HF, rather than relying on autoactive constructs.

These experiments could help clarify whether puncta formation reflects NLR activation or is instead a secondary outcome of autoactivity.

We agree that these experiments would help better understand the dynamics of puncta formation. Unfortunately, we haven’t yet identified a suitable Pik-1+ Pik-2 combination that is not autoactive when fused to fluorescent proteins. We are currently exploring indirect imaging techniques to circumvent this issue. However, the system is not yet ready for this study.

• OPTIONAL: For image clarity I suggest to add Size (kDa) to all WB and BN-PAGE gels.

We made the suggested adjustments.

Minor comments (including typos and presentation issues)

• Figure 3A: lane labels at the top of the blot appear misaligned and should be repositioned. Ponceau blot seems not to be "boxed" as in the other images.

• Figure 3B: scale bars are illegible; remove them from the images and report magnification or scale clearly in the legend.

• Labelling in different panels along S4 is hard to understand on Max projection or confocal plane. Please rewrite. Details on laser excitation and acquisition in the legend should be moved to M&Ms, currently missing. Also the number of cells with puncta now indicated as a fraction is not very indicative, I suggest making an additional graph with these quantifications.

• Figure 5. Please label the plasma membrane.

• In confocal microscopy (Methods), please indicate the acquisition wavelength ranges used for each fluorophore. Correct the reference from Figure S5 to Figure S4. Language and typographical issues

We made the suggested adjustments.

-Legend Fig1. "(kDa) are shown at left" to "on the left".

-Correct "focussing" to "focusing"

-"0.45 μM filter" to "0.45 μm filter"

-"leaf disk were sampled" to "leaf disks were sampled".

-Improve clarity in "High-order oligomeric resting states were also observed..." → "...have also been observed."

-Please cross-check Refs 33 and 72.

We made the suggested adjustments.

**Referees cross-commenting**

After reading both reports, I am quite pleased to noticed quite a bit of overlap between Reviewer 1's points and my own. Here is a summary of the main points I would highlight: -NLR constructs: 1) Both reviewers flagged that the GFP-tagged or "enhancer" Pikm-1 constructs might not fully reflect the natural NLR complex. 2) The claim that the hetero-oligomer at the plasma membrane is inactive is not completely supported-yet I acknowledge it is a complex task. Some additional controls or discussion are needed to make this clear (e.g., empty vector, single NLR expression or other activity readouts).

Thank you for the summary. As mentioned above, we have now added controls to the HR assays and carried out ion leakage assays to show that Pik-1 and Pik-2 co-expressed with Rx or without their cognate effector/ligand are not autoactive. We also added a new confocal imaging experiment with a plasma membrane marker and performed additional replicates of the membrane fraction assays. We hope this additional evidence strengthens the claim that the Pik pair is not autoactive in N. benthamiana and that the Pik complex accumulates at the plasma membrane.

-Evidence for inactivity1) Mild chlorosis or other subtle phenotypes suggest that overexpression might induce some activity. 2) I agree with Reviewer 1 that more functional evidence would strengthen the claim that the pre-assembled complex is truly inactive.

See comments above.

-Membrane localization: 1) The confocal images are hard to interpret quantitatively. Cytosolic signal, inconsistent intensity profiles and different magnifications make it difficult to conclude membrane localization. 2) Using a plasma membrane marker (like FM4-64) or alternatively plasmolysis assays would help, as would standardizing imaging parameters across samples.

See comments above.

• Co-IP and BN-PAGE data: 1) Background bands and ambiguous molecular weights make it tricky to confidently interpret oligomeric states-I would understand in some cases finding extra bands for using N.benthamiana transient expression, not so importnant SDS-PAGE in the CoIPs but given the poposed hypothesis oligomeric state for NLRs this should be better addressed, indicated or discussed. 2) Improvement on molecular weight markers, clearer labeling

Labelling and alignment with molecular weight markers have been refined. Additionally, the ~ 1 MDa band on the blue native is only observed upon coexpression of Pik-1 and Pik-2 and absent in other lanes where the same constructs are used, which demonstrates that this is not an non-specific band.

-Mechanistic interpretation: 1) The resting-state complex is very interesting and aligns with a recent study on NLR oligomer resting-state (Toth et al, 2026 Nature Plants). Since the data here does not fully explain how the complex is inhibited or regulated, I would also suggest authors to refer to that model in this study in their discussion. 2) Discussion should acknowledge this and consider alternative mechanisms, including conformational changes or other interacting partners.

We added this suggestion.

• Figures and clarity: 1) Several figures have small or misaligned text, illegible scale bars or confusing labels (especially Figures 1, 3, S4). 2) Terms should be defined at first use and should clearly explain acquisition parameters and molecular weight labels.

We have implemented these suggestions.

Overall: This work is technically solid and conceptually interesting, it aligns with the current direction in the field and proposes a new mechanistic model but it does not fully characterize it. Revisions are needed to clarify some aspects, provide additional evidence at least for inactivity status and subcellular plasma membrane localization. Other changes such as improve figure presentation, readability and format would also be required. Addressing all these points would make the manuscript much clearer, more convincing and ready for publication.

Reviewer #2 (Significance (Required)):

This is a strong and conceptually interesting study in a very challenging area of work that provides novel insight into the resting-state organisation of paired NLR immune receptors. The authors also acknowledge the limitations of the study as it is very challenging working biochemically with NLRs in the context of cell death. The experimental approach is elegant and adequate, and the findings will be of broad interest to the plant immunity community. Addressing the issues above, particularly figure clarity, membrane localisation evidence, and mechanistic interpretation will substantially strengthen the manuscript and its impact

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

Summary

This manuscript investigates the resting-state organisation of the rice NLR pair Pikm-1/Pikm-2 and reports that these receptors form a ~1 MDa hetero-oligomeric complex that accumulates at the plasma membrane prior to activation. Using a combination of experiments (coIP, Blue Native-PAGE, subcellular fractionation and confocal microscopy) the authors provide evidence that both native and engineered Pikm-1 associate with Pikm-2 in a pre-activation. The study addresses an important and timely question in plant immunity on how paired sensor-helper NLRs are organised before activation and offers some conceptual advances relevant to NLR mechanistic. The work is technically ambitious and generally well executed (proper controls, loading samples). However, some data presentation, interpretation and experiments, especially regarding membrane localisation, and proposed functional implications would benefit with further clarification.

Major comments

• Clarity and focus of the Introduction: Some paragraphs in the Introduction are very dense and read more like a review article than a research manuscript. While the background is comprehensive, streamlining several sections would improve focus and help guide the reader more directly toward the specific questions addressed in this study.
• Interpretation of intermediate oligomeric status: Intermediate oligomeric bands are observed along the manuscript when Pikm-1 or Pikm-1Enhancer is expressed without Pikm-2. While mentioned, their possible significance is not fully discussed. Would this intermediates be functionally relevant, assembly precursors or artefacts of overexpression? A clearer discussion would help contextualise the ~1 MDa complex.In same lines, the statement "Overall, the biochemical nature of these puncta remains elusive, as they might consist of resistosome foci or clusters of inactive NLR complexes." would benefit from further clarification.
• The organisation of Figure 1C is somewhat confusing. I suggest rearranging the blot so that the Ponceau S staining is placed directly under the corresponding input lanes, as both should originate from the same membrane. The immunoprecipitated (IP v5) samples could then be shown below.
• Given the central role of membrane localisation in the proposed model, the membrane fractionation data raise concerns. In Figure 3A, the decrease in soluble Pikm-1 upon co-expression with Pikm-2 is not clearly accompanied by a corresponding increase in the membrane fraction, whereas Figure S3 suggests a more pronounced enrichment. Similar inconsistencies appear for Pikm-2. In addition, the plasma membrane ATPase control shows variable enrichment between Figure 3A and Figure S3. Because these experiments underpin key conclusions about pre-assembly and membrane recruitment, I strongly suggest repeating and consolidating these fractionation experiments with clearer quantification.
• The reference to Fig. 4"We detected a GFP signal (using anti-FLAG antibodies) at ~1 MDa only when GFP was co-expressed with Pikm-1Enhancer and Pikm-2EE. " is misleading as GFP is also detected in Pikm1 homo-oligomers at 480 kDa in Fig.4B anti FLAG lane 1. Please clarify, explain or acknowledge.
• The confocal imaging data are not fully convincing as presented. The use of FDA as a cytosolic marker is acceptable, but the fluorescence intensity profiles differ substantially between samples (peaks vs slopes in fg3.B), and scale bars does not appear consistent, text cannot be read. Not all the presented images show the epidermal cell periphery. To strengthen the conclusions, the authors could consider use a plasma membrane marker (FM4-64 or PI) and/or plasmolysis assays to more definitively demonstrate plasma membrane localisation. Intensity plots should span comparable distances across conditions.
• Several figures contain very small text, making them difficult to read (e.g. Fig. 1A, 1C, plots in Fig. 2B, and Fig. S4). Panel sizes in Fig. S4 are particularly small and should be enlarged.
• The authors state the use of Pikm2 EE to abolish downstream cell death but conclusive results from this experiments did not show any major difference in NLR pair association Pikm1Enh and Pikm2EE biochemichaly. A more explicit discussion on alternative activation models (e.g. conformational changes within a pre-assembled complex, changes in membrane topology or altered interactions with additional components) and how to address this issue would strengthen discussion section.
• OPTIONAL experimental suggestion: it would be informative to examine the dynamics of puncta formation using fluorescently tagged, non-autoactive versions of the NLRs during activation by GFP-HF, rather than relying on autoactive constructs. These experiments could help clarify whether puncta formation reflects NLR activation or is instead a secondary outcome of autoactivity.
• OPTIONAL: For image clarity I suggest to add Size (kDa) to all WB and BN-PAGE gels.

Minor comments (including typos and presentation issues)

• Figure 3A: lane labels at the top of the blot appear misaligned and should be repositioned. Ponceau blot seems not to be "boxed" as in the other images.
• Figure 3B: scale bars are illegible; remove them from the images and report magnification or scale clearly in the legend.
• Labelling in different panels along S4 is hard to understand on Max projection or confocal plane. Please rewrite. Details on laser excitation and acquisition in the legend should be moved to M&Ms, currently missing. Also the number of cells with puncta now indicated as a fraction is not very indicative, I suggest making an additional graph with these quantifications.
• Figure 5. Please label the plasma membrane.
• In confocal microscopy (Methods), please indicate the acquisition wavelength ranges used for each fluorophore. Correct the reference from Figure S5 to Figure S4. Language and typographical issues -Legend Fig1. "(kDa) are shown at left" to "on the left". -Correct "focussing" to "focusing" -"0.45 μM filter" to "0.45 μm filter" -"leaf disk were sampled" to "leaf disks were sampled". -Improve clarity in "High-order oligomeric resting states were also observed..." → "...have also been observed." -Please cross-check Refs 33 and 72.

Referees cross-commenting

After reading both reports, I am quite pleased to noticed quite a bit of overlap between Reviewer 1's points and my own. Here is a summary of the main points I would highlight: - NLR constructs: 1) Both reviewers flagged that the GFP-tagged or "enhancer" Pikm-1 constructs might not fully reflect the natural NLR complex. 2) The claim that the hetero-oligomer at the plasma membrane is inactive is not completely supported-yet I acknowledge it is a complex task. Some additional controls or discussion are needed to make this clear (e.g., empty vector, single NLR expression or other activity readouts). - Evidence for inactivity1) Mild chlorosis or other subtle phenotypes suggest that overexpression might induce some activity. 2) I agree with Reviewer 1 that more functional evidence would strengthen the claim that the pre-assembled complex is truly inactive. - Membrane localization: 1) The confocal images are hard to interpret quantitatively. Cytosolic signal, inconsistent intensity profiles and different magnifications make it difficult to conclude membrane localization. 2) Using a plasma membrane marker (like FM4-64) or alternatively plasmolysis assays would help, as would standardizing imaging parameters across samples. - Co-IP and BN-PAGE data: 1) Background bands and ambiguous molecular weights make it tricky to confidently interpret oligomeric states-I would understand in some cases finding extra bands for using N.benthamiana transient expression, not so importnant SDSPAGE in the CoIPs but given the poposed hypothesis oligomeric state for NLRs this should be better addressed, indicated or discussed. 2) Improvement on molecular weight markers, clearer labeling - Mechanistic interpretation: 1) The resting-state complex is very interesting and aligns with a recent study on NLR oligomer resting-state (Toth et al, 2026 Nature Plants). Since the data here does not fully explain how the complex is inhibited or regulated, I would also suggest authors to refer to that model in this study in their discussion. 2) Discussion should acknowledge this and consider alternative mechanisms, including conformational changes or other interacting partners. - Figures and clarity: 1) Several figures have small or misaligned text, illegible scale bars or confusing labels (especially Figures 1, 3, S4). 2) Terms should be defined at first use and should clearly explain acquisition parameters and molecular weight labels. Overall: This work is technically solid and conceptually interesting, it aligns with the current direction in the field and proposes a new mechanistic model but it does not fully characterize it. Revisions are needed to clarify some aspects, provide additional evidence at least for inactivity status and subcellular plasma membrane localization. Other changes such as improve figure presentation, readability and format would also be required. Addressing all these points would make the manuscript much clearer, more convincing and ready for publication.

Significance

This is a strong and conceptually interesting study in a very challenging area of work that provides novel insight into the resting-state organisation of paired NLR immune receptors. The authors also acknowledge the limitations of the study as it is very challenging working biochemically with NLRs in the context of cell death. The experimental approach is elegant and adequate, and the findings will be of broad interest to the plant immunity community. Addressing the issues above, particularly figure clarity, membrane localisation evidence, and mechanistic interpretation will substantially strengthen the manuscript and its impact.

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

In this manuscript, Pai et al show that the NLR pair Pikm-1/Pikm-2 is putatively present as an hetero-oligomer at the plasma membrane in the inactive state. This report could show that the mechanisms of NLR inhibition are diverse and could potentially inform strategies to engineer synthetic NLRs. As such, it could be an interesting study. However, there are major issues in this study.

Major comments:

One major comment comes from the use of modified Pik receptors. In this study, the fact that GFP is seen in the Pikm-1 enhancer / Pikm-2 active complex in fig 4 may not represent the normal active state of the NLR pair. It is interesting that such a complex can exist, but the author should clarify figure 5 and precise that the complex represented is not an NLR-effector complex but an artificial NLR-GFP complex. It is claimed that the NLR pair oligomerizes at the plasma membrane in the inactive state. It cannot be ruled out that the pair is partially active when overexpressed. Activity of NLRs does not always result in cell death. In figure 2C, a mild chlorosis phenotype is clearly seen in the mcherry co-expression side. This experiment needs more controls (empty vector, use EV + Pikm-1, EV + Pikm-2) and some other proxy for NLR activation should be used to claim that the complex is inactive (gene expression or else as appropriate).

I am not convinced by the confocal microscopy data presented in figure 3 and by the Co-IP data in figure 1. Figure 3: The confocal microscopy presented in figure 3 needs some refining. This experiment may not be suitable to estimate the change in receptor localization as the difference is quantitative. We can always see some signal in the cytoplasm and putatively in the plasma membrane and it is difficult to evaluate what is signal and what is noise. A plasma membrane marker should be used in this experiment to conclude on the localization of the receptors. Upper panels: It is claimed that Pikm-1 fully co-localized with fluoresceine when co-expressed with Rx. On the figure, I can see purple signal and blue signal that do not co-localize. Co-localization of Pikm-1 when co-expressed with Rx or Pikm-2 is not clearly different. Most importantly, the images were not taken using the same magnification which prevents a clear comparison. Define FDA in the caption. Figure 1: Co-IP experiment shows many bands that may or may not be considered as background noise. In the first lane, Pikm1-v5 is expressed with Rx-HA. On the v5 blot of the input, we can see a band at approximately 130kDa that is supposedly Pikm1-v5. On the HA blot, we can also see a band at 130kDa that is supposed to be Rx-Ha. However, on the third lane of the v5 input blot, Rx-v5 is much lower. Thus, it is not clear what this 130kDa band is. Size of Pik1 and 2 are said to be around 110kDa. In the IPv5 blot v5 part, lane 1 where Pikm-1-v5 is co-expressed with Rx-HA, we cannot see a clear Pikm-1 band at around 130kDa. Both Pikm1 and 2 bands are supposed to be around 130kDa on this gel, as indicated by the red arrows, but this size is very close to this non-specific band. Overall, there are too many non-specific bands to draw conclusions from this experiment.

Minor comments:

I would like to ask the author to be careful about the use of jargon and to always define terms at first use. In the abstract, Pikm is not defined; in the introduction, ID is not defined, ZAR1, Sr35, WAI3 etc... The term Pikm1 "enhancer" is confusing, it seems that this protein is just a hyperactive version of Pikm-1. Please try to be more accessible to students and non-specialists, this field is becoming increasingly opaque for non-specialists.

Figure 3: A: Labels are not aligned with the lanes. Page 7"To determine whether treatment with the ligand would alter the Pik hetero-complex" this statement is confusing, this is not what you test.

Significance

This study is potentially interesting but the novelty is limited. The interaction of these NLRs was shown before. Here the authors do not show the nature of the complex, its stoichiometry. The presence of effector in the complex is shown using an artificial NLR and GFP that may not represent the normal complex.

If the NLRs were forming oligomers and were present at the plasma membrane (and this is still not clearly demonstrated), the question is: How is the complex inhibited? If the authors were to describe this putative inhibition mechanism, this would be highly interesting.

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Reply to the reviewers

The authors thank the reviewers for their extensive work.

All comments have been included in the revised manuscript.

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Referee #3

Evidence, reproducibility and clarity

Summary:

Zhao et. al. report that in progression of MASLD to MASLD-HCC, there is a disease stage-specific switch in which non-canonical NF-kB signaling replaces canonical NF-kB as the primary activator of Interleukin-32 (IL-32), forming an auto-amplifying inflammatory loop. The switch is enabled by FOXO1, which acts as a pioneer factor to maintain chromatin accessibility at the IL-32 and NF-kB loci. Functionally, IL-32 is coupled to lipid metabolism through DGAT2, but becomes uncoupled in HCC, where DGAT2 loss rewires NF-kB/ERK signaling without recapitulating global remodeling, sensitizing cells to inflammatory activation. The authors present evidence for their conclusions through matched transcriptomic and metabolomic data analysis of MASLD and MASLD-HCC cohorts generated in-house, and outside publicly available datasets (transcriptomic, lipidomic, proteomic, CHIP-seq, ATAC-seq). Evidence presented from MASLD and MASLD-HCC (tumor and adjacent non-tumor) shows correlation of IL-32 expression with dysregulated lipidomic and metabolomic intermediates, as well as alterations in expression of canonical and non-canonical NF-kB members and select metabolic proteins. Additional evidence to support their model is provided through analyses of publicly available datasets of disease-specific (MASLD, MASH-HCC, primary and metastatic HCC) and genetic modulation of pertinent factors (FOXO1, DGAT2, IL-32, NF-kB1, NF-kB2, others).

Major Comments:

1. The largest weakness in this study is the heavy reliance on already published datasets to argue the overall hypothesis. Specifically, the authors are proposing the involvement of a novel axis (EZH2-FOXO1-NF-kB-IL32-DGAT2) as important in driving progression from MASLD to MASLD-HCC. While the in-house MASLD / MASLD-HCC data are convincing, utilization of the public datasets seemed a bit haphazard, selecting datasets that fit their desired genetic manipulation, but not necessarily relevant to MASLD (hepatocytes). For example, while there were datasets derived from experiments on HepG2 cells, others were not hepatocyte or liver related, such as NFkB1-knockdown in MCF-7 cells. For the IL32-knockout experiments, these were only referred to as "cells", with the given reference (18) leading to a review article that did not describe these cells - are these relevant to MASLD? To remedy this limitation and strengthen the working model, I suggest running some validation experiments in hepatocyte-specific cells, particularly so that conditions can be strictly controlled.
2. Some of the evidence from public datasets was weak in that the p-values were not very significant (for example, Figure 2G, Figure 3B, Figure 3D {p-values shown in Figure S3a}, Figure 4D, etc) or low n's (PPAR analyses in Figure 2G looks to have only an n of 1, many others only had an n of 2). This again necessitates some validation studies, or at minimum other public datasets to strengthen conclusions.
3. The generation of the in-house MASLD and MASLD-HCC cohort datasets (matched histologic, transcriptomic and metabolomic data) are very useful and provide an important resource to integrate transcriptomic signatures with metabolic states and liver pathologies. However, I wasn't sure if the MASLD cohorts included MASH patients or were strictly MASLD with little inflammatory/immune involvement. Figure 1B shows the correlation between IL-32 expression and steatosis, but what is the S score on the x-axis? Is this the full NAS score, or only the steatosis component of NAS? If the former, what were the levels of immune involvement (this seems important to report)? For more severe cases (MASH samples, with substantial inflammation) what do the IL-32 expression levels show - Does it continue to increase, reach some plateau level, or go back to baseline? I think MASH samples should be included in this analysis. Additionally, as increased expression at the RNA level does not necessarily equate to increased protein levels, it would be useful to run western blots, immunohistochemistry and/or ELISAs for IL32 to confirm increased levels in your cohorts.
4. Some evidence from included public datasets involved mouse samples, but mice do not express IL-32 (as was indicated in text). Can you justify using these datasets as any results arising from this would not support IL-32 as being involved.

Minor Comments:

Figure 1C - may be more useful to show IL32 correlation to combined TAG length/saturation in a single graph (eg, medium chain low unsaturated, etc, instead of separate chain length and saturation states). Also, how are you defining TAG chain length? Medium chain TAG typically refers to attached fatty acids with chain lengths of 6-12 carbons (total in TAG 18 - 36), but in Fig S1A (and Fig 1D), you are showing mostly long chain TAG.

Figure 1D - What kind of cells are these? There is no description in the manuscript other than "IL32 CRISPR/Cas9 KO cells", and reference 18 (given in methods section) is a review paper that does not describe these cells. For your argument of the importance of IL32 in driving MASLD -> MASLD-HCC, at minimum these experiments should be run in a hepatocyte cell line. Experiments using a hepatocyte cell line (or better primary hepatocytes) where IL32 is knocked down, and then examine metabolomic changes is needed to support your argument.

Figure 1E-G - interesting analysis but does not necessarily implicate IL32 as a driver of these observations. Supporting this argument the IL32 KO data shown in Fig S1e-f, but again, what cells are these? Is it relevant to MASLD -> MASLD-HCC transformation?

Figure 2A - What are the genes in bottom of plot (NFkB1, ENPP2, etc)? Are these not significant? Please indicate in figure legend.

Figure 2B - "commons" in title is cut off

Figure 2C - What is the status of the other isoforms? Do they not change? I think include plots of these in supplement.

Figure 2D - This is the same as supplemental Figure S2A. I think replace 2D with S2A, or better is to include excel sheet in supplement listing metabolite, fold change and p-values.

Figure 3C - What does the dashed red line at variance = 0.2 indicate? Please include in legend.

Figure 3D - also shown in Figure S3a, but without p-values. Figure S3a would be better as main figure and removed from supplement. Also, "k" is missing in panel title

Figure 4A, B - Legends are reversed to panels

Figure 4C - what is the baseline for these, ie without LPS? Would be useful to include

Figure 4E - Need to indicate stat significance in legend (what significance is ****)

Figure S1A - names are cut off with unsaturation species greater than 10

Figure S1C - what about other IL32 isoforms? Do these stay the same or go down? It would be useful to also show these in supplement figure

Figure S3E - need to show p-values

Figure S5B - No call to figure panel in text

In text on page 11, "Besides, EZH2 expression inversely..." is duplicated

Significance

General assessment:

This study provides an interesting and important hypothesis explaining the transition from MASLD to MASLD-HCC, not only expanding basic biology knowledge, but also potentially leading to novel therapeutic and prophylactic interventions against MASLD-associated HCC. However, there are important points that need to be addressed before the study is ready for publication.

Advance: IL-32 and NF-kB signaling have been linked to both alterations in lipid metabolism and inflammatory signaling, particularly in HCC. This study would fill a gap showing an important regulatory connection of a switch from canonical to non-canonical NF-kB signaling in driving an IL-32 activity in driving progression to HCC in MASLD.

Audience: This study will be of interest to both basic scientists and clinical professionals, specializing in liver biology and disease, as well as mechanisms of oncogenic transformation.

Expertise: I have been studying liver development and diseases for over 12 years, with focus on MASLD/MASH, fibrosis, and cholangiopathies, with particular emphasis on lipid and sugar metabolism.

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Referee #2

Evidence, reproducibility and clarity

Using integrated multiomics analyses of two human cohorts spanning MASLD and MASLD-associated HCC (MASLD: n=114; paired HCC cohort: n=47), together with lipidomics, single-cell/spatial transcriptomics, and functional gene perturbation studies, this study aimed to resolve the paradoxical role of IL-32 in liver disease. The authors identified a disease-stage specific switch from canonical to noncanonical NF-κB (NFKB2/RELB) signaling as the primary driver of IL-32 expression, with FOXO1 maintaining chromatin accessibility to support this transition. While IL-32 is normally linked to lipid metabolism through DGAT2 in MASLD, this metabolic coupling is lost in HCC. DGAT2 loss rewires NF-κB/ERK signaling, increasing inflammatory sensitivity and sustaining a pro-inflammatory state. Overall, the findings demonstrate that IL-32 functions as a context-dependent regulator of metabolic and inflammatory signaling, with its regulatory network being reprogrammed during hepatocarcinogenesis to promote chronic inflammation and tumor progression.

Major comments:

1. This study is purely computational in nature. The functional gene perturbation analyses were conducted exclusively using sequencing data from relevant knockout or knockdown in vitro and in vivo models. Therefore, the evidence supporting the causal relationships proposed in the manuscript is limited.
2. Most of the conclusions remain speculative and require further experimental validation, particularly regarding the proposed role of IL-32 in promoting MASLD-associated HCC. Experimental validation of the proposed mechanisms in MASLD-associated HCC animal models would substantially strengthen the study.

Referee cross-commenting

I agree with the other two reviewers' comments regarding the need for additional experimental verification and stricter criteria for dataset selection to avoid bias.

Significance

This study provides a notable conceptual advance by resolving the long-standing paradox of IL-32 in liver disease and proposing a mechanistic framework for its context-dependent role during the progression from MASLD to HCC. Through integrated analyses of transcriptomic, metabolomic, lipidomic, single-cell, and spatial transcriptomic data from human cohorts, the authors identify a disease stage-specific switch from canonical to noncanonical NF-κB signaling and disruption of the IL-32-DGAT2 axis as key events that reprogram IL-32 from a metabolically linked factor in MASLD to a promoter of sustained inflammatory signaling in HCC. The findings will be of particular interest to the liver disease, hepatology, cancer biology, immunology, inflammation, and metabolism research communities, especially investigators studying MASLD/MASH progression, hepatocarcinogenesis, and the crosstalk between metabolic and inflammatory pathways. However, the impact of the study is tempered by the lack of direct experimental validation establishing the causal roles of the proposed mechanisms.

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Referee #1

Evidence, reproducibility and clarity

Summary:

The authors present an intriguing manuscript, IL-32 is a stress-responsive node locked in a non-canonical NF-κB inflammatory loop during MASLD to HCC transition, that outlines a novel IL32 - NF-kB signalling loop that is proposed to drive inflammation during liver disease progression to liver cancer. The MS includes examination of human patient cohorts with MASLD of increasing steatosis grade and a second group including matched HCC with normal adjacent tissue. Analysis of these samples drives the study. Work performed on these cohorts is supplemented by cell-based data and in vivo experiments, including analysis of existing datasets and new experimental work.

Major comments:

It is my opinion that significant limitations within this study need to be addressed before it could be considered suitable for publication. Figure-specific comments of major points for the authors to consider are included below. In a general sense, the main limitations of the currently presented study include:

1. Limited confirmation of patient findings with extant published large datasets of MASD/MASH
2. Lack of consistency in the in vitro systems examined for molecular insight, and particularly a lack of reliable liver-focused analysis
3. Inclusion of murine data to support conclusions on an IL-32 pathway when IL-32 is not present within mice.
4. Disconnected data on FOXO1 that is include but immaterial to the main proposed model.

Figure 1:

1. IL-32 analyses within the patient cohorts should be validated against extant published datasets on MASLD/MASH, for example Govaere et al. 2020 & 2023.
2. There is consistent mention in the intro and figurer text for potential IL32 crosstalk between hepatocytes and the immune environment. To what extent can changes in the immune population, for example, the increased neutrophils and pro-fibrotic macrophages present in MASH vs MASLD as potential responders to IL-32 explain context-dependent roles for early vs HCC IL32 expression
3. Were all IL-32 isoforms examined in this panel? Clarification needed for the focus on IL-32 B/g in the figure.

Figure 2:

1. To what extent are the altered consequences of IL-32 activity present in pre-neoplastic MASH? This could be examined in published datasets depending on disease features present in the S2 steatosis cohort vs S0/1.
2. An important in vitro experiment here would be to confirm that IL32 induction can be reliably modelled after lipid overload in human liver/HCC cell lines. As HepG2 and Huh7 are used at points in the study, this would be a good test. More physiologically relevant for MASLD than TGFb induction.

Figure 3:

1. Figure 3B links IL32 induction with HNF4a -mediated maintenance of the NFkB network. Many early HCC lesions actively suppress HNF4a as part of broader de-differentiation programming to drive tumorigenesis (for example- Ning et al. 2010). This is not recapitulated in the HepG2 cells. This needs to be engaged with and confirmed in additional liver cell lines (Huh7).
2. The main argument is that steatotic environment is the driving feature in MASLD/MASLD-HCC that causes IL32 activity. Cell work needs to reflect this by showing different or enhanced activity +/- lipid loading.
3. Figure 3C data is taken from T-cells? Again, this is not immediately relevant to the liver context without clear justification and supporting liver in vitro work.
4. The data presented in 3D and S3A appear to be duplicates. Was the experiment only conduced in the breast cancer MCF7 cell line? Given the proposed tissue and context-dependence of the pathway of interest, it is not sufficient to use a non-liver cell line here. Confirmation across HepG2 and Huh7 cells would be needed.
5. As mentioned by the authors later in the text, mice don't express IL32. In addition, the MC38 tumour cell lines used in the published dataset is a colon adeno carcinoma line. This is not a good fit for the proposed liver-centric model. For both reasons, analysis of murine transcriptional changes +/- NFKB2 o/e are not good support for the underlying proposed model. Data from humanised IL32 mice or from the human cell lines in lipid-loaded conditions would make a clearer argument here.

Figures 4/5:

1. Functional consequences of FOXO1 depletion should be confirmed across multiple human liver cell lines using a relevant approach (ie- lipid loading / 'MASLD'-like conditions). It is interesting the LPS stimulation of HepG2 cells +/- FOXO1 altered downstream DGAT2 and IL-32 in basal media, but not directly a good proof of similar regulation in fatty hepatocytes.
2. Similarly, analysis of FOXO1 regulation of NFkB target promoters within murine T-cells (Figure 5) is not a clear-cut mechanistic link to human liver data given the issues with murine models (no IL32) and non-liver cell type. Confirmation in liver-relevant systems needed.

Figure 6.

1. Genetic ablation studies presented in Huh7 cells should examine whether DGAT2 deficiency phenotypes are exacerbated in lipid-loaded conditions. They should also be generalised to an additional liver cell line (HepG2).

Significance

The paper has potential to add nuance to our knowledge of the molecular mechanisms that underpin MASLD to HCC transition in humans. The authors also identify a novel molecular link to explain disparate observations of IL32 activity in MASLD (disease-limiting) vs HCC (tumour-promoting). For these reasons, the findings presented in the MS would be of interest to the hepatology community and broader NF-kB field.

Further work could expand on these observations to determine whether local or systemic IL32 levels represent a viable biomarker for disease trajectory in MASLD. They could also provide initial support for targeted approaches against IL32 and non-canonical NFkB signalling in MASLD-HCC.

Reviewer expertise:

I am a mid-career PI with research interests based on identifying molecular rational for novel anti-cancer interventions against diet-induced HCC. My background is in the molecular biology of cancer with an emphasis on the development and characterisation of genetically engineered mouse models of disease.

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Reply to the reviewers

Manuscript number: RC-2026-03717

Corresponding author(s): Brian, Robinson

1. General Statements [optional]

The ability to adapt and respond to oxidative stress is a critical function for metazoans who encounter excess loads of oxidants from a variety of intracellular and extracellular sources. In this manuscript, we delineated a novel mechanism placing endolysosomal acidification upstream of stress activated protein kinase and innate immune signaling pathway outputs in response to oxidative stress in the Drosophila intestine. These findings shed light on important aspects of cell biology, developmental biology, and gastrointestinal pathobiology, and build upon prior observations implicating endolysosomal acidification as a direct modulator of cell-signaling cascades. Our manuscript received generally positive comments: "Overall, this is a well-executed genetic study. The experiments are generally well quantified, controlled, and presented in a logical manner. There is a substantial amount of original data, and these generally support the authors' conclusions" (Reviewer 1); "By linking intracellular vesicle acidification to tissue-level stress responses and intestinal homeostasis, the study addresses an important and potentially broadly relevant question" (Reviewer 2); "This study addresses a biologically important and understudied question: how organelle pH dynamics regulate inflammatory signaling in the intestinal epithelium under oxidative stress. The central finding that V-ATPase depletion is protective rather than sensitizing against oxidative stress is counterintuitive and novel, challenging the default assumption that lysosomal function is uniformly beneficial under stress conditions." (Reviewer 3). We are encouraged by this feedback and remain optimistic we can address concerns outlined below.

Several suggestions were raised to strengthen the manuscript, many which we have addressed and included in the revised manuscript (see section 3 below). There were additional experiments that were suggested which we believe will strengthen our manuscript but require some time to optimize and execute; we have devised a plan to address those concerns with additional experimentation (see section 2 below). Importantly, the additional planned experiments are highly feasible, and we have all the reagents in hand. Moreover, our strong preliminary data makes us confident they will corroborate the proposed model, while adding to the robustness of the data.

2. Description of the planned revisions

Reviewer 1

• As noted above, it remains unclear whether the protective effects of Vha44 depletion result specifically from reduced endolysosomal acidification or from another function of the V-ATPase complex. To distinguish between these possibilities, the authors could deplete additional genes required for endolysosomal acidification or V-ATPase assembly, such as auxilin/aux, and determine whether these manipulations phenocopy Vha44 depletion.

• Response and Plan: We believe that orthogonal methods to alter endolysosomal acidification would strengthen the argument that generalized endolysosomal acts as a key mediator of the protective effects versus other functions ascribed to V-ATPase activity. Therefore, we will test the ability of NHE2-IR, Aux-IR, and rbcn1a-IR to modify lifespan when depleted in the Drosophila intestine during oxidative stress. Given that NHE2-o/e has demonstrated similar effects in larval wing discs as VHA44-o/e, and shows similar effects on JNK signaling, we expect to see similar phenocopy in our model (PMID: 23335205).

• In addition, the conclusion that Vha44 depletion alters endolysosomal acidification currently relies on LysoTracker staining, which reports the accumulation of dye in acidic compartments but does not directly measure luminal pH. Additional data using more quantitative reporter, such as LysoSensor, could provide stronger evidence for altered acidification, as opposed to changes in endolysosomal vesicle size.

• Response and Plan: This suggestion was raised by multiple reviewers. Therefore, we will test the effects of VHA-depletion on modulating the activation of LysoSensor Green DND-189 (Molecular Probes catalog number L-7535), a cell permeable vital dye that is sensitive to endolysosomal pH. While we couldn’t find evidence that this reporter has been utilized in the Drosophila intestine, studies have demonstrated that it can effectively reflect endolysosomal pH in the Drosophila fat body. If utilization of the reporter proves challenging, we will also test the effect of VHA depletion on Cathepsin activity using the Cathepsin-B Assay Kit (Immunochemistry Technologies LLC, ICT937), which is dependent on endolysosomal acidification and which we have optimized in our lab in other studies.

• Does Vha44 depletion in ECs reduce the ROS accumulation caused by H₂O₂ or PQ? This question could be addressed using DHE staining or other validated ROS reporters....This distinction is important for the central mechanistic model.

• Response and Plan: We agree that by modulating antioxidant loads or ROS levels prior to stimulus, VHA depletion could modify sensitivity to oxidative stress and offer a mechanism distinct from the model proposed. Therefore, we will test whether VHA44-depletion alters the levels of ROS in intestines using the cell permeable ROS-sensitive dye ROS-star while also testing the levels of CM-H2DCFA via gut imaging and plate read. These are standard methods that have been utilized to assess the in vivo levels of ROS in metazoans, notable Drosophila intestinal tissues (PMID: 39730463).

• As shown in Fig. S1C, whole-body overexpression of Vha44 or VhaSFD shortens lifespan. Is overexpression of V-ATPase subunits in ECs sufficient to induce ROS accumulation, JNK/IMD signaling, cell death, or intestinal barrier dysfunction in the absence of exogenous oxidative stress? Testing this would provide a useful gain-of-function complement to the RNAi results and help establish whether elevated V-ATPase activity is sufficient to damage the intestinal epithelium.

• Response and Plan: We have generated new data that shows that overexpression of VHA in the intestine sensitizes animals to oxidative stress (see Fig 1F) and are currently in the process of analyzing downstream pathways (including p-JNK levels and DCP-1 levels). In a pilot experiment, we find that overexpression of VHA44 in the intestine drives hyperphosphorylation of JNK relative to control animals. Moreover, given studies that have looked at VHA-overexpression and have observed JNK-activation (PMID: 23335205), including p-JNK expression, we expect to observed p-JNK in the setting of oxidative stress in the intestine in VHA-o/e animals.

• Is EC-specific depletion of Tak1 sufficient to suppress oxidant-induced lethality? Since the authors propose Tak1 as a key regulator connecting oxidative stress and V-ATPase activity to JNK and IMD/NF-κB signaling, testing the effect of Tak1 RNAi on oxidant-induced mortality could provide important loss-of-function evidence for this model.

• Response and Plan: We agree with the assertion that if VHA modulates inputs into TAK1 to alter outcomes to oxidative injury, TAK1 loss should phenocopy VHA-depletion with respect to oxidative-stress induced lethality and in the intestine. We have obtained a validated RNAi transgenic line that targets TAK1 and are currently generating F1 offsprings to measure sensitivity to oxidative stress in Myo>TAK1-IR animals.

• Recent publications have provided data showing that the p38-MAPK pathway, including another MAP3K (Ask1) is an important ROS-responsive stress sensing pathway in Drosophila and in the midgut. It could be informative for Terry et al. to check whether the Ask1-Licorne-p38 pathway is also involved in the effects shown here.

• Response and Plan: We have purchased commercial antibodies for pp38 and plan to examine via immunofluorescence and western blot analysis whether VHA-depletion alters p-p38 levels during oxidative stress in the intestine. We note that in many studies, VHA is downstream of p38, and not vice versa as the reviewer postulates (PMID: 12210724). Moreover, we note that there are studies in model organisms that show VHA mutations yielding no effect on p38 levels or activation (PMID: 38678555).

• For Fig. 2A-D, higher-magnification images should be provided. The authors should also indicate whether Vha55-lacZ was induced in ECs, progenitor cells, or both.

• Response and Plan: As vATPase activation has been shown to regulate Drosophila ISC populations, and here we show a role in regulating EC populations, we agree with clarification to the cell type specificity of our effects. In pilot experiments, we find VHA55-lacZ localizes to PDM-1 positive (enterocyte) and focally PDM-1 negative (enteroblast and ISC populations); we are currently validating these finding using esg-GFP as a marker of immature (ISC and enteroblast) populations, where we will analyze VHA55-lacZ in this background in the setting of oxidative stress. We expect to find VHA55-lacZ in EC’s and progenitors, however, our strong genetic data clearly dissects a role of VHA in mature EC’s in regulating lifespan phenotypes. +

• Furthermore, since Vha55 is the proposed oxidant-induced V-ATPase subunit, it would be informative to test whether Vha55-RNAi produces protective effects similar to those caused by depletion of Vha44, Vha68-2, and VhaSFD in Fig. 1.

• Response and Plan: We have obtained a validated RNAi transgenic line that targets VHA55 and are currently generating F1 offsprings to measure sensitivity to oxidative stress in Myo>Vha55-IR animals.

• The effects of Vha44-RNAi on pJNK (Fig. 4C-D) and Rel-GFP (Fig.5C-D) appear relatively subtle in the representative images, although the fluorescence-intensity measurements indicate statistically significant differences. Because these observations are central to the proposed mechanism, we suggest that the authors validate them using a more quantitative assay, such as western blotting.

• Response and Plan: We agree that using an orthogonal method to test p-JNK and Relish levels would strengthen our assertion that VHA-depletion modulates inputs into these pathways. We will perform a western blot analysis of dissected Myo>+ and Myo>Vha44-IR intestines at baseline and 2-4 days post-treatment. Given the myriad of studies that show parallel findings between IF and Western blot for p-JNK analysis, we expect these data to support our model that VHA44 modulates inputs into innate signaling pathways.

• Although the Smurf assays support the conclusion that Vha44 depletion preserves intestinal barrier function, examining epithelial junction organization using markers such as Armadillo (Arm) or Discs large (Dlg) could provide more specific evidence of a barrier defect.

• Response and Plan: We have obtained Dlg antibody and validated our protocol on WT animals to detect septate junctions in Drosophila intestines. We will perform IF for DLG in Myo>+ and Myo>Vha44-IR animals to test whether the protected SMURF phenotypes maps to an in vivo marker of barrier function (preserved junctional DLG staining in enterocytes).

• In Fig. 5B-E, please add the "Myo1A>Vha44-IR vehicle" control. (minor comment)

• Response and Plan: We will examine Rel-GFP in Myo and Myo>Vha44-IR intestines at baseline (and by western).

Reviewer 2

• A single Vha55-lacZ reporter is insufficient to support the broader conclusion that oxidant exposure rapidly induces multiple V-ATPase subunits. As RNA samples are available, the authors should quantify the subunits functionally interogated by RT-qPCR following H2O2 and/or PQ exposure. Higher-magnification images of the R4-R5 region, together with cell-type markers, are also needed to identify the cellular source of Vha55-lacZ induction

• Response and Plan: We are intrigued with the model of broad activation of transcriptional programs that increase lysosomal membrane biogenesis and activity, including Vha subunit expression, in response to oxidative stress (notably CLEAR pathway activation). We agree with the reviewer that examining expression of multiple subunits might strengthen this result; thus, we are performing RT-PCR towards Vha44, VhaSFD, and Vha68 subunits in WT control and WT H2O2 exposed animals. In pilot data, we find that expression of each subunit is increased with H2O2 exposure, however, this experiment was under-powered to include in our currently revised manuscript. We plan to repeat this experiment with increased biologic replicates. +

• PQ has previously been shown to activate JNK in multiple cell types of the adult female intestine (Biteau et al., 2008; PMID: 18940735; doi: 10.1016/j.stem.2008.07.024). Higher-magnification of phospho-JNK images, combined with cell-type markers, are therefore required to establish which cells respond to oxidative stress in the adult male intestine and how this response changes following enterocyte-specific Vha44 depletion.

• Response and Plan: We have modified the text to note this uncertainty. The Biteau et al., results and our own imaging indicate JNK activity is broadly upregulated in multiple cell types in the intestine following oxidative stress and the reduction of this upregulation does not appear to be cell type specific following EC-specific Vha44 This may reflect non-autonomous amplification of this pathway during stress. In parallel, we have set up crosses to examine puc-lacZ JNK pathway transcriptional activity reporter, as was done in PMID: 18940735, in Myo and Myo>Vha44-IR backgrounds, and will co-stain with PDM-1 to delineate enterocyte and non-enterocyte (EB, ISC) populations. The nuclear localization of puc-lacZ allows for easier cell type delineation than pJNK stain.

Reviewer 3

• Given that the manuscript's central argument revolves around endolysosomal acidification, it is imperative to incorporate ratiometric, pH-calibrated measurements to substantiate the paper's key findings. We recommend that the authors consider this addition.

• Response and Plan: This concern was also raised by Reviewer 1 (see above). We will test the effects of Vha-depletion on modulating levels of LysoSensor Green DND-189 (Molecular Probes catalog number L-7535), a cell permeable vital dye that is sensitive to endolysosomal pH. While we couldn’t find evidence that this reporter has been utilized in the Drosophila intestine, studies have demonstrated that it can effectively reflect endolysosomal pH in the Drosophila fat body. If utilization of the reporter proves challenging, we will also test the effect of Vha depletion on Cathepsin activity using the Cathepsin-B Assay Kit (Immunochemistry Technologies LLC, ICT937), which is dependent on endolysosomal acidification and which we have optimized in our lab in other studies.

• *...but never measured Vha44 protein levels in the knockdown intestine. V-ATPase subunits may exhibit compensatory upregulation or incomplete knockdown; therefore, validation at the protein level is crucial for interpreting the magnitude and completeness of loss of function. *

• Response and Plan: We have obtained an endogenous Vha44-GFP transgenic line that has been previously used to assess for Vha44 levels in Drosophila tissues (PMID: 23335205). Additionally, we will perform RT PCR to validate knockdown in transgenic Myo>Vha44-IR, Myo>Vha68-IR, and Myo>VhaSFD-IR animals.

• Repeat key survival and signaling experiments with Myo1A-Gal4, tub-Gal80ts to confirm that the protective phenotype is due to adult V-ATPase depletion rather than developmental effects.

• Response and Plan: To test that our phenotypes are not secondary to a developmental defect, we have crossed Myo-TS to control and UAS-Vha44-IR flies (as suggested by the reviewer) and will reduce knockdown by maintaining at the restrictive temperature during embryonic and larval development and test fitness to oxidant challenges in adults and the permissive temperature. We note that Myo1A-Gal4 driven depletion of V-ATPase subunits does not result in pupariation delay, nor any fitness defect (in fact vehicle lifespan is enhanced Figs 1G, S1E), and eclose morphologically unremarkable guts.

• (minor comment)....A more rigorous approach would be to measure AMP expression in dissected fat body or gut-free carcass tissue. This is a minor point but affects the strength of the "local vs. systemic" conclusion.

• Response and Plan: We plan to examine Myo and Myo>Vha44-IR guts and carcasses (which are mostly fat body tissue and muscle) in setting of oxidative stress and will perform RT-PCR towards target AMP genes discussed previously.

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

Reviewer 1

• *In Fig. 4L, please add a comparison between "Myo1A>UAS-Bsk" and "Myo1A>Vha-IR, UAS-Bsk" groups. *

• Response: The text has been revised, and we have added significance to graph and updated legend: “Log-rank (Mantel-Cox) test with Holm-Šídák correction for multiple comparisons; brackets indicate the comparisons tested.”

• Please add the "Myo1A>Tak1 vehicle" and "Myo1A>Tak1, Vha44-IR vehicle" controls in Fig. 6G-H.

• Response: We have revised Fig6 G-H to have the groups indicated by this reviewer.

Reviewer 2

• The evidence for intestinal enrichment of V-ATPase subunits is based largely on FlyAtlas 2 data presented in Figure 1B, which is unreadable at the current size and resolution. The authors may complement this analysis with publicly available adult intestinal single-cell or single-nucleus RNA-sequencing datasets to establish, which cell populations express the relevant V-ATPase subunits.
• Response: We had added new data generated from Fly Cell Atlas single-nucleus data (see Fig S1A) and text: “Complementing this tissue level data, analysis of publicly available single-nucleus RNA-sequencing data from Fly Cell Atlas indicates that these V-ATPase subunits are expressed across all major midgut cell populations in adult flies (S1A Fig, data from [50])” and correlates with Myo1A expression.
• The stress-survival and lifespan experiments appear to include very few animals, in some cases (n=11). Given the inherent variability of these assays, also evident from the control groups throughout the study, such sample sizes are insufficient to support robust conclusions. Survival and lifespan experiments should include several replicate vials, adequate cohort sizes, preferably approximately 100 or more flies per genotype and condition, and independent repetitions performed at different times (Piper and Partridge, 2016; doi: 10.1007/978-1-4939-6371-3_18, PMID: 27730590). Because these assays form the foundation of the study, the Methods should specify the number of flies per vial, the number of vials per genotype and condition, the definition of (n), and the number of independent experiments. Independent experiments might be provided as supplementary figure.

• Response: We have revised the text and sample sizes are listed in legends. Additionally, the definition of n has been updated in methods. The robustness of our effect is shown through knockdown of multiple V-ATPase subunits and bidirectionality of the effect is now shown with V-ATPase subunit overexpression. For our survival experiment with the fewest animals (Fig 6A), we will conduct additional survival replicates to increase the power of our observations.

• It appears that the same Myo1A>+ control survival curve may have been used in Figure 1C and Supplementary Figure S1A. The authors should clarify whether these data originate from the same experiment and if so stated the fact in the figure legend.

• Response: As the reviewer notes, these data did originate from the same experiment. The figure has been updated to make this more clear such that all results from the experiment are in Fig 1C and this is indicated the text: “While little effect was observed with esg-driven RNAi expression, we find that depletion of each of these V-ATPase subunits from ECs suppresses oxidative stress-induced lethality (Fig 1C-D). In parallel, we tested whether genetic depletion of cathepsin D, the principal lysosomal aspartic protease [48, 56], could impact organismal survival in the setting of oxidative stress. In contrast to V-ATPase subunit depletion, we find that depletion of cathD is not protective to H2O2 exposure (Fig 1C-D).”

• It is important to discern whether improved survival could result from reduced feeding, and therefore reduced oxidant intake, rather than protection caused directly by decreased V-ATPase activity in adult enterocytes. The authors should quantify food intake under control and oxidant-treated conditions for the key genotypes and document developmental timing, adult body size and baseline intestinal morphology. Ideally, key findings should be confirmed using an adult-inducible (TARGET or a drug-inducible) system to restrict transgene expression to adulthood.

• Response: In new data we generated, we show that while H2O2 alters food intake in animals, the amount of food intake remained the same between control and VHA-depleted animals (S1B Fig). As mentioned above, we plan to use the TARGET system (Myo-TS) to restrict VHA depletion during development and then challenge animals at the permissive temperature as adults.

• The authors should state whether the driver and RNAi stocks were backcrossed into a common genetic background.

• Response: To clarify, we have added the following text to our methods to clarify genetic backgrounds: “All driver and RNAi knockdown experiments were performed in heterozygous test progeny to control for background differences.”

• Several microscopy panels are too small, and the green/cyan color combination provides insufficient contrast. In Figure 3E-H, DAPI, hid-GFP and Dcp-1 signals cannot be reliably distinguished. Enlarged views and separate grayscale channels should be provided.

• Response: Figures have been updated to use higher resolution images, the green/cyan color combination has been replaced, and separate grayscale channels have been provided.

• Several important conclusions rely on image-based measurements, yet the Methods provide insufficient information about image acquisition and analysis such as exposure settings across genotypes, background subtraction, normalization procedures, thresholding, and measures used to control inter-experimental variability. They should also state whether imaging and quantification were performed blinded to genotype and treatment.

• Response: We have updated our methods to clarify image-based measurements: “Laser settings were kept the same across genotypes for each stain. Image analysis was performed in Fiji image processing software. Mean fluorescent intensity for each gut was obtained by averaging three 50um2 regions from the R4/5 region of each gut, thereby capturing variation within each gut. For LysoTracker Red area measurements thresholding was performed with Fiji as described in [52].”

• It would be helpful to describe the nature of the Rel-GFP reporter. Is it a transcriptional reporter or a Relish protein fusion? If it is a protein fusion, active Relish would be expected to show nuclear enrichemnt of its active N-terminal fragment. However, the signal in Figure 5H appears predominantly cytoplasmic even after H2O2 The authors should explain this observation and quantify nuclear versus cytoplasmic signal.

• Response: We have revised the text to clarify the nature of the Rel-GFP reporter: “Relish is activated by endoproteolytic cleavage, which releases the N-terminal Rel homology domain to the nucleus while the C-terminal ankyrin repeat fragment is retained as a stable protein in the cytoplasm [86, 87]. Because this Rel-GFP reporter is a C-terminus tagged Rel-GFP fusion protein, GFP remains in the cytoplasm following Relish activation by cleavage thus nuclear:cytoplasmic ratio could not be assessed, and it reflects Relish abundance rather than nuclear translocation.”

• In Figure 6G,H, some groups appear to contain only three observations. With (n=3), normality and equality of variance cannot be meaningfully assessed, weakening the justification for a parametric one-way ANOVA. Šídák correction addresses multiple comparisons but does not resolve violations of the assumptions underlying ANOVA.

• Response: We have updated the text to address this concern. The legend has been updated to state: “Each point represents an independent biological replicate of 10 flies; n=3-5 for each genotype. Given the wide variance and small number of replicates, no inferential testing was performed.” Additionally, the results section has been modified to clarify comparisons: “However, in animals with EC-specific Tak1 overexpression mean whole-body DptA was higher in Tak1-overexpressing animals and lower upon Vha44 co-depletion, with AttC showing the same direction. Replicate-to-replicate variability was substantial, and these differences were not tested statistically (Fig 6G-H)”

• The relevant age and sex of the animals should be stated in each figure legend.

• Response: We have updated the text to indicate the sex of animals on all graphs on survival curves. To clarify, males were used throughout all other experiments and ages were kept consistent, this has been updated in all relevant parts of methods “Males of the specified genotypes were collected 2-5 days post-eclosion and placed on vehicle or drug treated food.”

• The authors should define precisely what is meant by "lysosomal membrane reporter expression."

• Response: We have clarified text: “Consistent with expansion of the lysosomal membrane compartment, steady state levels of GFP-tagged Lysosomal-Associated Membrane Protein 1, LAMP1-GFP,…” and “steady-state levels of lysosomal membrane protein reporter”

• The authors should also discuss whether the observed responses may be sex-specific or provide corresponding evidence from females.

• Response: In new data (see Fig S1D), we show that “Protection was likewise not sex-specific, as EC-specific Vha44 depletion also extended survival in females fed H₂O₂ (Fig S1D).”

• the authors should consider the potential impact of V-ATPase deficiency on endocytosis, nutrient absorption or other aspects of enterocyte physiology.

• Response: We have expanded our Discussion to include the impact of V-ATPase deficiency on endocytosis, nutrient absorption or other aspects of enterocyte physiology “V-ATPase can support endocytosis and nutrient absorption in addition to lysosomal proteolysis and signal transduction, and we cannot exclude contributions from these processes. However, Vha44-depleted animals eat normally (S1B Fig), maintain barrier function (Fig 3A-C) and live longer on unchallenged food (Fig 1G), arguing against globally compromised enterocytes. Yet direct assessment of nutrient absorption and endocytic flux in Vha44-depleted enterocytes remains an open question.”

• An important unresolved issue is whether the identified V-ATPase-dependent mechanism is specific to oxidative stress or represents a more general response to intestinal damage, dysbiosis, or pathogenic infection. Direct comparisons, or at least a more comprehensive discussion of these contexts, would help increase the study relevance to broader readership.

• Response: We have added new data which highlights the specificity of these effects, including new data that shows VHA-depletion does not protect against DSS-induced intestinal injury. These findings support the model that VHA-mediated protection is specific to oxidative injury. We have updated the text of the Results to document these findings: “However, this protection appears specific to oxidative injury as neither depletion nor overexpression of Vha44 in ECs altered survival following exposure to dextran sodium sulfate (DSS) (Fig 1H), which damages the intestine through disruption of the basement membrane [59].”

Reviewer 3:

• Without at least a basic characterization of aged Vha44-depleted flies (e.g., age-dependent barrier function, gut pathology, or signaling), the lifespan claim should be qualified as preliminary or removed from the main conclusions.

• Response: We have revised the text to qualify the preliminary nature of these findings: “…and potentially implicate intestinal endosomal acidification as a regulator of lifespan and aging in metazoans.” “reduced endolysosomal amplification of stress signaling may lower the baseline inflammatory tone that accumulates with age, though this remains to be tested directly”.

• Some figure legends lack explicit definition of which groups are being compared. Please ensure all statistical comparisons are explicitly defined in every figure legend.

• Response: We have updated the text to clearly state that “Brackets indicate the comparisons tested” and added this text to the relevant legends.

• *The heat map of V-ATPase subunit expression across adult tissues is described as "adapted from FlyAtlas 2 data" in the text but this attribution is not included in the figure legend. Please add the data source attribution to the figure legend for clarity and proper credit. *

• Response: Our text indicates the source of the data used to generate the heat map, including: “Heat map of V-ATPase subunit transcript levels across adult tissues, generated from FlyAtlas 2 data [55]”

• The finding that DSS does not induce Vha55-lacZ expression (Fig 2D-E) is interesting and potentially informative, it suggests that V-ATPase upregulation is specific to oxidative injury rather than a generic stress response. However, this is mentioned only in passing in the Results. The authors should either discuss why DSS differs mechanistically from oxidant injury.

• Response: We agree with the reviewer that this is an intriguing observation and have updated our discussion to articulate this findings: “The V-ATPase requirement is also insult-specific. Oxidant exposure induced Vha55-lacZ and oxidant induced lethality was sensitive to V-ATPase depletion, whereas DSS did not induce Vha55-lacZ and lethality was unaffected by Vha44 expression modulation (Fig 2A-D, Fig 1H). This is unlikely to reflect absence of injury, as DSS reduced survival in our hands and is an established inducer of compensatory basement membrane damage and compensatory proliferation in the Drosophila DSS incorporates into the intestinal basement membrane so the primary lesion is extracellular and basal, whereas, oxidants act on enterocytes directly, generating damage that drives JNK and IMD/NF-κB. That endolysosomal acidification is neither engaged by nor required for the response to DSS indicates that it is not a general injury-response amplifier and may instead be specifically coupled to oxidative damage in the intestinal epithelium. However, while manipulating Vha44 levels does not influence survival on DSS, depletion of Vha44 and other V-ATPase subunit transcripts extends survival and overexpression of V-ATPase subunit transcripts decreases survival on vehicle food alone. How V-ATPase activity shapes lifespan in the absence of injury and the mechanism underlying this effect remains an open question.”

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

Reviewer 2

• Furthermore, the vehicle-treated intestines in Figure 5F,G appear different from those in Supplementary Figure S5A,B. In one case, the signal appears predominantly associated with enterocytes, whereas in Figure S5A,B it appears to label ISC/EB-like cells. This discrepancy should be addressed using higher-resolution images and appropriate cell-type markers.
• Response: The vehicle-treated intestines in 5F,G are Drs-GFP while S5A,B are Rel-GFP, thus the pattern of expression is distinct and based on the reporter.

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Referee #3

Evidence, reproducibility and clarity

The manuscripts "Endolysosomal acidification amplifies JNK and IMD/NF-κB signaling and exacerbates oxidative injury in the Drosophila intestine" presents a novel and biologically interesting finding with a solid genetic foundation. The counterintuitive protective effect of V-ATPase depletion against oxidative stress is well-supported by multiple lines of genetic evidence. However, for publication at EMBO Journal, the mechanistic depth needs to be strengthened, the specific issues that need to be focused on are as follows:

Majors:

1. The entire interpretive framework of this paper is predicated on the premise that V-ATPase depletion leads to a reduction in endolysosomal acidification, which subsequently attenuates JNK/IMD signaling. However, the sole functional readout for acidification employed is LysoTracker Red staining (Figure 2F-I). In addition to pH, LysoTracker accumulation can be affected by factors such as vesicle volume, membrane potential, and dye uptake kinetics. Given that the manuscript's central argument revolves around endolysosomal acidification, it is imperative to incorporate ratiometric, pH-calibrated measurements to substantiate the paper's key findings. We recommend that the authors consider this addition.
2. All key conclusions depend on RNAi-mediated depletion of Vha44 (as well as other subunits). The paper indirectly demonstrated transcriptional-level effects through the Vha55-lacZ reporter gene (a different subunit) and qPCR of downstream pathway targets, but never measured Vha44 protein levels in the knockdown intestine. V-ATPase subunits may exhibit compensatory upregulation or incomplete knockdown; therefore, validation at the protein level is crucial for interpreting the magnitude and completeness of loss of function. Furthermore, no RNAi-resistant rescue experiments were provided to rule out off-target effects.
3. Both whole-body and EC-specific Vha44 depletion extend lifespan on normal food. This is a significant claim that broadens the study's relevance to aging, but the mechanism is not explored. Is lifespan extension due to reduced basal JNK/IMD signaling? Reduced EC apoptosis? Altered gut microbiota? Improved age-dependent barrier function? Without at least a basic characterization of aged Vha44-depleted flies (e.g., age-dependent barrier function, gut pathology, or signaling), the lifespan claim should be qualified as preliminary or removed from the main conclusions.
4. The experiments use constitutive Myo1A-Gal4 to drive RNAi from development through adulthood. V-ATPases are essential for many developmental processes, and even though Myo1A is constitutive expression during pupal development could alter gut architecture, EC differentiation, or basal physiology in ways that confound the adult stress response. Repeat key survival and signaling experiments with Myo1A-Gal4, tub-Gal80ts to confirm that the protective phenotype is due to adult V-ATPase depletion rather than developmental effects.

Minors:

1. The conclusion that oxidant-induced IMD activation "remains confined to the intestinal epithelium" at 48h (line 261) is based on whole-animal DptA/AttC measurements. However, whole-animal RNA extraction includes the gut, so a lack of induction could reflect dilution by non-induced tissues rather than true confinement to the intestine. A more rigorous approach would be to measure AMP expression in dissected fat body or gut-free carcass tissue. This is a minor point but affects the strength of the "local vs. systemic" conclusion.
2. Some figure legends lack explicit definition of which groups are being compared.Please ensure all statistical comparisons are explicitly defined in every figure legend.
3. The heat map of V-ATPase subunit expression across adult tissues is described as "adapted from FlyAtlas 2 data" in the text but this attribution is not included in the figure legend. Please add the data source attribution to the figure legend for clarity and proper credit.
4. The finding that DSS does not induce Vha55-lacZ expression (Fig 2D-E) is interesting and potentially informative, it suggests that V-ATPase upregulation is specific to oxidative injury rather than a generic stress response. However, this is mentioned only in passing in the Results. The authors should either discuss why DSS differs mechanistically from oxidant injury.

Significance

This study addresses a biologically important and understudied question: how organelle pH dynamics regulate inflammatory signaling in the intestinal epithelium under oxidative stress. The central finding that V-ATPase depletion is protective rather than sensitizing against oxidative stress is counterintuitive and novel, challenging the default assumption that lysosomal function is uniformly beneficial under stress conditions.The work will likely stimulate further investigation into endolysosomal pH as a therapeutic target in chronic inflammatory conditions of the intestine, and may be of interest beyond the Drosophila field to researchers studying lysosomal regulation of inflammation in mammalian systems.

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Referee #2

Evidence, reproducibility and clarity

Summary

The authors investigated the role of V-ATPases, particularly V-ATPase-dependent lysosomal acidification, in the response of the Drosophila intestine to oxidative stress induced by hydrogen peroxide (H2O2) or paraquat (PQ) feeding. The study stems from an analysis of FlyAtlas 2 data indicating enrichment of V-ATPase subunit expression in the adult intestine. Focusing on the posterior midgut of adult males, the authors report that oxidant exposure increases Vha55-lacZ reporter activity and lysosomal acidification. They further show that enterocyte-specific, but not ISC/progenitor-specific, knockdown of Vha44 reduces intestinal barrier dysfunction, ISC proliferation and Dcp-1-positive enterocyte death, while improving survival under oxidative stress and extending lifespan. Based on reporter assays, immunostaining, RT-qPCR and genetic epistasis, the authors propose that V-ATPase-dependent lysosomal acidification promotes JNK and IMD/Relish signaling, activation of which compromises intestinal and organismal survival following oxidant exposure.

The proposed sequence of events linking oxidative stress-induced lysosomal acidification to the activation of stress signaling, subsequent disruption of intestinal barrier integrity, and ultimately reduced organismal survival is potentially important. However, several central conclusions of the study are currently based on experiments that lack sufficient replication/robustness and are insufficiently described regarding the design and controls. The imaging data do not allow reliable assessment of cell-type specificity. Specifically, the survival experiments, the evidence for oxidant-induced V-ATPase expression, and the proposed placement of V-ATPase upstream of JNK and IMD/Relish signaling would benefit from additional support. The current data epistasis experiment do not yet establish that oxidant-induced V-ATPase expression and acidification directly drive detrimental JNK and IMD/Relish activation. A more thorough reflection/discussion of the existing literature, including possible sex-specific effects and comparison with other intestinal stress paradigms such as bacterial infection, would further broaden the relevance and impact of the study.

Major concerns

The evidence for intestinal enrichment of V-ATPase subunits is based largely on FlyAtlas 2 data presented in Figure 1B, which is unreadable at the current size and resolution. The authors may complement this analysis with publicly available adult intestinal single-cell or single-nucleus RNA-sequencing datasets to establish, which cell populations express the relevant V-ATPase subunits.

A single Vha55-lacZ reporter is insufficient to support the broader conclusion that oxidant exposure rapidly induces multiple V-ATPase subunits. As RNA samples are available, the authors should quantify the subunits functionally interogated by RT-qPCR following H2O2 and/or PQ exposure. Higher-magnification images of the R4-R5 region, together with cell-type markers, are also needed to identify the cellular source of Vha55-lacZ induction. Without additional evidence, the conclusion regarding rapid induction of V-ATPase subunit expression should be moderated and not generalized.

The stress-survival and lifespan experiments appear to include very few animals, in some cases (n=11). Given the inherent variability of these assays, also evident from the control groups throughout the study, such sample sizes are insufficient to support robust conclusions. Survival and lifespan experiments should include several replicate vials, adequate cohort sizes, preferably approximately 100 or more flies per genotype and condition, and independent repetitions performed at different times (Piper and Partridge, 2016; doi: 10.1007/978-1-4939-6371-3_18, PMID: 27730590). Because these assays form the foundation of the study, the Methods should specify the number of flies per vial, the number of vials per genotype and condition, the definition of (n), and the number of independent experiments. Independent experiments might be provided as supplemnetary figure.

It appears that the same Myo1A>+ control survival curve may have been used in Figure 1C and Supplementary Figure S1A. The authors should clarify whether these data originate from the same experiment and if so stated the fact in the figure legend.

Gut-specific V-ATPase disruption can affect larval growth, nutrient utilization and feeding behavior (Dennison et al., 2020; PMID: 32269334). Because the authors used Myo1A-Gal4 driver active alredy in larval stages, V-ATPase depletion may have affected development and adult physiology before oxidant exposure. It is important to discern whether improved survival could result from reduced feeding, and therefore reduced oxidant intake, rather than protection caused directly by decreased V-ATPase activity in adult enterocytes. The authors should quantify food intake under control and oxidant-treated conditions for the key genotypes and document developmental timing, adult body size and baseline intestinal morphology. Ideally, key findings should be confirmed using an adult-inducible (TARGET or a drug-inducible) system to restrict transgene expression to adulthood.

The authors should state whether the driver and RNAi stocks were backcrossed into a common genetic background. TRiP lines obtained from the Bloomington Drosophila Stock Center carry markers and mutant alelles that may affect stress resistance and lifespan. Several important conclusions rely on image-based measurements, yet the Methods provide insufficient information about image acquisition and analysis such as exposure settings across genotypes, background subtraction, normalization procedures, thresholding, and measures used to control inter-experimental variability. They should also state whether imaging and quantification were performed blinded to genotype and treatment.

Minor comments

It would be helpful to describe the nature of the Rel-GFP reporter. Is it a transcriptional reporter or a Relish protein fusion? If it is a protein fusion, active Relish would be expected to show nuclear enrichemnt of its active N-terminal fragment. However, the signal in Figure 5H appears predominantly cytoplasmic even after H2O2 treatment. The authors should explain this observation and quantify nuclear versus cytoplasmic signal.

Furthermore, the vehicle-treated intestines in Figure 5F,G appear different from those in Supplementary Figure S5A,B. In one case, the signal appears predominantly associated with enterocytes, whereas in Figure S5A,B it appears to label ISC/EB-like cells. This discrepancy should be addressed using higher-resolution images and appropriate cell-type markers.

Several microscopy panels are too small, and the green/cyan color combination provides insufficient contrast. In Figure 3E-H, DAPI, hid-GFP and Dcp-1 signals cannot be reliably distinguished. Enlarged views and separate grayscale channels should be provided. PQ has previously been shown to activate JNK in multiple cell types of the adult female intestine (Biteau et al., 2008; PMID: 18940735; doi: 10.1016/j.stem.2008.07.024). Higher-magnification of phospho-JNK images, combined with cell-type markers, are therefore required to establish which cells respond to oxidative stress in the adult male intestine and how this response changes following enterocyte-specific Vha44 depletion.

In Figure 6G,H, some groups appear to contain only three observations. With (n=3), normality and equality of variance cannot be meaningfully assessed, weakening the justification for a parametric one-way ANOVA. Šídák correction addresses multiple comparisons but does not resolve violations of the assumptions underlying ANOVA. In general, the authors should indicate in figure legends whether the plotted measurements originate from one experiment or from several independent experiments.

• Figures 4K and 5K should include control groups without PQ exposure.
• The relevant age and sex of the animals should be stated in each figure legend.
• The authors should define precisely what is meant by "lysosomal membrane reporter expression."

Significance

General assessment

The strength of this study is the functional evidence that V-ATPase-dependent lysosomal acidification in enterocytes contributes to the regulation of stress-signaling pathways following oxidative damage, influencing epithelial integrity and organismal survival. By linking intracellular vesicle acidification to tissue-level stress responses and intestinal homeostasis, the study addresses an important and potentially broadly relevant question.

The main limitations concern experimental robustness, cell-type resolution, and the description of the experimental design. Several conclusions would benefit from additional controls, increased numbers of biological replicates, and a clearer presentation of statistical analyses. The cellular specificity of the observed effects should also be examined in more detail. The findings should be discussed in the context of established V-ATPase functions in other intestinal cell types e.g. interstitial cells. Given that the experiments appear to focus predominantly on males, the authors should also discuss whether the observed responses may be sex-specific or provide corresponding evidence from females. To strenghten the proposed signaling axis linking lysosomal acidification to JNK-IMD pathway activation, the authors should consider the potential impact of V-ATPase deficiency on endocytosis, nutrient absorptio or other aspects of enterocyte physiology. Potential effects on feeding behavior should be evaluated or excluded.

An important unresolved issue is whether the identified V-ATPase-dependent mechanism is specific to oxidative stress or represents a more general response to intestinal damage, dysbiosis, or pathogenic infection. Direct comparisons, or at least a more comprehensive discussion of these contexts, would help increase the study relevance to broader readership.

Advance

The study extends current knowledge by functionally linking V-ATPase-dependent lysosomal acidification in enterocytes to stress-signaling pathway activation, maintenance of intestinal barrier integrity, and organismal survival under oxidative stress. Lysosomal acidification is presented not only as a housekeeping process required for degradation, but as an active regulator of the epithelial response to oxidative damage.

Audience

The study will be of primary interest to a specialized basic-research audience working on intestinal biology, lysosomal function, stress signaling, epithelial homeostasis, and Drosophila physiology. It may attract attention of readers interested in studying how organelle function influences inflammatory and tissue-damage responses in other experimental systems.

Field of expertise

My areas of expertise include functional genetics, stress signaling, mechanisms of gene regulation and epithelial biology.

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Referee #1

Evidence, reproducibility and clarity

Summary & General Assessment:

In this manuscript, Terry et. al. investigate the function of Vacuolar ATPases (V-ATPases) in response to oxidative damage in the Drosophila gut epithelium. They show that oxidative stress induced by H₂O₂ or paraquat (PQ) increases the expression of the Vha55-lacZ reporter and the abundance of acidified vesicles in the midgut. Depletion of V-ATPase subunits (e.g., Vha44, Vha68-2) in gut enterocytes (ECs) suppresses oxidant-induced lethality, intestinal barrier failure, and cell death. These findings are novel and potentially important to the fields of intestinal damage response and regeneration. Further, the authors show that Vha44 is required for oxidant-, and Tak1-induced activation of JNK and IMD/NF-κB signaling. This original discovery, connecting vesicle acidification by V-ATPases to oxidative stress, is quite interesting and has potentially wide-ranging, significant implications in cell biology.

Overall, this is a well-executed genetic study. The experiments are generally well quantified, controlled, and presented in a logical manner. There is a substantial amount of original data, and these generally support the authors' conclusions. However, the molecular mechanism(s) by which V-ATPases/vesicle acidification promote oxidant-induced JNK and IMD/NF-κB activation, intestinal barrier dysfunction, and cell death remain unclear. Two fundamental questions are left unanswered that, ideally, would be addressed. First, do the effects of Vha44 depletion reflect a general requirement for endolysosomal acidification, or some other specific function of the V-ATPase complex? Second, does Vha44 depletion directly affect the signaling and cellular responses examined (DCP-1, LAMP-GFP, pJNK, Rel-GFP, etc.), or does it primarily alter ROS abundance, thereby indirectly affecting lysosomal responses, JNK and IMD/NF-κB activation, and cell death? Addressing these questions could substantially strengthen the mechanistic conclusions of the study. With appropriate revision, this manuscript could be suitable for PLOS Genetics, EMBO Reports, or any other comparable Review Commons affiliate journals.

Major Comments:

1. As noted above, it remains unclear whether the protective effects of Vha44 depletion result specifically from reduced endolysosomal acidification or from another function of the V-ATPase complex. To distinguish between these possibilities, the authors could deplete additional genes required for endolysosomal acidification or V-ATPase assembly, such as auxilin/aux, and determine whether these manipulations phenocopy Vha44 depletion. In addition, the conclusion that Vha44 depletion alters endolysosomal acidification currently relies on LysoTracker staining, which reports the accumulation of dye in acidic compartments but does not directly measure luminal pH. Additional data using more quantitative reporter, such as LysoSensor, could provide stronger evidence for altered acidification, as opposed to changes in endolysosomal vesicle size.
2. Does Vha44 depletion in ECs reduce the ROS accumulation caused by H₂O₂ or PQ? This question could be addressed using DHE staining or other validated ROS reporters. If Vha44 depletion reduces ROS levels, the observed suppression of JNK and IMD/NF-κB signaling may be an indirect consequence of reduced oxidative stress. Conversely, if ROS levels remain elevated after Vha44 depletion, this would support the conclusion that the V-ATPase (or endolysosomal acidification) acts downstream of, or in parallel to, ROS accumulation to regulate these pathways. This distinction is important for the central mechanistic model.
3. As shown in Fig. S1C, whole-body overexpression of Vha44 or VhaSFD shortens lifespan. Is overexpression of V-ATPase subunits in ECs sufficient to induce ROS accumulation, JNK/IMD signaling, cell death, or intestinal barrier dysfunction in the absence of exogenous oxidative stress? Testing this would provide a useful gain-of-function complement to the RNAi results and help establish whether elevated V-ATPase activity is sufficient to damage the intestinal epithelium.
4. Is EC-specific depletion of Tak1 sufficient to suppress oxidant-induced lethality? Since the authors propose Tak1 as a key regulator connecting oxidative stress and V-ATPase activity to JNK and IMD/NF-κB signaling, testing the effect of Tak1 RNAi on oxidant-induced mortality could provide important loss-of-function evidence for this model.
5. Recent publications have provided data showing that the p38-MAPK pathway, including another MAP3K (Ask1) is an important ROS-responsive stress sensing pathway in Drosophila and in the midgut. It could be informative for Terry et al. to check whether the Ask1-Licorne-p38 pathway is also involved in the effects shown here.
6. For Fig. 2A-D, higher-magnification images should be provided. The authors should also indicate whether Vha55-lacZ was induced in ECs, progenitor cells, or both. Furthermore, since Vha55 is the proposed oxidant-induced V-ATPase subunit, it would be informative to test whether Vha55-RNAi produces protective effects similar to those caused by depletion of Vha44, Vha68-2, and VhaSFD in Fig. 1.
7. The effects of Vha44-RNAi on pJNK (Fig. 4C-D) and Rel-GFP (Fig.5C-D) appear relatively subtle in the representative images, although the fluorescence-intensity measurements indicate statistically significant differences. Because these observations are central to the proposed mechanism, we suggest that the authors validate them using a more quantitative assay, such as western blotting.
8. Although the Smurf assays support the conclusion that Vha44 depletion preserves intestinal barrier function, examining epithelial junction organization using markers such as Armadillo (Arm) or Discs large (Dlg) could provide more specific evidence of a barrier defect.

Minor Comments:

1. In Fig. 4L, please add a comparison between "Myo1A>UAS-Bsk" and "Myo1A>Vha-IR, UAS-Bsk" groups.
2. In Fig. 5B-E, please add the "Myo1A>Vha44-IR vehicle" control.
3. Please add the "Myo1A>Tak1 vehicle" and "Myo1A>Tak1,Vha44-IR vehicle" controls in Fig. 6G-H.

Significance

Overall, this is a well-executed genetic study. The experiments are generally well quantified, controlled, and presented in a logical manner. There is a substantial amount of original data, and these generally support the authors' conclusions. However, the molecular mechanism(s) by which V-ATPases/vesicle acidification promote oxidant-induced JNK and IMD/NF-κB activation, intestinal barrier dysfunction, and cell death remain unclear. Two fundamental questions are left unanswered that, ideally, would be addressed. First, do the effects of Vha44 depletion reflect a general requirement for endolysosomal acidification, or some other specific function of the V-ATPase complex? Second, does Vha44 depletion directly affect the signaling and cellular responses examined (DCP-1, LAMP-GFP, pJNK, Rel-GFP, etc.), or does it primarily alter ROS abundance, thereby indirectly affecting lysosomal responses, JNK and IMD/NF-κB activation, and cell death? Addressing these questions could substantially strengthen the mechanistic conclusions of the study. With appropriate revision, this manuscript could be suitable for PLOS Genetics, EMBO Reports, or any other comparable Review Commons affiliate journals.

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Reply to the reviewers

Reviewer #1

Comment: A limitation of this study is that it is mainly descriptive. It lacks a clear indication of the most promising targets that should help to advance our understanding of PMP22 biology in Schwann cells.

Response: We thank the reviewer for this important comment. We agree that the original version did not adequately prioritize the identified PMP22 interaction candidates. To address this concern, we performed additional cross-cell type enrichment and protein interaction network analyses to identify the most biologically relevant pathways emerging from the dataset. Moreover, we performed new orthogonal validation experiments using NanoBRET and in situ PLA, thereby moving beyond purely descriptive proteomic observations. Changes in the manuscript: • We added a new paragraph to the Results section entitled “Cross-cell type enrichment and network analysis highlight (sphingo-)lipid metabolism as a prominent cluster among PMP22-ALFA PPIs” (p.9, l.27) corresponding to new Figure 5: “Cross-cell type enrichment, PPI network analysis and initial orthogonal validation”. Previous Figure 5B- B’’ was moved to the supplementary material as new Supplementary Figure 4. • We introduced a cross-cell type pathway enrichment analysis integrating GO, KEGG and curated pathway databases (new Figure 5B-D). • We added a PPI network analysis highlighting lipid metabolism and sphingolipid biosynthesis pathways as recurring biological themes (new Figure 5C,D). • We added BRET ratios of PMP22-HaloTag and NanoLuc-tagged PPI candidates, demonstrating close proximity in living cells (new Figure 5E). • We added images showing in situ PLA of PMP22-ALFA and endogenous PPI candidates in MDCKII cells (new Supplementary Figure 5). • The methodology describing these analyses was added to the Methods section under “PPI and functional annotation enrichment analysis” (p.16, l.26), NanoBRET assay” (p.16, l.43) and “In situ PLA” (p.17, l.4). • We have adapted the part of the previous discussion highlighting enzymes of the de novo sphingolipid synthesis pathway as PMP22 PPI candidates and moved it to the Results section (new sub-heading “PPIs of PMP22 are in line with specialized functions of adhesion and lipid metabolism in epithelial cells”, p.6, l.43), as enzymes of sphingolipid metabolism, in addition to other potentially important lipid-associated proteins (CAV1, PLLP), appear as enriched PPI candidates for the first time in the MDCKII data. • In the Discussion section we additionally highlighted a possible connection between PMP22’s role in regulation of calcium signaling and lipid metabolism through ORMDL3 (p.12, l.24).

Comment: The Schwann cell experiments are the most important. However, considering the low transfection efficacy (primary SC) or the low differentiation (MSC80) these are very limiting in the present form. A suggestion could be to improve transfection efficiency by nucleofection or by using lentiviral vectors to transduce primary rat Schwann cells.

Response: We agree that the incomplete differentiation status of MSC80 cells and the limited transfection efficacy of primary Schwann cells represent important limitations of the present study, which we acknowledge in the Results section (p.8, l.15; p.9, l.18) and in the revised Discussion (p.13., l.16). By discussing DNA-editing in more complex cellular systems as a potential approach for future studies, we are also proposing a method that can address these shortcomings all at once (p.13, l.19). While nucleofection or viral transduction may indeed improve transgene delivery, the establishment and validation of these approaches go beyond the scope of the present study, particularly in light of the alternative discussed, which we have in fact already begun to implement as part of a new project. To strengthen confidence in the identified candidates–also in the experiments using Schwann cells–despite the limitations of the present study, we performed new orthogonal validation experiments and expanded the presentation of the top candidates in the volcano plots. Changes in the manuscript: • We added NanoBRET and in situ PLA data described in the previous response (Figure 5E, Supplementary Figure 5). • To better illustrate that we have identified multiple myelin proteins in Schwann cells as PMP22 PPI candidates despite the limitations, we have modified the annotations of the hits in the volcano plots so that the 25 top enriched proteins are now displayed in an enlarged inset instead of 15. This revealed several canonical myelin proteins such as MPZ, PLP1, MCAM, and CMTM5 in these plots (Figure 4A, D).

Reviewer #2

Comment: This study across different cell types is the most comprehensive to date to document PPIs of PMP22. Disappointingly the PPIs differ enormously between cells.

Response: We thank the reviewer for raising this, because we believe our data allow us to distinguish between the two explanations for the limited overlap–technical drop-out versus genuine context-dependence–and we had not made this argument explicit enough. Cell-type specific non-detection occurred in two distinct situations: for proteins that were absent from the ALFA-IP input altogether, and for proteins that were clearly present in the input yet were not co-purified. E.g. in MDCKII cells, the myelin proteins MPZ and PLP1 were absent from the input sample, whereas ER proteins of early protein processing such as SRPRA, SEC11A, DPAGT1 and PRAF2 were present in the input but did not co-purify (Supplementary Figure 4). The second case cannot be explained by detection failure: these proteins were detectable in the lysate and were simply not associated with PMP22 in that cellular context. We therefore interpret the divergence between cell types as genuine, context-dependent binding, and in the revised manuscript we also discuss as to how these results reflect the multifunctional role of PMP22, whose partners are determined by the cell type in which it is expressed (p.11, l.39). We would add that this context-dependence is one reason a cross-context dataset is worth generating: a single-cell type interactome would have reported one of these signatures and missed the others.

Comment: The study appears to have been performed well and the results are clearly presented on the whole. This reviewer was expecting to see some sort of illustration in figure 5 (or separately in the Discussion) that distils the principal linked candidates according to biological processes or pathways with a scoring or ranking system to communicate how strong a case we are looking at.

Response: We thank the reviewer for this excellent suggestion. In response to this criticism, as well as the concerns raised by Reviewer #1 that the study was merely descriptive, we added a new integrative analysis that summarizes the major biological themes emerging from the dataset and highlights (sphingo-)lipid metabolism as an example of particular interest to PMP22 biology (new Figure 5B-D). Changes in manuscript: • Figure 5A summarizing overlap between datasets was adopted after minor calculation errors were corrected. • The original overlap-based presentation was moved to the supplementary material and in the main replaced by a new integrative analysis framework (Figure 5B–D) that prioritizes biological pathways and interaction clusters, as also described in our response to the first comment by Reviewer #1. • Figure 5B presents pathway enrichment analysis integrating GO, KEGG and curated pathway databases across cell types and conditions. Resulting clusters are sorted by significance and P-values of representative terms displayed as a heatmap. Additionally, the top 3 enriched PPI candidates per term across all cell types and conditions are indicated along with their highest log2-fold enrichment in the PMP22-ALFA eluate. • Figure 5C presents a PPI network of all identified interaction candidates. • Figure 5D highlights proteins associated with lipid metabolism and sphingolipid biosynthesis, as these analyses identify these pathways as one of the most prominent recurring biological themes across datasets.

Comment: In the version downloaded from the website the discussion appears as a single paragraph, which affects clarity and masks the limited depth of conclusions. The text needs to be structured better to be clear where discussion of each topic begins and ends, and the repetition from other sections should be removed. ¨ In the Schwann cell line MSC80 we found the term myelin sheath enriched (Fig. 4B), with several known myelin proteins like PLP1, MPZ, MCAM and ANXA1 enriched in the PMP22-ALFA eluates of MSC80 and primary Schwann cells. At the onset of myelination, Schwann cells mount a transcriptional program enabling coordinated synthesis of both myelin proteins and lipids that are required in large quantities for myelin sheath formation (LeBlanc et al, 2005; Pertusa et al, 2007; Fledrich et al, 2018; Kim et al, 2018; Poitelon et al, 2020).¨ The link to sphingolipid synthesis (that follows) could be improved, this reviewer missed entirely the fact that there is a link until the third time of reading.

Response: We fully agree and have revised the Results and Discussion section. Changes in manuscript: • As already stated in our response to the first comment by Reviewer #1, we adapted the part of the previous Discussion in which we highlighted enzymes of the de novo sphingolipid synthesis pathway as PMP22 PPI candidates and moved it to the Results (p.6, l.43) in order to reflect the central theme of our findings already at this point, which is continued in new Figure 5 (“Cross-cell type enrichment, PPI network analysis and initial orthogonal validation”) and in the newly added paragraph “Cross-cell type enrichment and network analysis highlight (sphingo-)lipid metabolism as a prominent cluster among PMP22-ALFA PPIs” (p.9, l.27). • We have organized the Discussion section thematically into four paragraphs, discussing (1) methodological advances of the DDM/ALFA-tag interactomics approach, and how our results can be interpreted with regard to PMP22’s multifunctional role across cell types and subcellular compartments, (2) a novel mechanistic link between PMP22 and lipid metabolism as the central biological theme of our findings, as well as a possible connection to the described role of PMP22 in calcium signaling, (3) limitations of Co-IP- based interactomics and our study in particular, along with suggestions for general use and future directions, and (4) summarizing, the significance of our study despite the limitations. • In addition, we have provided the individual parts of the Results section with subheadings so that important findings can be grasped at a glance.

Comment: Re sphingolipid synthesis, SPTLC1 and 2 are quite far down the list in figure 5 and ORMDLs that are mentioned in the text don´t appear at all. On further reading we come to 2 stronger candidates CERS and KDSR, so the section needs reordering. The fact that SPTLC, CERS and KDSR are not known to interact comes at the end of this section not mixed up in the middle.

In the same section is interfere the right word? In any case likely seems too strong given the lack of validation. ¨It seems likely that PMP22 can directly interfere with sphingolipid synthesis in the ER.

Response: We thank the reviewer for this insightful observation. In the revised Results section, we now list the candidates ordered by enrichment (p.7, l.24). ORMDL2, which was previously easy to overlook, is listed along with other candidates in Figure 5B and D. We also agree that “interfere” is too strong with regard to our results, and now state: “Our results thus indicate that PMP22 associates with multiple ER-resident enzymes of the de novo sphingolipid synthesis, with a possible functional role of contributing to physiological regulation of sphingolipid supply to the myelin sheath and to its dysregulation in CMT1A.” (p12, l.22)

Comment: The limitations are substantial and largely acknowledged by the authors, above all a complete lack of further investigation of any of the candidates; and with these in mind the study amounts to a list of PPIs of PMP22 that will be of value to the narrow field of those specializing in CMT1A, and might also be given a cursory glance by those with an interest in sphingolipid synthesis. Overall without further validation the work is somewhat preliminary. Generally omic studies are used to build hypotheses, which are then further investigated, whereas this study is limited to proteomic analyses.

This reviewer is not an expert in CMT or PMP22, but has carried out a number of protoemic studies and has extensive experience of cell and molecular biology. This reviewer is not an expert in CMT or PMP22, but has carried out a number of protoemic studies and has extensive experience of cell biology.

Response: We thank the reviewer for stating the limitation plainly, and we agree with its factual content: this study does not functionally dissect individual candidates. We have revised the framing of the manuscript accordingly, and it is now submitted as a Methods and Resources article–a category for which new biological insight is encouraged but is not a requirement for consideration. What we would offer in response is evidence that the methodological contribution is substantial rather than incremental. Applied to PMP22, the workflow recovers 53 of the 296 PPIs reported across 22 previous studies and identifies 1,073 new candidates, which is more than all prior work on this protein combined (new Supplementary Figure 6). Following the reviewers' comments we added cross-cell type pathway and network analyses to prioritize candidates (Figure 5B-D), orthogonal validation by NanoBRET in living cells (Figure 5E), and in situ PLA against endogenous protein (new Supplementary Figure 5). Since posting of our preprint, an independent BioID2 study in a different Schwann cell model has appeared (Holt et al, 2025). 71 of the 284 proteins it reports as PMP22-exclusive are also among our candidates, 1.7-fold more than expected by chance when both datasets are restricted to the proteins detectable in both studies (p = 8.9 x 10^-7), including the sphingolipid enzymes CERS2 and SPTLC3. We also argue that also in absence of functional data, our study represents a significant step forward in uncovering the molecular role of the still poorly understood PMP22. We not only reveal a molecular link to (sphingo-)lipid biosynthesis, but by making our dataset available as a resource, we also provide starting points for the research community to conduct structural and functional studies in various directions. Our functional and structural characterization of the prioritized candidates, beginning with the PMP22-CAV1 interaction, is the subject of a separate study currently underway. We agree that this is the logical next step and believe that this topic is better addressed in a dedicated study.

Reviewer #3

Comment: This is a beautiful proteomics study to identify proteins that interact with peripheral myelin protein 22 (a tetraspan membrane protein) in four different cell types: HEK293T (a generic model mammalian cell line), MDCKII epithelial cells, a Schwann cell line, and primary rat Schwann cells. An impressively-optimized protocol was used based on fusing the recently-developed alpha tag to the C-terminus of PMP22 employed. This work also presents an optimized protocol for solubilizing the PMP22, regardless of which intracellular compartment it is in. While there have been previous proteomic studies of PMP22, this study VERY significantly extends previous results. The manuscript is clearly written and the figures are clear. One suggestion for improvement is that I did not find clear descriptions of the contents of supporting Tables 1 and 2. This is needed and also the columns of those excel tables could be improved to make them easier to grasp.

Response: We thank the reviewer for the positive assessment of our study, and for their suggestion to improve the supplementary tables. Changes in manuscript: • We revised the legends and layouts of Supplementary Tables 1 and 2. • In Supplementary Table 2, additional rows containing differential hit counts together with explanations of table contents were added to facilitate readability as well as traceability of Figures 2A, 3A, 4A, 5B, Supplementary Figure 4 and the candidate numbers we state in the text.

Comment:

**Referee cross-commenting**

The other two authors have raised concerns and offered suggestions that are excellent and worthy of address. However, my enthusiasm for this work remains high and I think that, even in the present version of this manuscript, this work advances of our understanding of PMP22 biology and pathobiology.

Response: In response to the concerns raised by the Reviewers #1 and #2, we substantially strengthened the manuscript by: • Adding a new integrative pathway and interaction network analysis (Figure 5A-D). • Performing new NanoBRET validation experiments (Figure 5E). • Performing new in situ PLA validation experiments (Supplementary Figure 5). • Expanding and restructuring the Discussion. • Improving prioritization of biologically relevant PMP22-associated pathways and PPI candidates. • Revising the shown volcano plots to make more PPI candidates visible at a glance (Figures 2B, 3B, 4B) • Revising the supplementary information. We believe that these additions have further strengthened the biological interpretation of the dataset and improved the overall significance of the study.

Comment: Gene variations that alter the expression levels or sequence of the tetraspan membrane protein PMP22 cause about 2/3 of all cases of Charcot-Marie-Tooth disease (CMT), a peripheral neuropathy that impacts 1:2500 humans, making it a top-10 genetic disorder. There is no treatment or cure for CMT beyond orthotics and physical therapy. The normal function of PMP22 in promoting myelination of peripheral nerve axons by Schwann cells is poorly understood, reflecting understudy. This paper presents results that represent a huge step forward relative to previous proteomics studies of PMP22 both in terms of the approach used and in terms of the novel insights derived. Of particular significance are the results present herein that PMP22 very likely plays a central role in regulating sphingolipid biosynthesis in Schwann cells. This extends previous results that PMP22 is involved in cholesterol homeostasis. Given that Schwann cells expand their membrane areas by a factor of several thousand during myelination and given the lipid-raft like composition of the myelin membranes, recognition that PMP22 is centrally involved in BOTH cholesterol and sphingolipid homeostasis illuminates its native function and suggests possible pathological roles for PMP22 under conditions of CMT. I think this paper will be of interest to the growing CMT research community, as well as to scientists interested the basic biology of the peripheral nervous system. While I would not describe this paper as having any significant weaknesses, as a "pulldown"-based proteomics study, the results are subject to the key limitation that observation that a given protein associates with PMP22 cannot be taken to indicate DIRECT interaction without additional studies. The observed proteomic interaction could be mediated by other proteins. Thus, the results of this work are most important both for supporting results from previous studies and for suggesting relationships of PMP22 to other proteins and their associated pathways that are worthy of future studies.

Response: We thank the reviewer for placing our study within the context of ongoing research on PMP22 and related neuropathies, as well as within the PNS field as a whole. In the Discussion, we acknowledge the limitation that the approaches used cannot distinguish between direct and indirect interactions, and we suggest alternative techniques to elucidate structural and functional details of the revealed PPIs in future investigations (p.13, l.10).

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Referee #3

Evidence, reproducibility and clarity

This is a beautiful proteomics study to identify proteins that interact with peripheral myelin protein 22 (a tetraspan membrane protein) in four different cell types: HEK293T (a generic model mammalian cell line), MDCKII epithelial cells, a Schwann cell line, and primary rat Schwann cells. An impressively-optimized protocol was used based on fusing the recently-developed alpha tag to the C-terminus of PMP22 employed. This work also presents an optimized protocol for solubilizing the PMP22, regardless of which intracellular compartment it is in. While there have been previous proteomic studies of PMP22, this study VERY significantly extends previous results. The manuscript is clearly written and the figures are clear. One suggestion for improvement is that I did not find clear descriptions of the contents of supporting Tables 1 and 2. This is needed and also the columns of those excel tables could be improved to make them easier to grasp.

Referee cross-commenting

The other two authors have raised concerns and offered suggestions that are excellent and worthy of address. However, my enthusiasm for this work remains high and I think that, even in the present version of this manuscript, this work advances of our understanding of PMP22 biology and pathobiology.

Significance

Gene variations that alter the expression levels or sequence of the tetraspan membrane protein PMP22 cause about 2/3 of all cases of Charcot-Marie-Tooth disease (CMT), a peripheral neuropathy that impacts 1:2500 humans, making it a top-10 genetic disorder. There is no treatment or cure for CMT beyond orthotics and physical therapy. The normal function of PMP22 in promoting myelination of peripheral nerve axons by Schwann cells is poorly understood, reflecting understudy. This paper presents results that represent a huge step forward relative to previous proteomics studies of PMP22 both in terms of the approach used and in terms of the novel insights derived. Of particular significance are the results present herein that PMP22 very likely plays a central role in regulating sphingolipid biosynthesis in Schwann cells. This extends previous results that PMP22 is involved in cholesterol homeostasis. Given that Schwann cells expand their membrane areas by a factor of several thousand during myelination and given the lipid-raft like composition of the myelin membranes, recognition that PMP22 is centrally involved in BOTH cholesterol and sphingolipid homeostasis illuminates its native function and suggests possible pathological roles for PMP22 under conditions of CMT. I think this paper will be of interest to the growing CMT research community, as well as to scientists interested the basic biology of the peripheral nervous system.

While I would not describe this paper as having any significant weaknesses, as a "pulldown"-based proteomics study, the results are subject to the key limitation that observation that a given protein associates with PMP22 cannot be taken to indicate DIRECT interaction without additional studies. The observed proteomic interaction could be mediated by other proteins. Thus, the results of this work are most important both for supporting results from previous studies and for suggesting relationships of PMP22 to other proteins and their associated pathways that are worthy of future studies.

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Referee #2

Evidence, reproducibility and clarity

PMP22 is primarily located in the compact myelin of the peripheral nervous system which explains why mutant forms cause CMT. Its partners and function in cells are still not well established although several previous studies have suggested 54 partners.

This study across different cell types is the most comprehensive to date to document PPIs of PMP22. Disappointingly the PPIs differ enormously between cells. The study appears to have been performed well and the results are clearly presented on the whole. This reviewer was expecting to see some sort of illustration in figure 5 (or separately in the Discussion) that distils the principal linked candidates according to biological processes or pathways with a scoring or ranking system to communicate how strong a case we are looking at.

In the version downloaded from the website the discussion appears as a single paragraph, which affects clarity and masks the limited depth of conclusions. The text needs to be structured better to be clear where discussion of each topic begins and ends, and the repetition from other sections should be removed.

¨ In the Schwann cell line MSC80 we found the term myelin sheath enriched (Fig. 4B), with several known myelin proteins like PLP1, MPZ, MCAM and ANXA1 enriched in the PMP22-ALFA eluates of MSC80 and primary Schwann cells. At the onset of myelination, Schwann cells mount a transcriptional program enabling coordinated synthesis of both myelin proteins and lipids that are required in large quantities for myelin sheath formation (LeBlanc et al, 2005; Pertusa et al, 2007; Fledrich et al, 2018; Kim et al, 2018; Poitelon et al, 2020).¨

The link to sphingolipid synthesis (that follows) could be improved, this reviewer missed entirely the fact that there is a link until the third time of reading.

Re sphingolipid synthesis, SPTLC1 and 2 are quite far down the list in figure 5 and ORMDLs that are mentioned in the text don´t appear at all. On further reading we come to 2 stronger candidates CERS and KDSR, so the section needs reordering. The fact that SPTLC, CERS and KDSR are not known to interact comes at the end of this section not mixed up in the middle.

In the same section is interfere the right word? In any case likely seems too strong given the lack of validation. ¨It seems likely that PMP22 can directly interfere with sphingolipid synthesis in the ER.

Significance

The limitations are substantial and largely acknowledged by the authors, above all a complete lack of further investigation of any of the candidates; and with these in mind the study amounts to a list of PPIs of PMP22 that will be of value to the narrow field of those specializing in CMT1A, and might also be given a cursory glance by those with an interest in sphingolipid synthesis.

Overall without further validation the work is somewhat preliminary. Generally omic studies are used to build hypotheses, which are then further investigated, whereas this study is limited to proteomic analyses.

This reviewer is not an expert in CMT or PMP22, but has carried out a number of protoemic studies and has extensive experience of cell and molecular biology.

This reviewer is not an expert in CMT or PMP22, but has carried out a number of protoemic studies and has extensive experience of cell biology.

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

This paper reports the identification of candidate interactors of PMP22, a myelin protein mutated in the most frequent form of Charcot-Marie-Tooth disease, the demyelinating CMT1A. The authors performed co-IP experiments using overexpressed PMP22-ALFA tagged at the C-terminus followed by LFQ-MS analysis to identify candidate interactors. Different cell types were used such as HEK, MDCK, MSC80, and primary rat Schwann cells. The authors also tested several lysate buffers and detergent to optimize PMP22 solubility without affecting binding to interacting partners.

The authors present a list of the most significant hits that have been identified in at least two different cell types. This result should represent a starting basis for functional analysis and further evaluation.

Significance

A limitation of this study is that it is mainly descriptive. It lacks a clear indication of most promising targets that should help to advance our understanding of the PMP22 biology in Schwann cells.

The Schwann cell experiments are the most important. However, considering the low transfection efficacy (primary SC) or the low differentiation (MSC80) these are very limiting in the present form. A suggestion could be to improve transfection efficiency by nucleofection or by using lentiviral vectors to transduce primary rat Schwann cells.

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Reply to the reviewers

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

Summary: This manuscript addresses how optic tectum development changes relative to innervation from the retina. While previous studies in zebrafish already showed a link between retinal input to optic tectum growth, the cellular and molecule cues that contribute to such innervation-dependent growth remain poorly understood. Here, Olivia Hagen and colleagues analyze cell survival and proliferation in the optic tectum in three experimental conditions: wild-type larvae; lakritz (lak) mutant larvae, lacking retinal ganglion cells and in consequence bearing no optic nerves; and wild-type one-eyed larvae, in which one eye has been surgically removed. Combining cellular and pharmacological approaches, the authors identify a critical period in which survival, proliferation, and differentiation of optic tectum cells require retinal nerve innervation. Further, they demonstrate an instructive role for innervation in activating Wnt/ β-catenin pathway activity to promote optic-nerve dependent proliferation in the optic tectum.

Major comments 1. Although conclusions reached by the authors are based on solid data and statistical analysis, the presentation of the experimental logic and results in the text are often not well structured. In consequence, the manuscript is difficult to read and to understand. For instance, throughout most of the results part, the conclusion of the experiment comes before the actual explanation of the experimental and quantification procedure. Further, why certain experiments are conducted is not well stated. Some specific examples:

• Page 3: Why the tectum neuropil is not taken in account in cell survival and cell proliferation quantifications is not stated.

The identity of the cells that were dying within the neuropil is currently unknown and not the focus of this manuscript. Text has been changed to explain our choice. See lines 99-101 in revised clean copy text which state “Despite this intriguing finding, the identity of the TUNEL+ cells within the neuropil are outside of the TPZ and their identity is currently unknown.”

• Page 4: The reason why authors asses neuronal differentiation together with proliferation in the different experimental conditions is not explained (Page 2).

Assessing neuronal differentiation with proliferating cells is thought to provide some insight into how quickly those proliferating cells are differentiating into neurons. We now begin the paragraph (starting on line 136 of the revised clean copy) with “To test whether progenitor cells in the lak mutant OT were possibly proliferating and differentiating more slowly, we estimated the rate of tectal neuron differentiation by performing EdU pulse-chase experiments in wild-type and lak mutants.”

• Page 4: Why the authors measure brain size is not explained. It is understood that it is to check the specificity of the phenotype, however it should be clearly stated.

We reorganized and rewrote the manuscript, including more nuanced analysis of data we gathered as controls for our analyses of lakritz mutants as well as the effects of dark rearing. Some examples include lines 147-151 and the paragraph that begins on line 211 of the revised clean copy manuscript.

• Page 6: End of the result section 'Physical connections between the eye and brain via the optic nerve link optic tectum cell survival and proliferation'. There is no conclusion to this section.

Now added (lines 222-226) in the revised manuscript, which now says “Collectively, these experiments address the extent to which optic nerve activity, most prominent in a typical lighted environment, may influence progenitor cell survival and proliferation in the OT. All of the resulting data illustrate that the physical presence of an optic nerve is positively correlated with OT cell proliferation and survival regardless of the amount of light-linked visual input the OT receives.”

• Page 7, section 'Extent of sox2+ expression correlates with innervation', there is no mentioning in the text that sox2 expression is assessed by fluorescent in situ hybridization.

Now added to line 230

On top of that, certain wording or phrasing can sometimes lead to a misleading message: - Page 4: Lines 137-138 'Statistical analyses suggest that both age and genotype influence proliferation (ANOVA, f(2)=3.215, p*Reviewer #3 also raised a related concern. The focus of this study is the role of Wnt/B-catenin and therefore we did not quantify the area of regions expressing Shh and Hh pathway genes. When we went back to the data, we realized we did not have enough high quality images for meaningful quantitation. We have removed mention of the Shh/Hh pathway in the results section and removed the original figure S7. *

Minor comments and typos:

1. Figure 1 very well shows retinal innervation of the optic tectum in the different experimental contexts. However, the images in the rest of the figures look very different, making it difficult to identify the structures of interest. In Figure 2, the different anatomical structures of interest (retina, OT, neuropil) should be clearly indicated in at least one image. A scheme recapitulating what is seen in the images (similar to the one of figure 9) would be helpful.

*We have added a panel to a revised Figure 1 to show the different anatomical structures of interest that will help to orient the reader throughout the manuscript. * 2. In all figures, please indicate the number of independent experiments and the number of larvae analyzed per experiment (even if this information is collected in the Tables S2 and S4)

*Total number of larvae analyzed is now stated in all figure captions. We also included more information in the methods about the number of independent experiments and the way the experiments were conducted. We often combined embryos and larvae from multiple clutches into a single dish/tube to conserve reagents. Therefore we do not have accurate batch information for many of the experiments. Figure 4 (and supplementary figure S4) represents an experiment where different people performed the same experiments at different times and at different institutions; we were therefore able to include that batch information in our analysis. * 3. The statistical results in brackets in the main text often difficult the reading. I would suggest removing them from the main text and place them in the figure legends instead.

*We’ve streamlined and rewritten the text to help with readability, but feel that it’s important to have some of the statistical analysis results in the main text. Hopefully we have struck the right balance here, especially with our extensively revised statistics and Table S3. * 4. I would indicate with an asterisk the denervated side instead of the intact or innervated one.

*Switched * 5. Here are some typos I spotted in the text:

Line 354 - 'While our EdU to analyses could also be also consistent with a longer cell cycle...' delete the words 'to' and 'also'.

Changed. * Line 356 - 'Both elevated levels of programmed cell death in as well as...' delete the word 'in'. Changed. * Line 370- 'Many open questions about how programmed cell death contributes to the neuronal circuit remodeling required for lifelong growth and development'. A word is missing here, 'remain' maybe?

Rewrote the sentence.

Figure 1 legend, third line- 'typical innervation of the tectum by the optic nerve, visible as the axons from the atoh7+ retinal ganglion cells'. This sentence is not clear, rephrase please.

*Figure 1 has been modified and the caption revised, addressing this and other concerns stated above and by other reviewers. * Reviewer #1 (Significance (Required)): The strengths of the manuscript are in the approaches. The systematic evaluation and quantification of optic tectum cell survival and proliferation across different experimental conditions, in which optic tectum innervation is impaired, make the results of this study very solid. Further, not only they report a correlation between Wnt/b-catenin downstream genes and innervations effects, but they provide a mechanistic causal insight via rescue experiments. Overall, this is a constructive advance in our understanding of mechanisms guiding neurogenesis during development, opening an interesting line of research to further explore these pathways not only during neurodevelopment, but also in the context of neuronal regeneration.

Reviewer #2 (Evidence, reproducibility and clarity (Required)): Summary: This manuscript focuses on defining the molecular pathways that couple retinal input to the growth of the optic tectum in the larval zebrafish. Using a mutant line lacking retinal ganglion cells as well as an elegant model of unilateral enucleation to prevent tectal innervation, the authors demonstrate that optic nerve input is required for the survival and proliferation of tectal cells at late stages regardless of environmental light conditions used. The authors further show that a lack of innervation correlates with a decreased expression of sox2+ and a down-regulation of Wnt signaling in the tectum. Importantly, treating larvae with BIO, a Wnt pathway activator, restores proliferation of tectal cells in the absence of innervation, supporting an essential role for Wnt signaling in innervation-dependent tectal growth.

Major comments: This study presents robust and convincing data supported by elegant approaches and strong statistical analyses. The following points should be addressed:

The authors nicely show reduced Wnt signaling in the absence of retinal innervation and that treatment with BIO restores proliferation in the tectum. While these results strongly suggest that Wnt signaling is the main pathway controlling innervation-dependent tectal proliferation, BIO's mode of action is to inhibit GSK3β, which might have other Wnt-independent effects. Does pharmacologically inhibiting Wnt signaling (for instance, by using IWR1) phenocopy the reduced proliferation seen in the absence of innervation?

*We performed a similar experiment, using the tankyrase inhibitor XAV939, which decreases Wnt/ β-catenin signaling by promoting the stabilization of Axin and the subsequent degradation of β-catenin. The data (and another student author who helped with that experiment) are now included in the revised manuscript. The new supplementary figure S7 shows a reduction in EdU+ cells when Wnt/ β-catenin pathway activity is inhibited in wild-type larvae. These additional data further substantiate our conclusion that Wnt/ β-catenin pathway activity supports cell proliferation in the optic tectum. *

Does activating the Wnt pathway using BIO also reduce the number of apoptotic cells observed when innervation is lacking?

*While we accept that modulating GSK3B and assessing cell death could add to our study and potentially extend our conclusions, it would take many months to fully repeat the TUNEL experiments reported in the paper with BIO (particularly in a lab powered by undergraduates). *

We did, however, complete a preliminary study in which lak and wild-type larvae were treated with BIO from 7-9 dpf as in figure 8 and then assessed for TUNEL staining at 9 dpf. These results are not sufficiently robust for publication, but we include them for reviewers. We have also added to our discussion about CNS response to injury, Wnt, and neurotrophic signals (which begins on line 414 of the revised clean copy text), noting that it remains unknown whether Wnt/*β-catenin pathway activation can also decrease cell death in our injury models. *

Figure R1: BIO treatment does not appear to significantly alter the number of apoptotic cells.

(A-D) Representative maximum intensity projections of dorsal views of dissected brains from wild-type (A,B) and lak-/- (C,D) larvae treated with DMSO (A,C) or BIO (B, D) showing TUNEL+ cells (green) and nuclei (DAPI, magenta) at 9 dpf. Bar is 50 µm. Genotypes and treatments indicated in the lower left corner of all panels. TUNEL+ cells in the boxed region of the optic tectum, excluding those in the tectal neuropil, were counted and compared.

(E) Box plots overlaid with individual data points show TUNEL+ cells as a function of genotype and treatment as indicated. For each developmental stage and genotype, n ≥ 8. Abbreviations: ns, not significant; negative binomial generalized linear modeling followed by pairwise estimated marginal means with Tukey multiple comparisons corrections.

(Optional) Figure 5 shows a clear decrease in sox2 staining in lak that indicates a reduced number of sox2+ neural progenitor cells. Do sox2+ cells die early or/and is their rate of proliferation reduced in the absence of innervation? Answering this question would provide an important clue regarding the identity of the cells that die (tectal neurons that lack or loose connections vs progenitors). *We appreciate this suggestion, but feel that it’s outside the scope of the current study. *

Minor comments: 1) A schematic that indicates where the TPZ is in relation to tectal neurons and the neuropil would help readers not familiar with zebrafish anatomy.

*Reviewer #1 had a similar suggestion and Figure 1 has been modified to incorporate an fixed, DAPI-stained brain with annotations to orient the reader. * 2) There is a discrepancy between the main text and figures regarding how TUNEL+ cells were quantified in denervated larvae: the text (lines 115-116 and 600-601, for instance) indicate that numbers of TUNEL+ cells in intact and denervated sides were substracted, whereas figure 2 indicates that a ratio between the innervated and denervated sides was calculated. A similar discrepancy is present for the number of EdU+ cells and in other figures. It might be easier for readers to calculate denervated - intact (rather than intact - denervated), so that positive values represent "more" and negative values, "less" (as of now, it is a bit counterintuitive that negative values represent more apoptotic cells, for instance).

*We’ve revised the text to emphasize that all of the one-eyed analyses used a difference ratio (intact-denervated/total). We prefer to keep the intact side as our starting number in this mathematical operation so that we can consistently examine how innervation (relative to loss of innervation) influences cell death and proliferation. *

3) Figure 4 shows nice SuperPlots for quantifications. Why not use SuperPlots for the other figures?

*This is one of two experiments where we have reliable batch information. For most other experiments, larvae from multiple clutches and/or small batches of larval brains were often combined into a single tube at or before the immunostaining step. Therefore we did not perform SuperPlots for the other figures. *

*While revising this figure and Supplemental Figure S$ to include its batch information, we found that the code we were using to show significance on the plot was not calling the correct p-values. With our updated statistical modeling and code, we can confirm that the correct p-values are used to indicate significance. *

4) Quantifications in Figures 4 and S4 indicate that the number of proliferating cells does not change between light-dark and dark conditions in wild-type. However, the EdU staining appears much stronger in panel 4H compared to panel 4F (another picture that better reflects quantifications might be more appropriate).

*Replaced. *

5) The authors might want to include in their discussion the study of Huang et al. describing neurogenesis in the optic tectum in the tadpole (PMCID: PMC10801852).

Added in the last paragraph of the discussion. Thanks! “For example, a recent study identified the DNA repair gene BRCA1 as essential for visual-experience dependent neurogenesis in Xenopus laevis tadpoles (Huang et al., 2024). Interestingly, BRCA1-regulated DNA repair have been linked to Wnt/*β-catenin pathway activation in some populations of adult stem cells as well as intestinal cancers (Kaur et al., 2021).” * 6) Although not the topic on the manuscript, do the authors know the identity of the cells that undergo apoptosis in the neuropil after denervation?

We wish we did! We are currently designing experiments and writing grants to be able to identify cells within the neuropil.

7) Please indicate the catalog numbers of the primary antibodies used in the study (anti-GFP, etc...)

Now included

8) typos: - line 356: remove "in" after "programmed cell death" - line 371 and lines 377/378: verb missing - Table 1: Oligonucleotides - In details of counts and measurements, brain volume_genotype is listed under Fig. S2 instead of Fig. S3 (misnumbering continues thereafter).

All Fixed. In addition, we rechecked and revised all of the supplementary tables, including details for all supplemental figures and correcting figure numbering.

Reviewer #2 (Significance (Required)): By delineating how the optic nerve regulates the growth and development of the brain region it innervates, this study addresses an important question in the field of neuroscience and advances our understanding of the mechanisms that coordinate neuronal input and stem cell behavior in communicating regions of the brain. The study presents robust and convincing data supported by elegant approaches and strong statistical analyses. A major strength of the study is the identification of Wnt signaling as an important pathway mediating innervation-dependent tectal growth. The study would be further strengthened by using a second approach to manipulate Wnt signaling, and by analyzing whether Wnt signaling also regulates innervation-dependent survival. Nevertheless, this is a very well written study that will be of high interest to neuroscientists studying development, sensory systems, and responses to injury, as well as to developmental biologists studying morphogenesis and communication between tissues.

Reviewer #3 (Evidence, reproducibility and clarity (Required)): This study investigates how optic nerve innervation regulates growth of the zebrafish optic tectum (OT) during development. Using a combination of lak mutants, which lack optic nerves, and unilateral eye extirpation approaches, the authors showed that cell survival and proliferation in the OT are dependent on optic nerve innervation specifically during a window between ~7 and 9 dpf. Dark-rearing experiments revealed that the dependency on optic nerve innervation does not require light-evoked visual activity. The authors then identified decreased expression of wnt3a and the Wnt/β-catenin target genes in non-innervated tecta. They also showed that pharmacological activation of the Wnt/β-catenin pathway with BIO restored proliferation in lak mutants to wild-type levels. Interestingly, only a partial rescue was achieved in denervated one-eyed larvae, suggesting potential injury-specific mechanisms yet to be uncovered. The experiments are well designed, using complementary models to distinguish developmental absence from injury-induced loss of innervation. The identification of wnt3a as a candidate molecule will undoubtedly prompt future research. However, several aspects of the analysis and reporting, as well as evidence supporting mechanistic insights, could be strengthened, as detailed below.

Major comments: 1. While the authors have reported that the overall OT volume is unchanged between WT and lak mutants at 9 dpf, there appeared to be a trend in developing larger OT in the measurements as well as in the representative images. A potential change in size could affect measurements in cell counts and volume. It is therefore suggested that OT size could be taken into account and internally corrected in all relevant analyses.

*We did not collect brain volume measurements for all of our experiments, but we did measure the DAPI-stained volume of a subset of lak mutant and wild-type sibling brains (Figure S3; fixed at 9 dpf) and found variation among brain sizes but not a statistically significant difference. *

*In Figure 5, we normalized sox2 volume to mid-brain volume to account for differences in mounting and imaging among those specimens. Throughout the study we did our best to control for changes in brain size by centering the quantification region on the same anatomical volume for all samples. *

Sox2+ volume, EdU+ cell number, and Wnt pathway markers were each quantified independently. This limits the interpretation as to whether the decline in EdU+ cells reflects a smaller sox2+ progenitor pool, a lower probability of individual sox2+ cells entering the cell cycle, or both occurring in parallel. Furthermore, it remains unclear whether axin2/lef1/wnt3a expression occurs within the sox2+ population itself or in a distinct neighbouring population. Co-labelling experiments and higher resolution imaging could directly test these possibilities.

*We agree and have revised the text to be as clear as possible about what and how we measured sox2 and EdU, doing our best to be conservative in our interpretations. *

The decrease in sox2 mRNA by qPCR and sox2+ volume should be interpreted with caution. It is unclear whether the decrease in volume is due to a smaller pool of sox2+ progenitors or an overall decrease in sox2 expression within the same pool size. The non-significant cyclin D1 mRNA difference may offer some insights into cell-cycle entry probability.

We have made several edits to the text related to sox2 levels and the various possibilities for cell cycle progression within lak mutant tecta. We emphasize that optic nerve innervation may be linked to “levels of sox2 expression and/or promote maintenance or proliferation of sox2+ neural stem cells in the optic tectum” on page 9 and further discuss possible connections between sox2 and Wnt pathway activation on pages 10 and 14.

Our measures of the levels of ccnD1 mRNA are unlikely to be predictive of cell cycle speed given that the mRNA was isolated from many midbrains (not just the OT) and that ccnD1 transcript is not known to fluctuate with the cell cycle.

The rationale for choosing lef1 as a Wnt/β-catenin readout, and the interpretation of its non-significance in some measurements, in contrast to the more consistently significant axin2, could be discussed.

We revised the text slightly to include more information about axin2, as an immediate (auto-regulatory) target of the pathway, and lef1, which is a known effector of the pathway and can be regulated by B-catenin. However, several studies provide evidence that transcription of lef1 can be activated in B-catenin as well as other signaling pathway-transcription factor combinations. For example, Grumolato et al., 2013 and Hao et al., 2019 (as well as other studies) provide evidence that lef1 can be activated independently of B-catenin by ATF2 and MYC).

5A. Partial rescue of proliferation by BIO in one-eyed larvae is a fascinating observation. Given that this is one of the more striking asymmetries in the paper between the two models, it would be important to discuss potential mechanisms involved. For example, the authors have reported acute neuropil apoptosis one day after eye extirpation, but how this might indirectly influence the adjacent TPZ progenitor cells is not discussed.

We agree. We’ve added a sentence to the discussion, which states “In addition, how cell death in the tectal neuropil resulting from optic nerve injury potentially signals to nearby tectal cells and impacts their behaviors, such as proliferation and cell death is an area ripe for further exploration.”

5B. Furthermore, any possible effects of the lak mutation directly within the OT independent of RGC/innervation loss would also have an impact on how comparable the lak and one-eyed models are. As far as we’re aware (from searching PubMed, ZFIN, and two sc-RNA-Seq datasets) atoh7 is expressed strongly and almost exclusively in the retina. It could be interesting for a future study to explore whether a small population of atoh7+ cells exists outside of the retina and what their function is.

Delta-Notch and Shh pathways are introduced in the introduction as plausible OT growth regulators, but only Wnt/β-catenin is functionally tested. The Shh pathway comparison (Fig S7) consists of representative images only, with no quantification, statistics, or reported sample size, and the images themselves show low signal and substantial background, making it difficult to assess whether the assay worked as intended.

We initially tried to be more comprehensive in our introduction but focused the manuscript on Wnt/B-catenin pathway. We have now streamlined the introduction, including less information about the various signaling pathways.

*After examining the images of the Shh ISH data, we realized that there are not enough images that are quantifiable and so opted to remove mention of Shh/Hh pathway in the introduction and results and removed the original Figure S7. *

Minor comments: 1. In the concluding statement within the introduction (lines 73-77), the authors stated that "survival, proliferation, and differentiation of OT cells require optic nerve innervation". However, the data suggest that "differentiate into HuC+ neurons at indistinguishable rates." This is a contradiction that requires clarification.

*Thanks! We removed “and differentiation” so the statement is now consistent. * 2. The ratio calculation appears counterintuitive. The authors used left-right/total which resulted in a positive number for when the effect is a reduction.

We prefer to keep the calculation the same for all of the figures and to keep the innervated/left side as the first term in the mathematical comparison so that the focus is on the positive effect of innervation.

Reviewer #3 (Significance (Required)): This is a well-designed study combining genetic and surgical models, dark-rearing controls, and a pharmacological rescue, to define a discrete developmental window (~7-9 dpf) when OT progenitor survival and proliferation depend on innervation. Core strength of the study is the insights into a critical period across two independent innervation paradigms with pharmacological rescue showing the involvement of Wnt/β-catenin signalling. The main limitations lie in quantification approaches and the lack of direct correlation between independently assessed parameters. This study could be strengthened by stronger focus and evidence into OT progenitor cell-type specific effects.

While the demonstration that OT growth depends on optic nerve innervation confirms existing knowledge in the field, this study offers several more specific advances:

• A critical window (~7-9 dpf) when OT development depends on optic nerve innervation achieved using complementary genetic/surgical models. • Evidence that this is independent of light-evoked visual activity. • Evidence that Wnt/β-catenin activity, specifically wnt3a, correlates with innervation-dependent OT proliferation, supported by rescue data.

This paper is suitable for visual/sensory system developmental neuroscientists interested in stem cell niches, neurogenesis, and activity-dependent circuit formation.

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Referee #3

Evidence, reproducibility and clarity

This study investigates how optic nerve innervation regulates growth of the zebrafish optic tectum (OT) during development. Using a combination of lak mutants, which lack optic nerves, and unilateral eye extirpation approaches, the authors showed that cell survival and proliferation in the OT are dependent on optic nerve innervation specifically during a window between ~7 and 9 dpf. Dark-rearing experiments revealed that the dependency on optic nerve innervation does not require light-evoked visual activity. The authors then identified decreased expression of wnt3a and the Wnt/β-catenin target genes in non-innervated tecta. They also showed that pharmacological activation of the Wnt/β-catenin pathway with BIO restored proliferation in lak mutants to wild-type levels. Interestingly, only a partial rescue was achieved in denervated one-eyed larvae, suggesting potential injury-specific mechanisms yet to be uncovered. The experiments are well designed, using complementary models to distinguish developmental absence from injury-induced loss of innervation. The identification of wnt3a as a candidate molecule will undoubtedly prompt future research. However, several aspects of the analysis and reporting, as well as evidence supporting mechanistic insights, could be strengthened, as detailed below.

Major comments:

1. While the authors have reported that the overall OT volume is unchanged between WT and lak mutants at 9 dpf, there appeared to be a trend in developing larger OT in the measurements as well as in the representative images. A potential change in size could affect measurements in cell counts and volume. It is therefore suggested that OT size could be taken into account and internally corrected in all relevant analyses.
2. Sox2+ volume, EdU+ cell number, and Wnt pathway markers were each quantified independently. This limits the interpretation as to whether the decline in EdU+ cells reflects a smaller sox2+ progenitor pool, a lower probability of individual sox2+ cells entering the cell cycle, or both occurring in parallel. Furthermore, it remains unclear whether axin2/lef1/wnt3a expression occurs within the sox2+ population itself or in a distinct neighbouring population. Co-labelling experiments and higher resolution imaging could directly test these possibilities.
3. The decrease in sox2 mRNA by qPCR and sox2+ volume should be interpreted with caution. It is unclear whether the decrease in volume is due to a smaller pool of sox2+ progenitors or an overall decrease in sox2 expression within the same pool size. The non-significant cyclin D1 mRNA difference may offer come insights into cell-cycle entry probability.
4. The rationale for choosing lef1 as a Wnt/β-catenin readout, and the interpretation of its non-significance in some measurements, in contrast to the more consistently significant axin2, could be discussed.
5. Partial rescue of proliferation by BIO in one-eyed larvae is a fascinating observation. Given that this is one of the more striking asymmetries in the paper between the two models, it would be important to discuss potential mechanisms involved. For example, the authors have reported acute neuropil apoptosis one day after eye extirpation, but how this might indirectly influence the adjacent TPZ progenitor cells is not discussed. Furthermore, any possible effects of the lak mutation directly within the OT independent of RGC/innervation loss would also have an impact on how comparable the lak and one-eyed models are.
6. Delta-Notch and Shh pathways are introduced in the introduction as plausible OT growth regulators, but only Wnt/β-catenin is functionally tested. The Shh pathway comparison (Fig S7) consists of representative images only, with no quantification, statistics, or reported sample size, and the images themselves show low signal and substantial background, making it difficult to assess whether the assay worked as intended.

Minor comments:

1. In the concluding statement within the introduction (lines 73-77), the authors stated that "survival, proliferation, and differentiation of OT cells require optic nerve innervation". However, the data suggest that "differentiate into HuC+ neurons at indistinguishable rates." This is a contradiction that requires clarification.
2. The ratio calculation appears counterintuitive. The authors used left-right/total which resulted in a positive number for when the effect is a reduction.

Significance

This is a well-designed study combining genetic and surgical models, dark-rearing controls, and a pharmacological rescue, to define a discrete developmental window (~7-9 dpf) when OT progenitor survival and proliferation depend on innervation. Core strength of the study is the insights into a critical period across two independent innervation paradigms with pharmacological rescue showing the involvement of Wnt/β-catenin signalling. The main limitations lie in quantification approaches and the lack of direct correlation between independently assessed parameters. This study could be strengthened by stronger focus and evidence into OT progenitor cell-type specific effects.

While the demonstration that OT growth depends on optic nerve innervation confirms existing knowledge in the field, this study offers several more specific advances:

• A critical window (~7-9 dpf) when OT development depends on optic nerve innervation achieved using complementary genetic/surgical models.
• Evidence that this is independent of light-evoked visual activity.
• Evidence that Wnt/β-catenin activity, specifically wnt3a, correlates with innervation-dependent OT proliferation, supported by rescue data.

This paper is suitable for visual/sensory system developmental neuroscientists interested in stem cell niches, neurogenesis, and activity-dependent circuit formation.

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

Summary:

This manuscript focuses on defining the molecular pathways that couple retinal input to the growth of the optic tectum in the larval zebrafish. Using a mutant line lacking retinal ganglion cells as well as an elegant model of unilateral enucleation to prevent tectal innervation, the authors demonstrate that optic nerve input is required for the survival and proliferation of tectal cells at late stages regardless of environmental light conditions used. The authors further show that a lack of innervation correlates with a decreased expression of sox2+ and a down-regulation of Wnt signaling in the tectum. Importantly, treating larvae with BIO, a Wnt pathway activator, restores proliferation of tectal cells in the absence of innervation, supporting an essential role for Wnt signaling in innervation-dependent tectal growth.

Major comments:

This study presents robust and convincing data supported by elegant approaches and strong statistical analyses. The following points should be addressed:

• The authors nicely show reduced Wnt signaling in the absence of retinal innervation and that treatment with BIO restores proliferation in the tectum. While these results strongly suggest that Wnt signaling is the main pathway controlling innervation-dependent tectal proliferation, BIO's mode of action is to inhibit GSK3β, which might have other Wnt-independent effects. Does pharmacologically inhibiting Wnt signaling (for instance, by using IWR1) phenocopy the reduced proliferation seen in the absence of innervation?
• Does activating the Wnt pathway using BIO also reduce the number of apoptotic cells observed when innervation is lacking?
• (Optional) Figure 5 shows a clear decrease in sox2 staining in lak that indicates a reduced number of sox2+ neural progenitor cells. Do sox2+ cells die early or/and is their rate of proliferation reduced in the absence of innervation? Answering this question would provide an important clue regarding the identity of the cells that die (tectal neurons that lack or loose connections vs progenitors).

Minor comments:

1) A schematic that indicates where the TPZ is in relation to tectal neurons and the neuropil would help readers not familiar with zebrafish anatomy.

2) There is a discrepancy between the main text and figures regarding how TUNEL+ cells were quantified in denervated larvae: the text (lines 115-116 and 600-601, for instance) indicate that numbers of TUNEL+ cells in intact and denervated sides were substracted, whereas figure 2 indicates that a ratio between the innervated and denervated sides was calculated. A similar discrepancy is present for the number of EdU+ cells and in other figures. It might be easier for readers to calculate denervated - intact (rather than intact - denervated), so that positive values represent "more" and negative values, "less" (as of now, it is a bit counterintuitive that negative values represent more apoptotic cells, for instance).

3) Figure 4 shows nice SuperPlots for quantifications. Why not use SuperPlots for the other figures?

4) Quantifications in Figures 4 and S4 indicate that the number of proliferating cells does not change between light-dark and dark conditions in wild-type. However, the EdU staining appears much stronger in panel 4H compared to panel 4F (another picture that better reflects quantifications might be more appropriate).

5) The authors might want to include in their discussion the study of Huang et al. describing neurogenesis in the optic tectum in the tadpole (PMCID: PMC10801852).

6) Although not the topic on the manuscript, do the authors know the identity of the cells that undergo apoptosis in the neuropil after denervation?

7) Please indicate the catalog numbers of the primary antibodies used in the study (anti-GFP, etc...)

8) typos:

• line 356: remove "in" after "programmed cell death"
• line 371 and lines 377/378: verb missing
• Table 1: Oligonucleotides
• In details of counts and measurements, brain volume_genotype is listed under Fig. S2 instead of Fig. S3 (misnumbering continues thereafter).

Significance

By delineating how the optic nerve regulates the growth and development of the brain region it innervates, this study addresses an important question in the field of neuroscience and advances our understanding of the mechanisms that coordinate neuronal input and stem cell behavior in communicating regions of the brain. The study presents robust and convincing data supported by elegant approaches and strong statistical analyses. A major strength of the study is the identification of Wnt signaling as an important pathway mediating innervation-dependent tectal growth. The study would be further strengthened by using a second approach to manipulate Wnt signaling, and by analyzing whether Wnt signaling also regulates innervation-dependent survival. Nevertheless, this is a very well written study that will be of high interest to neuroscientists studying development, sensory systems, and responses to injury, as well as to developmental biologists studying morphogenesis and communication between tissues.

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Referee #1

Evidence, reproducibility and clarity

Summary

This manuscript addresses how optic tectum development changes relative to innervation from the retina. While previous studies in zebrafish already showed a link between retinal input to optic tectum growth, the cellular and molecule cues that contribute to such innervation-dependent growth remain poorly understood. Here, Olivia Hagen and colleagues analyze cell survival and proliferation in the optic tectum in three experimental conditions: wild-type larvae; lakritz (lak) mutant larvae, lacking retinal ganglion cells and in consequence bearing no optic nerves; and wild-type one-eyed larvae, in which one eye has been surgically removed. Combining cellular and pharmacological approaches, the authors identify a critical period in which survival, proliferation, and differentiation of optic tectum cells require retinal nerve innervation. Further, they demonstrate an instructive role for innervation in activating Wnt/ -catenin pathway activity to promote optic-nerve dependent proliferation in the optic tectum.

Major comments

1. Although conclusions reached by the authors are based on solid data and statistical analysis, the presentation of the experimental logic and results in the text are often not well structured. In consequence, the manuscript is difficult to read and to understand. For instance, throughout most of the results part, the conclusion of the experiment comes before the actual explanation of the experimental and quantification procedure. Further, why certain experiments are conducted is not well stated. Some specific examples:
2. Page 3: Why the tectum neuropil is not taken in account in cell survival and cell proliferation quantifications is not stated.
3. Page 4: The reason why authors asses neuronal differentiation together with proliferation in the different experimental conditions is not explained (Page 2).
4. Page 4: Why the authors measure brain size is not explained. It is understood that it is to check the specificity of the phenotype, however it should be clearly stated.
5. Page 6: End of the result section 'Physical connections between the eye and brain via the optic nerve link optic tectum cell survival and proliferation'. There is no conclusion to this section.
6. Page 7, section 'Extent of sox2+ expression correlates with innervation', there is no mentioning in the text that sox2 expression is assesed by fluorescent in situ hybridization.

On top of that, certain wording or phrasing can sometimes lead to a misleading message: - Page 4: Lines 137-138 'Statistical analyses suggest that both age and genotype influence proliferation (ANOVA, f(2)=3.215, p<0.05) with age as the main driver of the observed differences (ANOVA, f(2)=43.05, p<0.001).' The use of the words 'main driver' is misleading. The sentence reads as the developmental stage and not the genotype is what is causing a reduction in proliferation in the lak mutants. I suppose that what the authors mean is that the developmental stage 'matter'. Differences in proliferation between WT and mutants arise at 9dpf, identifying a developmental time window in which retinal innervation seems to be important for proliferation in the tectum. There are more examples of this in other parts of the text that should be revised.

Overall, I think the authors should carefully revise the text and re-write it, to make it clearer and more understandable. It is a pity that such good work is hidden under confusing writing. 3. In page 7, section 'Wnt/b-catenin pathway is upregulated in the OT with retinal innervation', I think it would be good to show quantification of expression areas for the Shh and Hh pathway genes, as done with Wnt/b-catenin pathway genes in Figure 6.

Minor comments and typos:

1. Figure 1 very well shows retinal innervation of the optic tectum in the different experimental contexts. However, the images in the rest of the figures look very different, making it difficult to identify the structures of interest. In Figure 2, the different anatomical structures of interest (retina, OT, neuropil) should be clearly indicated in at least one image. A scheme recapitulating what is seen in the images (similar to the one of figure 9) would be helpful.
2. In all figures, please indicate the number of independent experiments and the number of larvae analyzed per experiment (even if this information is collected in the Tables S2 and S4)
3. The statistical results in brackets in the main text often difficult the reading. I would suggest removing them from the main text and place them in the figure legends instead.
4. I would indicate with an asterisk the denervated side instead of the intact or innervated one.
5. Here are some typos I spotted in the text:

Line 354 - 'While our EdU to analyses could also be also consistent with a longer cell cycle...' delete the words 'to' and 'also'.

Line 356 - 'Both elevated levels of programmed cell death in as well as...' delete the word 'in'.

Line 370- 'Many open questions about how programmed cell death contributes to the neuronal circuit remodeling required for lifelong growth and development'. A word is missing here, 'remain' maybe?

Figure 1 legend, third line- 'typical innervation of the tectum by the optic nerve, visible as the axons from the atoh7+ retinal ganglion cells'. This sentence is not clear, rephrase please.

Significance

The strengths of the manuscript are in the approaches. The systematic evaluation and quantification of optic tectum cell survival and proliferation across different experimental conditions, in which optic tectum innervation is impaired, make the results of this study very solid. Further, not only they report a correlation between Wnt/b-catenin downstream genes and innervations deffects, but they provide a mechanistic causal insight via rescue experiments. Overall, this is a constructive advance in our understanding of mechanisms guiding neurogenesis during development, opening an interesting line of research to further explore these pathways not only during neurodevelopment, but also in the context of neuronal regeneration.

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Reply to the reviewers

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

This study addresses an important question at the intersection of inflammation, aging, and neurodegeneration by investigating how antimicrobial peptides (AMPs) affect neuronal integrity. Using a combination of Drosophila genetics, imaging, behavioral assays, electrophysiology, and microbiota manipulations, the authors provide evidence that infection and aging increase phosphatidylserine (PS) exposure at the neuromuscular junction (NMJ), thereby promoting AMP binding and neuronal damage. This study further shows that stress-induced Turandot proteins (Tots) antagonize AMP-PS interactions and protect motoneurons from degeneration. The findings are interesting, mechanistically relevant, and build on the authors' previous work demonstrating a protective role of Turandots in the tracheal system. Overall, I find the study potentially suitable for publication. However, several aspects of the experimental design, data interpretation, and presentation require clarification before publication.

Major comments 1. Relationship to the authors' previous study and tissue specificity of the Turandot-AMP-PS pathway The current study can be viewed as a direct extension of the authors' previous work demonstrating that Turandot proteins protect tracheal tissues from AMP-induced cytotoxicity through masking of negatively charged phospholipids. The present manuscript extends this model to the peripheral nervous system and links it to neurodegeneration. While this extension is interesting, the manuscript does not sufficiently discuss what new conceptual insight is gained beyond demonstrating a similar mechanism in a different tissue. More specifically, it remains unclear whether the Turandot-mediated protection against AMP toxicity is a neuron-specific phenomenon or represents a general tissue-protective mechanism operating throughout the organism. This issue becomes particularly relevant because Figure 1E shows PS exposure not only in neurons but also in muscle cells. Likewise, the authors' previous study demonstrated PS-dependent AMP toxicity in tracheal tissues. Therefore, the manuscript would benefit from a more explicit discussion of tissue specificity versus generality of the AMP-PS-Turandot axis and a clearer explanation of how the current findings advance the conclusions of the previous study.

Although this manuscript can be viewed as a follow-up to our previous study describing Turandot-mediated protection of the tracheal epithelium, it provides several important new findings. First, using endogenously tagged antimicrobial peptides (AMPs), we show that AMPs can bind directly to the surface of neurons. Combined with the generation of new knock-in lines, this approach allowed us to monitor AMP binding to host tissues in vivo and definitively demonstrate that this binding depends on lipid scrambling. Moreover, the increased AMP binding observed in Tot mutants provides in vivo evidence that Turandot proteins compete with AMPs for membrane binding, extending our previous observations made in vitro. To our knowledge, direct binding of AMPs to neuronal membranes has not previously been reported, and our results provide direct evidence for AMP-mediated neurotoxicity that had previously been suggested only by indirect observations. Second, we show that systemic infection induces phosphatidylserine (PS) exposure, revealing an unexpected link between infection and this negatively charged phospholipid, which is more commonly associated with apoptotic cell death. Third, whereas our previous study described a toxic process occurring during metamorphosis, the present study identifies a protective mechanism operating in adult flies. Importantly, the adult-onset phenotype allows us to precisely follow the sequence of events leading to neurodegeneration and to distinguish the effects of infection, PS exposure, AMP binding, and neuronal loss. These findings that are highly relevant to the proposed connection between infection, PS exposure, and neurodegeneration are now included in the Discussion.

We agree that the specificity of Turandot protection was not properly discussed in the manuscript. So far, we have documented Tot-mediated protection in the trachea and in neurons that expose PS. We believe that the specificity of the protection is given by the propensity to expose PS, as not all tissues expose similar levels of PS upon stress. Tissues like enterocytes or oenocytes do not expose significant amounts of PS after infection, as shown in NEW_Figure_EV2. We anticipate that all PS-exposing tissues may be protected from AMPs by Tot. However, not all tissues may be similarly susceptible to AMPs, raising the possibility that these tissues do not need Turandot protection. The universality vs. specificity of PS exposure upon stress and Turandot-mediated protection is now extensively discussed in the Discussion.

Temporal relationship between AMP induction and Turandot-mediated protection The proposed model assumes that Turandot proteins protect neurons by competing with AMPs for binding to PS-exposed membranes. However, the kinetics of this interaction remain unclear. AMP expression is typically induced rapidly following infection, whereas most experiments in the manuscript examine relatively late time points (16-40 hours post-infection). It is therefore difficult to understand when and how Turandots exert their protective effect. If the function of Turandots is to prevent AMP-PS interactions, one might expect Turandot accumulation to occur before or at least concomitantly with AMP recruitment. The manuscript would benefit from additional discussion of, or ideally, experimental data on the temporal dynamics of AMP induction, Turandot induction, and AMP recruitment to the NMJ.

We followed the reviewer’s advice and have added significant experimental work to address this question. We now show the expression pattern of the antibacterial peptide DptA and TotA in the fat body after infection in NEW_Figure_EV1. Our results show that both DptA and TotA are induced at early timepoints, although TotA expression peaks later than DptA. We also quantified neuronal PS exposure at different timepoints and found that it happens as early as 6 h post-infection (NEW_Figure 1). Because DptA and TotA are not fully matched in terms of expression kinetics, neurons may pass through an early period in which PS is exposed while Turandot protection is still developing. This point is also highlighted in the Discussion.

Relationship between AMP binding, PS exposure, and neuronal damage One aspect of the proposed model that I found difficult to fully understand concerns the relationship between AMP binding, PS exposure, and neuronal damage. The authors propose that AMPs are recruited to PS-exposing neurons and that Turandot proteins limit this interaction. However, Figure 1B and Figure 1D show detectable DptA-HA localization at NMJs even under unchallenged conditions, where obvious neuronal damage is not apparent. In addition, Figures 2A and 2B indicate that infection alone does not induce overt bouton fragmentation in wild-type flies despite detectable AMP recruitment. These observations raise a question regarding the sequence of events. Is PS exposure the primary event that attracts AMPs to neuronal membranes, or could AMP accumulation itself contribute to membrane stress and subsequent PS externalization? The manuscript does not necessarily need to resolve this question experimentally, but a more detailed discussion of these possibilities would help readers better understand the proposed mechanism and reconcile the observations made under basal and infection conditions.

DptA-HA localization at NMJs presented in Figure 1B and Figure 1D is only seen upon overexpression of DptA-HA, not with the endogenously tagged DptA-HA. This suggests that balanced expression of TotA and DptA prevents DptA binding in normal context. Constitutively high expression of DptA by Gal4-driven overexpression probably overwhelms Turandots, leading to NMJ binding. The same arguments apply regarding the results shown in Figure 2. We have modified the Discussion to address the comments on the interplay between Tot and AMPs, the sequence of events and the involvement of AMPs in PS exposure.

Interpretation of the Relish knockdown experiment (Figure 1C)

The interpretation of Figure 1C is somewhat confusing. The authors conclude that fat body-derived AMPs bind neurons because Relish knockdown in the fat body abolishes DptA-HA recruitment to NMJs following infection. However, Relish is required for DptA expression itself. Therefore, loss of neuronal staining in this experiment is expected simply because DptA is no longer produced. While the experiment supports the conclusion that infection-induced DptA originates from the fat body, it does not directly address the mechanism of neuronal recruitment. The authors should revise the interpretation accordingly.

Indeed, the use of Relish fat body knockdown only shows that DptA originating from the fat body can bind to neurons, without addressing the mechanism. This sentence has been rephrased to provide better clarity.

1. Systemic versus local accumulation of Turandot proteins In Figure 2C, TotA accumulation is observed at the NMJ after infection. However, the staining pattern appears broadly distributed rather than restricted to the NMJ. Given that Turandots are known circulating humoral factors, the data seem more consistent with systemic accumulation following infection than with specific targeting of NMJs. The authors should discuss this point and clarify whether they propose any tissue-specific recruitment mechanism.

As mentioned above in response to point 1, we propose that PS exposure defines the specificity of tissue recruitment. PS is not equally exposed by all tissues. Similarly, Tots do not bind to all tissues. As shown in Figure 1 and NEW_Figure_EV2, PS is preferentially exposed by neurons, glia and muscle at the NMJ but poorly detected on other tissues (except trachea). This point is now discussed in the Discussion section.

AMP specificity Figure 2F demonstrates that deletion of the four Cecropin genes partially rescues the phenotype, whereas deletion of twelve AMP genes produces a stronger rescue. This suggests that some AMP classes contribute more strongly than others to neuronal toxicity. It would be valuable to discuss whether AMP potency correlates with known biochemical properties such as net positive charge, membrane affinity, or phosphatidylserine-binding capacity. If relevant literature is available, discussing it would strengthen the mechanistic interpretation.

A paragraph has been added to the Discussion to describe the biochemical properties of Cecropins that may explain their contribution to the PS-dependent phenotype.

Interpretation of the Draper experiment (Figure 4E) I had difficulty following the logic underlying the Draper experiments. Exposed PS on neuronal cells is classically regarded as an "eat-me" signal that promotes clearance of PS-exposed neuronal cells through the PS receptor Draper. Under this framework, one would expect that impaired glial engulfment would reduce the clearance of damaged neuronal material and potentially exacerbate degeneration. Instead, the authors appear to test whether Draper-dependent glial activity actively contributes to bouton fragmentation. While the negative result is used to conclude that glial phagocytosis is not responsible for the phenotype, the rationale behind this prediction is not sufficiently explained. A clearer discussion of the expected outcomes and their interpretation would greatly improve the accessibility of this section, particularly since similar arguments are presented in the Discussion (lines 298-302).

The reviewer is correct. We use here the Draper mutants not to confirm that the bouton fragmentation we observed is not caused by glial phagocytosis. We have restructured this paragraph as well as the Discussion to better explain the rationale of this experiment.

Interpretation of muscle-specific phosphatidylserine manipulation experiments (Figure 4D and 4F) I found the muscle-specific PS manipulation experiments interesting, but I was not entirely sure how they support the conclusion presented in the text. The authors conclude that these data "highlight the specific contribution of neuronal PS exposure" (lines 264-265). My understanding is that reducing PS exposure specifically in muscles does not affect motoneuron fragmentation in Tot-deficient animals (Figure 4D), and that increasing PS exposure in muscles is also insufficient to induce the phenotype (Figure 4F). These results clearly argue that muscle PS exposure alone is not sufficient to drive degeneration. However, it is less clear whether these experiments, by themselves, establish a specific requirement for neuronal PS exposure. Rather, this conclusion appears to rely on combining these muscle-specific manipulations with neuron-targeted perturbations presented elsewhere in the manuscript. More generally, because PS exposure is observed in both neuronal and muscle compartments following infection (Figure 1E), and given previous evidence for AMP-PS interactions in other tissues, it remains possible that PS exposure represents a more general stress response. In this context, additional clarification of how tissue specificity is inferred, and to what extent systemic versus local effects are excluded, would strengthen the mechanistic interpretation.

Modulating PS exposure in muscles and neurons using specific gal4 driver allows us to show that neurodegeneration likely results from neuron exposing PS, not muscles. Indeed, motoneuron-specific knockdown of scramb1 is sufficient to abolish motoneuron degeneration in Tot-deficient flies, arguing for a cell-autonomous phenotype rather than a systemic effect. In line with this idea, performing the same manipulation in muscles failed to rescue NMJ degeneration in Tot mutants, suggesting that PS exposure in muscles does not drive the NMJ degeneration. This result also suggests that NMJ degeneration is not rescued by lowering PS exposure in any tissue, arguing against a systemic consequence of reducing total exposed PS.

Following the reviewer’s advice, we have edited the text to adjust the interpretation and elaborate on the specificity of the response in the Discussion. We also discuss the potential differences in resilience to AMPs between muscles and neurons.

Minor comments 1. Several markers and assays are introduced without sufficient explanation for non-specialist readers. For example, the rationale for using anti-HRP as a neuronal marker is not explained. Likewise, additional background on how bouton fragmentation is inferred from Brp and Vglut staining would improve accessibility.

This is a good point and we are sorry for this lack of clarity. We have now improved the explanation of the methods used and their rationale by three means. First, we added a NEW Figure 1B representing a schematic of a NMJ, its different compartments and the markers used to define them. We also rephrased the result section to clarify the use of anti-HRP and Vglut staining. Finally, we expanded the method section to better explain the strategy used for quantification.

The organization of the Results section could be improved. In several cases, transitions between figures are difficult to follow (e.g., Figure 1C-D and Figure 3K-L). Reorganizing sections to better align with the experimental narrative would improve readability. In addition, some negative results (e.g., Figure 3G-K) might be more appropriate for the supplementary material, particularly because the manuscript subsequently returns to bouton fragmentation analyses in Figure 3L-O.

As suggested, we have moved Figure 3G-K panels and all data related to electrophysiological measurements as supplementary material (NEW Figure EV3). We have also rewritten the transition from figure 1C to 1D to give better clarity. We thank the reviewers for this comment and hope that the revision improves clarity.

In lines 216-217, the authors state that they observed a decline in both forms of neurotransmission. If so, statistical comparisons between day 5 and day 20 samples should also be provided.

As suggested, the statistical comparisons have been added when significant and the text has been edited accordingly.

In Figure 4A, the description of a "slight increase" (line 256) is vague. Please clarify which age groups differ significantly and which comparison this statement refers to.

We thank the reviewer for pointing this out, there was a mistake in the statistical analysis. It has been corrected and the manuscript has been amended. We now state that the increase is moderate and not significant.

Reviewer #1 (Significance (Required)):

Field of expertise Drosophila neurobiology, neuroimmune interactions, synaptic physiology, glial biology, antimicrobial peptide biology. I am not an expert in the biochemical properties of Turandot proteins or AMP-lipid binding at the structural level, and my evaluation is based primarily on genetic and functional interpretation.

General assessment This study investigates how antimicrobial peptides (AMPs) contribute to neuronal degeneration and proposes that phosphatidylserine (PS) exposure at the neuromuscular junction promotes AMP binding, while Turandot proteins provide protection by interfering with this interaction. The authors combine Drosophila genetics, imaging, and functional assays to support this model. The work is technically solid and uses a broad experimental toolkit. Its main strengths are the in vivo functional analysis of AMP-induced synaptic defects and the extension of previously described Turandot functions to the nervous system. However, the mechanistic interpretation is limited by incomplete clarification of causal relationships between PS exposure, AMP binding, and neuronal damage, as well as uncertainty regarding tissue specificity versus systemic effects.

Advance The study extends prior work on Turandot-mediated protection from AMP toxicity by proposing a lipid-based mechanism operating at synaptic membranes in the peripheral nervous system. If fully supported, this would provide a conceptually interesting link between innate immune effectors and phospholipid exposure in neuronal degeneration. However, the extent to which this represents a neuron-specific mechanism, rather than a broader systemic stress response affecting multiple tissues, remains unclear. As a result, the main advance is best viewed as a proposed extension of an existing AMP-lipid interaction framework into neuronal tissue, rather than a fully established tissue-specific mechanism.

Audience The study will be of interest to researchers in neurobiology, neuroimmunology, and Drosophila-based systems neuroscience, particularly those studying synaptic maintenance, glial function, and innate immune signaling. It may also be relevant to broader audiences interested in infection- or inflammation-induced neurodegeneration.

Overall significance Overall, the study proposes a potentially interesting mechanism linking antimicrobial peptides to synaptic degeneration via PS exposure. Its main limitation lies in the incomplete resolution of whether this mechanism is neuron-specific or reflects a more general systemic response to stress.

We hope that our revision has now clarified the points raised by this reviewer and indeed reveals that PS exposure by neurons upon systemic infection create a vulnerability to antimicrobial peptides.

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

In this manuscript, Lemaitre and coll extend a previous report from their group (PMID : 38484734) on the critical role played by proteins of the Turandot family in the protection of host tissues against the toxic, membrane targeted effects of antimicrobial peptides. Whereas the prior study published in 2024 largely focused on protection of the respiratory tract, here the authors investigate the protective effect of Turandot proteins on the peripheral nervous system and establish a connection with protection against neurodegeneration during aging. The study fully exploits the assets of the drosophila model for studies in integrative biology, combining elegant genetics and imaging to obtain experimental data that support the claims of the authors. The manuscript reads well, appropriate controls are present in all experiments and I did not detect any flaw in the logic.

We are pleased that the reviewer is very positive on our manuscript and thank them for their comments. As mentioned above, we want to stress that this paper is not just an extension of previous work but reveals for the first time the binding of AMP to host tissues, the role of PS in this context and the impact of infection on PS exposure.

Minor comments: 1) It is not clear why two different scramblases are used, Xkr8 and scramb1 (e.g., Fig1G-H or Fig4D vs 4G-H).

We used two complementary approaches to test the involvement of PS scrambling, the heterologous expression of a mouse scramblase (Xkr8) and the knockdown of a Drosophila protein involved in scrambling (scramb1). Although Scramb1 was demonstrated to participate in lipid scrambling, its molecular function is still debated in the field as its predicted structure does not harbor the features of a canonical scramblase. We have changed the text to better explain this point.

2) The authors may want to provide some explanation for the choice of conditions for the challenges with bacteria (e.g., 16h or 40h post infection in Fig1; 36h post infection in Fig2, or 96h after injection of heat killed bacteria).

The choice of timepoints was mostly dictated by different expression kinetics of AMPs (endogenous vs. ectopic expression) and technical reasons. AMP immunostainings are performed in one day, therefore early timepoints such as 6h post infection require complex logistics. We therefore chose later timepoints (16h) in which endogenous DptA is still detectable at NMJs. When AMPs were overexpressed by UAS/Gal4 system, we chose to increase the incubation post-infection to 36-40h to achieve stronger AMP expression levels. Finally, we used 96h incubation after infection with heat-killed bacteria as we found that the presence of tissue debris in earlier timepoints prevented robust imaging and quantification of synaptic boutons. We have clarified this point in the Methods section.

3) Line 156: a reference for Brp is missing

We have added a reference for Brp (Wagh et al., 2006).

4) Fig2C: the colocalization is hard to see, I see mainly purple, reflecting induction of TotA. Please point to the areas showing TotA enrichment at the NMJ following infection.

The magnification was increased and some pointers were added in NEW Figure 2C to show TotA enrichment at the NMJ.

5) Fig3A: background for the use of Vglut should be provided.

As mentioned above, we have now improved the explanation of the methods used and their rationale. First, we added a NEW Figure 1B representing a schematic of a NMJ, its different compartments and the markers used to define them. We also rephrased the Results section to clarify the use of anti-HRP and Vglut staining.

6) Fig3D: why is a ts driver used to control Trio expression? When is expression turned on? Information regarding the ts-dependent expression of AMPs in Fig3N-O is also lacking.

Trio needs to be expressed conditionally after the animal has eclosed to avoid growth/guidance phenotypes. We have added more information on the TS expression of Trio: Expression is turned on one week after eclosion. Information regarding the ts-dependent expression of AMPs and trio is now described in the Methods section.

7) Line 248: the effect of DptA does not reach statistical significance, please correct the statement.

The statement regarding DptA has been removed from the text.

8) Fig4F,G: according to the text (line 273) the panel for motoneurons should be F and muscles should be G

This was a mistake. Panels F and H have been swapped to match the text. The figure legend has been corrected accordingly.

9) It would be interesting to include some speculations/hypothesis in the discussion on (i) the primary contribution of cecropin peptides (Fig4H) and (ii) the mechanism mediating exposure on PS on the surface upon infection. As requested by two reviewers, we have added a section in the Discussion speculating on the specific contribution of Cecropins to the phenotype. The section discussing mechanisms mediating PS exposure has been rewritten to better describe the various hypotheses, including a potential contribution of AMPs themselves.

Reviewer #2 (Significance (Required)):

This manuscript extends a previous study describing the protective role of Turandot proteins on host tissues. Its strength is the exploitation of the model of drosophila fruit flies to provide solid in vivo evidence on the toxic effects of antimicrobial peptides and on the important contribution of Turandot proteins to limit damage. By convincingly demonstrating a key function of Turandot in the protection of the peripheral nervous system and establishing a connection between aging, dysbiosis, induction of antimicrobial peptides and promotion of neurodegeneration, the manuscript fills an important fundamental gap and should have a broad impact. The results presented imply that factors functionally similar to Turandot proteins are likely to exist in other animals, including humans: their discovery and characterization would have a major influence in the field of aging and neurodegeneration.

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

In this excellent paper, the authors follow up on their previous finding (Rommelaere et al. 2024, ref. 48)that the Turandot (Tot) peptides can protect stressed cells, which expose phosphatidylserine on the surface, from attack by antibacterial peptides. This becomes particularly evident at the neuromuscular junction, which becomes damaged when antibacterial peptides are induced when an immune response is triggered in a Tot-negative mutant. While the detrimental effects of the antimicrobial peptides are relatively weak, the Tot-dependent rescue is consistent and convincing. The authors have gone to great lengths to test their conclusions in several independent ways. This may resolve the long-standing enigma about the role of the Tot peptides, which are produced in the fly under a range of stressing conditions.

Some mysteries remain. Antimicrobial peptides, similar or identical to those in D. melanogaster, are produced in most insects, but Tot genes have so far only been found in Drosophila species of the melanogaster and obscura groups (and they even seem to be lost in the ananassae subgroup). How do other species manage? And why are the Tot peptides so many and so extremely variable in sequence? They are more variable than most antimicrobial peptides. If the role of Tots is simply to block the antimicrobial attack by interacting with phosphatidylserine in the membrane, you might expect that a single conserved sequence could do the job. These are questions for the future and I don't expect the authors to present a solution here, but I'm curious about their ideas. Their data are convincing.

We thank the reviewer for their positive comments. We agree that Turandot proteins are fascinating and we are still far to have the whole picture. We still believe that PS-binding proteins could evolved quickly, masking protein conservation despite similar function. An exciting possibility is that microbes have hijacked the Turandot protective mechanism to shield themselves from AMPs. In this scenario, Turandot diversification could represent an evolutionary countermeasure, favoring specific recognition of host lipids while avoiding bacterial membranes and thereby preserving AMP-mediated bacterial killing. We have no data to support this idea and decided to not include it in the Discussion.

I have only minor points to raise:

1. Please guide the non-specialist reader better through the images of neuromuscular junction preparations. In Fig. 1A, what are round structures with Dpt-staining peripheral dots? (boutons?) In Fig. 1B, what are the thin Dpt-HA staining "ribs"? And, in Fig 2 and 3, how can you count the number of active zones per bouton? I find it difficult to se the margins of individual boutons.

As mentioned above, we added a NEW Figure 1B representing a schematic of a NMJ, its different compartments and the markers used to define them. In figure 1A, the round structures that are not HRP-positive have not been characterized yet. They look like hemocytes that could be recruited during infection, or pruned boutons that have lost the HRP reactivity. More work is needed to define these structures unambiguously. The ‘ribs’ likely show the pattern of muscle fibers. The staining seems specific but we have not investigated this thoroughly. We have expanded the Methods section to better explain the strategy used for quantification. The pictures shown here are maximum-intensity projections and the margins of the boutons may appear slightly blurrier than they are on single stacks.

Reference 63 is not complete.

We thank the reviewer for their careful reading. The reference is now completed in the revised manuscript.

Reviewer #3 (Significance (Required)):

This manuscript represents a major step forward regarding what may seem like a relatively small question: how a limited number of fly species have found a way to tamper toxic effects of their own immune defence, using an odd family of small proteins. The findings will be of great interest to workers in the field of Drosophila immunity, but it may also have much wider implications, as it may tell us something about the control of detrimental stress responses in general.

My own expertise is mainly in the field of insect immune responses and their evolution and molecular mechanisms. I lack expertise on neuromuscular junctions and on the techniques used here to study their function.

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

In this excellent paper, the authors follow up on their previous finding (Rommelaere et al. 2024, ref. 48)that the Turandot (Tot) peptides can protect stressed cells, which expose phosphatidylserine on the surface, from attack by antibacterial peptides. This becomes particularly evident at the neuromuscular junction, which becomes damaged when antibacterial peptides are induced when an immune response is triggered in a Tot-negative mutant. While the detrimental effects of the antimicrobial peptides are relatively weak, the Tot-dependent rescue is consistent and convincing. The authors have gone to great lengths to test their conclusions in several independent ways. This may resolve the long-standing enigma about the role of the Tot peptides, which are produced in the fly under a range of stressing conditions.

Some mysteries remain. Antimicrobial peptides, similar or identical to those in D. melanogaster, are produced in most insects, but Tot genes have so far only been found in Drosophila species of the melanogaster and obscura groups (and they even seem to be lost in the ananassae subgroup). How do other species manage? And why are the Tot peptides so many and so extremely variable in sequence? They are more variable than most antimicrobial peptides. If the role of Tots is simply to block the antimicrobial attack by interacting with phosphatidylserine in the membrane, you might expect that a single conserved sequence could do the job. These are questions for the future and I don't expect the authors to present a solution here, but I'm curious about their ideas. Their data are convincing.

I have only minor points to raise:

1. Please guide the non-specialist reader better through the images of neuromuscular junction preparations. In Fig. 1A, what are round structures with Dpt-staining peripheral dots? (boutons?) In Fig. 1B, what are the thin Dpt-HA staining "ribs"? And, in Fig 2 and 3, how can you count the number of active zones per bouton? I find it difficult to se the margins of individual boutons.
2. Reference 63 is not complete.

Significance

This manuscript represents a major step forward regarding what may seem like a relatively small question: how a limited number of fly species have found a way to tamper toxic effects of their own immune defence, using an odd family of small proteins. The findings will be of great interest to workers in the field of Drosophila immunity, but it may also have much wider implications, as it may tell us something about the control of detrimental stress responses in general.

My own expertise is mainly in the field of insect immune responses and their evolution and molecular mechanisms. I lack expertise on neuromuscular junctions and on the techniques used here to study their function.

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

In this manuscript, Lemaitre and coll extend a previous report from their group (PMID : 38484734) on the critical role played by proteins of the Turandot family in the protection of host tissues against the toxic, membrane targeted effects of antimicrobial peptides. Whereas the prior study published in 2024 largely focused on protection of the respiratory tract, here the authors investigate the protective effect of Turandot proteins on the peripheral nervous system and establish a connection with protection against neurodegeneration during aging. The study fully exploits the assets of the drosophila model for studies in integrative biology, combining elegant genetics and imaging to obtain experimental data that support the claims of the authors. The manuscript reads well, appropriate controls are present in all experiments and I did not detect any flaw in the logic.

Minor comments:

1. It is not clear why two different scramblases are used, Xkr8 and scramb1 (e.g., Fig1G-H or Fig4D vs 4G-H).
2. The authors may want to provide some explanation for the choice of conditions for the challenges with bacteria (e.g., 16h or 40h post infection in Fig1; 36h post infection in Fig2, or 96h after injection of heat killed bacteria).
3. Line 156: a reference for Brp is missing
4. Fig2C: the colocalization is hard to see, I see mainly purple, reflecting induction of TotA. Please point to the areas showing TotA enrichment at the NMJ following infection.
5. Fig3A: background for the use of Vglut should be provided.
6. Fig3D: why is a ts driver used to control Trio expression? When is expression turned on? Information regarding the ts-dependent expression of AMPs in Fig3N-O is also lacking.
7. Line 248: the effect of DptA does not reach statistical significance, please correct the statement.
8. Fig4F,G: according to the text (line 273) the panel for motoneurons should be F and muscles should be G
9. It would be interesting to include some speculations/hypothesis in the discussion on (i) the primary contribution of cecropin peptides (Fig4H) and (ii) the mechanism mediating exposure on PS on the surface upon infection.

Significance

This manuscript extends a previous study describing the protective role of Turandot proteins on host tissues. Its strength is the exploitation of the model of drosophila fruit flies to provide solid in vivo evidence on the toxic effects of antimicrobial peptides and on the important contribution of Turandot proteins to limit damage. By convincingly demonstrating a key function of Turandot in the protection of the peripheral nervous system and establishing a connection between aging, dysbiosis, induction of antimicrobial peptides and promotion of neurodegeneration, the manuscript fills an important fundamental gap and should have a broad impact. The results presented imply that factors functionally similar to Turandot proteins are likely to exist in other animals, including humans: their discovery and characterization would have a major influence in the field of aging and neurodegeneration.

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

This study addresses an important question at the intersection of inflammation, aging, and neurodegeneration by investigating how antimicrobial peptides (AMPs) affect neuronal integrity. Using a combination of Drosophila genetics, imaging, behavioral assays, electrophysiology, and microbiota manipulations, the authors provide evidence that infection and aging increase phosphatidylserine (PS) exposure at the neuromuscular junction (NMJ), thereby promoting AMP binding and neuronal damage. This study further shows that stress-induced Turandot proteins (Tots) antagonize AMP-PS interactions and protect motoneurons from degeneration. The findings are interesting, mechanistically relevant, and build on the authors' previous work demonstrating a protective role of Turandots in the tracheal system.

Overall, I find the study potentially suitable for publication. However, several aspects of the experimental design, data interpretation, and presentation require clarification before publication.

Major comments

1. Relationship to the authors' previous study and tissue specificity of the Turandot-AMP-PS pathway The current study can be viewed as a direct extension of the authors' previous work demonstrating that Turandot proteins protect tracheal tissues from AMP-induced cytotoxicity through masking of negatively charged phospholipids. The present manuscript extends this model to the peripheral nervous system and links it to neurodegeneration. While this extension is interesting, the manuscript does not sufficiently discuss what new conceptual insight is gained beyond demonstrating a similar mechanism in a different tissue. More specifically, it remains unclear whether the Turandot-mediated protection against AMP toxicity is a neuron-specific phenomenon or represents a general tissue-protective mechanism operating throughout the organism. This issue becomes particularly relevant because Figure 1E shows PS exposure not only in neurons but also in muscle cells. Likewise, the authors' previous study demonstrated PS-dependent AMP toxicity in tracheal tissues. Therefore, the manuscript would benefit from a more explicit discussion of tissue specificity versus generality of the AMP-PS-Turandot axis and a clearer explanation of how the current findings advance the conclusions of the previous study.
2. Temporal relationship between AMP induction and Turandot-mediated protection The proposed model assumes that Turandot proteins protect neurons by competing with AMPs for binding to PS-exposed membranes. However, the kinetics of this interaction remain unclear. AMP expression is typically induced rapidly following infection, whereas most experiments in the manuscript examine relatively late time points (16-40 hours post-infection). It is therefore difficult to understand when and how Turandots exert their protective effect. If the function of Turandots is to prevent AMP-PS interactions, one might expect Turandot accumulation to occur before or at least concomitantly with AMP recruitment. The manuscript would benefit from additional discussion of, or ideally, experimental data on the temporal dynamics of AMP induction, Turandot induction, and AMP recruitment to the NMJ.
3. Relationship between AMP binding, PS exposure, and neuronal damage One aspect of the proposed model that I found difficult to fully understand concerns the relationship between AMP binding, PS exposure, and neuronal damage. The authors propose that AMPs are recruited to PS-exposing neurons and that Turandot proteins limit this interaction. However, Figure 1B and Figure 1D show detectable DptA-HA localization at NMJs even under unchallenged conditions, where obvious neuronal damage is not apparent. In addition, Figures 2A and 2B indicate that infection alone does not induce overt bouton fragmentation in wild-type flies despite detectable AMP recruitment. These observations raise a question regarding the sequence of events. Is PS exposure the primary event that attracts AMPs to neuronal membranes, or could AMP accumulation itself contribute to membrane stress and subsequent PS externalization? The manuscript does not necessarily need to resolve this question experimentally, but a more detailed discussion of these possibilities would help readers better understand the proposed mechanism and reconcile the observations made under basal and infection conditions.
4. Interpretation of the Relish knockdown experiment (Figure 1C) The interpretation of Figure 1C is somewhat confusing. The authors conclude that fat body-derived AMPs bind neurons because Relish knockdown in the fat body abolishes DptA-HA recruitment to NMJs following infection. However, Relish is required for DptA expression itself. Therefore, loss of neuronal staining in this experiment is expected simply because DptA is no longer produced. While the experiment supports the conclusion that infection-induced DptA originates from the fat body, it does not directly address the mechanism of neuronal recruitment. The authors should revise the interpretation accordingly.
5. Systemic versus local accumulation of Turandot proteins In Figure 2C, TotA accumulation is observed at the NMJ after infection. However, the staining pattern appears broadly distributed rather than restricted to the NMJ. Given that Turandots are known circulating humoral factors, the data seem more consistent with systemic accumulation following infection than with specific targeting of NMJs. The authors should discuss this point and clarify whether they propose any tissue-specific recruitment mechanism.
6. AMP specificity Figure 2F demonstrates that deletion of the four Cecropin genes partially rescues the phenotype, whereas deletion of twelve AMP genes produces a stronger rescue. This suggests that some AMP classes contribute more strongly than others to neuronal toxicity. It would be valuable to discuss whether AMP potency correlates with known biochemical properties such as net positive charge, membrane affinity, or phosphatidylserine-binding capacity. If relevant literature is available, discussing it would strengthen the mechanistic interpretation.
7. Interpretation of the Draper experiment (Figure 4E) I had difficulty following the logic underlying the Draper experiments. Exposed PS on neuronal cells is classically regarded as an "eat-me" signal that promotes clearance of PS-exposed neuronal cells through the PS receptor Draper. Under this framework, one would expect that impaired glial engulfment would reduce the clearance of damaged neuronal material and potentially exacerbate degeneration. Instead, the authors appear to test whether Draper-dependent glial activity actively contributes to bouton fragmentation. While the negative result is used to conclude that glial phagocytosis is not responsible for the phenotype, the rationale behind this prediction is not sufficiently explained. A clearer discussion of the expected outcomes and their interpretation would greatly improve the accessibility of this section, particularly since similar arguments are presented in the Discussion (lines 298-302).
8. Interpretation of muscle-specific phosphatidylserine manipulation experiments (Figure 4D and 4F) I found the muscle-specific PS manipulation experiments interesting, but I was not entirely sure how they support the conclusion presented in the text. The authors conclude that these data "highlight the specific contribution of neuronal PS exposure" (lines 264-265). My understanding is that reducing PS exposure specifically in muscles does not affect motoneuron fragmentation in Tot-deficient animals (Figure 4D), and that increasing PS exposure in muscles is also insufficient to induce the phenotype (Figure 4F). These results clearly argue that muscle PS exposure alone is not sufficient to drive degeneration. However, it is less clear whether these experiments, by themselves, establish a specific requirement for neuronal PS exposure. Rather, this conclusion appears to rely on combining these muscle-specific manipulations with neuron-targeted perturbations presented elsewhere in the manuscript. More generally, because PS exposure is observed in both neuronal and muscle compartments following infection (Figure 1E), and given previous evidence for AMP-PS interactions in other tissues, it remains possible that PS exposure represents a more general stress response. In this context, additional clarification of how tissue specificity is inferred, and to what extent systemic versus local effects are excluded, would strengthen the mechanistic interpretation.

Minor comments

1. Several markers and assays are introduced without sufficient explanation for non-specialist readers. For example, the rationale for using anti-HRP as a neuronal marker is not explained. Likewise, additional background on how bouton fragmentation is inferred from Brp and Vglut staining would improve accessibility.
2. The organization of the Results section could be improved. In several cases, transitions between figures are difficult to follow (e.g., Figure 1C-D and Figure 3K-L). Reorganizing sections to better align with the experimental narrative would improve readability. In addition, some negative results (e.g., Figure 3G-K) might be more appropriate for the supplementary material, particularly because the manuscript subsequently returns to bouton fragmentation analyses in Figure 3L-O.
3. In lines 216-217, the authors state that they observed a decline in both forms of neurotransmission. If so, statistical comparisons between day 5 and day 20 samples should also be provided.
4. In Figure 4A, the description of a "slight increase" (line 256) is vague. Please clarify which age groups differ significantly and which comparison this statement refers to.

Significance

Field of expertise

Drosophila neurobiology, neuroimmune interactions, synaptic physiology, glial biology, antimicrobial peptide biology.

I am not an expert in the biochemical properties of Turandot proteins or AMP-lipid binding at the structural level, and my evaluation is based primarily on genetic and functional interpretation.

General assessment

This study investigates how antimicrobial peptides (AMPs) contribute to neuronal degeneration and proposes that phosphatidylserine (PS) exposure at the neuromuscular junction promotes AMP binding, while Turandot proteins provide protection by interfering with this interaction. The authors combine Drosophila genetics, imaging, and functional assays to support this model. The work is technically solid and uses a broad experimental toolkit. Its main strengths are the in vivo functional analysis of AMP-induced synaptic defects and the extension of previously described Turandot functions to the nervous system. However, the mechanistic interpretation is limited by incomplete clarification of causal relationships between PS exposure, AMP binding, and neuronal damage, as well as uncertainty regarding tissue specificity versus systemic effects.

Advance

The study extends prior work on Turandot-mediated protection from AMP toxicity by proposing a lipid-based mechanism operating at synaptic membranes in the peripheral nervous system. If fully supported, this would provide a conceptually interesting link between innate immune effectors and phospholipid exposure in neuronal degeneration. However, the extent to which this represents a neuron-specific mechanism, rather than a broader systemic stress response affecting multiple tissues, remains unclear. As a result, the main advance is best viewed as a proposed extension of an existing AMP-lipid interaction framework into neuronal tissue, rather than a fully established tissue-specific mechanism.

Audience

The study will be of interest to researchers in neurobiology, neuroimmunology, and Drosophila-based systems neuroscience, particularly those studying synaptic maintenance, glial function, and innate immune signaling. It may also be relevant to broader audiences interested in infection- or inflammation-induced neurodegeneration.

Overall significance

Overall, the study proposes a potentially interesting mechanism linking antimicrobial peptides to synaptic degeneration via PS exposure. Its main limitation lies in the incomplete resolution of whether this mechanism is neuron-specific or reflects a more general systemic response to stress.

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

Our central claim is that loss of Uts2r3 creates an abnormal mechanical state in the developing axis before overt spinal curvature, characterized by reduced active force measured from the axial preparation and increased passive resistance to stretch. These findings identify Urotensin signaling as a regulator of axial tissue mechanics during growth, and suggest that a breakdown of axial mechanics underlies spinal curvature phenotypes that are similar to idiopathic scoliosis. The cellular origin of this body-scale mechanical phenotype remain to be resolved and will be the subject of future work.

Summary of the reviews and revision strategy

__Overall assessment: __The reviews are highly positive about the importance of the question our manuscript addresses, the quality of the work, and our central observation that altered axial mechanicals precede spinal curvature. Reviewer 1 states that "The paper is well written and easy to follow" and, importantly, that "The conclusions are supported by the presented data." The same reviewer describes this as the first study showing that changes in muscle biomechanical function precede curvature in a model of idiopathic scoliosis. Reviewer 3 likewise states that "The data presented generally support the conclusions" and that the study "has the potential to advance the field". Reviewer 2 is more cautious, but also recognizes that the study addresses an interesting biological question and provides evidence that altered muscle function contributes to the spinal phenotype.

Main issues raised: The reviews converge on a small number of issues: (1) the incomplete characterization of uts2r3 expression; (2) insufficient context and reporting of the RNA-seq dataset; (3) interpretation of the mechanical phenotype, especially whether reduced force reflects intrinsic contractile dysfunction, reduced contractile cross-sectional area, altered tissue composition, or altered force transmission; (4) the relationship between active and passive mechanical measurements in the intact tail preparation; and (5) methodological details, including the force-velocity analysis, sample numbers, statistical values, and RNA-seq deposition.

Summary of our revision plan:

1. uts2r3 expression and fiber type: We will revisit direct expression experiments across relevant stages and analyze existing public single-cell datasets. We will revise the manuscript so that prior evidence is described accurately as strongest for dorsal slow muscle rather than generalized pan-muscle expression. If direct localization remains inconclusive, we will state that limitation explicitly and be sure not to over-interpret negative data. These experiments are underway.
2. RNA-seq context: We will add library, sequencing and quality control details, numbers of significantly upregulated and downregulated genes, fold changes for highlighted genes, a complete differential expression table, and a less redundant enrichment analysis. Our dataset has now been deposited public database.
3. Contractile CSA and tissue composition: We will use transverse sections to quantify muscle area and connective tissue composition. We will incorporate MyHC/protein data if interpretable. Regardless of the experimental outcome, we will revise the manuscript to acknowledge the possibility of a 'less contractile tissue' explanation for the physiological phenotypes we observe. These histology and protein experiments are underway.
4. Interpretation of active mechanics: We will soften the claims that the assay isolates intrinsic sarcomeric force generation, and reframe the measurements as integrated axial mechanics to distinguish force generation from force transmission. Additionally, we will remove the claim that active and passive abnormalities are necessarily independent (we did not mean to imply that). In our discussion, we will add molecular mechanisms through which these mechanical changes may manifest, including myotome shortening, notochord/myoseptal mechanics, and attachment site compliance. These changes to the writing of our manuscript will be performed prior to re-submission.
5. Methods, statistics and figure reporting: We will expand the mechanics methods, clarify CSA measurements and mutant genotype, reconcile all n and p values, and add the requested kinetic data. The revision will make a clear and deliberate distinction between what the current experiments establish and what remains unresolved. The central supported conclusion is that loss of Uts2r3 produces a pre-curvature biomechanical state characterized by reduced active force measured from the axial preparation and increased passive resistance, accompanied by muscle-associated transcriptional changes and subtle changes in birefringence. The revised manuscript will not claim that these effects are proven to be muscle cell-autonomous.

Detailed response to reviewer comments

Reviewer #1

Evidence, reproducibility and clarity

The work by O'Hara-Smith et al. explores if alterations in muscle development and function underly the formation of spinal curvature in zebrafish uts2r3 mutants. Using transcriptomic analyses, immunofluorescence and birefringence, the authors reveal a reduction in the expression of muscle-associated genes as early as 28hpf with only mild reduction in birefringence and otherwise no overt changes in muscle morphology or symmetry, even at stages where spinal curvature becomes apparent (14dpf). Biomechanical analyses further show that loss of uts2r3 leads to a reduction in active force and an increased passive resistance to stretch, indicating that urotensin signaling plays a role in the regulation of muscle function.

Response: We thank the reviewer for this clear summary of the study and for recognizing the combination of transcriptional, structural, and biomechanical evidence. We will preserve this central framing in the revision, while sharpening the distinction between the directly measured phenotype and the unresolved cellular mechanism.

Major comment 1: The paper is well written and easy to follow. The majority of experiments are described in sufficient detail, and all of the used reagents are listed. The conclusions are supported by the presented data.

Response: We appreciate this positive assessment.

Major comment 2: Optional additional experiments that could significantly improve the paper would be a detailed characterization of the expression of uts2r3 as previous expression analyses were limited to one early time point and mostly used analyses of mosaic transgene expression. However, performing detailed expression analyses would be both costly and time consuming.

Response: We agree that a clearer account of uts2r3 expression would improve interpretation of the mechanical phenotype. We are therefore revisiting expression using complementary approaches: in situ hybridizations, immunofluorescence using custom-made antibodies, and analysis of single-cell transcriptomic datasets from a range of pre-curvature stages. We will also revise the Introduction and Discussion so that prior expression evidence is described more precisely, including evidence for dorsal slow muscle expression and the current uncertainty about the expression in other muscle subtypes. If direct localization remains below reliable detection, we will minimally report single cell transcriptomic data and note the limitation explicitly in the manuscript.

Minor comment 1: Additional details on the RNA-seq experiment should be added to the methods section to allow interpretation of the results. Was mRNA selection or ribosome depletion used? What was the sequencing mode (paired or single-end)? What read length was used? How many reads were obtained per sample and how many filtered reads could be aligned to the reference transcriptome?

Response: We agree, and apologize for missing these details in our initial submission. We will be sure to include these details in our expanded Methods section.

Minor comment 2: To understand the extend of the changes detected by the transcriptomic analyses it would be helpful to include the total number of significantly up- and down-regulated genes as well as the magnitude of change (fold-change) for the highlighted muscle related genes.

Response: We will report the total numbers of significantly up- and down-regulated genes at the stated adjusted P value threshold and provide the fold changes of all genes available as a supplementary table. Additionally, our data has already been made available on a public repository, and we will provide the accession number in the revised manuscript.

Minor comment 3: Similarly, for the GO terms a list of differentially expressed genes for each term should be provided and largely overlapping GO terms should be removed. The fact that all terms show almost the exact same fold enrichment could point to a large overlap between the differentially expressed genes detected for each term.

Response: We appreciate this comment. We will re-analyze the enrichment, collapse highly redundant terms, and provide the gene membership underlying each term.

Minor comment 4: As the ratio of twitch and tetanic force was quantified and used as a measure for myosin dynamics and force transmission, it would be helpful to show that data in fig. 3 in addition or instead of panel D. Similarly, the half-relaxation time data should be added.

Response: We will add the twitch-to-tetanus ratio and half-relaxation time measurements to the revised figures. We will also revise the text to allow for more nuanced interpretation that includes other potential explanations for our results in light of Reviewer 3's comments about altered tissue composition in the tail cross section.

Minor comment 5: In the methods section, it would be helpful for non-experts to indicate that the MANDRA-1 antibody detects dystrophin.

Response: We agree, and will be more explicit about this in the Methods.

Minor comment 6: Additional details on how the cross-sectional area was determined should be added to the methods section.

Response: We will add: "Because zebrafish larvae are semi-translucent at this stage, sarcomere length was measured using an inverted microscope positioned beneath the force-length apparatus. Once secured, specimens were adjusted to a sarcomere length of 1.9 µm, confirmed by visualization of the thick and thin filament striations. Total specimen length was then measured at low magnification (4x), allowing the entire specimen to be viewed within a single field of view. Next, three transverse dimensions were measured at higher magnification (40x) at equally spaced positions along the specimen, centered on the anal vent (Fig. 3A′). Using a pair of prisms integrated into the mounting chamber, the orthogonal transverse dimension was measured at the same three positions from the dorsoventral perspective. Assuming an elliptical cross-section, the paired orthogonal measurements at each position were used to calculate cross-sectional area. The mean of the three cross-sectional area measurements was used as the specimen CSA."

Minor comment 7: While this is the first report linking urotensin signaling to muscle function in idiopathic scoliosis, previous research has shown a role for urotensin signaling in skeletal muscle metabolism (PMID: 35605093, PMID: 24116164, PMID: 36167277). The findings presented in these studies and how they relate or could help interpret the findings of this study should be discussed.

Response: We thank the reviewer for pointing out these studies. In the revised Discussion, we will mention these studies with the broader point that Urotensin signaling can influence skeletal muscle metabolism.

__Minor comment 8: __Previous studies imply that uts2r3 is expressed in dorsal skeletal muscle, which would imply that dorsal and ventral muscles are differently affected in uts2r3 mutants. The authors should discuss this asymmetric expression of uts2r3 in skeletal muscle and its relevance for the observed phenotype. Furthermore, it would be helpful to include future directions on how to dissect differences between dorsal and ventral muscle activity.

Response: In our revised Discussion, we will bring up the dorsal-enrichment of uts2r3 and its possible relevance to the curvature in uts2r3 mutants. We will also mention the caveats associated with that expression result, namely, it was seen only in a small number of transient transgenic zebrafish. We will note that our intact tail mechanical measurements integrate dorsal and ventral, superficial and deep, and can be influenced by non-contractile tissues. This is advantageous as it provides a tissue-level view of mechanical properties. We will emphasize that future work could involve region- and fiber type-specific mechanical measurements and tissue-specific perturbations, experiments which are currently beyond our scope.

Significance: Despite the relatively high prevalence of scoliosis in the human population (2-3%) our understanding of the underlying pathomechanisms are limited. To my knowledge this is the first study that shows that changes in muscle biomechanical function proceed the formation of spinal curvature in a model of idiopathic scoliosis. The study advances our understanding of the mechanisms underlying the formation of spinal curvature. If early changes in biomechanical properties of skeletal muscles are found to be a general feature of idiopathic scoliosis, this study could be impactful for the early detection and potentially treatment of idiopathic scoliosis.

Therefore, these findings will be of interest to researchers focused on basic science but also for translational and clinical research.

A major strength of the study is that the observed transcriptional changes could be linked to functional consequences through biomechanical testing of muscle function. However, the pathways that link urotensin signaling to the observed alterations in gene expression and muscle mechanical properties were not explored. Previous reports show uts2r3 expression in dorsal skeletal muscle but are limited to one early time point and analyses of mosaic transgene expression. As the presented study explores uts2r3 function in skeletal muscle, detailed analyses of uts2r3 expression at different stages and in different muscle subpopulations would help interpret the results and significantly improve the study.

Response: We appreciate the reviewer's assessment of the novelty and potential significance of the pre-curvature biomehanical phenotype.

Expertise: zebrafish genetics, skeletal development, scoliosis, CRISPR/Cas9, transcriptomics.

Reviewer #2

Evidence, reproducibility and clarity

In this manuscript, the authors build upon previous findings showing that disruption of Urp1/Urp2 signaling, or loss of their receptor Uts2r3, results in abnormalities in spine morphology. The authors note that Urp1 and Urp2 are expressed by cerebrospinal fluid-contacting neurons surrounding the central canal, whereas Uts2r3 is expressed in skeletal muscle. To gain mechanistic insight into how this pathway regulates spine development, they performed bulk RNA-sequencing of 28 hpf Uts2r3 mutant embryos, prior to the onset of spinal deformities. Their analysis identified changes in the expression of several muscle-related genes. Although they did not detect major structural abnormalities in skeletal muscle, they found altered muscle force production, suggesting that impaired muscle function may contribute to the spinal phenotype. While the study addresses an interesting biological question, I have several concerns regarding the strength of the mechanistic conclusions.

Response: We thank the reviewer for identifying the central mechanistic issue. We agree that some statements in the manuscript should be modified to distinguish the observed pre-curvature biomechanical phenotype from stronger claims of tissue autonomy or a particular molecular mechanism. This distinction will be made explicit in our revision.

Major comment 1: Expression pattern of Uts2r3. It remains unclear where Uts2r3 is expressed. Apart from the statement that it is present in skeletal muscle, I could not find a detailed characterization of its expression pattern. This information is essential for interpreting the specificity of the phenotype and for understanding whether the observed defects arise directly from muscle or from additional tissues expressing the receptor.

Response: We agree that the current wording is too broad. We will expand the expression analysis as described in our response to Reviewer 1, including in situ hybridization, immunofluorescence, and single cell transcriptomic data. We will modify statements that currently describe Uts2r3 as 'muscle-expressed' to distinguish supported dorsal slow muscle expression from other tissues, where expression is less certain. We will also make it clear that the current experiments do not establish that our measured biomechanical phenotypes are direct muscle cell-autonomous consequences.

Major comment 2: Transcriptomic analysis. The RNA-seq analysis lacks important context. I could not determine how many genes were significantly differentially expressed in the mutant embryos or what the overall transcriptional changes were. The manuscript focuses primarily on muscle-related genes, but it would be important to know whether these represent a small subset of widespread transcriptional changes or whether the effects are relatively specific to muscle. Presenting the complete dataset, together with pathway enrichment analyses, would help place the findings into a broader biological context.

Response: We apologize for the lack of context we provided. In our revised manuscript, we will provide the numbers of differentially expressed genes (downregulated and upregulated), a more broad enrichment analysis with less redundancy between categories, and a complete supplementary table of all gene expression changes with fold changes.

Major comment 3: Mechanism of Urp1/Urp2 signaling. The manuscript does not sufficiently explain how Urp1/Urp2, which are produced by CSF-contacting neurons around the central canal, signal to receptors expressed in skeletal muscle. Is there evidence that these peptides are secreted into the cerebrospinal fluid and reach the musculature? Alternatively, are there intermediate signaling mechanisms? This represents an important mechanistic gap in the proposed model.

Response: We agree that the physical route by which Urp1/Urp2 peptides reach Uts2r3-positive target cells remain unresolved. In our revised manuscript, we will discuss this issue, and note plausible routes. We will remove any language which implies this route is already known. However, experimentally discovering how Urp1/Urp2 peptides travel to Uts2r3 receptors is far beyond the scope of our study.

Major comment 4: Relationship between muscle defects and spinal deformity. Although the authors report altered muscle force production, they do not detect obvious structural defects in the muscle. It therefore remains unclear whether the altered muscle function is the primary cause of the spinal phenotype or simply a secondary consequence of broader developmental abnormalities. Response: We agree that we have not established muscle as the cell autonomous cause of this phenomenon. Indeed, tissue-scale biomechanical changes may and often do, derive from multiple factors within composite tissue such as skeletal muscle. In our revised manuscript, we will be clear that we have discovered a pre-curvature axial mechanical state, some aspects of which strongly suggest myofilament antecedents, rather than implying that muscle dysfunction is necessarily a primary cause.O

Major comment 5: Tissue specificity. A major limitation of the study is that neither the genetic model nor the transcriptomic analysis is tissue-specific. The Uts2r3 mutation affects the whole embryo, and the RNA-seq was performed on whole embryos rather than isolated muscle. Consequently, it is difficult to determine whether the observed transcriptional changes reflect direct effects within skeletal muscle or indirect systemic effects of the mutation. Tissue-specific genetic manipulation and muscle-specific transcriptomic analyses would considerably strengthen the mechanistic conclusions.

Response: We agree with the reviewer and we have attempted tissue-specific experiments including muscle-cell specific Cas9 expression. However, this has failed for technical reasons, which we have learned is not uncommon. We agree that the present data do not establish muscle cell autonomy and we will state this explicitly throughout the manuscript. Nevertheless, we consider tissue-specific experiments to constitute a substantial new mechanistic study rather than a necessary control for our existing biomechanical phenotype. In our revised version, we will be clear to note the supported conclusion that whole animal loss of Uts2r3 produces pre-curvature axial mechanical defects.

Overall assessment: The study extends previous work implicating the Urp1/Urp2-Uts2r3 pathway in regulating spine morphology and provides evidence that altered muscle function may contribute to this phenotype. However, the current data provide only limited mechanistic insight into how this signaling pathway regulates muscle physiology or spine development. In particular, the lack of tissue-specific genetic and transcriptomic analyses makes it difficult to distinguish direct muscle-specific effects from broader developmental consequences of Uts2r3 deficiency. Additional experiments addressing these issues would substantially strengthen the manuscript.

Response: We appreciate these comments and will revise the manuscript accordingly. Our goal in the revision will be to make the mechanistic level of the study precise: this paper identifies and quantitatively defines a pre-curvature biomechanical state downstream of Uts2r3 loss. It does leave the precise route of Urp1/Urp2 signaling and the cell autonomous response as open molecular questions, which are beyond the scope of our current work, and which future work will aim to address.

Reviewer #3

Evidence, reproducibility and clarity

This manuscript uses the zebrafish model system, integrating genetic, histological, transcriptomic, and functional approaches to address a challenging and relevant biological question. The authors conclude from their data that urotensin signaling defects affect both passive and active mechanical properties of the larval zebrafish's muscular tail independently, creating an imbalance of forces during development that ultimately leads to a scoliosis-like phenotype. Previous studies in zebrafish had linked urotensin signaling to the developing trunk muscles through the receptor Uts2r3. The present study shows that loss of Uts2r3 leads to changes in muscle specific gene expression, loss of active myotomal muscle force, and increase in passive viscoelastic forces, without overt morphological or dystrophic changes to in the muscle. Importantly, these changes are seen prior to the development of the tail-curvature phenotype.

Response: We thank the reviewer for highlighting the integrated strength of our study and the importance of measuring active and passive responses prior to curvature.

Major comment 1: The authors predict involvement of myotomal muscles in the progression of the curvature phenotype based on the reported expression of the Uts2r3 receptor in myotomal muscles during development. According to the cited studies, the receptor is expressed specifically in dorsal slow-twitch muscle fibers (Zhang 2018). Supporting this, the upward tail bending effect of urotensin overexpression is abolished in mutant larvae lacking slow twitch fibers (lu 2020, Gillard 2023). The assertion from these studies being that urotensin regulates tail curvature via regulating dorsal slow muscle tone. Too much signaling increases force and bends the tail upwards; two little has the opposite effect. This interpretation is relevant because slow twitch fibers make up only ~7% of the total myotomal muscle CSA in 5dpf larvae and are not thought to contribute meaningfully to the high speed forces measured using the intact tail mechanics approach. The remaining >90% of CSA consists of fast twitch muscle active only during brief escape maneuvers. According to the same studies, fast fibers do not appear to express Uts2r3. If this is the case, the reported loss of force is more challenging to interpret. As written, fiber type is not mentioned. This is an issue that should be discussed and considered when interpreting the data.

Response: We agree and consider this an important point. The revised manuscript will explicitly address the potential slow-twitch exclusive expression of the Uts2r3 receptor and how such selective, fiber-type specific targeting in this study may alter interpretation of our findings. We do note, that the previous findings showing dorsal slow-twitch enrichment were based on a small number of transient transgenic zebrafish, meaning expression in other locations was likely missed. We are performing a broader expression analysis using stains as well as single cell transcriptomics. We will therefore test whether there is support for additional expression in presomitic mesoderm or fast muscle populations, and interpret our findings accordingly, in line with the reviewer's suggestions. In any case, a defect present in ~10% of the transactional cross section may still have significant impacts on chronic stress applied to the developing spinal column, especially if that expression is limited to more chronically active, slow-twitch fibers. These important caveats to our initial interpretation will be included in the revised manuscript.

__Major comment 2: __The authors conclude that twitch and tetanus force deficits in Uts2r3 mutant larvae result from changes in contractility at the sarcomere level. Mis regulation of muscle gene expression and mild loss of structural organization are cited as causes. An alternative explanation, overall reduction in contractile CSA, is ruled out based on estimates from whole animal dimensions (see specific comments below). There are a couple of reasons why this may still be the simplest explanation. First, myotomal muscle accounts for ~70% of the total CSA of the tail, with myofibril CSA a large sub-fraction of that. Therefore, significant changes in the CSA relevant to contractile force may be difficult to resolve from whole-body estimates. This is especially true if increases in passive stiffness result from increased CSA of connective tissue, etc. Second, birefringence is a good measure of damage or structural disruptions to myotomal muscles that are heterogeneous within a sample, as in models of DMD. Uniform reduction in intensity (Fig S2) may result from disruption of the regular order of myosin heads within the sarcomere but could also reflect a reduction in myofibrillar volume. Third, dynamic measurements of contractile function (twitch kinetics, F/V) appear to be unchanged. Disruption of sarcomere organization, a shift in contractile protein isoforms (such as myosin heavy chain), or other changes affecting actomyosin function would be more likely to show up in the kinetics, whereas changes in myofibril CSA would not. Finally, to the extent mRNA levels represent protein abundance, the data presented also support a 'less muscle' explanation. There are experiments that could get at these questions directly, such as a histological examination of tail cross sections. But for the purposes of this study, a more thorough discussion of these possibilities would be sufficient.

Response: We agree that the submitted manuscript likely overinterprets myotome morphology and whole body dimensions to assume similar muscle transverse cross sectional area. A whole preparation CSA estimate cannot distinguish myofibrillar tissue from other axial tissues, and the uniform reduction in birefringence is indeed compatible with more than one structural interpretation. We are therefore examining matched transverse sections to quantify myotomal area and connective tissue composition via histology. We are also evaluating protein/MyHC measurements via electrophoretic separation as an independent readout of muscle composition, normalized to the measured specimen volume. These data will be included if they are sufficiently quantitative and reproducible and our pilot experiments are promising. Irrespective of the outcome of these additional experiments, we will remove the claim that the force deficit necessarily reflects a sarcomere-level contractile defect, and the revised discussion will explicitly consider the other explanations the reviewer suggests — for which we are grateful.

Major comment 3: The authors conclude that 'active and passive defects are unlikely to be simple consequences of one another', claiming 'increased passive stiffness does not readily explain the reduction in active force generation.' This may be true but the issue is complex and needs more discussion. The mechanical approach used (Mead 2020) is quite different from how the tail functions in vivo and comes with some caveats. One observation in that study is that 'isometric' contractions, in which the preparation is held at a fixed length, result in the shortening of contracting myotomes by about 10%, accompanied by the stretching of tissue near the tail attachment points. Because of this, there are a couple of ways in which changes in passive properties could impact measured forces in this assay. For example, the notochord is a structure that functions to resist tail compression during swimming in vivo. So, any stiffening of the notochord, or of connections between myotomal muscle and notochord could reduce muscle forces transmitted to the force transducer. Also, unless tails were pre-stretched by ~10% before activation, as in Mead 2020, forces reported here may have been generated at muscle lengths on the ascending limb of the length-tension curve. Therefore, changes in the passive mechanical properties of the tissue at the attachment points could have large effects on measured force by changing the SL at which force is measured. This could be checked if SL or myotome length was measured during contractions as was done in that study. The paper would be strengthened if the interdependence of active and passive mechanical changes were considered in this light.

Response: We thank the reviewer for these helpful comments. We will remove the statement that the active and passive abnormalities are unlikely to be consequences of one another and include the more complete and potential interrelated nature of these measures, considering notochord involvement as suggested by the reviewer. We will therefore treat the preparation as an integrated mechanical system in which force generation, shortening, myoseptal and notochord mechanics, tissue compliance, and force transmission all interact. We will point out that specimens were secured to the force/length apparatus in these experiments using an approach distinct from Mead et al 2020, and this may have reduced compliance to some degree, as we observed but sarcomere tracking at these speeds was not tenable in our hands. Further, during active measurements, specimens were initially adjusted to a sarcomere length of 1.9 µm before stimulation. This was accomplished by stretching the specimen to ~1.95 or 2.0 µm and then reducing the length slightly. Because the specimens resist further compression beyond 1.9 µm, this at least ensures specimens were as close as possible to optimal contractile length. Because the same specimens were stretched prior to activation during the kinetic experiments to measure force deficits at varying velocities, we will review these data to see if greater strain produced further differences in isometric tension prior to shortening. This will help guide interpretation as to whether resistance to notochord compression influenced active contractile deficits. e While we believe these additional considerations and measures may support the notion that muscle contractile function is altered in Uts2r3 mutants, we cannot exclude the possibility that passive properties alter effective muscle operating length or force transmission and will state this limitation directly in the revised manuscript. We will also discuss how it may change the interpretation of reduced measured force.

Minor comment 1: Are the Uts2r3 mutant fish used in the study heterozygotes or homozygous null? This line was previously described, but it would be helpful if the type of mutation as well as the when and how the phenotype develops are at least briefly described here as well.

Response: All mutants are homozygous mutants (b1436) which lack Uts2r3. In the results, when the mutant is first mentioned, we will describe the allele, rather than requiring readers to retrieve the previous publication.

Minor comment 2: Mechanical measurements are reported as being performed as described in Mead 2020. Deviations are mentioned in method of attachment, instrumentation, and SL measurement. However, it would be helpful to have a more thorough description of the approach. Specific parameters used should be included. For example: length of preparations, any anatomical landmarks for suture placement, range of muscle lengths used for isovelocity maneuvers, etc.

Response: We agree, and will enlarge our Methods descriptions including specimen preparation and length, suture landmarks, bath composition and temperature, starting sarcomere length, stimulation parameters, shortening velocities and imposed length changes, and the number of specimens contributing to each assay.

Minor comment 3: Force velocity data (Fig. 3E) shows a force depression at 28 l/sec of only ~30% at 18˚C. This result predicts a Vmax over 100 l/sec at 18C, and possibly twice that at physiologically relevant temperatures, assuming a q10 of 2. Mead et al (2020 and 2024) predicted a Vmax of 45 l/sec at 28˚C and reported ~80% drop in force at ~12 l/sec at 23˚C, stating that limitations inherent to the instrumentation and the tail preparation precluded accurate measurement at higher velocities. Can the authors comment on the discrepancy? Were any modifications made to the approach in order to access these higher velocities?

Response: We will address this discrepancy in our resubmission. We plan to double check the original code, including exact length changes, velocity normalization, and the isometric contractions used to normalize force. We will reanalyze force-velocity data and compare the resulting relationship directly with Mead et al. If the expected Vmax is not obtained, we will highlight this discrepancy with appropriate assumptions and limitations. In this case, we will revise any interpretations that implies physiologically accurate Vmax at the highest imposed velocities.

__Minor comment 4: __How were CSA measurements made? Methods states tails were measured in two dimensions at three points. Were anatomical landmarks used? These should be included.

Response: We agree, and as also noted in response to Reviewer 1, we will add the exact measurement procedure and anatomical reference points. Additionally, we are significantly expanding our histology and CSF analysis in our resubmission, and we will be sure to include detailed methods to address these points.

Minor comment 5: Stated sample numbers do not match the number of individual points in figures 3 B, C, D, E. P value for tetanus tension stated in text (0.008) does not match Fig 3 C (0.014). The next sentence appears redundant and states a third p value of Response: We apologize for these inconsistencies. Due to technical limitations at the time of data collection, tension data were not recorded in all of the same specimens at all velocities. Similarly, passive mechanics were collected in some specimens but not others. Last, CSA data were lost on one sample, contributing non-normalized data, but no CSA normalized data (tension). We will be more explicit about data inclusion/exclusion for these figures and tables in the revised text, and re-run statistical analysis, then correct inconsistent p values in figures and in the text.

Minor comment 6: Will RNA seq data be reported in a supplemental file or uploaded to a database? Both are standard practice.

Response: Yes, we plan to provide a table of all differentially expressed genes and their fold changes and adjusted p values.

Minor comment 7: The primary curvature defect in the Uts2r3 mutant seems to be dorsal-ventral in nature, though this is not explicitly described in the text. Can any insight into this or any other specific feature of the phenotype be gained from the data? Why down and not up or left vs right? The data presented shows no change in the relative 2D area of hemisomites resulting from this curvature. However, geometry would indicate some remodeling (different-modeling?) must take place in these mutant fish. Is possible to measure either muscle fiber length, sarcomere length, or sarcomere number from these images?

Response: We will describe the phenotype more explicitly, instead of relying on readers accessing the earlier publication. The current hemisomite data argue against a gross dorsoventral difference in 2D muscle area or myoseptal angle, but they do not explain why the curve is ventrally directed. We will state in our discussion that our present data do not resolve the directional basis of the curve phenotype. We agree with the reivewer that this is worth discussing as it is a particularly interesting aspect of the Urotensin-associated curve phentotype.

Minor comment 8: Fig S3B is very hard to see. Can 'hemisomite abstraction overlay' be defined in the figure caption?

Response: Apologies. We will improve the visibility of the figure and be explicit about definitions in the figure legend.

Significance: The main strength of this study is in exploiting the highly integrative nature of the zebrafish model to explore a challenging and relevant biological question. The methods used here, in particular the mechanical experiments, are extremely challenging to perform an interpret. The data presented generally support the conclusions, but important context is missing. A more nuanced discussion of potential mechanisms and experimental caveats will better inform subsequent experiments and improve the overall impact of the paper. This study has the potential to advance the field by incorporating direct mechanical measurements of active and passive muscle force in a genetically tractable vertebrate model system. It will be of interest to the fields of muscle development and regulation, tissue mechanics, scoliosis research. My main expertise is in comparative physiology, evolution, and biophysics of muscle contraction. I have experience with a wide range of model species, including zebrafish. I have a more recent interest in muscle development and repair. I am not familiar with the fields of scoliosis research and urotensin signaling.

Response: We appreciate this assessment and agree with the proposed direction of revision. The revised paper will place the direct mechanics at the center of the study while adding the missing physiological context and being more explicit about what an intact axial preparation can and and cannot resolve.

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Referee #3

Evidence, reproducibility and clarity

Summary

This manuscript uses the zebrafish model system, integrating genetic, histological, transcriptomic, and functional approaches to address a challenging and relevant biological question. The authors conclude from their data that urotensin signaling defects affect both passive and active mechanical properties of the larval zebrafish's muscular tail independently, creating an imbalance of forces during development that ultimately leads to a scoliosis-like phenotype. Previous studies in zebrafish had linked urotensin signaling to the developing trunk muscles through the receptor Uts2r3. The present study shows that loss of Uts2r3 leads to changes in muscle specific gene expression, loss of active myotomal muscle force, and increase in passive viscoelastic forces, without overt morphological or dystrophic changes to in the muscle. Importantly, these changes are seen prior to the development of the tail-curvature phenotype.

Major comments

1. The authors predict involvement of myotomal muscles in the progression of the curvature phenotype based on the reported expression of the Uts2r3 receptor in myotomal muscles during development. According to the cited studies, the receptor is expressed specifically in dorsal slow-twitch muscle fibers (Zhang 2018). Supporting this, the upward tail bending effect of urotensin overexpression is abolished in mutant larvae lacking slow twitch fibers (lu 2020, Gillard 2023). The assertion from these studies being that urotensin regulates tail curvature via regulating dorsal slow muscle tone. Too much signaling increases force and bends the tail upwards; two little has the opposite effect. This interpretation is relevant because slow twitch fibers make up only ~7% of the total myotomal muscle CSA in 5dpf larvae and are not thought to contribute meaningfully to the high speed forces measured using the intact tail mechanics approach. The remaining >90% of CSA consists of fast twitch muscle active only during brief escape maneuvers. According to the same studies, fast fibers do not appear to express Uts2r3. If this is the case, the reported loss of force is more challenging to interpret. As written, fiber type is not mentioned. This is an issue that should be discussed and considered when interpreting the data.

2. The authors conclude that twitch and tetanus force deficits in Uts2r3 mutant larvae result from changes in contractility at the sarcomere level. Mis regulation of muscle gene expression and mild loss of structural organization are cited as causes. An alternative explanation, overall reduction in contractile CSA, is ruled out based on estimates from whole animal dimensions (see specific comments below). There are a couple of reasons why this may still be the simplest explanation. First, myotomal muscle accounts for ~70% of the total CSA of the tail, with myofibril CSA a large sub-fraction of that. Therefore, significant changes in the CSA relevant to contractile force may be difficult to resolve from whole-body estimates. This is especially true if increases in passive stiffness result from increased CSA of connective tissue, etc. Second, birefringence is a good measure of damage or structural disruptions to myotomal muscles that are heterogeneous within a sample, as in models of DMD. Uniform reduction in intensity (Fig S2) may result from disruption of the regular order of myosin heads within the sarcomere but could also reflect a reduction in myofibrillar volume. Third, dynamic measurements of contractile function (twitch kinetics, F/V) appear to be unchanged. Disruption of sarcomere organization, a shift in contractile protein isoforms (such as myosin heavy chain), or other changes affecting actomyosin function would be more likely to show up in the kinetics, whereas changes in myofibril CSA would not. Finally, to the extent mRNA levels represent protein abundance, the data presented also support a 'less muscle' explanation. There are experiments that could get at these questions directly, such as a histological examination of tail cross sections. But for the purposes of this study, a more thorough discussion of these possibilities would be sufficient.

3. The authors conclude that 'active and passive defects are unlikely to be simple consequences of one another', claiming 'increased passive stiffness does not readily explain the reduction in active force generation.' This may be true but the issue is complex and needs more discussion. The mechanical approach used (Mead 2020) is quite different from how the tail functions in vivo and comes with some caveats. One observation in that study is that 'isometric' contractions, in which the preparation is held at a fixed length, result in the shortening of contracting myotomes by about 10%, accompanied by the stretching of tissue near the tail attachment points. Because of this, there are a couple of ways in which changes in passive properties could impact measured forces in this assay. For example, the notochord is a structure that functions to resist tail compression during swimming in vivo. So, any stiffening of the notochord, or of connections between myotomal muscle and notochord could reduce muscle forces transmitted to the force transducer. Also, unless tails were pre-stretched by ~10% before activation, as in Mead 2020, forces reported here may have been generated at muscle lengths on the ascending limb of the length-tension curve. Therefore, changes in the passive mechanical properties of the tissue at the attachment points could have large effects on measured force by changing the SL at which force is measured. This could be checked if SL or myotome length was measured during contractions as was done in that study. The paper would be strengthened if the interdependence of active and passive mechanical changes were considered in this light.

Minor comments

1. Are the Uts2r3 mutant fish used in the study heterozygotes or homozygous null? This line was previously described, but it would be helpful if the type of mutation as well as the when and how the phenotype develops are at least briefly described here as well.

2. Mechanical measurements are reported as being performed as described in Mead 2020. Deviations are mentioned in method of attachment, instrumentation, and SL measurement. However, it would be helpful to have a more thorough description of the approach. Specific parameters used should be included. For example: length of preparations, any anatomical landmarks for suture placement, range of muscle lengths used for isovelocity maneuvers, etc.

3. Force velocity data (Fig. 3E) shows a force depression at 28 l/sec of only ~30% at 18˚C. This result predicts a Vmax over 100 l/sec at 18C, and possibly twice that at physiologically relevant temperatures, assuming a q10 of 2. Mead et al (2020 and 2024) predicted a Vmax of 45 l/sec at 28˚C and reported ~80% drop in force at ~12 l/sec at 23˚C, stating that limitations inherent to the instrumentation and the tail preparation precluded accurate measurement at higher velocities. Can the authors comment on the discrepancy? Were any modifications made to the approach in order to access these higher velocities?

4. How were CSA measurements made? Methods states tails were measured in two dimensions at three points. Were anatomical landmarks used? These should be included.

5. Stated sample numbers do not match the number of individual points in figures 3 B, C, D, E. P value for tetanus tension stated in text (0.008) does not match Fig 3 C (0.014). The next sentence appears redundant and states a third p value of < 0.05.

6. Will RNA seq data be reported in a supplemental file or uploaded to a database? Both are standard practice.

7. The primary curvature defect in the Uts2r3 mutant seems to be dorsal-ventral in nature, though this is not explicitly described in the text. Can any insight into this or any other specific feature of the phenotype be gained from the data? Why down and not up or left vs right? The data presented shows no change in the relative 2D area of hemisomites resulting from this curvature. However, geometry would indicate some remodeling (different-modeling?) must take place in these mutant fish. Is possible to measure either muscle fiber length, sarcomere length, or sarcomere number from these images?

8. Fig S3B is very hard to see. Can 'hemisomite abstraction overlay' be defined in the figure caption?

Significance

The main strength of this study is in exploiting the highly integrative nature of the zebrafish model to explore a challenging and relevant biological question. The methods used here, in particular the mechanical experiments, are extremely challenging to perform an interpret. The data presented generally support the conclusions, but important context is missing. A more nuanced discussion of potential mechanisms and experimental caveats will better inform subsequent experiments and improve the overall impact of the paper.

This study has the potential to advance the field by incorporating direct mechanical measurements of active and passive muscle force in a genetically tractable vertebrate model system. It will be of interest to the fields of muscle development and regulation, tissue mechanics, scoliosis research.

My main expertise is in comparative physiology, evolution, and biophysics of muscle contraction. I have experience with a wide range of model species, including zebrafish. I have a more recent interest in muscle development and repair. I am not familiar with the fields of scoliosis research and urotensin signaling.

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Referee #2

Evidence, reproducibility and clarity

In this manuscript, the authors build upon previous findings showing that disruption of Urp1/Urp2 signaling, or loss of their receptor Uts2r3, results in abnormalities in spine morphology. The authors note that Urp1 and Urp2 are expressed by cerebrospinal fluid-contacting neurons surrounding the central canal, whereas Uts2r3 is expressed in skeletal muscle. To gain mechanistic insight into how this pathway regulates spine development, they performed bulk RNA-sequencing of 28 hpf Uts2r3 mutant embryos, prior to the onset of spinal deformities. Their analysis identified changes in the expression of several muscle-related genes. Although they did not detect major structural abnormalities in skeletal muscle, they found altered muscle force production, suggesting that impaired muscle function may contribute to the spinal phenotype. While the study addresses an interesting biological question, I have several concerns regarding the strength of the mechanistic conclusions.

Major comments

1. Expression pattern of Uts2r3 It remains unclear where Uts2r3 is expressed. Apart from the statement that it is present in skeletal muscle, I could not find a detailed characterization of its expression pattern. This information is essential for interpreting the specificity of the phenotype and for understanding whether the observed defects arise directly from muscle or from additional tissues expressing the receptor.

2. Transcriptomic analysis The RNA-seq analysis lacks important context. I could not determine how many genes were significantly differentially expressed in the mutant embryos or what the overall transcriptional changes were. The manuscript focuses primarily on muscle-related genes, but it would be important to know whether these represent a small subset of widespread transcriptional changes or whether the effects are relatively specific to muscle. Presenting the complete dataset, together with pathway enrichment analyses, would help place the findings into a broader biological context.

3. Mechanism of Urp1/Urp2 signaling The manuscript does not sufficiently explain how Urp1/Urp2, which are produced by CSF-contacting neurons around the central canal, signal to receptors expressed in skeletal muscle. Is there evidence that these peptides are secreted into the cerebrospinal fluid and reach the musculature? Alternatively, are there intermediate signaling mechanisms? This represents an important mechanistic gap in the proposed model.

4. Relationship between muscle defects and spinal deformity Although the authors report altered muscle force production, they do not detect obvious structural defects in the muscle. It therefore remains unclear whether the altered muscle function is the primary cause of the spinal phenotype or simply a secondary consequence of broader developmental abnormalities.

5. Tissue specificity A major limitation of the study is that neither the genetic model nor the transcriptomic analysis is tissue-specific. The Uts2r3 mutation affects the whole embryo, and the RNA-seq was performed on whole embryos rather than isolated muscle. Consequently, it is difficult to determine whether the observed transcriptional changes reflect direct effects within skeletal muscle or indirect systemic effects of the mutation. Tissue-specific genetic manipulation and muscle-specific transcriptomic analyses would considerably strengthen the mechanistic conclusions.

Overall assessment The study extends previous work implicating the Urp1/Urp2-Uts2r3 pathway in regulating spine morphology and provides evidence that altered muscle function may contribute to this phenotype. However, the current data provide only limited mechanistic insight into how this signaling pathway regulates muscle physiology or spine development. In particular, the lack of tissue-specific genetic and transcriptomic analyses makes it difficult to distinguish direct muscle-specific effects from broader developmental consequences of Uts2r3 deficiency. Additional experiments addressing these issues would substantially strengthen the manuscript.

Significance

Overall assessment

The study extends previous work implicating the Urp1/Urp2-Uts2r3 pathway in regulating spine morphology and provides evidence that altered muscle function may contribute to this phenotype. However, the current data provide only limited mechanistic insight into how this signaling pathway regulates muscle physiology or spine development. In particular, the lack of tissue-specific genetic and transcriptomic analyses makes it difficult to distinguish direct muscle-specific effects from broader developmental consequences of Uts2r3 deficiency. Additional experiments addressing these issues would substantially strengthen the manuscript.

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Referee #1

Evidence, reproducibility and clarity

The work by O'Hara-Smith et al. explores if alterations in muscle development and function underly the formation of spinal curvature in zebrafish uts2r3 mutants. Using transcriptomic analyses, immunofluorescence and birefringence, the authors reveal a reduction in the expression of muscle-associated genes as early as 28hpf with only mild reduction in birefringence and otherwise no overt changes in muscle morphology or symmetry, even at stages where spinal curvature becomes apparent (14dpf). Biomechanical analyses further show that loss of uts2r3 leads to a reduction in active force and an increased passive resistance to stretch, indicating that urotensin signaling plays a role in the regulation of muscle function.

Major Comments:

The paper is well written and easy to follow. The majority of experiments are described in sufficient detail, and all of the used reagents are listed. The conclusions are supported by the presented data. Optional additional experiments that could significantly improve the paper would be a detailed characterization of the expression of uts2r3 as previous expression analyses were limited to one early time point and mostly used analyses of mosaic transgene expression. However, performing detailed expression analyses would be both costly and time consuming.

Minor Comments:

1. Additional details on the RNA-seq experiment should be added to the methods section to allow interpretation of the results. Was mRNA selection or ribosome depletion used? What was the sequencing mode (paired or single-end)? What read length was used? How many reads were obtained per sample and how many filtered reads could be aligned to the reference transcriptome?

2. To understand the extend of the changes detected by the transcriptomic analyses it would be helpful to include the total number of significantly up- and down-regulated genes as well as the magnitude of change (fold-change) for the highlighted muscle related genes.

3. Similarly, for the GO terms a list of differentially expressed genes for each term should be provided and largely overlapping GO terms should be removed. The fact that all terms show almost the exact same fold enrichment could point to a large overlap between the differentially expressed genes detected for each term.

4. As the ratio of twitch and tetanic force was quantified and used as a measure for myosin dynamics and force transmission, it would be helpful to show that data in fig. 3 in addition or instead of panel D. Similarly, the half-relaxation time data should be added.

5. In the methods section, it would be helpful for non-experts to indicate that the MANDRA-1 antibody detects dystrophin.

6. Additional details on how the cross-sectional area was determined should be added to the methods section.

7. While this is the first report linking urotensin signaling to muscle function in idiopathic scoliosis, previous research has shown a role for urotensin signaling in skeletal muscle metabolism (PMID: 35605093, PMID: 24116164, PMID: 36167277). The findings presented in these studies and how they relate or could help interpret the findings of this study should be discussed.

8. Previous studies imply that uts2r3 is expressed in dorsal skeletal muscle, which would imply that dorsal and ventral muscles are differently affected in uts2r3 mutants. The authors should discuss this asymmetric expression of uts2r3 in skeletal muscle and its relevance for the observed phenotype. Furthermore, it would be helpful to include future directions on how to dissect differences between dorsal and ventral muscle activity.

Significance

Despite the relatively high prevalence of scoliosis in the human population (2-3%) our understanding of the underlying pathomechanisms are limited. To my knowledge this is the first study that shows that changes in muscle biomechanical function proceed the formation of spinal curvature in a model of idiopathic scoliosis. The study advances our understanding of the mechanisms underlying the formation of spinal curvature. If early changes in biomechanical properties of skeletal muscles are found to be a general feature of idiopathic scoliosis, this study could be impactful for the early detection and potentially treatment of idiopathic scoliosis.

Therefore, these findings will be of interest to researchers focused on basic science but also for translational and clinical research.

A major strength of the study is that the observed transcriptional changes could be linked to functional consequences through biomechanical testing of muscle function. However, the pathways that link urotensin signaling to the observed alterations in gene expression and muscle mechanical properties were not explored. Previous reports show uts2r3 expression in dorsal skeletal muscle but are limited to one early time point and analyses of mosaic transgene expression. As the presented study explores uts2r3 function in skeletal muscle, detailed analyses of uts2r3 expression at different stages and in different muscle subpopulations would help interpret the results and significantly improve the study.

Expertise: zebrafish genetics, skeletal development, scoliosis, CRISPR/Cas9, transcriptomics

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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

This manuscript describes the characterization of PfDCX, which is localized to an apical structure in ookinetes, likely to be the conoid. The knockout of PfDCX resulted in no phenotype in merozoites, consistent with its lack of expression at this stage. Interestingly, the PfDCXKO parasite exhibited a strong defect in transmission in the mosquito vector. Structurally, PfDCXKO results in reduced subpellicular-MT rafts in gametocytes. The data is solid and well presented with appropriate analysis. There are a few points that need to be addressed, related to assessing the DCXKO phenotype in the ookinete stage, data interpretation, and citations.

1. Phenotype in ookinetes: PfDCX is located to the apical structure/conoid in the ookinete. However, there is no phenotype analysis for the ookinete stage. In particular, the motility phenotype of the parental and PfDCXKO ookinetes should be examined and compared, because ookinete motility is directly related to parasite transmission in the mosquito vector. Additionally, the organization and structure of the subpellicular MTs of the parental and PfDCXKO ookinetes should be analyzed and compared with the phenotype in gametocytes.
2. Data interpretation:

a. There is no evidence to support that "...DCX is required for P. falciparum transmission to the mosquito independently of conoid function." (abstract and Discussion- p23). First of all, no structural analysis was performed for the apical structures of gametocyte or ookinete, and thus the impact of pfDCX knockout on the conoid is unknown. Secondly, the change in the subpellicular MT rafts in the gametocyte of the DCX KO mutant is not necessarily the cause for the phenotype in parasite transmission in the mosquito vector. It also does not exclude the involvement of DCX's conoid-related function.

b. The following two sentences appear to be contradictory Results, p17, last sentence: "While DCX-HA expression was detected by western blot in gametocytes, we were unable to localise the protein using either IFA or U-ExM possibly due to low or transient expression, which may prevent its detection with our current approaches. Discussion, p24, first paragraph: "Interestingly, although DCX localises to the conoid and is required for the proper organisation of gametocyte SPMTs..." 3. Citations:

a. Introduction (p3, first paragraph): For this sentence, "In this parasite, conoid fibres are initially assembled as canonical 13- protofilament microtubules and undergo a maturation process that transitions them into a distinctive nine-protofilament left-handed comma-shaped structure", in addition to Hu et al's 2002 JCB paper, Li et al's 2023 Adv Sci paper should also be included ("Cryo-Electron Tomography of Toxoplasma gondii indicates that the conoid fiber may be derived from microtubules."). The Hu et al paper first revealed that the mature conoid fibers are open, ribbon-shaped tubulin-polymers. The Li et al. paper showed the structural differences of forming versus mature conoid fibers.

b. Several additional findings in Leung et al.'s 2020 BMC-MCB paper should be included in the introduction and/or discussion ("A doublecortin-domain protein of Toxoplasma and its orthologues bind to and modify the structure and organization of tubulin polymers.", reference#15). First, the heterologous expression of PfDCX in Xenopus cells shows that it can associate with MTs. Second, the heterologous expression of TgDCX in Xenopus cells induces the formation of MT rafts, often with a c-shaped tube at the end, quite similar to the supellicular MT-rafts in the wild-type gametocyte. The data in this paper suggests that PfDCX has similar activities, judging by the reduced MT raft when PfDCX was knocked out.

Significance

This work revealed important functions of DCX in Plasmodium falciparum, as well as an interesting divergence of its function impact between P. falciparum and P. berghei. It is also an important addition to the studies of the apicortin family proteins and structural determinants of the apicomplexan MT cytoskeleton. Assessing the DCXKO phenotype in the ookinete stage, however, will significantly strengthen the work.

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Referee #1

Evidence, reproducibility and clarity

The manuscript uses multiple techniques to evaluate the role of the DCX protein during the Plasmodium falciparum life cycle. DCX has been associated, in a previous publication, with the conoid of the ookinetes. DCX is dispensable in Plasmodium berghei for all stages. However, disruption of DCX causes a block to P. falciparum transmission in the mosquito, and this defect is independent of conoid function. Rather, the loss of DCX leads to a reduction of branching of the subpellicular microtubules in gametocytes, a previously unrecognized function. The gametocyte SPMTs are interesting and divergent with variable numbers of protofilaments and branching. The decreased transmission data upon DCX deletion are very robust. The U-ExM of the purified ookinetes from mosquitoes are quite striking. The authors should also be commended on the use of some very difficult in vitro studies of P. falciparum gametocytes. Figure 6 shows the changes in SPMT branching. These data are remarkable. In addition, the use of cryo-ET with quantification is excellent and provides strong data to support their hypotheses. The manuscript is very good, and I have mostly small suggestions.

Major:

1. The distance measurements in Fig 3C,D are remarkable. It is unclear how the 5.3 nm was calculated. Is this a back calculation to the "true" distance by some expansion factor? Or is this an expanded distance? This needs to be clarified. Also, how many ookinetes were these measurements made in? The images are impressive, but they are only of a single or a few cells. These measurements should be made more robust with statistics.
2. It is unfortunate that DCX could not be localized in the gametocytes. If possible, the authors should try some additional or different epitope tags or potentially some iterative techniques to boost signal. One option is to use a biotinylated secondary antibody then use a tertiary anti-biotin antibody, etc.

Minor:

1. Introduction - I do not think there is evidence that the SPMTs provide structural support or rigidity in merozoites. The evidence for the other stages seems better, but it is lacking for merozoites.
2. Results - "one within an exogenous 2loxPint intron"; I think the "2" should not be present?
3. Fig 1B,C - the whole schizont should be shown with a zoomed in box for the single merozoite. It is useful for the reader to see the level of background staining of the entire schizont.
4. Fig 3 - while the mCling is a nice addition, it does not show new information that is absent from the NHS staining. For a non-expert of expansion microscopy, the inclusion of the mCling only adds to confusion. This should likely be removed from the main figure.

Significance

The manuscript is an important addition to the understanding of gametocyte biogenesis and function in Plasmodium falciparum.

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Reply to the reviewers

Response to reviews is provided as an attached file.

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Referee #3

Evidence, reproducibility and clarity

Summary

In this manuscript, the authors report how they have investigated the presence of the Drosomycin gene in insects, starting from the unexpected discovery of five Drosomycin-like genes in Drosophila busckii of the subgenus dorsilopha whereas it had been found only in the Melanogaster group of the Sophophora subgenus and has not been identified in closer relatives such as other groups of the Sophophora subgenus or the Drosophila subgenus. They document that the presence of Drosomycin-like clusters in both D. melanogaster and D. busckii may result from horizontal gene transfer based on synteny arguments. Importantly, two D. busckii Drosomycin-like genes appear to be preferentially induced by a Gram-positive bacterial challenge than one by Gram-negative bacteria, in keeping with a possible regulation of their expression by the Toll and not Immune deficiency pathway. They then extend their bioinformatics strategy to discover further Drosomycin-like genes in sequence or expression data from 24 winged insect orders. This analysis reveals that only a limited number of orders and a limited number of species within orders have acquired Drosomycin-like genes in their genomes. They conclude that the acquisition of the Drosomycin-like genes has proceeded through Horizontal Gene Transfer (HGT) followed by some cases of secondary losses.

Major comments

The authors make a compelling argument for the hypothesis of seven events of HGT vs. more than 50 secondary loss events required to account for their data if a common ancestor were assumed (Fig. S5). This reviewer is convinced by this study and has mostly minor comments to improve the manuscript, except for two major comments detailed below.

Fig. 5 should include the Drosomycin gene discovered in Musca domestica. By the same token, the text in the summary is inaccurate: " We show that in Diptera...". It should read: "We show in Drosophilidae..". Actually, the authors of ref. 44 have not relied solely on a protein database entry as wrongly claimed by the authors. Ref. 44 states: "In addition, our BLASTP search retrieved a hit from Musca domestica that has identical sequence to Drosomycin. We also confirmed its presence in the M. domestica genome by PCR amplification and DNA sequencing (Fig. 6b)." Thus, the authors should be more cautious in their statements: this apparent mistake weakens their overall argument and questions the sensitivity of their approach. At the very least, they should check by PCR amplification and DNA sequencing on several isolates of M. domestica whether they can amplify the Drosomycin gene as reported by Zhu & Gao.

Anoither shortcoming is the poor description of the RTqPCR data that seem to depend on only three experiments. It is not described how many times the experiments have been independently performed, whether the only three data points correspond to biological replicates of a single experiment, and which type of statistical analysis has been used (of note, in theory, a parametric test can be applied only if the data have been shown to follow a Normal law of distribution...). If the data correspond to three biological replicates of five flies each, then the experiment cannot be validated, especially given the variability of the signal for Drsl4 after a mixed challenge (Fig. 1D). The advice is to have more independent experiments to increase the confidence in the presented data, which is not expected to take much time and should very easily be completed within two months (a week if flies are available...).

Minor comments

1. "sanger" sequencing: while becoming a common name is a testimony to how popular a device or method has become, the authors may want to remember that Prof. Fred Sanger is the only researcher awarded two Nobel Prices in the same discipline...
2. p7, left column: "to this end, we screened up to 15 insect genomes". In the right-hand column, one reads: "However, within Orthoptera (N=23)"...
3. Ref. 75, included in the Discussion on the antifungal activity of Drosomycin and Drosomycin-like Defensin peptides: this reference deals with Metchnikowin, which is a proline-rich antimicrobial peptide and does not belong to the Defensin family.
4. Argument on the short promoters that may be transferred (interesting idea): while indeed NF-kappaB binding sites are often found in the proximal region of the promoter, they can also be found in other positions, e.g., the third binding site of the Diptericin promoter that is more than a kb away from the transcription start site. If this reviewer recalls correctly, there is also a kappaB site that lies downstream of the D. melanogaster Drosomycin gene. Thus, the authors might want to validate their concept more carefully in future work by performing a more detailed analysis of potential kappaB binding sites in the Drosomycin-like genes regions.
5. SRA: the definition is given only in the Supplementary Text and not in the main text.
6. Several figures are really difficult to read as they are too small: Fig. 3, Fig. 4, Fig. S2 and also Fig. S4 (names of the species difficult to read). Even at high magnification on the computer, it is very difficult to read the sequences displayed in 4A, due to poor resolution.
7. Fig. S2: the figure legend does not adequately describe the figure. What are the turquoise and yellow arrows? The exact sequences of the kappaB sites should be provided in a second panel of this figure.
8. Legends Fig. S3 and Fig. S7: please, give the reference numbers, respectively 61-62-3 and 112.
9. Legend Fig.S4. It may help the reader to indicate that Liposcelis sp. sequences are on top of the panel. It would also be desirable to highlight the D. mel sequence when present in multiple alignments.
10. Ref. 76 is not correct; the article has recently been published in PLoS Pathogens and not in Immunology.

Significance

This study provides a careful analysis of the distribution of Drosomycin-like genes in insects and provides a compelling argument for HGT being the mechanism behind the remarkably patchy distribution of this antifungal gene within insect order and species. This however is not a surprise in that the antifungal function of Drosomycin was discovered upon realizing that it presented sequence similarity to that of a plant antifungal peptide (rs-AFP2; Terras et al., FEBS Letters 1993, 316, 233-240.). An even more striking observation is that the Drosomycin gene has been found to be transferred to nematodes through HGT (ref. 44) and has also been found in humans (ref. 74). It would have been worth mentioning specifically these observations that generalize even more the work made by the authors on insects. Indeed, these disparate observations may fit well with the authors' proposition of an initial development of this type of molecules in bacteria in their warfare against fungi that might have been repeatedly transferred to eukaryotes. How related at the sequence level are the Drosomycins found in plants, ecdysozoans, and humans? A limitation of the study acknowledged by the authors is that no "wet" experiments have been performed to determine whether the different peptides identified in this study are bona fide antifungal effectors of the innate immune response. This approach would be needed to fully understand the evolution of function of these sequences in the different recipient hosts.¬¬

This work will be of interest to evolutionary immunologists and more generally to anyone interested in antimicrobial peptides and innate immunity.

This reviewer is an expert of the study of Drosophila innate immunity and is not a specialist of evolutionary processes.

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Referee #2

Evidence, reproducibility and clarity

Summary

This study investigates the evolutionary origin of the drosomycin (Drs) across insects using comparative genomics, transcriptomics, phylogenetics, and gene expression analyses. The authors screen >670 genomes/transcriptomes across 24 insect orders and report a highly discontinuous distribution of Drs genes. They identify Drs homologs in Drosophila (restricted clades), cockroaches, mantises, select beetles, a katydid, and pseudogenes in booklice, but not in most other insect lineages. To explain this pattern, the authors argue that multiple horizontal gene transfer (HGT) events (~7) are more parsimonious than extensive gene loss (>50 independent losses). Supporting evidence includes: Genomic synteny analyses suggesting independent insertions, Codon conservation (serine usage bias) inconsistent with convergence, Paraphyletic phylogenetic clustering of Drs sequences. Evidence of immune inducibility in at least one non-Drosophila lineage. The study concludes that HGT is an underappreciated mechanism for immune gene innovation in insects, potentially enabling rapid acquisition of pathogen defense traits.

General comment

This is an ambitious and conceptually important study addressing a long-standing question in immune gene evolution: how similar antimicrobial peptides appear across distantly related taxa. The dataset is large and the integrative approach (genomics + expression + phylogenetics) is a major strength. However, the central claim-multiple HGT events of an AMP gene-is not yet fully supported at the level required for such a strong evolutionary conclusion. While the authors present suggestive evidence, key alternative explanations (e.g., extreme gene loss, convergence under constraint, contamination, or assembly artifacts) are not fully excluded. The manuscript would benefit from stronger phylogenetic and genomic evidence of HGT, more rigorous exclusion of contamination and assembly issues, and clearer framing of conclusions as probabilistic rather than definitive Overall, the study is promising and potentially impactful but requires substantial revision to strengthen evidence and temper conclusions.

Major comments

Strength of evidence for HGT vs alternative explanations The core claim-that Drs distribution is best explained by HGT-is plausible but not conclusively demonstrated. The argument relies heavily on parsimony (7 gains vs >50 losses) , but parsimony alone is insufficient in deep evolutionary contexts where gene loss is common. Alternative explanations are not fully ruled out: Extensive lineage-specific gene loss, Convergent evolution under structural constraints, and hidden homologs missed due to rapid divergence Specific revisions: Reframe conclusions as "consistent with HGT" rather than definitive evidence. Provide statistical model comparison (e.g., likelihood-based gain/loss models vs HGT scenarios) Phylogenetic analysis is insufficiently resolved The phylogenetic trees show low posterior support and limited resolution due to short sequence length (~80-130 nt). Paraphyly is used as evidence of HGT, but low support weakens this claim. No clear donor-recipient relationships are identified

3.3 Functional validation is lacking The manuscript assumes Drs homologs are functional AMPs, but no antimicrobial assays are performed. Expression data are limited (only one lineage tested experimentally) This weakens claims that HGT contributes to functional immune innovation

3.4 Contamination and assembly artifacts not fully excluded The study relies heavily on public genomic datasets. Some assemblies are acknowledged as previously contaminated (e.g., cockroach genome issues). Limited validation (PCR in some taxa) is performed

3.5 Limited mechanistic evidence for HGT The manuscript speculates on mechanisms (e.g., transposons), but no clear vector or mechanism identified. No consistent association with mobile elements. Please clearly separate speculation from evidence

3.6 Sampling bias and absence inference Absence of Drs is used heavily in arguments, but benome completeness varies across taxa. Absence detection is uncertain, Authors should provide quantitative completeness metrics (e.g., BUSCO) for all datasets

3.7 Overinterpretation of codon usage analysis The serine codon argument is interesting but not definitive as codon conservation could reflect functional constraint, not shared ancestry. Limited number of informative sites

Minor comments - Clarify replication and statistical tests for qPCR experiments. Provide exact sample sizes and variance measures. Define thresholds for HMM/BLAST detection more explicitly

Significance

General assessment

The study addresses a highly significant and unresolved question in evolutionary immunology: the origin of antimicrobial peptides across taxa. Its strength lies in large-scale comparative analysis and integration across disciplines. There are some minor issues as Evidence for HGT remains circumstantial rather than conclusive and functional relevance is largely inferred Audience

Reproducibility and rigor

Strengths:

• Large dataset (673 genomes/transcriptomes)
• Multiple complementary methods (HMM, BLAST, phylogeny, expression)

Concerns:

• Limited methodological detail for:
  • Filtering criteria
  • Statistical analyses
• Reproducibility would benefit from:
  • Public pipelines/code
  • Full dataset availability
• Suggested major revisions (summary)

Required

1. Temper conclusions regarding HGT; present as best-supported hypothesis
2. Strengthen phylogenetic analyses and report support values clearly
3. Improve contamination controls and validation
4. Clarify reproducibility (methods, thresholds, statistics)
5. Expand discussion of alternative explanations

Optional

1. Functional validation of Drs peptides
2. Advanced phylogenetic reconciliation analyses
3. Mechanistic exploration of HGT vectors

Final recommendation

Major revision

The manuscript has strong potential and addresses an important question, but key claims require more rigorous support and more cautious interpretation before publication.

Reviewer expertise - insect biology and genomics.

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Referee #1

Evidence, reproducibility and clarity

In this manuscript, Aumont and colleagues conduct a thorough search of numerous insect genomes for the presence of genes encoding Drosomycin family antimicrobial peptides. They take advantage of a large set of existing genome sequences and use an appropriate search algorithm to find Drosomycin paralogs. They then map the presence or absence of paralogs onto a known phylogeny of the insects. Based on the patterns of presence and absence across the tree, they infer that an excessively large number of independent evolutionary losses would be required to explain the disparate distribution of Drosomycins across insects, and that repeated horizontal gene transfer is a more likely explanation.

The detection of Drosomycin paralogs is performed well, and the degree of similarity in primary amino acid across distantly related species is striking. The inference that horizontal transfer is more likely than evolutionary convergence or repeated independent loss is logical and probably true, but is not formally tested against any evolutionary model other than parsimony. There are opportunities for more complete evolutionary analyses, including examination of gene turnover rate within the Drosomycin family after each putative horizontal transfer. The extreme amino acid similarity in the mature peptides contrasts sharply with high divergence in the signal peptides, but this contrast is not explored. Are the Drosomycin mature peptides more similar across species than other housekeeping genes are, as would be expected under HGT? By inferring ancestral sequences of the Drosomycins, is it possible to guess which taxonomic groups were the origins of each transfer? If the signal peptides are assumed to evolve approximately neutrally, it might be possible to use them to date the age or order of gene duplication events after each horizontal transfer, or to date the transfers themselves after inferring an ancestral sequence. Not all such analyses may be fruitful and the authors could select the most informative ones for inclusion in the manuscript, but the total absence of any of them leaves the paper feeling more a like an interesting anecdote than a thorough work of evolutionary biology.

Gene family turnover dynamics are alluded to throughout the manuscript but are never formally described. The first paragraph of Results section could be a good place to do that. The paragraph describes restriction of Drosomycin genes to the Melanogaster subgroup, but the Drosomycins are not described as a gene family in that paragraph. Thus, the occurrence of 5 Drosomycin-like paralogs from D. busckii in the next paragraph appears to be exceptional in number as well as evolutionary placement. But I believe there are 12 Drosomycin-like genes in melanogaster, so busckii actually has fewer. Establishing Drosomycins as encoded by dynamic multigene families will give context to the remainder of the manuscript. At the end of the last paragraph of the right column in page 3, the authors could indicate explicitly whether they believe the busckii family results from a single transfer and subsequent expansion, and based on what evidence.

The D. busckii Drsl genes 1-3 were not induced by infection, left column of Results page column 5. In D. melanogaster, Drosomycin-like peptides are expressed in the gut. The authors could dissect D. busckii guts and look for expression of the DbDrsl genes. The logic presented in the right column of page 12, that the genes are small enough that their regulatory sequences could be transferred with them, would also apply to enhancers that drive expression in the gut.

The passages on detection of Drosomycins from cockroaches, mantids, and katydid are very interesting and I agree with the authors that they probably occur by ancient horizontal transfer. However, the authors have not formally rejected a hypothesis of evolutionary convergence in these passages. I think that alternative hypothesis should be easy to reject based on the similarity of the mature peptides as shown in Figure 3, but it should be formally tested.

The analysis of the Serine codons is clever and forms a convincing argument against convergent evolution. The authors could quantify the probability of each of the 4 serines using the same codon across all taxa under convergent evolution and it is probably vanishingly small. On the other hand, identical codon usage is exactly what you would predict if the entire Drosomycin family is descended from a paralog that was present in the ancestor of insects. The HGT model as applied to this data does assume a common ancestor at the base of Insecta, and that could be explained in this passage.

The last paragraph of the left column and first paragraph of the right column on page 8 describe unexpected similarity of signal peptides between cockroaches and beetles, but the sequence divergence between these groups is neither quantified nor benchmarked to any expectation. That results in these paragraphs coming across as vague and unrigorous.

In Figure 4, I would suggest adding phylogeny of the insect taxa. Some readers of this paper will not be entomologist and will not know how the species groups relate to each other. Seeing the insect tree will allow comparison of the Drosomycin tree for concordance. A larger insect tree is given in Figure 5, so I would give just the focal taxa in Figure 4.

Minor comments

It would be easier to refer to specific passages in the manuscript if line numbering was employed.

In the middle of the right column on page 2, the authors mention convergent evolution of a similar structure in Defensins and cite two recent papers. This same observation was made more than 30 years ago by Broekaert et al (1995) Plant Physiol. 108:1353-8. The authors could decide at their discretion whether they would like to include a reference to the earlier paper.

If the authors wish for a contextual example of repeated horizontal transfer in insect defenses, they could look to the aip and cdt genes of aphids and Drosophila.

The second paragraph of the right column on page 3 states that the annotated Drs in housefly is probably a contamination but does not provide any evidence to support that statement. The paragraph should more clearly state that the authors examined the Musca genome carefully and could not find evidence of the reported paralog. It might also be worth noting whether the alleged Musca paralog matches the sequence of any other known Drosomycin, thereby suggesting a possible source of contamination (eg, is it a D. melanogaster sequence?).

In the left column of page 5, I'm not sure why it is surprising that the DptC of D. busckii is induced by infection by both G+ and G- bacteria. The Toll=G+, IMD=G- dichotomy of D. melanogaster is probably restricted to melanogaster and closely related species. One of the authors of this paper has previously shown that D. busckii has 8 DptC genes (https://www.biorxiv.org/content/10.1101/2025.06.06.658223v1) so it is not clear which paralog is being referenced in this paragraph.

Delete the period after "pomonae" in the left column of page 8.

The right column of page 9 refers to "a remarkably specific pattern of evolution" but I did not catch what specific pattern is being referenced. The repeated loss of Drosomycins but not other genes? There is no formal analysis here, only verbal argument and intuition so the verbal argument should be precise.

The discussion might benefit from an explanation of how transposon-mediated horizontal transfer between distantly related species would work. Especially because the authors do not find sequence signatures of TEs, this suggestion appears weak. However, there does not appear to be any other plausible argument either.

In the top of the left paragraph on page 14, it is unclear whether the suggested dietary shift is inferred to cause pressure on gut-expressed Drosomycins, risk of systemic infection, or both.

The passage at the top of the right column of page 14 describes shifting understanding of the evolutionary history of Drosocin and Attacins. As written, this passage will probably be difficult to understand for readers who are not already familiar with those genes.

I do not think this paper needs a summary conclusion section. I would delete that section.

Significance

In this manuscript, Aumont and colleagues conduct a thorough search of numerous insect genomes for the presence of genes encoding Drosomycin family antimicrobial peptides. They take advantage of a large set of existing genome sequences and use an appropriate search algorithm to find Drosomycin paralogs. They then map the presence or absence of paralogs onto a known phylogeny of the insects. Based on the patterns of presence and absence across the tree, they infer that an excessively large number of independent evolutionary losses would be required to explain the disparate distribution of Drosomycins across insects, and that repeated horizontal gene transfer is a more likely explanation.

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Reply to the reviewers

We thank both reviewers for their careful evaluations. Their comments have led us to strengthen the experimental analysis, sharpen the conceptual framework, and qualify the mechanistic interpretation.

REVIEWER 1

Summary

In this study, the authors investigate how extracellular matrix (ECM) properties and repulsive guidance cues cooperate to regulate vessel growth and patterning during angiogenesis. To address this question, they develop a mathematical framework that integrates endothelial cell network formation, ECM mechanics, and semaphorin-mediated repulsive signaling. Their simulations predict that reductions in ECM stiffness or density impair vessel extension, while reductions in either ECM density or semaphorin gradient distribution promote vessel fusion, suggesting that ECM properties and semaphorin signaling act together to guide vascular sprouts and maintain vessel patterning.

The authors then test these predictions experimentally using zebrafish intersegmental vessels (ISVs) as an in vivo model of sprouting angiogenesis. Through morpholino-mediated depletion of laminin 1, laminin 4, fibronectin 1a, and fibronectin 1b, alone and in combination, they examine the consequences of ECM disruption on ISV growth and organization. They report defects in vessel extension and patterning, including increased ectopic vessel fusion, and conclude that laminin- and fibronectin-dependent ECM organization is required for proper ISV migration, growth, and patterning.

The study combines computational modeling with experimental analysis to address an important question in vascular development and provides a potentially valuable framework for understanding how mechanical and guidance cues are integrated during angiogenic sprouting.

Major comments

Comment 1

1. The evidence does not convincingly demonstrate that laminin/fibronectin directly regulate ISV patterning

The authors developed a mathematical model incorporating endothelial cell network formation, ECM mechanics, and semaphorin-mediated repulsive signaling. The simulations predict that reduced ECM stiffness or density slows vessel growth, whereas reduction of either ECM density or the semaphorin gradient promotes vessel fusion, suggesting that ECM properties and semaphorin signaling cooperate to guide vessel trajectories.

The experimental data, however, do not convincingly establish that the observed ISV patterning defects are a direct consequence of laminin/fibronectin loss. As acknowledged by the authors, combined depletion of laminin and fibronectin severely disrupts somite and notochord morphogenesis. Given the well-established role of somites and semaphorin-mediated repulsive signaling in restricting ISV growth and preventing ectopic branching or fusion, it remains unclear whether the vascular phenotypes arise from direct endothelial-ECM defects or indirectly from altered trunk patterning.

The authors argue that ISV disorganization is still observed in embryos with comparatively preserved somite morphology (e.g., MO L14Fb). However, the assessment of somite preservation is based on relatively low-magnification images, and it is unclear whether molecular patterning within the somites remains intact. In particular, the manuscript does not address whether semaphorin expression or distribution is altered in MO L14Fa, MO L14Fb, or the corresponding rescue conditions. This is an important omission because semaphorin gradients are explicitly incorporated into the mathematical model and are predicted to strongly influence vessel guidance by preventing ectopic vessel fusion.

Therefore, to support the conclusion that laminin/fibronectin directly regulate ISV patterning, it would be important to determine whether semaphorin expression and/or distribution are preserved following laminin/fibronectin depletion. Without such data, the possibility remains that the vascular mispatterning phenotype is secondary to defects in somite and notochord development.

Furthermore, previous studies disrupting endothelial-ECM adhesion have generally reported defects in ISV growth and elongation without accompanying vessel mispatterning:

• Talin1-deficient zebrafish (tln1 uqal−/−) exhibit impaired ISV growth and an increased frequency of disconnected ISVs but do not display ectopic branching or aberrant vessel patterning (Chau et al., 2022; doi:10.1242/dev.200454).

• A second talin1 mutant (fl02k) similarly shows defects in vascular development without ISV mispatterning (Wu et al., 2015; doi:10.1096/fj.15-273409).

• Loss of integrin β1b results in impaired ISV elongation but does not disrupt ISV patterning (Iida et al., 2018; doi:10.1111/gtc.1264).

These studies suggest that impaired endothelial-ECM interactions alone are insufficient to produce the extensive ISV fusion and mispatterning observed here, raising the possibility that secondary defects in trunk tissue organization contribute substantially to the phenotype.

Authors’ response

We agree that the original manuscript did not sufficiently distinguish a direct endothelial-ECM effect from indirect effects arising from disruption of the surrounding trunk tissues. We have therefore substantially revised both the experimental analysis and our interpretation.

First, we added whole-embryo bright-field imaging to document gross morphology across the principal ECM perturbation conditions. These analyses show that MO L14Fa displays pronounced trunk and somite abnormalities, whereas MO L14Fb retains comparatively preserved gross segmental morphology despite strong vascular disorganization.

Second, because Semaphorin/Plexin signaling is an established regulator of ISV pathfinding and is explicitly represented in our mathematical model, we directly examined sema3aa and sema3ab expression. Whole-mount HCR RNA-FISH showed that both transcripts remained detectable in the trunk. The sema3ab spatial expression pattern, which is implicated in ISV guidance, appeared broadly preserved, whereas sema3aa showed more apparent local differences in the more severely affected MO L14Fa embryos. Complementary RT-qPCR performed on ΔCt values detected no significant differences in overall sema3aa or sema3ab transcript abundance between Control, MO L14Fa, and MO L14Fb. Nevertheless, these transcript-level analyses cannot exclude changes in local Semaphorin protein distribution or activity.

We therefore interpret these data as arguing against wholesale loss of sema3aa/sema3ab expression as the sole explanation for the vascular phenotype, while explicitly acknowledging that local tissue disorganization and altered presentation of guidance signals may still contribute, particularly in MO L14Fa.

Third, we added genetic validation experiments in which MO L14 was combined with homozygous fn1a or fn1b mutant backgrounds. Laminin depletion strongly increased aberrant ISV patterning in both fibronectin mutant backgrounds. These experiments provide independent genetic support for a laminin-fibronectin interaction, although we explicitly acknowledge that the laminin component remains morpholino-based.

Fourth, chimeric fn1a and fn1b mRNA rescue significantly reduced the vascular patterning phenotype in the corresponding combined perturbation backgrounds.

In response to the reviewer’s central concern, we have also revised the wording throughout the manuscript. We no longer claim that the experiments establish a purely endothelial or cell-autonomous mechanism. The revised Results explicitly state that the combined genetic, rescue, and Semaphorin analyses support an ECM-dependent contribution to ISV patterning “without establishing a purely endothelial or cell-autonomous mechanism.”

We have additionally incorporated the studies cited by the reviewer concerning Talin1 and integrin β1. In the revised Discussion, we distinguish perturbation of a single endothelial adhesion component from combined laminin/fibronectin perturbation, which can simultaneously influence ligand availability, ECM organization and mechanics, neighboring tissues, and multiple receptor systems.

Comment 2

1. Quantification of ISV growth using "ISV volume" requires further justification

The authors estimate average ISV volume by dividing the total segmented trunk vascular volume by the number of ISVs. This metric raises several concerns.

First, the segmented vascular volume appears to include non-ISV structures such as the dorsal longitudinal anastomotic vessel (DLAV). Consequently, the calculated parameter does not exclusively represent ISV volume and may not accurately reflect ISV growth.

Second, several morpholino conditions (e.g., MO Fn1ab, MO L14, MO lama1/4 fn1a, and MO lama1/4 fn1b) exhibit pronounced developmental delay and shortened trunk length. Under these conditions, reduced vascular volume may simply reflect overall embryonic growth retardation rather than a specific defect in ISV growth. Therefore, it is difficult to distinguish primary vascular phenotypes from secondary consequences of reduced embryo size.

Finally, ISV growth is normalized to the dorsal-ventral axis length. Because overall embryonic dimensions are reduced in several experimental groups, this normalization may partially mask genuine ISV growth defects.

The authors should therefore provide additional justification for this metric and discuss its limitations. Direct measurements of ISV length may provide more robust assessments of ISV growth.

Authors’ response

We agree with this criticism and have replaced the previous volume-based analysis.

The revised manuscript no longer uses average segmented vascular volume or normalization to the embryo dorsal-ventral axis as the primary measure of ISV growth. Instead, ISV extension was measured directly in micrometers during time-lapse imaging from approximately 22–28 hpf.

For each embryo, three ISVs that had only recently initiated dorsal extension from the dorsal aorta at the beginning of the recording were selected and followed over time. ISVs that had already undergone substantial extension were excluded. The three measurements were averaged to obtain an embryo-level value at each time point, and an embryo-level growth rate in µm/h was calculated over the six-hour interval. Thus, the revised analysis directly measures ISV elongation and avoids the concerns associated with inclusion of non-ISV vascular structures, differences in overall embryo dimensions, and dorsal-ventral normalization.

Minor comments

Minor comment 1

1. When describing tip-cell filopodia and lamellipodia dynamics in ISVs, the authors should cite Phng et al., 2013 (doi:10.1242/dev.097352).

Authors’ response

Added. Phng et al., 2013, is now cited together with the relevant literature on endothelial tip-cell behavior.

Minor comment 2

1. Page 3 contains a "?" in place of a reference citation.

Authors’ response

Corrected during revision of the Introduction and references.

Minor comment 3

1. Transgenic line nomenclature should be italicized throughout the manuscript.

Authors’ response

The nomenclature was reviewed and standardized throughout the manuscript.

Minor comment 4

1. mRNA transcript names should be italicized throughout the manuscript.

Authors’ response

The nomenclature was reviewed and standardized throughout the manuscript.

Minor comment 5

1. Figure 1E is presented at insufficient magnification to evaluate ISV morphology and patterning. Higher-magnification images similar to those shown in Figures 5 and 6 would be helpful.

Authors’ response

Figure 1 has been reorganized and now contains higher-magnification representative trunk images that allow individual ISV trajectories and patterning defects to be evaluated more clearly.

Minor comment 6

1. Figure 3 legend refers to a fourth simulation condition ("reduction of both fiber stiffness and fiber density"), but this condition is not shown in the figure. This statement should be removed unless the corresponding data are presented.

Authors’ response

Corrected. The revised figure and legend describe only the simulation conditions that are presented.

Minor comment 7

1. Statistical comparisons should be provided for Figure 3C-F.

Authors’ response

Added. The revised Figure 3 legend now reports the statistical tests, multiple-comparison procedures, sample sizes, and adjusted p-values for the relevant comparisons.

Minor comment 8

1. In Figure 3B-F, reductions in ECM density and ECM stiffness both decrease vessel length and growth speed. Both perturbations also reduce focal adhesion number, yet only ECM stiffness reduction decreases focal adhesion lifetime. The authors should clarify how these distinct focal adhesion phenotypes converge on a similar vascular outcome.

Authors’ response

We have clarified this point in the revised Results and Discussion. Both decreased stiffness and decreased fiber density reduce the total number of focal adhesions and slow vessel extension, but reduced stiffness produces a stronger reduction in focal-adhesion lifetime. We now interpret reduced density primarily as decreasing the availability of attachment sites, while reduced stiffness has a particularly strong effect on focal-adhesion stabilization. Although these perturbations influence focal-adhesion dynamics differently, both ultimately reduce efficient sprout extension.

Minor comment 9

1. In Figure 5F, the control group should be presented first (leftmost position) for consistency with the other panels.

Authors’ response

The control group is now presented in the leftmost position in the corresponding revised figure panel.

Minor comment 10

1. In Figure 5C (lower panels), image orientation should be standardized such that anterior is positioned on the left side.

Authors’ response

Image orientation was standardized. Embryo and trunk images are now consistently presented with anterior to the left and dorsal up, and this orientation is specified in the figure legends.

Minor comment 11

1. In Figure 6A, fn1a and fn1b mRNA overexpression appear to exert different effects on ISV volume. Specifically, fn1a overexpression increases ISV volume relative to control, whereas fn1b overexpression appears to decrease it. The authors should discuss the basis for these differing effects.

Authors’ response

We agree that the original presentation encouraged comparisons between experiments that had been performed independently. The fn1a and fn1b rescue series were carried out as separate experiments in different endothelial reporter backgrounds and are now analyzed and interpreted independently.

Because these rescue experiments were performed independently and in different endothelial reporter backgrounds, we do not interpret differences between the fn1a and fn1b mRNA-only groups as evidence of distinct biological effects of the two fibronectin paralogs. The revised analysis therefore evaluates each mRNA condition against its corresponding experimental control, rather than making direct comparisons across the two rescue series.

Minor comment 13

1. The phenotypic severity of MO L14Fa and MO L14Fb appears inconsistent between Figures 5 and 6. In Fig. 5B, ISV volume of MO L14Fb is bigger than MO L14Fa while in Fig. 6A, ISV volume of MO L14Fb is smaller than MO L14Fa. In Fig. 5C, aberrant ISV number in MO L14Fb is significantly smaller than MO L14Fa while in Fig. 6A, they are comparable. The authors should clarify whether these experiments were performed independently and explain the source of these discrepancies.

Authors’ response

We agree that the original presentation encouraged comparisons between experiments that had been performed independently. The fn1a and fn1b rescue series were carried out as separate experiments in different endothelial reporter backgrounds and are now analyzed and interpreted independently.

The revised manuscript therefore does not use the relative severity of MO L14Fa versus MO L14Fb across these independent rescue experiments as a biological comparison. Instead, rescue is assessed within each matched experimental series.

Moreover, the original manuscript had figure 5C with an absolute number of aberrant ISVs whereas figure 6A had it as a percentage of aberrant ISVs. Now we show all aberrant ISVs as a percentage of the total ISVs analyzed.

Significance assessment — Nature and significance of the advance

This work represents a primarily conceptual advance in the field of angiogenesis by proposing a mechanism through which ECM mechanical properties and semaphorin-mediated repulsive signaling cooperate to guide vessel growth and patterning. The integration of computational modeling with in vivo experiments is a notable strength and has the potential to provide new insights into how multiple environmental cues are combined to regulate angiogenic behavior.

The study builds upon a substantial body of work demonstrating that ECM composition and mechanics influence endothelial migration and sprouting, as well as studies showing that semaphorin signaling restricts aberrant vessel branching and fusion during zebrafish vascular development. The novelty of the present work lies in its attempt to unify these mechanisms within a single theoretical and experimental framework. However, the extent to which the experimental data support a direct role for laminin and fibronectin in vessel patterning, as opposed to indirect effects arising from disrupted somite and notochord development, remains an important question that should be addressed before the proposed mechanism can be fully established.

Significance assessment — Audience

The findings are likely to be of interest to researchers working in vascular biology, developmental biology, angiogenesis, collective cell migration, extracellular matrix biology, mechanobiology, and computational modeling of morphogenesis.

Reviewer expertise

My expertise includes vascular development, sprouting angiogenesis, endothelial cell biology, mechanobiology and zebrafish models of vascular development.

I am comfortable evaluating the developmental biology, vascular phenotyping, endothelial cell biology, and interpretation of the zebrafish experiments. While I can assess the biological assumptions and interpretation of the computational framework, I do not have specialized expertise in mathematical modeling and therefore cannot fully evaluate the technical implementation, parameterization, or numerical aspects of the model.

REVIEWER 2

Summary and general assessment

This manuscript combines zebrafish genetics, live imaging, rescue experiments, and mathematical modeling to investigate the roles of laminin and fibronectin during intersegmental vessel (ISV) development. The integration of experimental and computational approaches is a strength of the study, and the manuscript presents potentially interesting findings suggesting that extracellular matrix (ECM) components, including laminin and fibronectin, cooperatively contribute to ISV growth and guidance. However, the current experimental evidence lacks sufficient rigor to convincingly support this conclusion and does not provide adequate support for the broader mechanistic and conceptual framework of ECM-guided self-organization proposed by the authors.

Overall, the observations presented in this manuscript may be of potential interest to the vascular biology field, but the manuscript requires substantial improvements in its presentation, conceptual framework, mechanistic evidence, and experimental rigor to support its main conclusions.

My major concerns regarding these points are outlined below. In its current form, the manuscript reads more like a dissertation chapter than a primary research article, with the excessively long Introduction and the Results section containing extensive methodological descriptions and discussions that obscure the main experimental findings. More importantly, while the experimental observations suggest a role for laminin and fibronectin during ISV development, the proposed mechanistic and conceptual framework of "ECM-guided self-organization" is neither sufficiently defined nor experimentally supported. Finally, several aspects of the experimental design require additional rigor, including developmental stage normalization, independent validation of morpholino-mediated phenotypes, and more careful interpretation of the observed vascular defects. Addressing these concerns would substantially improve both the clarity and scientific impact of the manuscript.

Major comments

Comment 1

1. The manuscript would benefit from substantial reorganization from its current dissertation-style structure into the format of a primary research article.

The manuscript appears to retain much of the organization and level of detail expected for a dissertation chapter rather than being revised into the concise format of a primary research article. A major reorganization is needed to substantially improve the scientific presentation of the study. The Introduction is considerably longer than necessary and contains an extensive literature review before introducing the specific biological question. Likewise, the Results frequently include lengthy methodological descriptions, literature comparisons, and biological interpretation, making it difficult to distinguish the main experimental findings from the discussion. Streamlining the Introduction, moving methodological details to the Methods or Supplementary Information where appropriate, reducing repetitive discussion throughout the Results, and presenting the experiments in a more concise and sequential manner would greatly improve the readability of the manuscript and allow readers to more readily appreciate its principal scientific findings.

Authors’ response

We agree and have substantially reorganized the manuscript.

The Introduction has been shortened and rewritten around a more focused progression: the relationship between angiogenic sprouting and endothelial network-forming behavior; the conceptual role of local endothelial interactions; ISV development as the experimental system; known Semaphorin and ECM guidance mechanisms; the specific laminin/fibronectin hypothesis; and the principal experimental strategy.

Extensive methodological information has been moved from the Results to the Materials and Methods, and literature discussion and interpretation have been reduced within individual Results sections. The Results now follow the experimental sequence more directly.

We believe this substantially improves the distinction between experimental findings, methodological details, and broader biological interpretation.

Comment 2

1. The central concept of "ECM-guided self-organization" is not clearly defined, and its conceptual advance is currently difficult to appreciate.

One of my primary concerns is the conceptual framework proposed throughout the manuscript. The term "self-organization" is never clearly defined, making it difficult to understand precisely what biological mechanism the authors intend to describe. Although the Introduction discusses endothelial morphogenesis as a process involving both endothelial cell-intrinsic programs and tissue-derived extrinsic regulatory mechanisms, it subsequently introduces the concept of "ECM-guided self-organization" without clearly explaining how this framework differs from existing models of angiogenic sprouting or endothelial morphogenesis.

This ambiguity is particularly important because endothelial sprouting is generally understood to result from integration of endothelial cell-intrinsic programs together with tissue-derived extrinsic mechanisms, including extracellular matrix components, angiogenic factors, and guidance cues. Indeed, the Introduction itself acknowledges this principle. Consequently, it remains unclear to me how the proposed model of "ECM-guided self-organization" differs conceptually from the current understanding of endothelial morphogenesis or whether it establishes a fundamentally new biological principle.

More broadly, the conceptual advance of the study remains difficult to appreciate. The importance of extracellular matrix components during endothelial migration, angiogenesis, and vascular morphogenesis is already well established. The present work aims to provide additional evidence that laminin and fibronectin contribute to ISV sprouting and patterning, but it is difficult to identify what new mechanistic or conceptual insight is established beyond the recognized roles of the extracellular matrix. A clearer definition of "self-organization" and a more explicit explanation of how the proposed model advances beyond existing concepts would greatly strengthen the manuscript and help readers better appreciate its conceptual contribution.

Authors’ response

We agree that the term 'guided self-organization' was insufficiently defined in the original manuscript.

The revised Introduction now distinguishes angiogenesis from vasculogenesis while noting that both involve a shared repertoire of dynamic endothelial interactions. We use “self-organization” to refer to the capacity of endothelial collectives to generate organized multicellular arrangements through local interactions between endothelial cells, without implying that angiogenesis and vasculogenesis are identical developmental processes.

The revised Introduction further explains that mathematical models based on local endothelial interactions can generate both network-like organization and sprouting depending on initial configuration and environmental constraints.

Within this framework, we define “guided self-organization” as a situation in which spatially patterned environmental cues channel endothelial network-forming and migratory behavior toward reproducible trajectories.

We have deliberately moderated the broader conceptual claim. Rather than arguing that angiogenesis and vasculogenesis represent the same biological process, the revised manuscript proposes that they may draw on overlapping endothelial self-organizing mechanisms whose outcomes depend on initial tissue configuration and environmental constraints. The conceptual contribution of our study is therefore not the identification of ECM regulation as a new mechanism in angiogenesis, but the integration of endothelial self-organizing behavior, mechanical cell–ECM interactions, and spatially patterned repulsive guidance within a common framework. This allows us to investigate, in the simulations, how changes in environmental constraints can shift endothelial behavior between directed sprouting and network-like organization. We prefer to retain the phrase “guided self-organization” in the title because the concept is now explicitly defined and constitutes the central framework tested by the combined experimental and modeling work.

Comment 3

1. The experimental evidence does not sufficiently support the proposed mechanistic model.

The current loss-of-function experiments, which primarily rely on morpholino-mediated knockdown, present potentially interesting observations suggesting that laminin and fibronectin contribute to ISV sprouting and vascular patterning. However, the mechanistic conclusions extend considerably beyond what is directly supported by the presented data, resulting in overinterpretation of the experimental findings.

For example, the manuscript does not determine the cellular source of the relevant ECM components during ISV development, whether endothelial cells directly respond to these matrices through specific receptor-mediated mechanisms, or whether the observed vascular phenotypes arise indirectly through disruption of surrounding tissues or altered presentation of established angiogenic and guidance molecules such as Vegfa or Semaphorins. Consequently, the current data do not distinguish among several possible mechanisms by which laminin and fibronectin may influence vascular morphogenesis.

Likewise, the manuscript does not investigate how laminin and fibronectin may interact with established endothelial guidance pathways. Developmental mechanisms governing ISV sprouting have been extensively investigated, and similar endothelial migration and misguidance phenotypes have been reported. The present study reports abnormal ISV defects in embryos that also exhibit broader tissue disorganization, making it difficult to determine whether the vascular phenotype represents a primary endothelial guidance defect or is secondary to disruption of tissue architecture. Additional analyses of somite organization and potential interactions with established endothelial guidance pathways would substantially strengthen the mechanistic conclusions.

Authors’ response

We agree that the original manuscript extended some mechanistic interpretations beyond what was directly demonstrated.

The revised manuscript now clearly separates experimentally supported conclusions from mechanistic hypotheses generated by the model.

Several additional analyses were incorporated:

1. Genetic fn1a and fn1b mutant backgrounds were combined with laminin depletion to provide orthogonal support for the laminin-fibronectin interaction.

2. Chimeric fibronectin mRNA rescue was used to test specificity of the fibronectin component.

3. Whole-embryo morphology was added to evaluate gross developmental and trunk abnormalities.

4. sema3aa and sema3ab were examined by whole-mount HCR and RT-qPCR.

5. The contrasting phenotypes of MO L14Fa and MO L14Fb were used to distinguish severe gross trunk disruption from vascular disorganization.

We have also added a dedicated Discussion of the possible cellular sources of the ECM. We explicitly state that the reporter lines show where laminin and fibronectin proteins accumulate but do not identify the cells responsible for depositing the matrix encountered by extending ISVs.

Likewise, we do not claim to have identified the relevant endothelial ECM receptors or to have directly demonstrated changes in VEGF, Dll4/Notch, or other candidate guidance pathways. These are now presented as potential mechanisms and limitations rather than established conclusions.

Comment 4

1. Several aspects of the experimental design require additional rigor.

Given the broad developmental functions of laminin and fibronectin, embryonic developmental delay represents an important potential contributing factor when interpreting the observed, impeded growth of ISV sprouting. The manuscript reports these phenotypes at defined time points (e.g., 22-28 hpf and 2 dpf), but it does not clearly describe how developmental stage was determined and normalized prior to quantitative comparisons. This issue is particularly important because ISV sprouting progresses rapidly during this developmental period, and even modest differences in developmental stage could substantially influence measurements of sprout extension, migration, and vascular patterning. Additional staging based on established developmental landmarks (e.g., somite number or comparable morphological criteria) would substantially strengthen the interpretation of the reported vascular phenotypes. Furthermore, because these analyses were performed during early embryogenesis, reporting developmental timing using precise hours post-fertilization (hpf), together with appropriate developmental staging criteria, would be more informative than referring broadly to embryos as "2 dpf."

Additionally, because the study depends primarily on morpholino-mediated knockdown, potential morpholino off-target effects and/or nonspecific toxicity should be more carefully considered. Although the manuscript describes the utilization of a Cas13d strategy, this approach ultimately does not provide independent validation of the vascular phenotypes. Independent confirmation using complementary genetic approaches (e.g., CRISPR-Cas9-mediated gene disruption) or other orthogonal perturbation methods, such as pharmacological inhibition or analysis of relevant receptor-mediated signaling pathways, would substantially increase confidence in the reported conclusions.

Together, rigorous developmental stage matching, careful evaluation of neighboring tissue organization, and independent validation using complementary experimental approaches would substantially enhance the scientific rigor of the findings presented in this study.

Authors’ response

We agree that developmental staging is particularly important during the rapid period of primary ISV sprouting.

In the revised analysis, developmental age for quantitative experiments is reported in hours post-fertilization rather than broadly as “2 dpf.” For the 22–28 hpf time-lapse experiments, we additionally selected vessels according to their stage of sprout development: only ISVs that had recently initiated dorsal extension at the beginning of imaging were analyzed, and ISVs that had already undergone substantial elongation were excluded. The same selection criteria were applied to all experimental groups.

This approach allowed us to compare vessels at a comparable stage of sprout development rather than relying exclusively on anatomical position or embryo size. Although this approach improves comparability at the level of individual sprout development, it does not fully exclude differences in overall embryonic developmental progression.

We nevertheless acknowledge in the revised Discussion that broader developmental effects of laminin and fibronectin perturbation may still influence sprout dynamics.

To strengthen independent validation of the morpholino phenotypes, we combined MO L14 with genetic loss of fn1a or fn1b. Both mutant backgrounds showed strongly increased vascular mispatterning following laminin depletion. Together with the independent fibronectin mRNA rescue experiments, these experiments substantially reduce reliance on fibronectin morpholino phenotypes alone.

We explicitly acknowledge that the laminin component remains morpholino-based and therefore describe this as partial rather than fully genetic validation.

Comment 5

1. Interpretation of the vascular phenotypes and mathematical modeling should be reconsidered.

The manuscript repeatedly refers to abnormal vascular patterning as "ISV fusion." However, similar vascular phenotypes have been extensively characterized as ISV misguidance or ectopic ISV sprouting following disruptions of several endothelial guidance or inhibitory pathways. Unless the authors provide evidence that the observed phenotype represents a biologically distinct vascular fusion process, the use of established terminology would help avoid confusion in the field.

Likewise, although the mathematical modeling represents a valuable component of the study, it simplifies many aspects of ISV morphogenesis, including endothelial cell behaviors, tissue architecture, extracellular matrix organization, and multiple signaling pathways that regulate vascular sprouting. Given the limited experimental evidence supporting the proposed mechanistic model, it remains difficult to determine how faithfully the computational model reflects the underlying biological processes occurring during zebrafish vascular development. The computational simulations may generate hypotheses and provide possible explanations for the observed phenotypes. However, the modeling alone cannot establish or validate the proposed in vivo mechanisms. The authors should therefore clearly distinguish experimentally supported conclusions from the hypotheses and predictions generated by computational modeling and avoid drawing mechanistic conclusions that are insufficiently supported by the in vivo experimental data.

Authors’ response

We agree with both aspects of this comment.

The terminology has been revised throughout the manuscript. Morphological abnormalities are now classified as ectopic branching, loss of the normal dorsoventral trajectory, or abnormal lateral/inter-ISV connections. The term “fusion” is reserved for events in which vessel joining is directly demonstrated by time-lapse imaging.

We added a time-lapse sequence (Supplementary Video 4) showing two initially distinct ISVs extending along abnormal trajectories and subsequently establishing a direct lateral connection. This event is described as direct evidence of an ISV fusion event, whereas similar static phenotypes are not automatically interpreted as fusion.

We have also revised the presentation of the computational model. The manuscript now explicitly states that ECM stiffness, attachment-site density, and Semaphorin gradients were not directly measured in the morphants. The stiffness- and density-reduction simulations are therefore presented as mechanistic hypotheses rather than literal representations of the knockdown conditions.

The Discussion further emphasizes that the model is deliberately simplified and should be interpreted as a framework for exploring possible mechanisms rather than as a direct molecular representation of laminin and fibronectin organization in vivo.

Minor comments

Minor comment 1

1. Please include whole-embryo brightfield images from the laminin and fibronectin loss-of-function experiments to demonstrate overall embryonic morphology. These images would allow readers to assess potential gross morphological defects and developmental delays that may contribute to the observed vascular phenotypes.

Authors’ response

Added as a new supplementary figure (Supplementary Figure 5). These images document gross morphology and developmental differences among the principal combined ECM perturbation conditions independently of endothelial fluorescence.

Minor comment 2

1. The transgenic reporter signals from Tg(lama1:lama1-GFP), Tg(fn1a:fn1a-mNeonGreen),

and Tg(fn1b:fn1b-mCherry) lines do not identify the cellular sources of these ECM components. To understand the cellular mechanisms underlying ECM-mediated regulation of vascular development, additional histological analyses (e.g., HCR, RNAscope, or characterization using BAC transgenic or knock-in reporter lines) would be valuable. In addition, please include lower-magnification, whole-embryo fluorescent images of these transgenic lines to better understand the overall distribution patterns of these ECM components.

Authors’ response

We agree that the reporter lines identify protein localization rather than cellular origin. The revised Discussion now explicitly states this limitation and summarizes available evidence for expression of lama1, lama4, fn1a, and fn1b in surrounding trunk tissues.

We additionally included lower-magnification, whole-embryo fluorescent images of the ECM reporter lines (Supplementary Figure S6 to provide broader spatial context. These images are intended as qualitative spatial-localization data and are not used for quantitative comparison of reporter abundance across lines.

Minor comment 3

1. Better characterize somite organization using an established somite marker to distinguish direct endothelial guidance defects from secondary tissue disorganization.

Authors’ response

We agree that a dedicated molecular somite marker would provide additional information. We did not add a separate molecular somite-marker experiment in the present revision.

Instead, we addressed the underlying concern using several complementary approaches: whole-embryo bright-field imaging, comparison of MO L14Fa and MO L14Fb, HCR analysis of the spatial expression of the established ISV guidance genes sema3aa and sema3ab, quantitative RT-qPCR of the same genes, genetic fibronectin validation, and mRNA rescue.

These data show that MO L14Fa has more pronounced trunk disruption, whereas MO L14Fb retains comparatively preserved gross segmental morphology despite clear vascular disorganization. We therefore no longer use gross morphology to infer normal molecular somite patterning. The revised text explicitly states that molecular somite patterning was not assessed, and the absence of a dedicated molecular analysis of somite organization is acknowledged as a limitation. Accordingly, our conclusion has been narrowed from a direct endothelial mechanism to the more conservative interpretation that gross trunk disorganization may exacerbate the vascular phenotype, but vascular abnormalities are also observed in embryos with comparatively preserved gross segmental morphology.

Minor comment 4

1. Refine the text throughout the manuscript after its reorganization, as it currently contains numerous typos, redundant statements, and awkward or unclear sentence constructions.

Authors’ response

The manuscript has been extensively edited and reorganized throughout. Redundant material has been removed, terminology has been standardized, and multiple sentences and figure legends have been rewritten for clarity.

Minor comment 5

1. Revise the manuscript title, particularly the phrase "Endothelial Self-Organization", as appropriate following manuscript revision.

Authors’ response

We carefully reconsidered the title in light of this comment. We have retained “Endothelial Self-Organization” because the revised Introduction now explicitly defines what we mean by self-organization and distinguishes this concept from the broader developmental distinction between angiogenesis and vasculogenesis.

The revised manuscript uses this term specifically to describe endothelial collective behaviors arising from local cell interactions whose resulting geometry is constrained by environmental cues. We believe that, with this clarification and the more cautious framing introduced throughout the manuscript, the current title accurately reflects the central question addressed by the combined experimental and mathematical work.

Significance assessment

General assessment: The manuscript investigates the roles of laminin and fibronectin during zebrafish intersegmental vessel development using morpholino-mediated gene knockdown, live imaging, and computational modeling. The integration of experimental and computational approaches is a strength of the study, and the work presents potentially interesting observations regarding extracellular matrix regulation of vascular morphogenesis. However, substantial improvements in manuscript organization, experimental rigor, and mechanistic validation are needed before the proposed conclusions can be fully justified.

Advance: The conceptual and mechanistic advances remain limited in the current form. Developmental mechanisms governing ISV sprouting have been extensively investigated, and essential roles of extracellular matrix components, endothelial guidance pathways, and tissue-derived regulatory cues in vascular morphogenesis are already well established in the vascular biology field. While the present study suggests that laminin and fibronectin cooperatively contribute to ISV development, the current evidence does not clearly establish a mechanism that distinguishes these findings from existing models or demonstrates a clearly new biological principle. Even if the proposed model were further validated, the conceptual advance beyond the current understanding of ISV development would likely remain modest unless clearer mechanistic insights or previously unrecognized regulatory mechanisms are established.

Audience: The study will be primarily of interest to researchers in vascular biology, angiogenesis, extracellular matrix biology, and zebrafish developmental genetics. In its current form, the mechanistic and conceptual advances appear limited, making broader interest outside these specialized research communities less likely.

Field of expertise

Field of expertise: Developmental vascular biology, zebrafish genetics, live imaging.

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

Summary:

This manuscript combines zebrafish genetics, live imaging, rescue experiments, and mathematical modeling to investigate the roles of laminin and fibronectin during intersegmental vessel (ISV) development. The integration of experimental and computational approaches is a strength of the study, and the manuscript presents potentially interesting findings suggesting that extracellular matrix (ECM) components, including laminin and fibronectin, cooperatively contribute to ISV growth and guidance. However, the current experimental evidence lacks sufficient rigor to convincingly support this conclusion and does not provide adequate support for the broader mechanistic and conceptual framework of ECM-guided self-organization proposed by the authors.

Overall, the observations presented in this manuscript may be of potential interest to the vascular biology field, but the manuscript requires substantial improvements in its presentation, conceptual framework, mechanistic evidence, and experimental rigor to support its main conclusions.

My major concerns regarding these points are outlined below. In its current form, the manuscript reads more like a dissertation chapter than a primary research article, with the excessively long Introduction and the Results section containing extensive methodological descriptions and discussions that obscure the main experimental findings. More importantly, while the experimental observations suggest a role for laminin and fibronectin during ISV development, the proposed mechanistic and conceptual framework of "ECM-guided self-organization" is neither sufficiently defined nor experimentally supported. Finally, several aspects of the experimental design require additional rigor, including developmental stage normalization, independent validation of morpholino-mediated phenotypes, and more careful interpretation of the observed vascular defects. Addressing these concerns would substantially improve both the clarity and scientific impact of the manuscript.

Major Comments

1. The manuscript would benefit from substantial reorganization from its current dissertation-style structure into the format of a primary research article.

The manuscript appears to retain much of the organization and level of detail expected for a dissertation chapter rather than being revised into the concise format of a primary research article. A major reorganization is needed to substantially improve the scientific presentation of the study. The Introduction is considerably longer than necessary and contains an extensive literature review before introducing the specific biological question. Likewise, the Results frequently include lengthy methodological descriptions, literature comparisons, and biological interpretation, making it difficult to distinguish the main experimental findings from the discussion. Streamlining the Introduction, moving methodological details to the Methods or Supplementary Information where appropriate, reducing repetitive discussion throughout the Results, and presenting the experiments in a more concise and sequential manner would greatly improve the readability of the manuscript and allow readers to more readily appreciate its principal scientific findings. 2. The central concept of "ECM-guided self-organization" is not clearly defined, and its conceptual advance is currently difficult to appreciate.

One of my primary concerns is the conceptual framework proposed throughout the manuscript. The term "self-organization" is never clearly defined, making it difficult to understand precisely what biological mechanism the authors intend to describe. Although the Introduction discusses endothelial morphogenesis as a process involving both endothelial cell-intrinsic programs and tissue-derived extrinsic regulatory mechanisms, it subsequently introduces the concept of "ECM-guided self-organization" without clearly explaining how this framework differs from existing models of angiogenic sprouting or endothelial morphogenesis.

This ambiguity is particularly important because endothelial sprouting is generally understood to result from integration of endothelial cell-intrinsic programs together with tissue-derived extrinsic mechanisms, including extracellular matrix components, angiogenic factors, and guidance cues. Indeed, the Introduction itself acknowledges this principle. Consequently, it remains unclear to me how the proposed model of "ECM-guided self-organization" differs conceptually from the current understanding of endothelial morphogenesis or whether it establishes a fundamentally new biological principle.

More broadly, the conceptual advance of the study remains difficult to appreciate. The importance of extracellular matrix components during endothelial migration, angiogenesis, and vascular morphogenesis is already well established. The present work aims to provide additional evidence that laminin and fibronectin contribute to ISV sprouting and patterning, but it is difficult to identify what new mechanistic or conceptual insight is established beyond the recognized roles of the extracellular matrix. A clearer definition of "self-organization" and a more explicit explanation of how the proposed model advances beyond existing concepts would greatly strengthen the manuscript and help readers better appreciate its conceptual contribution. 3. The experimental evidence does not sufficiently support the proposed mechanistic model.

The current loss-of-function experiments, which primarily rely on morpholino-mediated knockdown, present potentially interesting observations suggesting that laminin and fibronectin contribute to ISV sprouting and vascular patterning. However, the mechanistic conclusions extend considerably beyond what is directly supported by the presented data, resulting in overinterpretation of the experimental findings.

For example, the manuscript does not determine the cellular source of the relevant ECM components during ISV development, whether endothelial cells directly respond to these matrices through specific receptor-mediated mechanisms, or whether the observed vascular phenotypes arise indirectly through disruption of surrounding tissues or altered presentation of established angiogenic and guidance molecules such as Vegfa or Semaphorins. Consequently, the current data do not distinguish among several possible mechanisms by which laminin and fibronectin may influence vascular morphogenesis.

Likewise, the manuscript does not investigate how laminin and fibronectin may interact with established endothelial guidance pathways. Developmental mechanisms governing ISV sprouting have been extensively investigated, and similar endothelial migration and misguidance phenotypes have been reported. The present study reports abnormal ISV defects in embryos that also exhibit broader tissue disorganization, making it difficult to determine whether the vascular phenotype represents a primary endothelial guidance defect or is secondary to disruption of tissue architecture. Additional analyses of somite organization and potential interactions with established endothelial guidance pathways would substantially strengthen the mechanistic conclusions. 4. Several aspects of the experimental design require additional rigor.

Given the broad developmental functions of laminin and fibronectin, embryonic developmental delay represents an important potential contributing factor when interpreting the observed, impeded growth of ISV sprouting. The manuscript reports these phenotypes at defined time points (e.g., 22-28 hpf and 2 dpf), but it does not clearly describe how developmental stage was determined and normalized prior to quantitative comparisons. This issue is particularly important because ISV sprouting progresses rapidly during this developmental period, and even modest differences in developmental stage could substantially influence measurements of sprout extension, migration, and vascular patterning. Additional staging based on established developmental landmarks (e.g., somite number or comparable morphological criteria) would substantially strengthen the interpretation of the reported vascular phenotypes. Furthermore, because these analyses were performed during early embryogenesis, reporting developmental timing using precise hours post-fertilization (hpf), together with appropriate developmental staging criteria, would be more informative than referring broadly to embryos as "2 dpf."

Additionally, because the study depends primarily on morpholino-mediated knockdown, potential morpholino off-target effects and/or nonspecific toxicity should be more carefully considered. Although the manuscript describes the utilization of a Cas13d strategy, this approach ultimately does not provide independent validation of the vascular phenotypes. Independent confirmation using complementary genetic approaches (e.g., CRISPR-Cas9-mediated gene disruption) or other orthogonal perturbation methods, such as pharmacological inhibition or analysis of relevant receptor-mediated signaling pathways, would substantially increase confidence in the reported conclusions.

Together, rigorous developmental stage matching, careful evaluation of neighboring tissue organization, and independent validation using complementary experimental approaches would substantially enhance the scientific rigor of the findings presented in this study. 5. Interpretation of the vascular phenotypes and mathematical modeling should be reconsidered.

The manuscript repeatedly refers to abnormal vascular patterning as "ISV fusion." However, similar vascular phenotypes have been extensively characterized as ISV misguidance or ectopic ISV sprouting following disruptions of several endothelial guidance or inhibitory pathways. Unless the authors provide evidence that the observed phenotype represents a biologically distinct vascular fusion process, the use of established terminology would help avoid confusion in the field.

Likewise, although the mathematical modeling represents a valuable component of the study, it simplifies many aspects of ISV morphogenesis, including endothelial cell behaviors, tissue architecture, extracellular matrix organization, and multiple signaling pathways that regulate vascular sprouting. Given the limited experimental evidence supporting the proposed mechanistic model, it remains difficult to determine how faithfully the computational model reflects the underlying biological processes occurring during zebrafish vascular development. The computational simulations may generate hypotheses and provide possible explanations for the observed phenotypes. However, the modeling alone cannot establish or validate the proposed in vivo mechanisms. The authors should therefore clearly distinguish experimentally supported conclusions from the hypotheses and predictions generated by computational modeling and avoid drawing mechanistic conclusions that are insufficiently supported by the in vivo experimental data.

Minor Comments

1. Please include whole-embryo brightfield images from the laminin and fibronectin loss-of-function experiments to demonstrate overall embryonic morphology. These images would allow readers to assess potential gross morphological defects and developmental delays that may contribute to the observed vascular phenotypes.
2. The transgenic reporter signals from Tg(lama1:lama1-GFP), Tg(fn1a:fn1a-mNeonGreen), and Tg(fn1b:fn1b-mCherry) lines do not identify the cellular sources of these ECM components. To understand the cellular mechanisms underlying ECM-mediated regulation of vascular development, additional histological analyses (e.g., HCR, RNAscope, or characterization using BAC transgenic or knock-in reporter lines) would be valuable. In addition, please include lower-magnification, whole-embryo fluorescent images of these transgenic lines to better understand the overall distribution patterns of these ECM components.
3. Better characterize somite organization using an established somite marker to distinguish direct endothelial guidance defects from secondary tissue disorganization.
4. Refine the text throughout the manuscript after its reorganization, as it currently contains numerous typos, redundant statements, and awkward or unclear sentence constructions.
5. Revise the manuscript title, particularly the phrase "Endothelial Self-Organization", as appropriate following manuscript revision.

Significance

General assessment: The manuscript investigates the roles of laminin and fibronectin during zebrafish intersegmental vessel development using morpholino-mediated gene knockdown, live imaging, and computational modeling. The integration of experimental and computational approaches is a strength of the study, and the work presents potentially interesting observations regarding extracellular matrix regulation of vascular morphogenesis. However, substantial improvements in manuscript organization, experimental rigor, and mechanistic validation are needed before the proposed conclusions can be fully justified.

Advance: The conceptual and mechanistic advances remain limited in the current form. Developmental mechanisms governing ISV sprouting have been extensively investigated, and essential roles of extracellular matrix components, endothelial guidance pathways, and tissue-derived regulatory cues in vascular morphogenesis are already well established in the vascular biology field. While the present study suggests that laminin and fibronectin cooperatively contribute to ISV development, the current evidence does not clearly establish a mechanism that distinguishes these findings from existing models or demonstrates a clearly new biological principle. Even if the proposed model were further validated, the conceptual advance beyond the current understanding of ISV development would likely remain modest unless clearer mechanistic insights or previously unrecognized regulatory mechanisms are established.

Audience: The study will be primarily of interest to researchers in vascular biology, angiogenesis, extracellular matrix biology, and zebrafish developmental genetics. In its current form, the mechanistic and conceptual advances appear limited, making broader interest outside these specialized research communities less likely.

Field of expertise: Developmental vascular biology, zebrafish genetics, live imaging.

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 investigate how extracellular matrix (ECM) properties and repulsive guidance cues cooperate to regulate vessel growth and patterning during angiogenesis. To address this question, they develop a mathematical framework that integrates endothelial cell network formation, ECM mechanics, and semaphorin-mediated repulsive signaling. Their simulations predict that reductions in ECM stiffness or density impair vessel extension, while reductions in either ECM density or semaphorin gradient distribution promote vessel fusion, suggesting that ECM properties and semaphorin signaling act together to guide vascular sprouts and maintain vessel patterning. The authors then test these predictions experimentally using zebrafish intersegmental vessels (ISVs) as an in vivo model of sprouting angiogenesis. Through morpholino-mediated depletion of laminin 1, laminin 4, fibronectin 1a, and fibronectin 1b, alone and in combination, they examine the consequences of ECM disruption on ISV growth and organization. They report defects in vessel extension and patterning, including increased ectopic vessel fusion, and conclude that laminin- and fibronectin-dependent ECM organization is required for proper ISV migration, growth, and patterning. The study combines computational modeling with experimental analysis to address an important question in vascular development and provides a potentially valuable framework for understanding how mechanical and guidance cues are integrated during angiogenic sprouting.

Major Comments

1. The evidence does not convincingly demonstrate that laminin/fibronectin directly regulate ISV patterning The authors developed a mathematical model incorporating endothelial cell network formation, ECM mechanics, and semaphorin-mediated repulsive signaling. The simulations predict that reduced ECM stiffness or density slows vessel growth, whereas reduction of either ECM density or the semaphorin gradient promotes vessel fusion, suggesting that ECM properties and semaphorin signaling cooperate to guide vessel trajectories. The experimental data, however, do not convincingly establish that the observed ISV patterning defects are a direct consequence of laminin/fibronectin loss. As acknowledged by the authors, combined depletion of laminin and fibronectin severely disrupts somite and notochord morphogenesis. Given the well-established role of somites and semaphorin-mediated repulsive signaling in restricting ISV growth and preventing ectopic branching or fusion, it remains unclear whether the vascular phenotypes arise from direct endothelial-ECM defects or indirectly from altered trunk patterning. The authors argue that ISV disorganization is still observed in embryos with comparatively preserved somite morphology (e.g., MO L14Fb). However, the assessment of somite preservation is based on relatively low-magnification images, and it is unclear whether molecular patterning within the somites remains intact. In particular, the manuscript does not address whether semaphorin expression or distribution is altered in MO L14Fa, MO L14Fb, or the corresponding rescue conditions. This is an important omission because semaphorin gradients are explicitly incorporated into the mathematical model and are predicted to strongly influence vessel guidance by preventing ectopic vessel fusion. Therefore, to support the conclusion that laminin/fibronectin directly regulate ISV patterning, it would be important to determine whether semaphorin expression and/or distribution are preserved following laminin/fibronectin depletion. Without such data, the possibility remains that the vascular mispatterning phenotype is secondary to defects in somite and notochord development. Furthermore, previous studies disrupting endothelial-ECM adhesion have generally reported defects in ISV growth and elongation without accompanying vessel mispatterning:
   • Talin1-deficient zebrafish (tln1 uqal−/−) exhibit impaired ISV growth and an increased frequency of disconnected ISVs but do not display ectopic branching or aberrant vessel patterning (Chau et al., 2022; doi:10.1242/dev.200454).
   • A second talin1 mutant (fl02k) similarly shows defects in vascular development without ISV mispatterning (Wu et al., 2015; doi:10.1096/fj.15-273409).
   • Loss of integrin β1b results in impaired ISV elongation but does not disrupt ISV patterning (Iida et al., 2018; doi:10.1111/gtc.1264). These studies suggest that impaired endothelial-ECM interactions alone are insufficient to produce the extensive ISV fusion and mispatterning observed here, raising the possibility that secondary defects in trunk tissue organization contribute substantially to the phenotype.
2. Quantification of ISV growth using "ISV volume" requires further justification The authors estimate average ISV volume by dividing the total segmented trunk vascular volume by the number of ISVs. This metric raises several concerns. First, the segmented vascular volume appears to include non-ISV structures such as the dorsal longitudinal anastomotic vessel (DLAV). Consequently, the calculated parameter does not exclusively represent ISV volume and may not accurately reflect ISV growth. Second, several morpholino conditions (e.g., MO Fn1ab, MO L14, MO lama1/4 fn1a, and MO lama1/4 fn1b) exhibit pronounced developmental delay and shortened trunk length. Under these conditions, reduced vascular volume may simply reflect overall embryonic growth retardation rather than a specific defect in ISV growth. Therefore, it is difficult to distinguish primary vascular phenotypes from secondary consequences of reduced embryo size. Finally, ISV growth is normalized to the dorsal-ventral axis length. Because overall embryonic dimensions are reduced in several experimental groups, this normalization may partially mask genuine ISV growth defects. The authors should therefore provide additional justification for this metric and discuss its limitations. Direct measurements of ISV length may provide more robust assessments of ISV growth.

Minor Comments

1. When describing tip-cell filopodia and lamellipodia dynamics in ISVs, the authors should cite Phng et al., 2013 (doi:10.1242/dev.097352).
2. Page 3 contains a "?" in place of a reference citation.
3. Transgenic line nomenclature should be italicized throughout the manuscript.
4. mRNA transcript names should be italicized throughout the manuscript.
5. Figure 1E is presented at insufficient magnification to evaluate ISV morphology and patterning. Higher-magnification images similar to those shown in Figures 5 and 6 would be helpful.
6. Figure 3 legend refers to a fourth simulation condition ("reduction of both fiber stiffness and fiber density"), but this condition is not shown in the figure. This statement should be removed unless the corresponding data are presented.
7. Statistical comparisons should be provided for Figure 3C-F.
8. In Figure 3B-F, reductions in ECM density and ECM stiffness both decrease vessel length and growth speed. Both perturbations also reduce focal adhesion number, yet only ECM stiffness reduction decreases focal adhesion lifetime. The authors should clarify how these distinct focal adhesion phenotypes converge on a similar vascular outcome.
9. In Figure 5F, the control group should be presented first (leftmost position) for consistency with the other panels.
10. In Figure 5C (lower panels), image orientation should be standardized such that anterior is positioned on the left side.
11. In Figure 6A, fn1a and fn1b mRNA overexpression appear to exert different effects on ISV volume. Specifically, fn1a overexpression increases ISV volume relative to control, whereas fn1b overexpression appears to decrease it. The authors should discuss the basis for these differing effects.
12. The phenotypic severity of MO L14Fa and MO L14Fb appears inconsistent between Figures 5 and 6. In Fig. 5B, ISV volume of MO L14Fb is bigger than MO L14Fa while in Fig. 6A, ISV volume of MO L14Fb is smaller than MO L14Fa. In Fig. 5C, aberrant ISV number in MO L14Fb is significantly smaller than MO L14Fa while in Fig. 6A, they are comparable. The authors should clarify whether these experiments were performed independently and explain the source of these discrepancies.

Significance

Nature and Significance of the Advance

This work represents a primarily conceptual advance in the field of angiogenesis by proposing a mechanism through which ECM mechanical properties and semaphorin-mediated repulsive signaling cooperate to guide vessel growth and patterning. The integration of computational modeling with in vivo experiments is a notable strength and has the potential to provide new insights into how multiple environmental cues are combined to regulate angiogenic behavior. The study builds upon a substantial body of work demonstrating that ECM composition and mechanics influence endothelial migration and sprouting, as well as studies showing that semaphorin signaling restricts aberrant vessel branching and fusion during zebrafish vascular development. The novelty of the present work lies in its attempt to unify these mechanisms within a single theoretical and experimental framework. However, the extent to which the experimental data support a direct role for laminin and fibronectin in vessel patterning, as opposed to indirect effects arising from disrupted somite and notochord development, remains an important question that should be addressed before the proposed mechanism can be fully established.

The findings are likely to be of interest to researchers working in vascular biology, developmental biology, angiogenesis, collective cell migration, extracellular matrix biology, mechanobiology, and computational modeling of morphogenesis.

Reviewer Expertise

My expertise includes vascular development, sprouting angiogenesis, endothelial cell biology, mechanobiology and zebrafish models of vascular development.

I am comfortable evaluating the developmental biology, vascular phenotyping, endothelial cell biology, and interpretation of the zebrafish experiments. While I can assess the biological assumptions and interpretation of the computational framework, I do not have specialized expertise in mathematical modeling and therefore cannot fully evaluate the technical implementation, parameterization, or numerical aspects of the model.

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Reply to the reviewers

General Statements

We thank the reviewers for their constructive comments, which helped us improve the manuscript. We expanded the Discussion to describe the limitations of our approach and its relation to other approaches more clearly. We also added simulations on a toy model that compare GBA with enzyme-constrained FBA, RBA, and the kinetic framework COBRA-k (Supplementary Fig. S3). In addition, we clarified the figure captions and the description of the model calibration. Point-by-point responses are given below. The reviewers’ comments are shown in black, our responses in blue, and the new text in the manuscript in red.

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

Summary:

This manuscript deals with the application of Growth Balance Analysis (GBA) on suboptimal protein expression. Using detailed kinetic models of cellular growth, the authors explore the protein costs involved in several different contexts, such as nutrient availability, toxin removal, and idle proteins. They show convincingly that GBA is able to capture different trade-offs that are consistent with experimental data. The exposition is detailed, and easy to follow.

This is a well-written manuscript, and I enjoyed reading it. I don't have major points of discussion.

We thank the reviewer for carefully reading the manuscript and providing constructive comments which have helped us improve the manuscript. Below, we answer each comment individually.

Major comments: none.

Minor comments:

I was, I think, most surprised that there was no mention at all of the only other theory that is equivalent in scope to GBA: EGM theory (De Groot et al., PLoSCB 2020, https://doi.org/10.1371/journal.pcbi.1007559). Although different in its rationale (focusing on concentrations rather than mass fractions, leading to a quite different kind of optimisation problem), the level of cellular detail is quite comparable, and I think all the trade-offs found in this paper could be replicated with it. (There is a model with toxin removal in the paper, for example.) I don't want to advocate people to use EGMs over GBA. I think GBA is very useful indeed.

We thank the reviewer for pointing out this paper. EGMs could be used as a complementary approach to GBA to characterize the solution space of models with alternative pathways. We have added the following paragraph to the Introduction:

"An optimization of cellular states can also be formulated based on elementary growth modes (EGM), introduced by (De Groot et al., PLoS CB 2020, https://doi.org/10.1371/journal.pcbi.1007559) for kinetic models. A variant of EGMs has also been developed for linear cell models (Mueller et al. 2022)."

The concavity of the plots in Fig 1 are also relevant for the claim proved in

https://www.biorxiv.org/content/10.1101/2024.07.09.602663v1 . It is (still) not published, so you might not want to cite it. But in this manuscript there is a full proof of the fact that the map (proteins -> growth rate) is concave in EFMs/EGMs. Of course GBA makes this quantitative, which is a real bonus.

We thank the reviewer for pointing us to this preprint. We agree that it is relevant. Our results agree with the preprint's concavity result around the optimum (and for some enzymes for the whole range of proteome fractions). We added a paragraph to the Discussion that cites the preprint and explains where our results sometimes differ. The proof assumes that total protein is constant and that metabolite mass and metabolite dilution by growth are negligible. GBA does not make these assumptions – when metabolites accumulate, total protein decreases and the growth rate is no longer concave in some proteins. We added the following paragraph to the discussion:

"The concave dependence of growth rate on protein concentrations seen around the optimum in Fig. 2 agrees with a recent proof that growth rate is a concave function of enzyme concentrations in elementary flux modes (Planque et al. 2024). That proof assumes quasi steady state metabolism, a constant total protein concentration, and negligible metabolite mass and dilution by growth. GBA does not make these assumptions, so concavity does not hold for every protein in every condition. When metabolites accumulate, they take up part of the cellular density, and total protein decreases. The model therefore extends the concavity result to conditions where metabolite pools are not negligible."

It would be good, when starting the informal discussion of the base model, to refer where the full description is given. At the moment, I found it by clicking on the Eq.(13) link, which seemed to be the first time I was given a direct pointer. It would be good to refer to the Methods section (whose title I missed on the first two reads, as it starts with a table, so my eyes glanced over it).

We added the following text to the first section of the Results:

"Fig. 1 shows the mass fraction matrix of the base model. The full model description is given in the Methods section. It contains all constraints, kinetic rate laws, and parameter values (Tables 2 and 3)."

It is a bit confusing sometimes that both references and equation numbers are referred to with (number). Most of the time, equations are referenced using Eq. (number), but in the paragraph below eq.(12) there are a few instances where this does not happen. In that same sentence, (31) refers to a paper. I would also advice paragraphs to be indented (the main text will be formatted by the journal, but the Supporting Information would also be more readable, in my opinion).

We agree with the reviewer and now refer to all equations as Eq. (number) or Eqs. (numberX–numberY), as appropriate. We have also reformatted the main text and Supporting Information with indentation for the bioRxiv version. However, the formatting of the main text may differ depending on the journal template.

Reviewer #1 (Significance (Required)):

Significance:

Advance: the authors mention that they 'extend' GBA to these suboptimal (rather than optimal) growth states. I believe they just 'apply' GBA to these states. I don't think there is a conceptual difference between the old papers (10), (30), (31) and the new. Also the protein costs formula (eq. S1), which is the most insightful theoretical relation in this paper, is not new but from ref (31). The main advance lies in the fact that the authors were able to make well-parameterised core models of cells, and apply GBA to get quantitative results on trade-offs, etc. This has not been done before. This is definitely very useful and worth publishing.

We thank the reviewer for the assessment. We softened the wording in the Introduction.

Audience: experimental and theoretical systems biologists, microbial physiologists.

My expertise: I have worked on microbial physiology using mathematical modelling for about 10 - 15 years. I have done quite some work on elementary modes theory in cells, and am well acquainted with (nonlinear) optimisation approaches in systems biology.

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

Summary:

Constraint-based approaches like flux balance analysis (FBA) have proven useful for modeling microbial metabolism, but they assume a fixed, predefined biomass objective function. This, together with their general lack of enzyme kinetics and regulatory mechanisms, limits their ability to capture complex, non-linear dynamics. In this manuscript, Szeliova et al. build on their previous GBA framework to analyze suboptimal protein allocation that cannot be captured using FBA. They first develop a coarse-grained model comprising a stoichiometric layer and kinetic layer that fits E. coli experimental data. Applying GBA to this model, they interrogate the effect of suboptimal protein allocation along different scenarios of interest to microbial physiology but also to metabolic engineering (enzyme overproduction, optimality during utilization of a secondary carbon source). Overall, I found the manuscript clear and well-written, and the coarse-grained model a promising basis for further extension, although the conceptual novelty relative to the authors' previous work (doi: 10.1038/s41467-020-14751-w) is somewhat limited. Below, I note several minor inconsistencies and suggestions that could improve the manuscript prior to publication.

We thank the reviewer for carefully reading the manuscript and providing constructive comments which have helped us improve the manuscript. Below, we answer each comment individually.

Major comments:

The authors rightfully note in the introduction that many coarse-grained approaches incorporating protein allocation, and sometimes enzyme kinetics, already exist (e.g., doi: 10.1038/msb.2009.82, 10.1016/j.ymben.2015.10.003, 10.1371/journal.pcbi.1004913). While I believe that simpler models are already helpful for capturing much of cellular dynamics, I think it would be useful and interesting to compare the GBA framework against some of these other tools.

We thank the reviewer for the assessment. We added explicit comparisons with related approaches. (i) We compared GBA with enzyme-constrained FBA (with the transporter, amino acid synthesis and the ribosome treated as enzymes), the kinetic COBRA-k framework (https://doi.org/10.1126/sciadv.aeb3022) and RBA (as formulated in https://doi.org/10.1038/s42003-024-05815-4) on the toy model (new Fig. S3). RBA gives the same curves as enzyme-constrained FBA, because both use linear capacity constraints and a fixed biomass composition. (ii) We did not run CAFBA separately, because it also uses linear capacity constraints and is therefore a similar method to enzyme-constrained FBA and RBA. (iii) Molenaar et al. formulated balanced growth as a nonlinear optimization problem and implemented it as a few specific small models in GAMS. It is not a method that we could run on our models, so we discussed it in the Discussion and did not benchmark it.

We added the following text to the results section:

"We also compared GBA with RBA (as formulated in Szeliova et al. 2024), enzyme-constrained FBA, and the kinetic COBRA-k framework (Bekiaris & Klamt 2026) on this toy model (Supplementary Section “Comparison with other modeling approaches”). The linear methods give two straight segments with a sharp optimum, and the kinetic COBRA-k model reproduces the rounded shape of GBA around the optimum only partly."

We also added a new section to the supplementary material with a figure and a more detailed description of the comparison (please see supplementary material in the revised version), and a Jupyter notebook with all three analyses is available on GitHub (https://github.com/diana-sz/ProtCost) and archived on Zenodo (https://doi.org/10.5281/zenodo.19683354).

What are the limitations of GBA across the different case studies, and what does it capture that other models do not?

We thank the reviewer for this question. We added the main limitations of GBA to the section "Model limitations and future directions": the nonlinear optimization is harder than the linear optimization of enzyme-constrained models, many kinetic parameters are unknown, and, unlike for enzyme-constrained FBA models (GECKO, AutoPACMEN), there is no automatic way to build a GBA model from a genome-scale reconstruction. We added the following clarifications to the text:

"In addition, the nonlinear optimization of GBA models is much harder than the linear optimization of enzyme-constrained models: the solution depends on the initial values, and the solver can fail for initial values far from the optimum (see Methods). Computational improvements, including better initialization strategies, convex approximations, and parallelization, will be important for extending nonlinear growth-cost analyses toward larger-scale models."

"A further limitation is that, unlike for enzyme-constrained models, for which tools such as GECKO (Sanchez et al. 2017) and AutoPACMEN (Bekiaris & Klamt 2020) build models automatically from genome-scale reconstructions and kinetic databases, there is currently no automatic procedure to derive coarse-grained GBA models. They must be built manually, and their kinetic parameters must be estimated by an expert on a case by case basis."

Maybe one limitation of the model is that overexpression of ADPS, and to some extent NTS, does not appear to reduce growth even at very high proteome fractions. This however does not hold true in vivo. Can the authors comment on this, or does it simply mean that the proteome-fraction "cost" of these enzymes is not high enough?

The predicted proteome fractions of ADPS and NTS in the unconstrained GBA model are very low (ϕADPS=0.24% and ϕNTS=2.1%). Consequently, even a five-fold overexpression corresponds to only a small absolute increase in their proteome fractions and therefore also a limited effect on the predicted growth rate in Fig. 2. In the Supplementary Information, we also show the growth-rate dependence on the absolute proteome fractions. For NTS, the growth rate decreases to zero as ϕNTS approaches 1. For ADPS, the predicted growth rate decreases by approximately 20% at ϕADPS=0.2. Beyond this extreme point, numerical convergence is not achieved anymore by the solver. Thus, the model does predict a growth penalty at sufficiently high absolute expression levels, but the effect is small within the physiologically relevant range explored in the main text.

The absolute costs are indeed related to the proteome fractions themselves, so changes in these low fractions have a small impact on the growth rate. A more general quantification of the impact of perturbations on growth would be (ϕi/𝜇) (𝛿𝜇/𝛿ϕi), which would capture the proportional change in growth relative to a proportional change in phi.

Another limitation is that density is maintained constant. However, multiple reports including from the authors highlight that cellular density can vary with growth rate (10-15%) (e.g., 10.1371/journal.pcbi.1011177 and 10.1073/pnas.2021416118). How would a growth dependency affect the current results ?

We thank the reviewer for this suggestion. The question of experimental variability of the cellular density at different growth conditions is indeed relevant in the larger context of modeling optimal cellular growth. These experimental results do not, however, clarify what exactly is the causal relationship relevant to our simple models: whether is the growth rate or is the environmental condition itself (e.g. via its osmolarity among other properties) determining the particular density.

A variable density would therefore need an empirical rule for the density as a function of the growth rate. This rule would be an additional input that depends on the outcome of the optimization, and its form would be an assumption that the data do not support. This does not fit our aim of predicting the cell state from optimality with a minimal set of assumptions

We therefore keep a constant density, at the cost of some realism, and consider the variation of the density to be outside the scope of this study. We thank the reviewer for the suggestion, and in future work the density could be included as a variable in the GBA framework.

(OPTIONAL) In classic FBA, the response to perturbation is often better approximated using Minimization Of Metabolic Adjustment (MOMA; doi: 10.1073/pnas.232349399) rather than full re-optimization of the objective. I was wondering if such an approach (minimizing the difference between the non-perturbed state and the perturbed state) could actually be more appropriate for some of the case studies presented here? Especially those involving a shift such as the lac operon induction (Fig. 3).

We thank the reviewer for this suggestion. In our simplified model, however, cellular states are estimated as if the cell had unlimited time to adapt to the corresponding environment. So our predictions can only be interpreted in that way as steady-states. For a generalization of the GBA models in transient states, please see the preprint https://doi.org/10.1101/2025.06.24.661369.

Minor comments:

The authors state (p3) that "growth laws emerge naturally from the first-principles formulation of cellular resource allocation" but since the kinetic parameters were themselves tuned to match the growth-rate and biomass data the model is later validated against, I'd suggest softening this language, or explicitly clarifying which validations are independent of the calibration data.

We thank the reviewer for this comment. We agree that the original wording was too strong. We softened the language and now state which data were used to calibrate the kinetic parameters and which comparisons are independent of the calibration. The revised paragraph is below:

"The kinetic parameters were calibrated to the growth rate and biomass composition of E. coli (see Methods). The dependence of the ribosomal fraction and the RNA/protein ratio on growth rate, and the response to a translation inhibitor, were not used in this calibration. Together, these results show that the model reproduces these growth laws without explicit implementation of the laws as model constraints."

In Fig. 1, I would suggest highlighting that the model also incorporates a kinetic layer which might not be obvious for a non-familiar reader. Also, S lumping together different internal metabolites should be reinforced for clarity, and it would also help to reiterate how growth is maximized in GBA. Similarly, it should also be stated that the numerical parameters shown within the matrix are obtained from a best fit to E. coli data.

We included these points into the figure caption. Here is the revised caption:

"A base model of a self-replicating cell, and its corresponding total mass fraction matrix Mtotal. The reactions between metabolites (circles) are catalyzed by specific catalytic proteins. Each reaction has an explicit kinetic rate law that links its flux to the metabolite concentrations and to the abundance of its catalyzing protein. The cell takes up small molecules Sext via a transporter (TS), and converts them into amino acids (AA) and nucleotides (NT) through amino acid synthesis (AAS) and nucleotide synthesis (NTS) reactions. The internal species S is a lumped variable that represents several different internal metabolites. Nucleotides are converted into ADP by the ADP synthesis reaction (ADPS). The ATP synthesis reaction (ATPS) uses S and ADP to generate ATP, producing a waste product Wext that is immediately excreted. Nucleotides are then used by DNA polymerase (DNAP) and RNA polymerase (RNAP) to synthesize DNA and RNA, respectively. Amino acids and ATP are used by ribosomes (R) to synthesize the proteome (P), which represents the total modeled proteome, defined as the sum of all proteins in the model. Small pink circles on top of the arrows indicate that a reaction requires ATP. Green lines with circles represent that a molecule is required for a reaction to proceed, but is not consumed in the reaction -- DNA is required by both polymerases as a template and RNA is required as a component of the ribosome. In GBA, the growth rate is maximized by optimizing the reaction fluxes under the constraints of balanced growth, constant cell density, and the kinetic rate laws. See SI for details about constructing the Mtotal matrix. The density and kinetic parameters are based on E. coli data (see Methods and Tables 2 and 3). Cell figure created with biorender.com."

In Fig. 2, for each subpanel, are the non-plotted proteins are held at their own optimal φ* values or are re-optimized as the plotted protein's φ is varied. The composition panels imply the latter, but this should be stated explicitly in the caption or main text to avoid ambiguity.

We thank the reviewer for this comment. The reviewer is correct: the fractions of all non-plotted proteins are re-optimized as the plotted protein's is varied. We added this statement to the caption of Fig. 2.

"For each point, the proteome fraction of the plotted protein is fixed, and the fractions of all other proteins are re-optimized to maximize growth rate."

In Fig. 4, what does each triangle represent? Also, I would suggest dividing the figure into panels (a, b, c) for clarity when referencing it in the text.

We thank the reviewer for these suggestions. Each gray triangle is one experimental measurement from Scott et al. (2010): the growth rate at a given proteome fraction of the overexpressed protein (-galactosidase), normalized to the maximum growth rate of the same condition. We added this explanation to the caption of Fig. 4. We also divided the figure into panels (a), (b), and (c), and the caption and the text now refer to them. The following text was added to the caption:

"Each gray triangle in (a) is one measurement from Scott et al. (2010) of the growth rate at a given proteome fraction of the overexpressed protein (-galactosidase). The data cover different growth conditions, and each growth rate is normalized to the maximum growth rate of its condition, measured without overexpression."

Reviewer #2 (Significance (Required)):

The manuscript offers both conceptual and technical novelty and is complementary to recent literature (e.g., doi: 10.1038/msb.2009.82, 10.1016/j.ymben.2015.10.003, 10.1371/journal.pcbi.1004913), though it should be more explicitly benchmarked against these related approaches to add significance from their previous study. It will be relevant to a wide range of scientists, from microbial physiologists to metabolic engineers. My expertise for reviewing this manuscript includes prior experience with microbial modeling (mainly FBA) and general expertise in metabolic engineering and systems biology in yeast and bacteria.

We thank the reviewer for the assessment. As described above, we added explicit comparisons with related approaches: (i) a comparison with RBA, enzyme-constrained FBA and with the kinetic COBRA-k framework on the toy model (new Fig. S3), (ii) a paragraph in the Discussion on the relation to the model of Molenaar et al. and what GBA adds to it, and (iii) a more detailed discussion of the limitations of GBA.

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

Summary:

Széliová and colleagues use a modified Growth Balance Analysis (GBA) model, parametrized with Escherichia coli data to simulate cell perturbations that steer microbial resource allocation away from its optim(um/a), such as titrating expression levels of growth-contributing proteins, introducing gratuitous protein expression, or introducing toxic metabolite that requires a protein to detoxify/expel the compound. Simulations confirm intuitive a priori guesses (and experiments) that perturbations reduce the predicted optimal growth rate in a dose-dependent manner.

We thank the reviewer for carefully reading the manuscript and providing constructive comments which have helped us improve the manuscript. Below, we answer each comment individually.

Major comments:

• Being familiar with different modeling formalisms of cellular growth, including the original coarse-grained resource allocation model of Douwe Molenaar and co., it is for me currently unclear what new insights the GBA models bring on the table, being parametrized in a similar manner as the Molenaar-type models. Is it the effects of reversible enzyme kinetics?

We thank the reviewer for this comment. GBA belongs to a similar class of coarse-grained self-replicator models as the model of Molenaar et al. The main differences are the following. (i) We use both irreversible and reversible enzyme kinetics (ii) In GBA the growth rate is an explicit function of independent variables, which also facilitates the study of suboptimal states that has not been done before in those type of nonlinear models, including in the seminal study of Molenar et al. As we have shown before via general analytical expressions, the minimal mathematical formulation of GBA gives the marginal value of each protein and its split into four terms, which shows that the growth cost of overexpression comes mainly from changes in metabolite concentrations and not from the synthesis of the protein itself. In this study we also apply these expressions to study the particular models developed here. (iii) The density constraint of GBA covers all biomass components, so that metabolite accumulation costs space. Molenaar et al. constrain only the protein concentration. We added to the text:

"GBA belongs to a similar class of coarse-grained self-replicator models introduced by Molenaar et al., which differ by being restricted to irreversible Michaelis-Menten kinetics and constrains only the total protein concentration. The GBA framework facilitates the creation and analysis of models in that class via an explicit function for the growth rate in terms of a minimal set of independent variables, which facilitates the derivation of the marginal value of each protein and its decomposition into four terms (Dourado et al. 2023), the density constraint includes all biomass components so that metabolite accumulation reduces the space for proteins, and general rate laws such as reversible kinetics can be used (Dourado et al., 2020)."

• Could you share any scenarios, where simulation results did not match the intuition/experimental data, and what could be the underlying reasons/known unknowns/unknown unknowns?

We thank the reviewer for this question. Our model deviates from experiments or intuition in three cases. (i) In experiments, overexpression sometimes does not affect growth until a threshold is reached, which points to spare capacity that GBA does not include. (ii) Idle proteins can have a nonlinear cost, as reported by Dekel and Alon for the lac proteins in the absence of lactose, for example through protein aggregation, effects on the membrane, or signaling, which the present model does not describe. (iii) The model can predict that metabolites accumulate to a large fraction of the biomass, which is unrealistic, because real cells would prevent this by regulation, or growth would stop before this point. Further deviations can come from kinetic parameters and mechanisms that are unknown or not included in the model. Point (i) was already discussed in "Model limitations and future directions". We added points (ii) and (iii) to the section "Linking protein expression to growth with growth balance analysis".

"Other types of burden, not yet captured by GBA, include protein misfolding, degradation, and regulatory feedback (Eguchi et al. 2018, Chen et al. 2018,Tomala et al. 2013). Such effects can also make the cost of an idle protein nonlinear. Dekel and Alon (2005) measured a nonlinear cost for the expression of the lac proteins in the absence of lactose, which may be related to the membrane transporter LacY, as discussed below. Further causes may include protein aggregation and signaling Tomala et al. 2013, Chen et al. 2018. GBA instead predicts a linear cost, in agreement with other measurements Scott et al. 2010, Kafri et al. 2016, because it describes an idle protein only by the space and resources that it uses."

"However, with irreversible kinetics, and in the lac model at high expression of the lactose enzyme, the model predicts that S or AA accumulate to a large fraction of the biomass, up to almost half (Fig. 3c and Fig. S9). Such accumulation is unlikely in real cells, which would limit it by regulation, for example by feedback inhibition or export, or growth would stop before this point. Adding an export reaction reduces the accumulation in the model (Fig. S11), so the growth costs predicted at high expression of such enzymes may be overestimated."

Reviewer #3 (Significance (Required)):

This study does extend the GBA modeling framework by considering non-optimal resource allocation states, and is validated by multiple perturbation scenarios, making it a solid technical advance. The simulation materials and code will likely also be useful for the community interesting in setting up such models for their biological questions.

Keywords: biosynthetic resource allocation, metabolic network modeling, microbial physiology

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Referee #3

Evidence, reproducibility and clarity

Summary:

Széliová and colleagues use a modified Growth Balance Analysis (GBA) model, parametrized with Escherichia coli data to simulate cell perturbations that steer microbial resource allocation away from its optim(um/a), such as titrating expression levels of growth-contributing proteins, introducing gratuitous protein expression, or introducing toxic metabolite that requires a protein to detoxify/expel the compound. Simulations confirm intuitive a priori guesses (and experiments) that perturbations reduce the predicted optimal growth rate in a dose-dependent manner.

Major comments:

• Being familiar with different modeling formalisms of cellular growth, including the original coarse-grained resource allocation model of Douwe Molenaar and co., it is for me currently unclear what new insights the GBA models bring on the table, being parametrized in a similar manner as the Molenaar-type models. Is it the effects of reversible enzyme kinetics?
• Could you share any scenarios, where simulation results did not match the intuition/experimental data, and what could be the underlying reasons/known unknowns/unknown unknowns?

Significance

This study does extend the GBA modeling framework by considering non-optimal resource allocation states, and is validated by multiple perturbation scenarios, making it a solid technical advance. The simulation materials and code will likely also be useful for the community interesting in setting up such models for their biological questions.

Keywords: biosynthetic resource allocation, metabolic network modeling, microbial physiology

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

Summary:

Constraint-based approaches like flux balance analysis (FBA) have proven useful for modeling microbial metabolism, but they assume a fixed, predefined biomass objective function. This, together with their general lack of enzyme kinetics and regulatory mechanisms, limits their ability to capture complex, non-linear dynamics. In this manuscript, Szeliova et al. build on their previous GBA framework to analyze suboptimal protein allocation that cannot be captured using FBA. They first develop a coarse-grained model comprising a stoichiometric layer and kinetic layer that fits E. coli experimental data. Applying GBA to this model, they interrogate the effect of suboptimal protein allocation along different scenarios of interest to microbial physiology but also to metabolic engineering (enzyme overproduction, optimality during utilization of a secondary carbon source). Overall, I found the manuscript clear and well-written, and the coarse-grained model a promising basis for further extension, although the conceptual novelty relative to the authors' previous work (doi: 10.1038/s41467-020-14751-w) is somewhat limited. Below, I note several minor inconsistencies and suggestions that could improve the manuscript prior to publication.

Major comments:

The authors rightfully note in the introduction that many coarse-grained approaches incorporating protein allocation, and sometimes enzyme kinetics, already exist (e.g., doi: 10.1038/msb.2009.82, 10.1016/j.ymben.2015.10.003, 10.1371/journal.pcbi.1004913). While I believe that simpler models are already helpful for capturing much of cellular dynamics, I think it would be useful and interesting to compare the GBA framework against some of these other tools. What are the limitations of GBA across the different case studies, and what does it capture that other models do not?

Maybe one limitation of the model is that overexpression of ADPS, and to some extent NTS, does not appear to reduce growth even at very high proteome fractions. This however does not hold true in vivo. Can the authors comment on this, or does it simply mean that the proteome-fraction "cost" of these enzymes is not high enough?

Another limitation is that density is maintained constant. However, multiple reports including from the authors highlight that cellular density can vary with growth rate (10-15%) (e.g., 10.1371/journal.pcbi.1011177 and 10.1073/pnas.2021416118). How would a growth dependency affect the current results ?

(OPTIONAL) In classic FBA, the response to perturbation is often better approximated using Minimization Of Metabolic Adjustment (MOMA; doi: 10.1073/pnas.232349399) rather than full re-optimization of the objective. I was wondering if such an approach (minimizing the difference between the non-perturbed state and the perturbed state) could actually be more appropriate for some of the case studies presented here? Especially those involving a shift such as the lac operon induction (Fig. 3).

Minor comments:

The authors state (p3) that "growth laws emerge naturally from the first-principles formulation of cellular resource allocation" but since the kinetic parameters were themselves tuned to match the growth-rate and biomass data the model is later validated against, I'd suggest softening this language, or explicitly clarifying which validations are independent of the calibration data.

In Fig. 1, I would suggest highlighting that the model also incorporates a kinetic layer which might not be obvious for a non-familiar reader. Also, S lumping together different internal metabolites should be reinforced for clarity, and it would also help to reiterate how growth is maximized in GBA. Similarly, it should also be stated that the numerical parameters shown within the matrix are obtained from a best fit to E. coli data.

In Fig. 2, for each subpanel, are the non-plotted proteins are held at their own optimal φ* values or are re-optimized as the plotted protein's φ is varied. The composition panels imply the latter, but this should be stated explicitly in the caption or main text to avoid ambiguity.

In Fig. 4, what does each triangle represent? Also, I would suggest dividing the figure into panels (a, b, c) for clarity when referencing it in the text.

Significance

The manuscript offers both conceptual and technical novelty and is complementary to recent literature (e.g., doi: 10.1038/msb.2009.82, 10.1016/j.ymben.2015.10.003, 10.1371/journal.pcbi.1004913), though it should be more explicitly benchmarked against these related approaches to add significance from their previous study. It will be relevant to a wide range of scientists, from microbial physiologists to metabolic engineers. My expertise for reviewing this manuscript includes prior experience with microbial modeling (mainly FBA) and general expertise in metabolic engineering and systems biology in yeast and bacteria.

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:

This manuscript deals with the application of Growth Balance Analysis (GBA) on suboptimal protein expression. Using detailed kinetic models of cellular growth, the authors explore the protein costs involved in several different contexts, such as nutrient availability, toxin removal, and idle proteins. They show convincingly that GBA is able to capture different trade-offs that are consistent with experimental data. The exposition is detailed, and easy to follow.

This is a well-written manuscript, and I enjoyed reading it. I don't have major points of discussion.

Major comments: none.

Minor comments:

I was, I think, most surprised that there was no mention at all of the only other theory that is equivalent in scope to GBA: EGM theory (De Groot et al., PLoSCB 2020, https://doi.org/10.1371/journal.pcbi.1007559). Although different in its rationale (focusing on concentrations rather than mass fractions, leading to a quite different kind of optimisation problem), the level of cellular detail is quite comparable, and I think all the trade-offs found in this paper could be replicated with it. (There is a model with toxin removal in the paper, for example.) I don't want to advocate people to use EGMs over GBA. I think GBA is very useful indeed.

The concavity of the plots in Fig 1 are also relevant for the claim proved in https://www.biorxiv.org/content/10.1101/2024.07.09.602663v1 . It is (still) not published, so you might not want to cite it. But in this manuscript there is a full proof of the fact that the map (proteins -> growth rate) is concave in EFMs/EGMs. Of course GBA makes this quantitative, which is a real bonus.

It would be good, when starting the informal discussion of the base model, to refer where the full description is given. At the moment, I found it by clicking on the Eq.(13) link, which seemed to be the first time I was given a direct pointer. It would be good to refer to the Methods section (whose title I missed on the first two reads, as it starts with a table, so my eyes glanced over it).

It is a bit confusing sometimes that both references and equation numbers are referred to with (number). Most of the time, equations are referenced using Eq. (number), but in the paragraph below eq.(12) there are a few instances where this does not happen. In that same sentence, (31) refers to a paper. I would also advice paragraphs to be indented (the main text will be formatted by the journal, but the Supporting Information would also be more readable, in my opinion).

Significance

Advance: the authors mention that they 'extend' GBA to these suboptimal (rather than optimal) growth states. I believe they just 'apply' GBA to these states. I don't think there is a conceptual difference between the old papers (10), (30), (31) and the new. Also the protein costs formula (eq. S1), which is the most insightful theoretical relation in this paper, is not new but from ref (31). The main advance lies in the fact that the authors were able to make well-parameterised core models of cells, and apply GBA to get quantitative results on trade-offs, etc. This has not been done before. This is definitely very useful and worth publishing.

Audience: experimental and theoretical systems biologists, microbial physiologists.

My expertise: I have worked on microbial physiology using mathematical modelling for about 10 - 15 years. I have done quite some work on elementary modes theory in cells, and am well acquainted with (nonlinear) optimisation approaches in systems biology.

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Reply to the reviewers

Reply to the Reviewers

We thank the editor and reviewers for their constructive assessment. The textual revisions and additions described in Section 3 have already been incorporated into the manuscript. The work planned in Section 2 comprises the statistical improvements and supplementary experiments or analyses specified under the individual reviewer comments.

Each comment is answered separately in the original reviewer order. Comments addressed by revising or qualifying the wording are classified as completed textual revisions. They do not create additional experimental commitments. Planned measurements and statistical reanalysis are described prospectively, and no new results or unchanged significance are assumed.

Reviewer 1

Major comment 1. Ciliary integrity is not yet established as the causal or unifying mechanism of microtubule-stabilizer-mediated recovery

A central conclusion of the manuscript is that preservation of ciliary integrity represents a shared structural checkpoint linking microtubule stabilization to spinal cord repair. The data clearly show that Noscapine treatment is associated with preservation of ciliary structures in ependymal cells and CSF-cNs, and that Paclitaxel produces similar cellular effects. However, I do not think the current experiments are sufficient to establish cilia as the causal mechanism underlying the functional benefits of these treatments. In particular, SANT-1 is a Smoothened antagonist and therefore interferes with Hedgehog/Smoothened signaling rather than specifically ablating cilia. Consequently, the partial loss of Noscapine-mediated recovery following SANT-1 treatment could reflect disruption of Hedgehog signaling rather than a specific requirement for ciliary structure. Conversely, Y-27632 is a ROCK inhibitor with broad effects on cytoskeletal organization and has previously been reported to improve recovery after SCI through cilia-independent mechanisms. Thus, while these pharmacological experiments are consistent with a contribution of cilia, they do not by themselves demonstrate that ciliary preservation is required for Noscapine-mediated repair.

The most direct way to test this model would be a temporally controlled genetic disruption of ciliogenesis in the relevant central canal-associated population, for example using the Foxj1-CreER;Ift88/Kif3a strategy already proposed by the authors, followed by assessment of whether Noscapine can still promote recovery. This would provide the strongest test of the central mechanistic claim, although it would represent a substantial experiment requiring several months depending on mouse-line availability. More tractable alternatives could nevertheless considerably strengthen the current evidence. First, the authors could test whether ciliary preservation is reproduced across the full panel of microtubule-targeting compounds used in the initial screen. At present, five compounds are used to support cross-chemotype convergence in functional recovery, whereas ciliary preservation is examined mainly for Noscapine and Paclitaxel. Demonstrating that Epothilone D, TPI-287 and TTI-237 similarly preserve ependymal and/or CSF-cN cilia would provide much stronger support for ciliary preservation as a shared downstream response. Second, if an appropriate primary spinal-cord ependymal or related culture system is available, genetic disruption of ciliogenesis through IFT88 or KIF3A depletion could be used to determine whether Noscapine-associated cellular effects are lost when ciliogenesis is impaired. Such an orthogonal genetic experiment would directly complement the current pharmacological evidence and could likely be completed within several weeks to a few months. Neither alternative would fully establish that ependymal cilia are necessary for functional recovery in vivo, but together they would substantially strengthen the proposed mechanism. If additional experiments are not feasible, the authors should instead moderate statements describing ciliary integrity as "required," a "shared structural checkpoint," or a "unifying downstream dependency," and restrict the conclusion to the evidence that microtubule stabilization is associated with ciliary preservation and that cilia-associated pathways may contribute to recovery.

Response:

We thank the reviewer for this thoughtful and constructive assessment. We agree that the current pharmacological evidence does not establish ciliary preservation as a causal requirement for Noscapine-mediated functional recovery.

To strengthen the evidence, we will first work to establish a suitable in vitro culture system using spinal cord ependymal or related cells. Once this system is established, we plan to compare the effects of the microtubule-targeting compounds used in our initial screen, including Noscapine, Paclitaxel, Epothilone D, TPI-287, and TTI-237, on ciliary structure and maintenance. This comparison will test whether the ciliary effects observed with Noscapine and Paclitaxel extend across the broader compound panel. We recognize that a shared structural response would strengthen evidence for convergence but would not, by itself, establish ciliary necessity.

In parallel, we have begun preparations for a Foxj1-CreER–based conditional Ift88 deletion mouse model for subsequent in vivo validation. Our aim is to determine whether Noscapine retains its beneficial effects when ciliogenesis is genetically disrupted in the targeted population.

Several mechanistic statements in the current preliminary revised manuscript have not yet undergone final coordinated revision, as we plan to validate these interpretations via the listed supplementary experiments. We have marked these relevant statements in red within the main text to indicate that these conclusions are pending revision. If the follow-up supplementary data cannot be obtained, yield inconclusive results, or fail to support the above inferences, we will qualify or remove the corresponding claims and retain only those observations directly supported by experimental data.

Major comment 2. Several conclusions extend beyond the experimental readouts

Several conclusions throughout the manuscript appear broader than the experimental readouts used to support them. I think these points should be addressed individually, either by providing additional quantitative analysis where this can reasonably be performed on existing material, or by revising the wording so that the conclusions more closely reflect what was directly measured.

a. Glial and fibrotic scarring. In the Abstract, the authors state that maintenance of ciliary architecture is associated with "reduced glial scarring" (line 31). However, the main quantitative assessment of scarring in Figure 2 is based on Laminin-positive area, which is described as evidence of reduced "ECM/fibrotic scarring" (lines 103-107). GFAP staining is shown, but glial scar formation itself does not appear to be qualitatively or quantitatively assessed. The claim of reduced glial scarring should therefore either be supported by further histological analysis (H&E staining, antibody staining for various ECM component, superficy of scar measurement and so on) or removed. Similarly, reduced Laminin deposition is consistent with altered ECM/fibrotic remodeling, but Laminin alone provides a relatively limited assessment of the fibrotic scar. If the authors wish to maintain the broader claim of reduced fibrotic scarring, additional characterization of the fibrotic compartment would strengthen this conclusion; otherwise, "reduced Laminin deposition" would more precisely describe the result.

Response____：

We thank the reviewer for pointing out our over‑interpretation of scar‑related results. We agree that Laminin staining alone is insufficient to support broad conclusions about glial and fibrotic scarring without additional histological quantification.

We have revised the manuscript to limit conclusions strictly to our available data. We replaced the claim of “reduced glial scarring” from the Abstract with “reduced Laminin deposition” (line 31). The expression of “reduced ECM/fibrotic scarring” throughout the text was also modified to use a more precise description of “reduced Laminin deposition”, matching our Figure 2 quantification (line 109, 125, 296 and 844).

b. Tissue continuity and circuit continuity. The Abstract states that treatment results in "improved tissue continuity" (line 31), but I could not identify a direct quantitative assessment of tissue continuity or lesion bridging. Figure 2 instead shows increased NeuN and SMI-312 labeling and Brainbow-positive "axon-like" or "tract-like" structures that appear to extend across the lesion (lines 107-115). The Results then conclude that these findings provide "structural substrates for cross-lesion circuit continuity" (lines 116-118). These anatomical observations are interesting, but they do not directly demonstrate tissue continuity or functional circuit reconstruction. If tissue continuity is an important outcome, a quantitative measurement of lesion/bridge dimensions could potentially be performed using the existing histological material. The Brainbow findings should otherwise be described as evidence of anatomical fiber continuity across the lesion rather than circuit continuity, unless additional evidence of synaptic or functional connectivity is provided.

Response____：

We thank the reviewer for this valuable comment on our interpretation of anatomical tracing results. We agree our original wording overstated evidence for tissue and circuit continuity without direct synaptic or functional validation.

Although we performed trans synaptic AAV tracing and observed labeled neuronal cell bodies caudal to the lesion core, these observations alone are insufficient to firmly establish genuine circuit reconstruction. We have revised the manuscript to moderate our conclusions. We replaced the claim of “improved tissue continuity” from the Abstract with “improved fiber continuity across the lesion” (line 31). The conclusions drawn from Brainbow tracing are now described as “evidence of anatomical fiber continuity across the lesion”, instead of “cross lesion circuit continuity” (lines 117-118, 284, 286 and 780-781).

c. Ciliary structure versus ciliary function. The authors directly demonstrate preservation of ciliary morphology, including a greater proportion of ciliated ependymal cells, more continuous ciliary arrays, increased cilia-associated gene expression, and increased ciliation in RPE-1 cells (lines 198-214). However, they subsequently conclude that Noscapine "protects ciliary structure and function" and suggest that this preservation maintains CSF flow, environmental sensing, and lineage competence (lines 215-218). None of these physiological functions are directly measured. This distinction is particularly clear because the authors themselves state in the Discussion that measurements of ciliary beat coordination, CSF flow, and IFT dynamics will be required to link structural preservation to physiological function (lines 337-340). I therefore suggest consistently referring to preservation of ciliary structure or ciliation rather than ciliary function unless functional measurements are added.

Response____：

We thank the reviewer for this important distinction between ciliary structure and ciliary function. We agree that our original text drew inferential conclusions about ciliary related physiological functions without direct experimental measurements.

Following the reviewer’s suggestion, we have revised the manuscript to consistently refer to preservation of ciliary structure/ciliary integrity throughout the text and removed all claims regarding preserved ciliary function (lines 227-230, 245, 256-258, 274-275).

d. CSF-cN survival. The manuscript repeatedly describes Noscapine as enhancing or preserving CSF-cN survival. For example, lines 175-179 state that PKD2L1 immunostaining "verified that Noscapine enhanced the survival of CSF-cNs," and similar language is used for Paclitaxel and SANT-1 experiments (lines 224-225 and 246-249). However, the presented readout appears to be the abundance or proportion of PKD2L1-positive cells at individual time points rather than a direct assessment of cell survival or cell death. The increased abundance of PKD2L1-positive cells is consistent with enhanced preservation of CSF-cNs but does not directly demonstrate increased survival. This conclusion could be strengthened relatively straightforwardly by assessing cell death specifically within PKD2L1-positive CSF-cNs, for example using TUNEL and/or cleaved caspase-3 staining at an appropriate early post-injury time point. Alternatively, the authors should describe the result as increased preservation or abundance of PKD2L1-positive CSF-cNs rather than enhanced survival.

Response____：

We thank the reviewer for pointing out this critical distinction. We agree that our PKD2L1 positive cells quantification reflects cell abundance at fixed time points, rather than a direct measurement of cell survival or cell death.

Following the reviewer’s advice, we have revised the manuscript and replaced statements about enhanced CSF-cNs survival with increased abundance of CSF-cNs (lines 188-190, 236, 254, 258-260, 272, 288, 320, 339, 348-350, 356).

Major comment 3. The proposed ependymal-to-astrocyte differentiation is not directly demonstrated

A second important component of the proposed central canal repair mechanism is that Noscapine promotes differentiation of ependymal cells toward a reparative astrocytic state. This conclusion is mainly based on the decrease in ependymal cells and increase in astrocytes between 2 and 3 wpi, Monocle pseudotime trajectories connecting these populations, and the increased proportion of GFAP+Foxj1+ cells following Noscapine treatment (lines 149-165). While these observations are consistent with a relationship between ependymal and astrocytic states, they do not demonstrate a lineage transition. Pseudotime analysis orders transcriptionally related cell states but cannot establish the developmental origin of individual cells, and GFAP expression in Foxj1+ cells could alternatively reflect activation or phenotypic changes within ependymal cells rather than their differentiation into astrocytes. Nevertheless, the manuscript subsequently refers to "lineage progression," "lineage-associated transition," and the emergence of ependymal cell-associated astrocytes as a component of the proposed mechanism (lines 180-183, 241-246, 303-305 and 327-329). The authors appropriately acknowledge at lines 163-165 that formal demonstration of an ependymal-to-astrocyte transition would require lineage tracing, but the stronger lineage interpretation is retained elsewhere in the Results and Discussion.

The most direct way to address this point would be lineage tracing of Foxj1-expressing ependymal cells, for example using a temporally controlled Foxj1-CreER reporter activated before injury, followed by SCI +/- Noscapine and assessment of whether labeled progeny acquire astrocytic identity. This would provide a clear test of whether Noscapine truly increases ependymal-derived astrocyte formation and would likely require several months depending on mouse-line availability. If such an experiment is beyond the scope of revision, I do not think an entirely new lineage-tracing study should necessarily be required. Instead, the authors should consistently limit their interpretation to what is directly supported-for example, that Noscapine is associated with an increased GFAP+Foxj1+ population and with transcriptional states connecting ependymal and astrocytic populations-rather than presenting these observations as demonstrated ependymal-to-astrocyte differentiation. Additional computational approaches such as RNA velocity could provide supporting evidence for directional state transitions, but would still not substitute for lineage tracing.

Response____：

We thank the reviewer for this important clarification. We agree that pseudotime analysis and GFAP/Foxj1 co-expression do not establish ependymal-to-astrocyte differentiation, and that the observed changes could alternatively reflect activation or phenotypic remodeling of ependymal cells.

Following the reviewer’s suggestion, we will make every effort to perform lineage-tracing experiments using Foxj1-CreER mice crossed with an appropriate Cre-dependent reporter line. We plan to induce labeling before injury, followed by SCI with or without Noscapine treatment, and assess whether lineage-labeled cells acquire astrocytic identity using appropriate markers. This experiment will help determine whether Noscapine increases the formation of astrocytes derived from Foxj1-expressing ependymal cells.

Completion will depend on establishing and validating the tracing system. If reliable experimental results cannot be obtained, we will revise all lineage-related statements throughout the manuscript to only describe the increased GFAP-positive/Foxj1-positive cell population and the transcriptional association between ependymal and astrocytic cell states. The final conclusions will be revised in accordance with the experimental evidence. If the additional evidence is unavailable, inconclusive, or does not support these interpretations, we will qualify or remove the corresponding claims and restrict the conclusions to the observations directly supported by the data. We highlighted these statements that remain subject to revision in red in the manuscript.

Minor comment 1. Statistical analysis should be reconsidered for several experiments

The Methods state that two-tailed Student's t-tests were used for statistical comparisons (lines 544-551). This does not appear appropriate for several datasets, particularly the longitudinal BMS measurements, experiments containing more than two groups, and repeated measurements at 4 and 8 wpi. The authors should clarify the statistical test used for each comparison and account for repeated measurements and multiple comparisons where appropriate. The experimental unit should also be clearly defined. For example, in the RPE-1 cilia-length experiments, individual cilia should not necessarily be considered independent biological replicates when multiple cilia are measured from the same culture or experiment.

Response____：

We thank the reviewer for highlighting this issue. We agree that two-tailed Student’s t-tests are not appropriate for all experimental designs in this study. We will systematically review and revise the statistical methods throughout the manuscript and reanalyze the data where necessary.

For longitudinal BMS measurements, we will use an appropriate repeated-measures or mixed-effects approach that accounts for observations from the same animal over time. Comparisons involving more than two groups will use an appropriate overall test followed by comparisons with correction for multiple testing. For measurements at 4 and 8 weeks post injury, the analysis will distinguish repeated observations from the same animals from measurements obtained from independent cohorts.

We will also clarify the experimental unit and distinguish biological replicates from technical measurements for each analysis. For RPE1 cilia length experiments, we carried out three independent culture experiments. Individual cilia obtained from the same culture were not treated as independent biological replicates. The Methods and figure legends will specify the tests used, biological sample sizes, treatment of repeated measurements, and multiple-comparison corrections where applicable. Statistical annotations and the corresponding conclusions will be updated according to the reanalysis.

Minor comment 2. The biological replication and sample structure of the single-cell RNA-seq experiment should be described explicitly.

The manuscript states that 51,117 cells were retained across the conditions analyzed at 2 and 3 wpi, but it is unclear how many independent animals contributed to each condition, whether spinal cords were pooled before library preparation, and how many independent sequencing libraries were generated per group (lines 123-128). The authors should report the number of biological replicates per condition, the number of animals contributing to each replicate, and whether samples from different animals were processed independently or pooled.

Response____：

We thank the reviewer for this constructive comment regarding the reporting of our scRNA-seq experimental design. For each experimental condition, tissues were collected from 8-10 independent animals. Tissue samples were pooled prior to library construction, and only one independent sequencing library was generated per group. We have explicitly supplemented these details about animal numbers, sample pooling strategy and library information within the “Single cell suspension preparation” and “Single cell RNA sequencing” subsections of the Methods in lines 565-609.

Minor comment 3. Statistical inference from the single-cell dataset should account for biological replication.

*The manuscript reports substantial differences in cell composition, including a reduction of microglia from >60% of recovered cells in control samples to Response____：

We thank the reviewer for this important reminder about statistical considerations for scRNA-seq data.

Each sequencing library in our study was generated from pooled tissues of 8‑10 independent mice. While we consider each library representative of its corresponding experimental group, we acknowledge that only one library was available per condition, and our differential‑expression analyses lack independent library‑level biological replication.

Following the reviewer’s suggestion, we now present the differential-expression analysis for our scRNA-seq dataset as descriptive/exploratory findings, rather than formal statistical comparisons supported by biological replicates. We have updated the manuscript text in Results.

Minor comment 4. Several in vivo drug-treatment details required for reproducibility are missing.

The Methods state that mice received daily injections of saline, Noscapine, Paclitaxel or SANT-1 after crush injury, but the in vivo dose, vehicle and formulation are not clearly provided for all compounds. In addition, Y-27632 is not included in this treatment description despite being used in Figure 6 (lines 424-428). The dose, vehicle, injection route, treatment duration, and timing relative to injury should be explicitly reported for each pharmacological treatment.

Response____：

We appreciate the reviewer’s valuable comment regarding the completeness and reproducibility of our in vivo pharmacological treatment protocols. We have thoroughly revised and supplemented all drug administration details in the revised manuscript to fully address this concern.

First, we have removed the previous ambiguous description of drug injection for crush injury models. Furthermore, we have explicitly and comprehensively reported the complete treatment regimens for both the crush SCI model and the complete transection SCI model, including drug dosage, formulation, vehicle solvent, injection route, treatment duration, and post-injury intervention timing for all compounds. Notably, we have supplemented the detailed in vivo administration parameters of Y-27632, which was previously omitted in the text but applied in Figure 6. All revisions are presented in lines 460-476 of the manuscript text.

Minor comment 5. The administration strategy used in the initial microtubule-stabilizer screen should be clarified.

Figure 1C reports concentrations in µM and describes microtubule stabilizers in combination with the LOCS, whereas later Noscapine experiments use systemic treatment in mg/kg (lines 755-766). It should be made clear which compounds were locally delivered through the scaffold, which were systemically administered, and how the concentrations used for the different compounds were selected.

Response____：

We greatly appreciate the reviewer’s insightful suggestion to clarify the administration strategies applied in our microtubule stabilizer screening and subsequent functional validation experiments. We have now comprehensively supplemented the detailed drug delivery regimens and dosage selection rationale in the revised manuscript.

Specifically, we explicitly distinguished local scaffold-based delivery and systemic intraperitoneal administration for different compounds. In the initial microtubule stabilizer screening assay shown in Figure 1C, all candidate drugs were locally delivered via LOCS incubation at the indicated micromolar concentrations. The dose-ranging experiment of noscapine combined both local and systemic administration. Follow-up validation experiments used systemic intraperitoneal injection at mg/kg doses, with doses selected according to published in vivo therapeutic ranges. The detailed administration regimens were further supplemented in the Methods (lines 445-476).

Minor comment 6. The description of the EB1 experiment appears inconsistent between the Results and Methods.

The Results state that all five compounds reduced EB1-positive comet density "in vivo" (lines 88-90). However, the Methods describe treatment of HeLa cells with these compounds specifically to assess microtubule dynamics (lines 385-392). The authors should clarify whether the EB1 experiment was performed in vivo or in vitro and correct the corresponding text.

Response____：

We have corrected the misused term “in vivo” to “in vitro” in line 89 to align with our experimental setup described in Methods.

Minor comment 7. The title of Figure 6 overstates the experiment presented.

Figure 6 is entitled "Ciliary integrity is a key factor in regulating the functional recovery from SCI," yet the figure assesses ciliation, GFAP/Foxj1-positive cells, and PKD2L1-positive CSF-cNs and does not include a functional recovery measurement (lines 872-892). Unless functional data are added, the title should be revised to reflect the cellular phenotypes actually examined.

Response____：

Following the reviewer’s suggestion, we have revised the Figure 6 title to “Y‑27632 maintains ciliary structural integrity of central canal-associated cells”, which accurately reflects the cellular phenotypes examined in this figure.

Minor comment 8. Randomization, blinding, sample-size determination and exclusion criteria should be reported more completely.

The authors appropriately state that BMS scoring was performed by two observers blinded to experimental groups (lines 429-432). However, it is unclear whether animals were randomized to treatment groups, whether histological quantification was performed blinded, how sample sizes were determined, or whether any animals or samples were excluded from analysis. These details should be provided.

Response____：

We have supplemented the details of randomization, blinding, sample-size determination and exclusion criteria within the “Quantification and statistical analysis” subsection of the Methods (lines 596-609).

Minor comment 9. The exclusive use of young female mice should be acknowledged as a limitation.

All experiments were performed using 6-8-week-old female C57BL/6J mice (lines 350-354). This does not invalidate the findings, but given the translational framing of the manuscript, the authors should briefly acknowledge that possible sex- and age-dependent differences in treatment response were not evaluated.

Response____：

We thank the reviewer for raising this important consideration. All experiments in this study were conducted using 6-8 weeks old female C57BL/6J mice. We acknowledge that potential sex and age dependent differences in treatment response have not been evaluated in the current work. We have added this limitation in the “Animals” subsection of the Methods section.

Minor comment 10. Availability of processed single-cell data and analysis code would improve reproducibility.

The raw sequencing data are deposited, but several downstream analyses are described as being performed using "custom R scripts" (lines 534-543). Providing the processed Seurat object, cell annotations and relevant analysis scripts would make the single-cell results considerably easier to reproduce and independently evaluate.

Response____：

We thank the reviewer for this helpful suggestion. In the final fully revised submission, we will make available the processed Seurat object, cell annotations, and relevant analysis scripts, including the custom R scripts used for downstream analyses. We will also provide accompanying documentation and software version information to facilitate reproducibility and independent evaluation. The Data and Code Availability statement will be updated with the corresponding repository links and access details.

Reviewer 2

Major comment 1. The statistical analysis needs to be revised throughout the manuscript

This is my main concern, as it may affect many of the conclusions in the paper. The Methods state that two-tailed Student's t-tests were used, but many experiments have designs for which pairwise t-tests are not appropriate. Examples include the multi-group screen in Figure 1C, longitudinal BMS measurements, experiments with three or four groups, the factorial Noscapine × SANT-1 experiment, and measurements of multiple cells or cilia from the same biological replicate.

Figure 1C requires an omnibus test followed by corrected post-hoc comparisons. Repeated pairwise t-tests across so many groups increase the risk of false-positive results, particularly given the small and unequal sample sizes.

BMS measurements are longitudinal and should be analyzed using a repeated-measures or mixed-effects model that accounts for animal and time. Similarly, Figure 5 is a 2 × 2 design, and the claim that SANT-1 attenuates the effect of noscapine requires testing the Noscapine × SANT-1 interaction. Showing that one comparison is significant and another is not is not sufficient.

There is also a risk of pseudoreplication. For example, Figure 4 reports measurements from 100 individual cilia per treatment, but individual cilia from the same experiment are not independent biological replicates. The analysis should either use replicate-level values or account for the nested structure of the data.

For each experiment, the authors should also clearly report the biological n, technical/cellular replicates, randomization, blinding, exclusion criteria, statistical test and multiple-comparison correction.

I consider a full statistical reanalysis essential before the quantitative conclusions of the manuscript can be properly evaluated. Importantly, the conclusions throughout the manuscript should then be revised according to the outcome of this reanalysis.

Response____：

We thank the reviewer for this detailed assessment. We agree that the statistical analyses must reflect the experimental designs and that a full statistical reanalysis is necessary to evaluate the quantitative conclusions. We will use appropriate omnibus tests with multiplicity-adjusted comparisons for multi-group experiments and repeated-measures or mixed-effects models for longitudinal BMS data, distinguishing repeated observations from independent cohorts for measurements at 4 and 8 weeks. We will directly test the Noscapine × SANT-1 interaction in the factorial experiment.

For RPE1 cilia length experiments, we carried out three independent culture experiments. Individual cilia obtained from the same culture were not treated as independent biological replicates. All quantifications were performed blinded.

We will clearly report the biological sample sizes, experimental units, statistical tests, and multiple-comparison corrections for each analysis. Following reanalysis, we will update the figure annotations, statistical results, and corresponding interpretations throughout the manuscript, qualifying or removing any conclusions that are no longer supported.

Major comment 2. Appropriate vehicle and baseline controls are missing or unclear in several experiments

The control groups need to be clarified throughout the paper.

In Figures 1D-I, the relevant comparison for showing a noscapine effect is vehicle versus noscapine, rather than untreated control versus noscapine.

More importantly, several crush experiments appear to lack a vehicle-treated SCI group. For example, Figures 3H-I compare uninjured, crush SCI and crush + noscapine animals, but there is no crush + vehicle group. If noscapine is administered in a vehicle with possible biological effects, untreated SCI is not an adequate control. The vehicle group should be shown if it was performed.

Figures 4C-D would also benefit from an uninjured baseline. Crush versus crush + noscapine shows a treatment-associated difference in ciliation, but without baseline values it is difficult to conclude that noscapine preserves normal ciliation rather than simply increasing it after injury.

The paclitaxel experiment in Figure S8 is also unclear. The manuscript appears to use saline-treated animals as controls, but conventional paclitaxel is poorly soluble in saline. Since both paclitaxel and paclitaxel liposomes are listed in the Methods, the authors should clarify which formulation was used and what the corresponding vehicle control was.

More generally, formulation, vehicle, dose, route and treatment duration should be clearly reported for every drug.

Responses____：

• We thank the reviewer for this thorough evaluation of our control groups and drug administration details. We will revise the statistical analyses for Figures 1D-I, Figure 2 and Figure S1 following updated statistical approaches. As suggested, comparisons will be performed between the vehicle treated group and the noscapine treated group. For our crush SCI model, Noscapine and other compounds were delivered via intraperitoneal injection using saline as the solvent with no biologically active excipients. Our existing crush SCI group received intraperitoneal saline injection, which serves as the corresponding vehicle control for drug treated groups.

We will add an uninjured control group to Figures 4C–D, including representative Arl13b/Foxj1 staining and quantification of the proportion of Foxj1-positive cells bearing Arl13b-positive cilia.

• We thank the reviewer for this thorough evaluation of our control groups and drug administration details. In Figure S8, we used paclitaxel liposome for intraperitoneal injection, which is soluble in saline. The corresponding control group received intraperitoneal saline injection. Complete information regarding drug formulation, vehicle, dosage, administration route and treatment duration for all compounds has been supplemented within the “Spinal cord injury surgery” subsection of the Methods.

  Major comment 3.____ The current pharmacological experiments do not establish that cilia mediate the effects of noscapine

This is the main mechanistic issue in the manuscript.

Figure 5 is entitled "Ciliary integrity is required for the functional recovery mediated by Noscapine." However, SANT-1 is a Smoothened antagonist that blocks Hedgehog signaling; it is not a specific tool to remove or disrupt cilia. Hedgehog signaling can itself affect proliferation, differentiation, inflammation, survival and tissue repair. Therefore, the fact that SANT-1 reduces ciliation and attenuates some noscapine-associated effects does not show that these effects are caused by loss of cilia. It shows that the response to noscapine is sensitive to Smoothened/Hedgehog inhibition.

The Y-27632 experiment has the same problem in the opposite direction. Y-27632 is a ROCK inhibitor with well-established effects on axonal growth, astrocytes and scar formation after SCI. Therefore, the observation that Y-27632 increases ciliation and reproduces some noscapine-associated phenotypes does not demonstrate that increased ciliation is responsible for these effects. Both could simply be parallel effects of ROCK inhibition.

This also leaves open an alternative explanation for the overall findings: cilia may be better preserved because noscapine reduces tissue damage, rather than cilia preservation being the mechanism that drives repair.

For this reason, the current data support an association between ciliary preservation and improved outcome, but do not establish that cilia are necessary or sufficient for recovery. Statements such as "ciliary integrity is required," "critical structural dependency," "structural checkpoint" and "cilia-dependent regenerative niche" should therefore be toned down.

Interestingly, the authors themselves state in the Discussion that cell-specific genetic approaches such as Foxj1-CreER with Ift88/Kif3a would be needed to test ciliary necessity. I agree. If the authors wish to retain the strong causal conclusions, such an experiment would be required. Otherwise, the claims should be revised to reflect the current pharmacological evidence.

Figure 6 should also be retitled, as it refers to regulation of "functional recovery" even though no behavioral or electrophysiological endpoint is shown.

Response____：

We thank the reviewer for this careful assessment. We agree that the current pharmacological experiments do not establish that ciliary preservation is necessary or sufficient for Noscapine-mediated recovery.

To address this mechanistic question, we have already begun preparing Foxj1-CreER;Ift88 conditional knockout mice for subsequent validation experiments. We plan to use temporally controlled Ift88 deletion in Foxj1-expressing cells and assess whether Noscapine retains its beneficial effects following disruption of ciliogenesis. Several mechanistic claims in the preliminary revised manuscript await final coordinated validation through our planned supplementary experiments. These passages are highlighted in red in the main text to flag conclusions subject to revision.

We have revised the Figure 6 title to “Y‑27632 maintains ciliary structural integrity of central canal-associated cells”, which accurately reflects the cellular phenotypes examined in this figure.

Major comment 4. The data do not yet support a shared cilia-dependent mechanism across all microtubule-targeting compounds

Figure 1 screens noscapine, epothilone D, TPI-287, TTI-237 and paclitaxel, and the authors suggest that these drugs converge on a common downstream mechanism. However, the only common outcome examined across all compounds is locomotor performance. Scar formation, axonal growth and ciliation are not studied across the full panel.

The cilia experiments are mainly performed with noscapine and, to a lesser extent, paclitaxel. The data may therefore support a shared response between these two drugs, but they do not establish a "unifying" mechanism across all five compounds. It is also unclear why the other compounds are included in the initial screen if they are not followed up mechanistically.

The terminology should also be more precise. Paclitaxel and epothilones are classical microtubule stabilizers, whereas noscapine mainly suppresses microtubule dynamics and does not act in the same way. I suggest using "microtubule-modulating compounds" when referring to the drugs collectively.

Finally, the Results state that the compounds reduce EB1-positive comet density "in vivo," whereas the Methods describe this experiment in HeLa cells. This should be corrected. Reduced EB1 comet density also indicates reduced growing microtubule plus ends, but does not by itself prove equivalent microtubule stabilization by all compounds.

Responses____：

• We thank the reviewer for this constructive assessment. We agree that the current data do not establish a shared cilia-dependent mechanism across all five compounds. To extend the mechanistic comparison, we will first work to establish a suitable in vitro culture system using spinal cord ependymal or related cells. Once established, we plan to compare Noscapine, Paclitaxel, Epothilone D, TPI-287, and TTI-237 for their effects on ciliary structure and maintenance. This will test whether the ciliary responses observed with Noscapine and Paclitaxel extend across the broader compound panel.

In parallel, we have begun preparations for a Foxj1-CreER–based conditional Ift88 deletion mouse model. Following establishment and validation of this model, we plan to investigate all five compounds to determine whether disruption of ciliogenesis in Foxj1-expressing cells alters their effects on recovery. By comparing treatment responses in conditional knockout mice and appropriate littermate controls, we aim to test whether these compounds share a dependence on cilia in the targeted population.

The final conclusions will be revised in accordance with the experimental evidence. If the additional evidence is unavailable, inconclusive, or does not support these interpretations, we will qualify or remove the corresponding claims and restrict the conclusions to the observations directly supported by the data. We highlighted these statements that remain subject to revision in red in the manuscript.

• As the reviewer noted, these agents have distinct molecular actions: paclitaxel and epothilones are classic microtubule stabilizers, whereas noscapine primarily suppresses microtubule dynamics. To avoid misrepresentation, we have changed “Microtubule stabilizing agents” to “microtubule modulating compounds” at lines 25 and 49. The EB1 comet‑density assay was performed in HeLa cells. We have corrected “in vivo” to “in vitro” at line 89 to resolve inconsistency between Results and Methods. EB1 comet density marks growing microtubule plus‑ends and reflects microtubule growth and catastrophe cycles. Reduced EB1 comet density indicates suppressed microtubule dynamics, which we present as preliminary evidence of microtubule stabilization.

Major comment 5. Ciliary structure and ciliary function should be clearly separated

Figure 4 contains some of the most interesting data in the study, but the conclusions go beyond what was measured.

The authors show changes in cilium number, cilium length and ciliary markers, but they do not directly measure ciliary function. There are no measurements of ciliary beating, CSF flow, cilia-dependent signaling, mechanosensory responses or PKD2L1-dependent function in CSF-cNs.

Therefore, statements about preserved CSF flow, environmental sensing, lineage competence or "ciliary function" are speculative. The manuscript should refer to ciliary structure, architecture or integrity unless a functional readout is provided.

In Figure 4F, the authors also state that a greater proportion of CSF-cNs retain intact cilia after noscapine treatment, but I could not identify a corresponding quantitative analysis. This result should be quantified at the biological-replicate level.

The State 1/State 2 nomenclature also appears inconsistent between Figures 3 and 4 and should be clarified.

Response____：

• We thank the reviewer for these careful comments on the interpretation of ciliary observations and the state nomenclature in pseudotime analysis. We agree that our measurements of ciliary markers only assess ciliary structural features, and statements about preserved CSF flow, environmental sensing, lineage competence and ciliary function are speculative without direct functional assays. We have removed all claims related to ciliary function throughout the manuscript and revised the text to describe only the preservation of ciliary structure/ciliary integrity (lines 227, 245, 256-258, 274-275).

• We thank the reviewer for pointing out the lack of quantitative support for this statement. PKD2L1-positive CSF-cNs are very sparse in the sampled tissue, which has limited the number of cells available for analysis. In the forthcoming experiments, we will make every effort to obtain sufficient sampling across independent animals to quantify the proportion of PKD2L1-positive CSF-cNs bearing identifiable acetylated-tubulin-positive ciliary structures. The final conclusions will be revised in accordance with the experimental evidence. We highlighted these statements that remain subject to revision in red in the manuscript.

• For the State 1/State 2 nomenclature inconsistency between Figures 3 and 4: State 1 and State 2 represent cell states derived from pseudotime analysis, combined with cell-type annotation. Specifically, we defined the ependymal cells at state 1 as “State 1 Ependymal cells” and the astrocytes at state 2 as “State 2 Astrocytes”. We have supplemented this definition at lines 177 and 199 of the manuscript to eliminate ambiguity.

  Major comment 6. The severity of the crush injury needs clarification

The BMS scores in the crush experiments, particularly Figure 5E, appear unexpectedly low. The authors report BMS scores around 2 after complete transection, yet the crush animals show similarly poor recovery at four weeks despite a crush injury normally preserving considerably more spinal cord tissue.

This raises questions about injury severity and reproducibility across the different experiments. The authors should explain why recovery is so limited in the crush controls and provide evidence that the injury was comparable between experimental groups.

This is particularly important because most of the mechanistic experiments in Figures 3-6 rely on the crush model.

Response____：

We thank the reviewer for this important question regarding injury severity and the limited BMS recovery observed in our crush model.

The thoracic crush spinal cord injury was performed using ultra-fine tip forceps to achieve spinal cord transection. During injury induction, the forceps were closed to a gap of 0 mm to achieve complete compression of the spinal cord, yielding a lesion of approximately 0.5 mm in length. Unlike conventional contusion injury, this crush model severs the spinal cord parenchyma, while the injured tissue segment is kept in place without tissue removal. This explains the poor locomotor recovery in crush SCI animals, which resembles the outcome of complete transection. Representative histological evidence of the lesion core after crush injury is provided in Figure S6B. We have supplemented the detailed injury procedure and instrument information in the “Spinal cord injury surgery” subsection of the Methods to clarify this specific crush model (lines 434-439).

Minor comment 1.

The opening statement that "microtubule-stabilizing agents consistently improve functional recovery after SCI" is too strong. The literature is not completely consistent. I suggest "have been reported to improve functional recovery after SCI."

Response____：

We thank the reviewer for this suggestion to moderate the opening statement. We agree that the original claim overstated the consensus in the published literature, as previous studies on microtubule-targeting compounds for SCI are not universally consistent. We have revised the sentence at lines 25–27 to state that “microtubule-modulating compounds have been reported to improve functional recovery after spinal cord injury”, which better reflects the existing literature.

Minor comment 2 and 3.

The description of paclitaxel and epothilones as binding "the taxane pocket within the β-tubulin lumen" is inaccurate. A clearer formulation would be "the taxane-binding pocket on the luminal surface of β-tubulin."

I would therefore revise the full sentence to: "Compounds such as paclitaxel and epothilones, which bind to the taxane-binding pocket on the luminal surface of β-tubulin, have been shown to promote axon regeneration, reduce fibrotic scarring, and improve locomotor outcomes in preclinical models of SCI."

Response____：

We thank the reviewer for correcting the description of the binding site on β-tubulin. We agree that the original wording was imprecise. Following the reviewer’s recommendation, we have updated the sentence to: “Compounds such as paclitaxel and epothilones, which bind to the taxane-binding pocket on the luminal surface of β-tubulin, have been shown to promote axon regeneration, reduce fibrotic scarring, and improve locomotor outcomes in preclinical models of SCI.” (lines 50-52).

Minor comment 4.

The hindlimb range-of-motion analysis in Figure 1 is unusual and relies on manually selected video frames and manually drawn angles. The authors should state whether frame selection and measurements were performed blinded and how reproducibility of this measurement was assessed.

Response____：

We thank the reviewer for this careful comment on the hindlimb range‑of‑motion analysis. All video frame selection and angle measurements for hindlimb range of motion in Figure 1 were performed by researchers blinded to experimental group assignments.

Measurement reproducibility has not yet been formally assessed. To address this, we will have a second blinded observer independently repeat the frame selection and angle measurements for a subset of videos and evaluate agreement between observers. The assessment will include both steps to capture variability arising from manual frame selection as well as angle measurement. The procedure and results will be reported in the fully revised manuscript.

Minor comment 5.

Laminin-positive area alone should not be described as fibrotic scar. Laminin is also present in vascular basement membranes and other ECM structures. Either additional markers should be included or the result should be described as reduced laminin/ECM deposition.

Response____：

We agree that laminin staining alone cannot specifically define fibrotic scar, as laminin also exists in vascular basement membranes and other extracellular matrix structures. In accordance with the reviewer’s suggestion, we have revised the relevant text and replaced statements describing “ECM/fibrotic scarring” with “laminin deposition” at lines 109, 125, 296 and 844.

Minor comment 6.

Increased NeuN-positive cells should be described as increased neuronal presence or survival unless neuronal replacement/neurogenesis is directly demonstrated.

Response____：

We thank the reviewer for this valuable suggestion to refine our description of NeuN-positive cells. We agree that greater NeuN-positive signal alone cannot confirm neuronal replacement or de novo neurogenesis. Following the reviewer’s recommendation, we have revised the corresponding text in the manuscript to describe this finding as “increased neuronal presence” at lines 110-112.

Minor comment 7.

Similarly, an increased proportion of PKD2L1-positive cells does not necessarily demonstrate increased CSF-cN survival. Absolute numbers or densities would provide stronger evidence.

Response____：

We thank the reviewer for this thoughtful comment on the interpretation of PKD2L1-positive cell proportion. We agree that a change in the proportion of PKD2L1-positive cells cannot directly prove improved survival of CSF-cNs. We have revised the manuscript and replaced statements claiming enhanced CSF-cNs survival with descriptions of increased CSF-cNs abundance at lines 188-190, 236, 254, 258-260, 272, 288, 320, 339, 348-350, 356.

Minor comment 8.

The rationale for selecting noscapine for the mechanistic part of the study could be explained more clearly. If CNS accessibility and safety are important reasons, these points should be appropriately referenced and related to the dose used here.

Response____：

We thank the reviewer for suggesting we clarify the rationale for selecting noscapine for mechanistic studies, and we have added this information together with references 13 and 20-22 in the manuscript at lines 94-98.

Minor comment 9.

The use of "chronic phase" for tissue collected three weeks after SCI should be reconsidered or justified.

Response____：

We thank the reviewer for pointing out the ambiguous use of “chronic phase” for tissue harvested at 3 weeks post‑SCI. According to references 1 and 26, secondary injury is categorized into acute (6 months) phases, with distinct pathological characteristics for each stage. The 3-week post-injury time point belongs to the intermediate phase, so we replaced the original “chronic phase” wording throughout the manuscript (lines 131-134, 171 and 823).

Minor comment 10.

The manuscript would benefit from careful editing of the causal language. In several places, association, structural preservation and causal mechanism are presented almost interchangeably. Keeping these concepts separate would make the conclusions clearer and better supported.

Response____：

We thank the reviewer for this suggestion. We will carefully revise the language and conclusions throughout the manuscript in light of the new experimental results, ensuring that all claims remain proportionate to the supporting evidence.

Several mechanistic claims in the preliminary revised manuscript await final coordinated validation through our planned supplementary experiments. These passages are highlighted in red in the main text to flag conclusions subject to revision. Should follow-up data be unavailable, inconclusive, or inconsistent with these interpretations, we will qualify or delete these statements and limit our conclusions to data-supported observations only.

Reviewer 3

Major comment 1.

One of the key conclusions is the CSF-cNs are preserved. Such as is stated: "At 4 weeks after complete transection SCI, CSF-cNs were detected in the noscapine group (Figure S7C), indicating that CSF-cNs may serve as a key responsive neuronal subtype contributing to functional recovery following treatment with Noscapine. We further performed immunostaining for PKD2L1 at 1 week post crush SCI, and the statistical results verified that Noscapine enhanced the survival of CSF-cNs (Figures S7D and S7E)." However, you state that for complete transection, spinal tissue is removed and replaced with a loaded biomaterial; are you referring to neurons adjacent to the lesion site? This should be quite clear. I do believe that the crush model is different, but for the transection, this is hard to understand and also relates to the RNA-seq as well (mentioned below). It could still be preservation from secondary damage, but this should be stated.

Response____：

We thank the reviewer for this thorough and insightful comment regarding the interpretation of CSF cNs signals in the complete transection SCI model. We appreciate the opportunity to clarify the anatomical location of these PKD2L1-positive cells and the biological interpretation of this result.

In Figure S7C, the CSF-cNs detected at 4 weeks post complete transection SCI in the Noscapine-treated group are located within the lesion core. All corresponding immunostaining images were acquired from tissue sections sampled at the lesion core (Figure 5, 6, S7, S8). Although a segment of spinal tissue was removed and substituted with biomaterial in this transection model, residual endogenous cells including CSF-cNs can persist within the lesion core region.

We have supplemented these clarifying statements in the manuscript at lines 185-188 to avoid confusion between the complete transection and crush injury models.

Major comment 2.

In Figure 2E, it is unclear where these pics are taken from; it seems to be adjacent to the biomaterial, as it is unlikely to be in the lesion core where the spinal tissue was removed. Please clarify, as this is quite an important point for this and other statements made.

Response____：

We thank the reviewer for this careful comment regarding the sampling location of images shown in Figure 2E. We apologize that our original description was ambiguous and caused confusion. The tissue sections used for Figure 2E were collected from the lesion core, corresponding to the region marked by the red dashed box in the schematic diagram in Figure 2B. Although part of the spinal tissue was resected and replaced with biomaterial in the complete transection model, this defined lesion-core region still contains residual cells that we assessed by immunostaining. We have clarified this sampling location at lines 110-112 in the manuscript text and figure legend to eliminate ambiguity.

Major comment 3.

In Figure 5, there is a great deal of supportive data, including cilia integrity with functional recovery after crush SCI, especially with the SANT-1 work. Why was axonal regeneration not examined in this SCI model as was done in Figure 2? Is this due to the sectioning of the cords coronally? This should be mentioned in the methods. It should still be possible to see if cilia integrity relates to axonal regeneration and functional recovery, or if it is due to something else. Correlative analysis between the different components or PCA would be helpful here. Additionally, were laminin levels examined here? It would be nice with the SANT-1 work to see if this has an effect on the fibroglial scar.

Response____：

We thank the reviewer for this thoughtful comment and valuable suggestions. We agree that examining axonal regeneration, laminin deposition and fibroglial scar formation in the crush SCI model of Figure 5, together with correlative analyses across multiple readouts, would deepen our mechanistic understanding.

As suggested by other reviewers, to more directly clarify whether ciliary integrity in Foxj1-positive cells is required for Noscapine-mediated functional recovery, we are preparing Foxj1-CreER;Ift88 conditional knockout mice. This genetic strategy enables temporally controlled, cell-specific disruption of ciliogenesis in Foxj1-expressing cells, overcoming the limitation of SANT‑1, which inhibits Smoothened/Hedgehog signaling rather than specifically ablating cilia. After verifying successful disruption of ciliogenesis in the target cell population, we will test Noscapine’s reparative effects in these conditional knockout mice and matched littermate controls using the crush SCI model. These genetic experiments will provide more direct evidence to evaluate the causal contribution of cilia to the repair response. The final conclusions will be revised in accordance with the experimental evidence. We highlighted these statements that remain subject to revision in red in the manuscript.

Major comment 4.

In Figure 6 was BMS not performed? It would be useful to compare to Figure 5 as all the other parameters are quite similar.

Response____：

We greatly appreciate the reviewer’s valuable suggestions. In follow-up experiments, we will perform relevant motor function assessments using the Foxj1-CreER;Ift88 conditional knockout mouse model. The final conclusions will be revised in accordance with the experimental evidence. We highlighted these statements that remain subject to revision in red in the manuscript.

We fully recognize that the absence of functional recovery data limits the conclusions we can draw for this figure. Accordingly, we have revised the Figure 6 title to “Y‑27632 maintains ciliary structural integrity of central canal-associated cells”.

Minor comment 1.

The linear-ordered collagen scaffold (LOCS) was used to span the distance of the removed tissue following the spinal transection. The authors should be clearer about whether 1 mm or 2 mm was removed. In the given span of axonal growth and cell infiltration into this area, it is necessary to know the size and what would be possible in a 4-week timeframe. Further, please provide a picture of the LOCS, as the panels in Figure 2 appear to show channel structure, and knowing its origin is important for understanding the work.

Response____：

We thank the reviewer for this thoughtful and important inquiry regarding the length of resected spinal tissue and the physical characteristics of the LOCS scaffold. This information is indeed critical to interpret the extent of axonal growth and cellular infiltration within the lesion gap over the 4-week experimental window.

The implanted LOCS scaffold, visible in the lower panel of Figure 1A at the injury site, has a length of approximately 1.5 mm, corresponding to the 1.5 mm segment of spinal cord tissue that was resected. The LOCS possesses a channeled structure and remains incompletely degraded at 4 weeks post-injury, which explains why these structures can be observed in the fluorescent images in Figure 2. We have supplemented these details about the resection length, scaffold features and degradation profile in the manuscript for clarity (lines 112-115 and 432).

Minor comment 2.

I am a bit unclear about the use of the Brainbow mice, is this mono- or trans-synaptic tracing? Are the different color specific for different tracts or the primary vs the secondary neuron or completely unspecific?

Response____：

We thank the reviewer for this thoughtful question regarding the Brainbow mouse strategy used in our study.

The Brainbow system labels individual neurons such that each neuron is assigned a distinct color; these colors do not distinguish neuronal subtypes, tracts, or primary versus secondary neurons. Importantly, the Brainbow mouse itself lacks trans synaptic activity. In addition, fluorescent protein expression in the Brainbow system requires Cre recombinase for activation. As shown in Figure 2I and S2, we delivered AAV-hSyn-cre to drive Brainbow fluorescent protein expression, and the trans synaptic property originates from the AAV serotype we employed, rather than the Brainbow mouse strain. We have supplemented these relevant descriptions in the manuscript at lines 116–120.

Minor comment 3.

It is stated that for the whole-cell single-cell RNA sequencing (scRNA-seq), the lesion core is taken, but in these experiments there is a biomaterial in the lesion core, so please state how much material and from exactly where it was taken. It seems unlikely this was only where the biomaterial was placed but also included surrounding tissue involved in secondary damage.

Response____：

We thank the reviewer for this careful and important question regarding the tissue harvesting strategy for our whole-cell single-cell RNA sequencing (scRNA-seq). For scRNA-seq, tissue samples were harvested from the lesion core region containing the implanted LOCS scaffold. The harvested spinal tissue was symmetrically dissected centred on the lesion core, with a total length of approximately 1.5–2 mm. We acknowledge that the harvested samples inevitably contained the adjacent surrounding regions undergoing secondary injury responses. We have added these precise sampling details in the manuscript to clearly define the anatomical region and sampling procedure (lines 547-549).

Minor comment 4.

On page 8 it is written, "intraflagellar transport (Ift122, Ift46)" and later IFT is used in the discussion, but it would be helpful to define it again, as it was hard to remember what this stood for from this reference on page 8.

Response____：

We thank the reviewer for this helpful suggestion regarding the definition of IFT. We agree that redefining the abbreviation in the Discussion will improve readability, since the first mention of intraflagellar transport (Ift122, Ift46) appears earlier on page 9. We have added the full term “IFT (intraflagellar transport)” at its first occurrence within the Discussion section at line 331 to remind readers of this abbreviation.

Minor comment 5.

It is stated that Paclitaxel is injected intraperitoneally; however, it isn't known to cross the BBB, so how was this possible? Please add more details to the methods.

Response____：

We thank the reviewer for this important question regarding the intraperitoneal administration of paclitaxel and its delivery across the blood spinal cord barrier (BSCB). In our study, we used paclitaxel liposome for intraperitoneal injection. While free paclitaxel exhibits limited penetration across the intact blood-spinal cord barrier (BSCB), liposomal formulation improves its tissue delivery profile. Furthermore, spinal cord injury causes substantial disruption of the BSCB at the lesion site, which facilitates extravasation of paclitaxel liposome into the injured spinal parenchyma. We have supplemented these details, including the formulation information and dosing regimen, within the Methods (lines 445-476).

Minor comment 6.

For the thoracic crush SCI, the type of forceps should be mentioned in the methods, as the width will determine the severity and lesion length.

Response____：

We thank the reviewer for this valuable suggestion regarding our thoracic crush spinal cord injury model. The crush injury was performed using ultra-fine tip forceps (Easybio, BE6129; minimal tip width: 0.1 mm). During injury induction, the forceps were closed to a gap of 0 mm to achieve complete compression of the spinal cord, yielding a lesion of approximately 0.5 mm in length. We have added these forceps specifications and injury parameters to the Methods section (lines 433--438).

Minor comment 7.

In Figure 1C to 1D, could you present the data in molarity or concentration (1mM vs 100mg/kg) so it is easier to compare from one panel to the next.

Response____：

We thank the reviewer for this helpful suggestion regarding the units presented in Figure 1C and 1D. We apologize that our original description did not explicitly distinguish the two drug delivery strategies, which caused confusion.

The different units originate from our distinct treatment designs. In Figure 1C, the drug was loaded onto LOCS, so experimental groups were labelled by drug concentration (μM/mM). In Figure 1D, the drug was administered via intraperitoneal injection, with doses reported as body weight based dosage (mg/kg). Given these fundamentally different delivery modes, it is not appropriate to unify them under a single type of unit. To help readers readily interpret this difference, we have added this rationale in the figure legend (lines 819-828).

Minor comment 8.

It is unclear how the number of animals were picked for each experiment, sometimes there are more and sometimes only 3 per group. Was a power analysis performed to determine this? It seems a bit underpowered.

Response____：

We thank the reviewer for this important comment regarding sample size selection across our experiments. We acknowledge the reviewer’s concern that some groups have only n=3 animals, which may appear underpowered.

Sample sizes in our study were selected based on our prior experience with this spinal transection/crush injury model and the expected variability of each assay. For histological measurements, we used at least n=3 per group; for behavioral BMS assessments, we increased the sample size to reduce variability. A formal power analysis was not performed before starting these in vivo experiments, which is a limitation of our work. We have noted this limitation explicitly in the methods at lines 604-609. We have labelled the number of animals (n value) for every experiment within the corresponding figure legends, and we have taken care not to overinterpret our findings.

Minor comment 9.

In Figure 2C, the boxes of the laminin staining are sometimes closer to the edge of the biomaterial and sometimes central; this could have an effect on the analysis. Was there a method for where this box was placed?

Response____：

We thank the reviewer for this careful observation regarding the selection of regions of interest (ROIs) for laminin staining analysis in Figure 2C. The ROIs in Figure 2C simply mark representative regions selected for magnification and visualization, and these boxes **do not define the regions used for quantitative analysis. For the quantitative measurement of laminin-positive area fraction shown in Figure 2D, we analyzed the entire lesion core region. Therefore, the quantification results were not affected by the position of these dashed boxes. We have added this clarification in the figure legend to avoid misinterpretation by readers (809-811).

Minor comment 10.

In Figure 2G, it is unclear where these pics are taken from; are they from the center of the biomaterial or from the edges? The axons don't look linear as the LOCS looked earlier in the figure. Does the LOCS degrade? When? This is important to understand the work shown here.

Response____：

We thank the reviewer for this important question regarding the images shown in Figure 2G. The tissue imaged in Figure 2G was harvested from the center of the biomaterial, corresponding to the area marked by the red dashed box in the schematic diagram (Figure 2B). The implanted LOCS undergoes degradation after injury. However, within our maximum 4-week observation window, the LOCS does not degrade completely. This explains some linearly arranged structures observed in our tissue samples. We have clarified these descriptions at lines 110-115 in the manuscript text to help readers interpret the axonal morphology and tissue architecture.

Minor comment 11.

Is it possible that the Paclitaxel Figure 2J picture on top right is turned upside down? The reason I ask is that the EGFP staining is so strong in what is the caudal region of a full transection, and this seems quite odd 4 weeks after SCI and doesn't really relate to the lesion core, which is where these axons must be coming through to end up on the caudal side.

Response____：

We thank the reviewer for this critical observation regarding the upper-right image in Figure 2J. We apologize for insufficient anatomical orientation description in our original manuscript, which caused confusion.

We have carefully rechecked the original image files of the Paclitaxel group and confirmed that this micrograph was not flipped or rotated upside down. Under our anterograde trans-synaptic tracing strategy, the intense EGFP signal indicates greater axonal transmission across the lesion site. This finding is consistent with previous literature demonstrating that paclitaxel and LOCS treatment effectively promote spinal cord injury recovery. Meanwhile, the paclitaxel group also displayed more nerve fiber signals within the lesion core compared with other treatment groups. We have added a clear explanation of the rostrocaudal orientation in the figure legend to help with understanding (lines 860-862).

Minor comment 12.

In this same Figure 2J, the caudal pics are the neurons that are shown here stained with something, or is this from trans-synaptic staining? Are they lower motoneurons?

Response____：

We appreciate the reviewer’s question about the identity of caudal signals and labelled cells in Figure 2J. No additional markers were used in this panel. Only three fluorescent proteins were detected. Importantly, this tracing strategy cannot distinguish neuronal subtypes. We have supplemented descriptions of the labelling strategy and characteristics of the Brainbow system at lines 116-120 of the manuscript.

Minor comment 13.

I really appreciate the clear marking of the timepoints and timelines in the figures. For Figure 3, the RNA-seq is from the full transection at 2 or 3 weeks. Why were these timepoints chosen? The following immunohistochemistry in the figure is crush SCI at 1 wpi, and while it is a less severe injury, it is unclear to me why this timepoint was chosen for this staining work. Please clarify.

Response____：

We thank the reviewer for this valuable question regarding the selection of time points for scRNA-seq and immunohistochemistry experiments in Figure 3.

For the scRNA-seq experiment, samples from the complete transection SCI model were collected at 2 weeks post-injury to represent the subacute phase and at 3 weeks post-injury as an intermediate phase. These two time points capture the transitional state of cellular responses following spinal cord injury.

For immunohistochemical analysis, we selected the 1-week time point after crush SCI in Figure 3H. This choice was based on the dynamic properties of ependymal cells; at 1 wpi, active cellular dynamics of ependymal cells can be clearly visualized at the histological level. We have clarified the rationale for the selection of injury models and time points in the manuscript (lines 134-135 and 168-170).

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Referee #3

Evidence, reproducibility and clarity

Summary:

Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate).

• Liu et al. in "Ciliary integrity defines a central canal repair checkpoint linking microtubule stabilization to spinal cord regeneration" show new evidence of various microtubular stabilizers directly affecting the integrity of cilia in astrocytes and cerebral spinal fluid contacting neurons (CSF-cNs) that leads to recovery after spinal cord injury. The work includes full transection and crush thoracic SCI models in mice, drug treatments, behavioral and electrophysiological analysis, along with in-depth RNA-seq analysis for mechanistic understanding of targets.

Major comments:

• Are the key conclusions convincing?

For the most part the key conclusions are convincing except for the following points listed below:

1. One of the key conclusions is the CSF-cNs are preserved. Such as is stated: "At 4 weeks after complete transection SCI, CSF-cNs were detected in the noscapine group (Figure S7C), indicating that CSF-cNs may serve as a key responsive neuronal subtype contributing to functional recovery following treatment with Noscapine. We further performed immunostaining for PKD2L1 at 1 week post crush SCI, and the statistical results verified that Noscapine enhanced the survival of CSF-cNs (Figures S7D and S7E)." However, you state that for complete transection, spinal tissue is removed and replaced with a loaded biomaterial; are you referring to neurons adjacent to the lesion site? This should be quite clear. I do believe that the crush model is different, but for the transection, this is hard to understand and also relates to the RNA-seq as well (mentioned below). It could still be preservation from secondary damage, but this should be stated.

2. In Figure 2E, it is unclear where these pics are taken from; it seems to be adjacent to the biomaterial, as it is unlikely to be in the lesion core where the spinal tissue was removed. Please clarify, as this is quite an important point for this and other statements made.

3. In Figure 5, there is a great deal of supportive data, including cilia integrity with functional recovery after crush SCI, especially with the SANT-1 work. Why was axonal regeneration not examined in this SCI model as was done in Figure 2? Is this due to the sectioning of the cords coronally? This should be mentioned in the methods. It should still be possible to see if cilia integrity relates to axonal regeneration and functional recovery, or if it is due to something else. Correlative analysis between the different components or PCA would be helpful here. Additionally, were laminin levels examined here? It would be nice with the SANT-1 work to see if this has an effect on the fibroglial scar.

4. In Figure 6 was BMS not performed? It would be useful to compare to Figure 5 as all the other parameters are quite similar.

5. Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

If the above is addressed then changes are not needed, however if not then claims may need to be adjusted.

• 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.

• 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.

• All requests above are realistic with given samples and would help tie elements together as is stated in the comments.

• Are the data and the methods presented in such a way that they can be reproduced?

With the suggestions made here they should be reproducible.

• Are the experiments adequately replicated and statistical analysis adequate?

As mentioned below it is not clear if a power analysis was done and why some experiments are so low on animals and others higher.

Minor comments:

• Specific experimental issues that are easily addressable.

• The linear-ordered collagen scaffold (LOCS) was used to span the distance of the removed tissue following the spinal transection. The authors should be clearer about whether 1 mm or 2 mm was removed. In the given span of axonal growth and cell infiltration into this area, it is necessary to know the size and what would be possible in a 4-week timeframe. Further, please provide a picture of the LOCS, as the panels in Figure 2 appear to show channel structure, and knowing its origin is important for understanding the work.

• I am a bit unclear about the use of the Brainbow mice, is this mono- or trans-synaptic tracing? Are the different color specific for different tracts or the primary vs the secondary neuron or completely unspecific?

• It is stated that for the whole-cell single-cell RNA sequencing (scRNA-seq), the lesion core is taken, but in these experiments there is a biomaterial in the lesion core, so please state how much material and from exactly where it was taken. It seems unlikely this was only where the biomaterial was placed but also included surrounding tissue involved in secondary damage.

• On page 8 it is written, "intraflagellar transport (Ift122, Ift46)" and later IFT is used in the discussion, but it would be helpful to define it again, as it was hard to remember what this stood for from this reference on page 8.

• It is stated that Paclitaxel is injected intraperitoneally; however, it isn't known to cross the BBB, so how was this possible? Please add more details to the methods.

• For the thoracic crush SCI, the type of forceps should be mentioned in the methods, as the width will determine the severity and lesion length.

• In Figure 1C to 1D, could you present the data in molarity or concentration (1mM vs 100mg/kg) so it is easier to compare from one panel to the next.

• It is unclear how the number of animals were picked for each experiment, sometimes there are more and sometimes only 3 per group. Was a power analysis performed to determine this? It seems a bit underpowered.

• In Figure 2C, the boxes of the laminin staining are sometimes closer to the edge of the biomaterial and sometimes central; this could have an effect on the analysis. Was there a method for where this box was placed?

• In Figure 2G, it is unclear where these pics are taken from; are they from the center of the biomaterial or from the edges? The axons don't look linear as the LOCS looked earlier in the figure. Does the LOCS degrade? When? This is important to understand the work shown here.

• Is it possible that the Paclitaxel Figure 2J picture on top right is turned upside down? The reason I ask is that the EGFP staining is so strong in what is the caudal region of a full transection, and this seems quite odd 4 weeks after SCI and doesn't really relate to the lesion core, which is where these axons must be coming through to end up on the caudal side.

• In this same Figure 2J, the caudal pics are the neurons that are shown here stained with something, or is this from trans-synaptic staining? Are they lower motoneurons?

• I really appreciate the clear marking of the timepoints and timelines in the figures. For Figure 3, the RNA-seq is from the full transection at 2 or 3 weeks. Why were these timepoints chosen? The following immunohistochemistry in the figure is crush SCI at 1 wpi, and while it is a less severe injury, it is unclear to me why this timepoint was chosen for this staining work. Please clarify.

• Are prior studies referenced appropriately?

The references are quite well done in the manuscript.

• Are the text and figures clear and accurate?

Overall, the figures and text are clear except where stated above.

• Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

Stated above.

Referees cross-commenting

In general, I agree with the other reviewers, but most strongly, my oversight of the statistical analysis that was laid out by Reviewer #2 should be carefully considered by the authros to address the type of analysis as well as the biological and technical replicates. I had asked if a power analysis was performed as the number of samples in groups seems to be low and underpowered. This new analysis could change the outcome of the results and would require a change in the presentation of data in the manuscript. Further, I agree that laminin alone is not fibrotic scarring and should be stated as laminin/ECM. As I mentioned, the GFAP glial scar should also be examined. Reviewer #1 states that ciliary structure and ciliary function should not be confused, and I agree that the authors are discussing ciliary structure here, not function and should ensure this is conveyed correctly. Overall, I agree with the other two reviewers who have laid out their opinions in a clear and logical manner that should be addressed by the authors.

Significance

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.

• This work shows that microtubule stabilizers can work in multiple ways and we may have not fully understood their full mechanistic abilities and this should be further examined.

• Place the work in the context of the existing literature (provide references, where appropriate).

• Typically microtubule stabilizers are thought to work directly on the tubulin of long descending or ascending axonal tracts and not on other neurons within the region that may have an effect that also contributes to functional recovery.

• State what audience might be interested in and influenced by the reported findings.

• This will influence those in the spinal cord injury and neuroregeneration field.

• Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.

• My background is in spinal cord injury, neuroregeneration, biomaterials and microtubule stabilizers. Although I am not an expert in bioinformatics, I have enough of a background to evaluate the findings.

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Referee #2

Evidence, reproducibility and clarity

SUMMARY:

Lin et al. investigate whether structurally distinct microtubule-targeting compounds converge on a common mechanism promoting repair after spinal cord injury (SCI). Using complete thoracic transection and crush SCI models in mice, the authors first compare several microtubule-modulating compounds, including noscapine, paclitaxel, epothilone D, TPI-287 and TTI-237, and subsequently focus primarily on noscapine. The study combines behavioral and electrophysiological assessment, histology, Brainbow/AAV-based tracing, single-cell RNA sequencing, and analysis of ciliary structures in spinal cord tissue and cultured hTERT-RPE1 cells.

The authors report that several microtubule-targeting compounds improve locomotor outcomes and that noscapine and paclitaxel reduce laminin deposition and increase neuronal and axonal markers within the lesion. Single-cell analysis identifies changes in central canal-associated populations, particularly ependymal cells and cerebrospinal fluid-contacting neurons (CSF-cNs), accompanied by alterations in ciliogenesis-associated transcriptional programs. Noscapine increases the proportion of cells displaying ciliary structures after SCI and promotes ciliation in cultured RPE1 cells. Finally, pharmacological inhibition of Smoothened with SANT-1 attenuates several effects of noscapine, while the ROCK inhibitor Y-27632 increases ciliation and reproduces some of the cellular phenotypes associated with noscapine treatment.

On this basis, the authors propose that preservation of ciliary integrity within a central canal-associated regenerative niche represents a common structural checkpoint connecting microtubule stabilization with spinal cord repair and functional recovery.

The association between microtubule modulation and ciliary structures in central canal-associated cells is interesting and potentially novel. However, substantial concerns regarding the statistical analyses, experimental controls and causal interpretation currently prevent several of the principal conclusions from being firmly supported. In particular, the statistical framework described in the manuscript is inappropriate for many of the experimental designs. Because statistical significance forms the basis for a large proportion of the reported treatment effects and subsequent mechanistic conclusions, the entire quantitative dataset requires reanalysis before the robustness of many of the claims can be assessed. In addition, the pharmacological experiments with SANT-1 and Y-27632 do not selectively manipulate cilia and therefore cannot demonstrate that ciliary integrity is necessary or sufficient for recovery.

MAJOR COMMENTS:

1. The statistical analysis needs to be revised throughout the manuscript This is my main concern, as it may affect many of the conclusions in the paper. The Methods state that two-tailed Student's t-tests were used, but many experiments have designs for which pairwise t-tests are not appropriate. Examples include the multi-group screen in Figure 1C, longitudinal BMS measurements, experiments with three or four groups, the factorial Noscapine × SANT-1 experiment, and measurements of multiple cells or cilia from the same biological replicate. Figure 1C requires an omnibus test followed by corrected post-hoc comparisons. Repeated pairwise t-tests across so many groups increase the risk of false-positive results, particularly given the small and unequal sample sizes. BMS measurements are longitudinal and should be analysed using a repeated-measures or mixed-effects model that accounts for animal and time. Similarly, Figure 5 is a 2 × 2 design, and the claim that SANT-1 attenuates the effect of noscapine requires testing the Noscapine × SANT-1 interaction. Showing that one comparison is significant and another is not is not sufficient. There is also a risk of pseudoreplication. For example, Figure 4 reports measurements from 100 individual cilia per treatment, but individual cilia from the same experiment are not independent biological replicates. The analysis should either use replicate-level values or account for the nested structure of the data. For each experiment, the authors should also clearly report the biological n, technical/cellular replicates, randomization, blinding, exclusion criteria, statistical test and multiple-comparison correction. I consider a full statistical reanalysis essential before the quantitative conclusions of the manuscript can be properly evaluated. Importantly, the conclusions throughout the manuscript should then be revised according to the outcome of this reanalysis.

2. Appropriate vehicle and baseline controls are missing or unclear in several experiments The control groups need to be clarified throughout the paper. In Figures 1D-I, the relevant comparison for showing a noscapine effect is vehicle versus noscapine, rather than untreated control versus noscapine. More importantly, several crush experiments appear to lack a vehicle-treated SCI group. For example, Figures 3H-I compare uninjured, crush SCI and crush + noscapine animals, but there is no crush + vehicle group. If noscapine is administered in a vehicle with possible biological effects, untreated SCI is not an adequate control. The vehicle group should be shown if it was performed. Figures 4C-D would also benefit from an uninjured baseline. Crush versus crush + noscapine shows a treatment-associated difference in ciliation, but without baseline values it is difficult to conclude that noscapine preserves normal ciliation rather than simply increasing it after injury. The paclitaxel experiment in Figure S8 is also unclear. The manuscript appears to use saline-treated animals as controls, but conventional paclitaxel is poorly soluble in saline. Since both paclitaxel and paclitaxel liposomes are listed in the Methods, the authors should clarify which formulation was used and what the corresponding vehicle control was. More generally, formulation, vehicle, dose, route and treatment duration should be clearly reported for every drug.

3. The current pharmacological experiments do not establish that cilia mediate the effects of noscapine This is the main mechanistic issue in the manuscript. Figure 5 is entitled "Ciliary integrity is required for the functional recovery mediated by Noscapine." However, SANT-1 is a Smoothened antagonist that blocks Hedgehog signaling; it is not a specific tool to remove or disrupt cilia. Hedgehog signaling can itself affect proliferation, differentiation, inflammation, survival and tissue repair. Therefore, the fact that SANT-1 reduces ciliation and attenuates some noscapine-associated effects does not show that these effects are caused by loss of cilia. It shows that the response to noscapine is sensitive to Smoothened/Hedgehog inhibition. The Y-27632 experiment has the same problem in the opposite direction. Y-27632 is a ROCK inhibitor with well-established effects on axonal growth, astrocytes and scar formation after SCI. Therefore, the observation that Y-27632 increases ciliation and reproduces some noscapine-associated phenotypes does not demonstrate that increased ciliation is responsible for these effects. Both could simply be parallel effects of ROCK inhibition. This also leaves open an alternative explanation for the overall findings: cilia may be better preserved because noscapine reduces tissue damage, rather than cilia preservation being the mechanism that drives repair. For this reason, the current data support an association between ciliary preservation and improved outcome, but do not establish that cilia are necessary or sufficient for recovery. Statements such as "ciliary integrity is required," "critical structural dependency," "structural checkpoint" and "cilia-dependent regenerative niche" should therefore be toned down. Interestingly, the authors themselves state in the Discussion that cell-specific genetic approaches such as Foxj1-CreER with Ift88/Kif3a would be needed to test ciliary necessity. I agree. If the authors wish to retain the strong causal conclusions, such an experiment would be required. Otherwise, the claims should be revised to reflect the current pharmacological evidence. Figure 6 should also be retitled, as it refers to regulation of "functional recovery" even though no behavioral or electrophysiological endpoint is shown.

4. The data do not yet support a shared cilia-dependent mechanism across all microtubule-targeting compounds Figure 1 screens noscapine, epothilone D, TPI-287, TTI-237 and paclitaxel, and the authors suggest that these drugs converge on a common downstream mechanism. However, the only common outcome examined across all compounds is locomotor performance. Scar formation, axonal growth and ciliation are not studied across the full panel. The cilia experiments are mainly performed with noscapine and, to a lesser extent, paclitaxel. The data may therefore support a shared response between these two drugs, but they do not establish a "unifying" mechanism across all five compounds. It is also unclear why the other compounds are included in the initial screen if they are not followed up mechanistically. The terminology should also be more precise. Paclitaxel and epothilones are classical microtubule stabilizers, whereas noscapine mainly suppresses microtubule dynamics and does not act in the same way. I suggest using "microtubule-modulating compounds" when referring to the drugs collectively. Finally, the Results state that the compounds reduce EB1-positive comet density "in vivo," whereas the Methods describe this experiment in HeLa cells. This should be corrected. Reduced EB1 comet density also indicates reduced growing microtubule plus ends, but does not by itself prove equivalent microtubule stabilization by all compounds.

5. Ciliary structure and ciliary function should be clearly separated Figure 4 contains some of the most interesting data in the study, but the conclusions go beyond what was measured. The authors show changes in cilium number, cilium length and ciliary markers, but they do not directly measure ciliary function. There are no measurements of ciliary beating, CSF flow, cilia-dependent signaling, mechanosensory responses or PKD2L1-dependent function in CSF-cNs. Therefore, statements about preserved CSF flow, environmental sensing, lineage competence or "ciliary function" are speculative. The manuscript should refer to ciliary structure, architecture or integrity unless a functional readout is provided. In Figure 4F, the authors also state that a greater proportion of CSF-cNs retain intact cilia after noscapine treatment, but I could not identify a corresponding quantitative analysis. This result should be quantified at the biological-replicate level. The State 1/State 2 nomenclature also appears inconsistent between Figures 3 and 4 and should be clarified.

6. The severity of the crush injury needs clarification The BMS scores in the crush experiments, particularly Figure 5E, appear unexpectedly low. The authors report BMS scores around 2 after complete transection, yet the crush animals show similarly poor recovery at four weeks despite a crush injury normally preserving considerably more spinal cord tissue. This raises questions about injury severity and reproducibility across the different experiments. The authors should explain why recovery is so limited in the crush controls and provide evidence that the injury was comparable between experimental groups. This is particularly important because most of the mechanistic experiments in Figures 3-6 rely on the crush model.

MINOR COMMENTS:

1. The opening statement that "microtubule-stabilizing agents consistently improve functional recovery after SCI" is too strong. The literature is not completely consistent. I suggest "have been reported to improve functional recovery after SCI."

2. The description of paclitaxel and epothilones as binding "the taxane pocket within the β-tubulin lumen" is inaccurate. A clearer formulation would be "the taxane-binding pocket on the luminal surface of β-tubulin."

3. I would therefore revise the full sentence to: "Compounds such as paclitaxel and epothilones, which bind to the taxane-binding pocket on the luminal surface of β-tubulin, have been shown to promote axon regeneration, reduce fibrotic scarring, and improve locomotor outcomes in preclinical models of SCI."

4. The hindlimb range-of-motion analysis in Figure 1 is unusual and relies on manually selected video frames and manually drawn angles. The authors should state whether frame selection and measurements were performed blinded and how reproducibility of this measurement was assessed.

5. Laminin-positive area alone should not be described as fibrotic scar. Laminin is also present in vascular basement membranes and other ECM structures. Either additional markers should be included or the result should be described as reduced laminin/ECM deposition.

6. Increased NeuN-positive cells should be described as increased neuronal presence or survival unless neuronal replacement/neurogenesis is directly demonstrated.

7. Similarly, an increased proportion of PKD2L1-positive cells does not necessarily demonstrate increased CSF-cN survival. Absolute numbers or densities would provide stronger evidence.

8. The rationale for selecting noscapine for the mechanistic part of the study could be explained more clearly. If CNS accessibility and safety are important reasons, these points should be appropriately referenced and related to the dose used here.

9. The use of "chronic phase" for tissue collected three weeks after SCI should be reconsidered or justified.

10. The manuscript would benefit from careful editing of the causal language. In several places, association, structural preservation and causal mechanism are presented almost interchangeably. Keeping these concepts separate would make the conclusions clearer and better supported.

Significance

GENERAL ASSESSMENT:

The main strength of this study is the unexpected link between microtubule-modulating treatments and ciliary architecture in central canal-associated cells after SCI. The focus on ependymal cells and CSF-contacting neurons is interesting, as these populations are still relatively understudied in spinal cord repair. The combination of pharmacology, two SCI models, transcriptomics, histology and functional analyses is also a strength.

The main limitation is that the manuscript presents the role of cilia as more mechanistically established than the data currently support. The experiments show a clear association between ciliary preservation and better outcomes, but the SANT-1 and Y-27632 experiments do not specifically manipulate cilia and therefore cannot establish that cilia are the causal link between microtubule modulation and recovery.

A second major concern is the statistical analysis. Inappropriate tests are used in several key experiments, including the compound screen, longitudinal behavioral measurements, factorial experiments and nested cellular data. Until these datasets are reanalysed appropriately, it is difficult to know how robust many of the quantitative conclusions are.

If the main findings remain significant after reanalysis and the causal claims are toned down, I think the link between microtubule modulation, central canal-associated cells and ciliary preservation could represent an interesting contribution to the field.

ADVANCE:

The beneficial effects of paclitaxel and epothilones on scarring, axonal growth and functional recovery after experimental SCI have already been reported. The main advance here is therefore not that microtubule-targeting compounds can improve SCI outcome.

The more novel aspect is the connection between microtubule modulation and ciliary architecture in central canal-associated cells, particularly ependymal cells and CSF-cNs. The use of noscapine in traumatic SCI also appears relatively unexplored.

At present, I would consider this mainly a conceptual and hypothesis-generating advance. The study points to a potentially important connection between microtubule dynamics and central canal/ciliary biology after SCI, but a causal role for cilia in recovery remains to be demonstrated.

AUDIENCE:

The study should be of interest to researchers working on spinal cord injury, CNS repair and regeneration, cytoskeletal biology, ependymal cells, cilia and CSF-contacting neurons.

It may also be relevant to researchers studying other forms of CNS injury in which cytoskeletal changes and ciliary alterations occur. At this stage, I see the main audience as basic and preclinical researchers, with possible longer-term translational relevance.

REVIEWER EXPERTISE:

Field of expertise: spinal cord injury; CNS injury and regeneration; zebrafish models.

My expertise covers experimental models and mechanisms of CNS injury and repair, including evaluation of experimental design and cellular responses. I do not have specialist expertise in cilia biology or structural microtubule pharmacology, so my assessment of those aspects focuses mainly on experimental design, causal interpretation and their relevance to CNS injury.

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Referee #1

Evidence, reproducibility and clarity

Lin et al. investigate how microtubule-stabilizing treatments promote recovery after spinal cord injury (SCI), with a particular focus on ciliary structures in cells associated with the central canal. Using mouse complete transection and crush SCI models, the authors first compare several structurally distinct microtubule-targeting compounds and report improved locomotor recovery across treatments. They then focus primarily on Noscapine and combine behavioral and electrophysiological assessment, histology, Brainbow-based neuronal tracing, and single-cell RNA sequencing. Noscapine and Paclitaxel are associated with reduced Laminin-positive signal at the lesion, increased neuronal and axonal markers, and greater anatomical continuity across the injured region. Single-cell analysis identifies ependymal cells and cerebrospinal fluid-contacting neurons (CSF-cNs) as prominent populations responding to Noscapine treatment.

Further analyses show increased cilia-associated transcriptional programs and preservation of ciliary structures in ependymal cells and CSF-cNs following Noscapine treatment, with similar effects observed following Paclitaxel treatment. The authors additionally report an increase in GFAP/Foxj1 double-positive cells and preservation of PKD2L1-positive CSF-cNs. Pharmacological inhibition of Smoothened signaling with SANT-1 partially attenuates several Noscapine-associated cellular and behavioral effects, whereas treatment with the ROCK inhibitor Y-27632 promotes ciliogenesis and reproduces several of the cellular phenotypes observed with Noscapine. Based on these findings, Lin et al. propose that preservation of ciliary integrity within a central canal-associated niche contributes to the beneficial effects of microtubule stabilization during spinal cord repair.

Major comments:

1. Ciliary integrity is not yet established as the causal or unifying mechanism of microtubule-stabilizer-mediated recovery

A central conclusion of the manuscript is that preservation of ciliary integrity represents a shared structural checkpoint linking microtubule stabilization to spinal cord repair. The data clearly show that Noscapine treatment is associated with preservation of ciliary structures in ependymal cells and CSF-cNs, and that Paclitaxel produces similar cellular effects. However, I do not think the current experiments are sufficient to establish cilia as the causal mechanism underlying the functional benefits of these treatments. In particular, SANT-1 is a Smoothened antagonist and therefore interferes with Hedgehog/Smoothened signaling rather than specifically ablating cilia. Consequently, the partial loss of Noscapine-mediated recovery following SANT-1 treatment could reflect disruption of Hedgehog signaling rather than a specific requirement for ciliary structure. Conversely, Y-27632 is a ROCK inhibitor with broad effects on cytoskeletal organization and has previously been reported to improve recovery after SCI through cilia-independent mechanisms. Thus, while these pharmacological experiments are consistent with a contribution of cilia, they do not by themselves demonstrate that ciliary preservation is required for Noscapine-mediated repair.

The most direct way to test this model would be a temporally controlled genetic disruption of ciliogenesis in the relevant central canal-associated population, for example using the Foxj1-CreER;Ift88/Kif3a strategy already proposed by the authors, followed by assessment of whether Noscapine can still promote recovery. This would provide the strongest test of the central mechanistic claim, although it would represent a substantial experiment requiring several months depending on mouse-line availability. More tractable alternatives could nevertheless considerably strengthen the current evidence. First, the authors could test whether ciliary preservation is reproduced across the full panel of microtubule-targeting compounds used in the initial screen. At present, five compounds are used to support cross-chemotype convergence in functional recovery, whereas ciliary preservation is examined mainly for Noscapine and Paclitaxel. Demonstrating that Epothilone D, TPI-287 and TTI-237 similarly preserve ependymal and/or CSF-cN cilia would provide much stronger support for ciliary preservation as a shared downstream response. Second, if an appropriate primary spinal-cord ependymal or related culture system is available, genetic disruption of ciliogenesis through IFT88 or KIF3A depletion could be used to determine whether Noscapine-associated cellular effects are lost when ciliogenesis is impaired. Such an orthogonal genetic experiment would directly complement the current pharmacological evidence and could likely be completed within several weeks to a few months. Neither alternative would fully establish that ependymal cilia are necessary for functional recovery in vivo, but together they would substantially strengthen the proposed mechanism. If additional experiments are not feasible, the authors should instead moderate statements describing ciliary integrity as "required," a "shared structural checkpoint," or a "unifying downstream dependency," and restrict the conclusion to the evidence that microtubule stabilization is associated with ciliary preservation and that cilia-associated pathways may contribute to recovery.

1. Several conclusions extend beyond the experimental readouts Several conclusions throughout the manuscript appear broader than the experimental readouts used to support them. I think these points should be addressed individually, either by providing additional quantitative analysis where this can reasonably be performed on existing material, or by revising the wording so that the conclusions more closely reflect what was directly measured.

a. Glial and fibrotic scarring. In the Abstract, the authors state that maintenance of ciliary architecture is associated with "reduced glial scarring" (line 31). However, the main quantitative assessment of scarring in Figure 2 is based on Laminin-positive area, which is described as evidence of reduced "ECM/fibrotic scarring" (lines 103-107). GFAP staining is shown, but glial scar formation itself does not appear to be qualitatively or quantitatively assessed. The claim of reduced glial scarring should therefore either be supported by further histological analysis (H&E staining, antibody staining for various ECM component, superficy of scar measurement and so on) or removed. Similarly, reduced Laminin deposition is consistent with altered ECM/fibrotic remodeling, but Laminin alone provides a relatively limited assessment of the fibrotic scar. If the authors wish to maintain the broader claim of reduced fibrotic scarring, additional characterization of the fibrotic compartment would strengthen this conclusion; otherwise, "reduced Laminin deposition" would more precisely describe the result.

b. Tissue continuity and circuit continuity. The Abstract states that treatment results in "improved tissue continuity" (line 31), but I could not identify a direct quantitative assessment of tissue continuity or lesion bridging. Figure 2 instead shows increased NeuN and SMI-312 labeling and Brainbow-positive "axon-like" or "tract-like" structures that appear to extend across the lesion (lines 107-115). The Results then conclude that these findings provide "structural substrates for cross-lesion circuit continuity" (lines 116-118). These anatomical observations are interesting, but they do not directly demonstrate tissue continuity or functional circuit reconstruction. If tissue continuity is an important outcome, a quantitative measurement of lesion/bridge dimensions could potentially be performed using the existing histological material. The Brainbow findings should otherwise be described as evidence of anatomical fiber continuity across the lesion rather than circuit continuity, unless additional evidence of synaptic or functional connectivity is provided.

c. Ciliary structure versus ciliary function. The authors directly demonstrate preservation of ciliary morphology, including a greater proportion of ciliated ependymal cells, more continuous ciliary arrays, increased cilia-associated gene expression, and increased ciliation in RPE-1 cells (lines 198-214). However, they subsequently conclude that Noscapine "protects ciliary structure and function" and suggest that this preservation maintains CSF flow, environmental sensing, and lineage competence (lines 215-218). None of these physiological functions are directly measured. This distinction is particularly clear because the authors themselves state in the Discussion that measurements of ciliary beat coordination, CSF flow, and IFT dynamics will be required to link structural preservation to physiological function (lines 337-340). I therefore suggest consistently referring to preservation of ciliary structure or ciliation rather than ciliary function unless functional measurements are added.

d. CSF-cN survival. The manuscript repeatedly describes Noscapine as enhancing or preserving CSF-cN survival. For example, lines 175-179 state that PKD2L1 immunostaining "verified that Noscapine enhanced the survival of CSF-cNs," and similar language is used for Paclitaxel and SANT-1 experiments (lines 224-225 and 246-249). However, the presented readout appears to be the abundance or proportion of PKD2L1-positive cells at individual time points rather than a direct assessment of cell survival or cell death. The increased abundance of PKD2L1-positive cells is consistent with enhanced preservation of CSF-cNs but does not directly demonstrate increased survival. This conclusion could be strengthened relatively straightforwardly by assessing cell death specifically within PKD2L1-positive CSF-cNs, for example using TUNEL and/or cleaved caspase-3 staining at an appropriate early post-injury time point. Alternatively, the authors should describe the result as increased preservation or abundance of PKD2L1-positive CSF-cNs rather than enhanced survival.

1. The proposed ependymal-to-astrocyte differentiation is not directly demonstrated

A second important component of the proposed central canal repair mechanism is that Noscapine promotes differentiation of ependymal cells toward a reparative astrocytic state. This conclusion is mainly based on the decrease in ependymal cells and increase in astrocytes between 2 and 3 wpi, Monocle pseudotime trajectories connecting these populations, and the increased proportion of GFAP^+Foxj1^+ cells following Noscapine treatment (lines 149-165). While these observations are consistent with a relationship between ependymal and astrocytic states, they do not demonstrate a lineage transition. Pseudotime analysis orders transcriptionally related cell states but cannot establish the developmental origin of individual cells, and GFAP expression in Foxj1^+ cells could alternatively reflect activation or phenotypic changes within ependymal cells rather than their differentiation into astrocytes. Nevertheless, the manuscript subsequently refers to "lineage progression," "lineage-associated transition," and the emergence of ependymal cell-associated astrocytes as a component of the proposed mechanism (lines 180-183, 241-246, 303-305 and 327-329). The authors appropriately acknowledge at lines 163-165 that formal demonstration of an ependymal-to-astrocyte transition would require lineage tracing, but the stronger lineage interpretation is retained elsewhere in the Results and Discussion. The most direct way to address this point would be lineage tracing of Foxj1-expressing ependymal cells, for example using a temporally controlled Foxj1-CreER reporter activated before injury, followed by SCI {plus minus} Noscapine and assessment of whether labeled progeny acquire astrocytic identity. This would provide a clear test of whether Noscapine truly increases ependymal-derived astrocyte formation and would likely require several months depending on mouse-line availability. If such an experiment is beyond the scope of revision, I do not think an entirely new lineage-tracing study should necessarily be required. Instead, the authors should consistently limit their interpretation to what is directly supported-for example, that Noscapine is associated with an increased GFAP^+Foxj1^+ population and with transcriptional states connecting ependymal and astrocytic populations-rather than presenting these observations as demonstrated ependymal-to-astrocyte differentiation. Additional computational approaches such as RNA velocity could provide supporting evidence for directional state transitions, but would still not substitute for lineage tracing.

Minor comments:

1. Statistical analysis should be reconsidered for several experiments. The Methods state that two-tailed Student's t-tests were used for statistical comparisons (lines 544-551). This does not appear appropriate for several datasets, particularly the longitudinal BMS measurements, experiments containing more than two groups, and repeated measurements at 4 and 8 wpi. The authors should clarify the statistical test used for each comparison and account for repeated measurements and multiple comparisons where appropriate. The experimental unit should also be clearly defined. For example, in the RPE-1 cilia-length experiments, individual cilia should not necessarily be considered independent biological replicates when multiple cilia are measured from the same culture or experiment.

2. The biological replication and sample structure of the single-cell RNA-seq experiment should be described explicitly. The manuscript states that 51,117 cells were retained across the conditions analyzed at 2 and 3 wpi, but it is unclear how many independent animals contributed to each condition, whether spinal cords were pooled before library preparation, and how many independent sequencing libraries were generated per group (lines 123-128). The authors should report the number of biological replicates per condition, the number of animals contributing to each replicate, and whether samples from different animals were processed independently or pooled.

3. Statistical inference from the single-cell dataset should account for biological replication. The manuscript reports substantial differences in cell composition, including a reduction of microglia from >60% of recovered cells in control samples to <5% following Noscapine treatment at 3 wpi, as well as changes in fibroblast and neurocyte populations (lines 129-137). However, the Methods describe differential-expression analysis using Seurat FindAllMarkers without indicating whether replicate-aware or pseudobulk approaches were used for comparisons between experimental groups (lines 527-543). Individual cells derived from the same animal or library should not be treated as independent biological replicates. The authors should clarify the statistical framework used for differential-expression and cell-composition analyses and, where sufficient replication is available, account for inter-replicate variability. If biological replication is insufficient, these comparisons should be presented as descriptive or exploratory.

4. Several in vivo drug-treatment details required for reproducibility are missing. The Methods state that mice received daily injections of saline, Noscapine, Paclitaxel or SANT-1 after crush injury, but the in vivo dose, vehicle and formulation are not clearly provided for all compounds. In addition, Y-27632 is not included in this treatment description despite being used in Figure 6 (lines 424-428). The dose, vehicle, injection route, treatment duration, and timing relative to injury should be explicitly reported for each pharmacological treatment.

5. The administration strategy used in the initial microtubule-stabilizer screen should be clarified. Figure 1C reports concentrations in µM and describes microtubule stabilizers in combination with the LOCS, whereas later Noscapine experiments use systemic treatment in mg/kg (lines 755-766). It should be made clear which compounds were locally delivered through the scaffold, which were systemically administered, and how the concentrations used for the different compounds were selected.

6. The description of the EB1 experiment appears inconsistent between the Results and Methods. The Results state that all five compounds reduced EB1-positive comet density "in vivo" (lines 88-90). However, the Methods describe treatment of HeLa cells with these compounds specifically to assess microtubule dynamics (lines 385-392). The authors should clarify whether the EB1 experiment was performed in vivo or in vitro and correct the corresponding text.

7. The title of Figure 6 overstates the experiment presented. Figure 6 is entitled "Ciliary integrity is a key factor in regulating the functional recovery from SCI," yet the figure assesses ciliation, GFAP/Foxj1-positive cells, and PKD2L1-positive CSF-cNs and does not include a functional recovery measurement (lines 872-892). Unless functional data are added, the title should be revised to reflect the cellular phenotypes actually examined.

8. Randomization, blinding, sample-size determination and exclusion criteria should be reported more completely. The authors appropriately state that BMS scoring was performed by two observers blinded to experimental groups (lines 429-432). However, it is unclear whether animals were randomized to treatment groups, whether histological quantification was performed blinded, how sample sizes were determined, or whether any animals or samples were excluded from analysis. These details should be provided.

9. The exclusive use of young female mice should be acknowledged as a limitation. All experiments were performed using 6-8-week-old female C57BL/6J mice (lines 350-354). This does not invalidate the findings, but given the translational framing of the manuscript, the authors should briefly acknowledge that possible sex- and age-dependent differences in treatment response were not evaluated.

10. Availability of processed single-cell data and analysis code would improve reproducibility. The raw sequencing data are deposited, but several downstream analyses are described as being performed using "custom R scripts" (lines 534-543). Providing the processed Seurat object, cell annotations and relevant analysis scripts would make the single-cell results considerably easier to reproduce and independently evaluate.

Significance

The study realized by Lin et al. presents an ambitious and generally well-structured body of work examining how microtubule-stabilizing treatments influence spinal cord repair, with a particular focus on ciliary preservation in ependymal cells and CSF-contacting neurons. A major strength of the manuscript is the wide range of its experimental approach, combining several microtubule-targeting compounds, complete transection and crush injury models, behavioral and electrophysiological measurements, histology, neuronal tracing, and single-cell RNA sequencing. The identification of central canal-associated cells as prominent responders to Noscapine, together with the observation that both Noscapine and Paclitaxel preserve ciliary structures, is interesting and provides a potentially valuable direction for understanding how microtubule-targeting therapies influence the injured spinal cord beyond their direct effects on axons. The main limitation is that several conclusions currently go beyond what is directly demonstrated. In particular, the data support an association between microtubule stabilization, ciliary preservation, and improved recovery, but do not yet establish ciliary integrity as the causal or unifying mechanism underlying these effects. The pharmacological approaches used to manipulate cilia-associated processes have broader biological actions, and a more specific genetic manipulation of ciliogenesis in the relevant cell populations would substantially strengthen this conclusion. More generally, some relatively limited readouts are used to support broader claims, for example Laminin staining as evidence of fibrotic scarring, GFAP/Foxj1 co-expression as evidence of ependymal-to-astrocyte differentiation, and anatomical fiber continuity as evidence of circuit reconstruction. The study would therefore benefit either from additional experiments directly addressing these processes or from a more cautious interpretation that remains closer to the measurements performed.

The beneficial effects of microtubule stabilization after SCI are already well established. Hellal et al. showed that moderate microtubule stabilization can reduce lesion-associated scarring while promoting axonal regeneration, and Ruschel et al. later demonstrated that systemic Epothilone B treatment promotes axon regeneration and functional recovery after SCI. More recently, Bodakuntla et al. provided a detailed structural mechanism showing how Epothilone B directly stabilizes microtubules at injured axon tips to support regenerative growth. The main advance of Lin et al. is therefore not the demonstration that microtubule stabilization improves recovery, but rather the proposal that these treatments may also act through preservation of ciliary architecture in central canal-associated cells.

References: - Hellal F. et al. Microtubule stabilization reduces scarring and causes axon regeneration after spinal cord injury. Science 331, 928-931 (2011). Ruschel J. et al. Systemic administration of epothilone B promotes axon regeneration after spinal cord injury. Science 348, 347-352 (2015). - Bodakuntla S. et al. In situ structural mechanism of epothilone-B-induced CNS axon regeneration. Nature 648, 477-487 (2025).

Ciliary biology has also previously been linked to spinal cord injury and regeneration. Ribeiro et al. showed that foxj1a-expressing ependymal cells are activated during zebrafish spinal cord regeneration, providing an earlier connection between central canal-associated cells, ciliary biology and regenerative responses. More recently, Zhang et al. provided direct genetic evidence that TTBK2-dependent ciliogenesis contributes to neuronal survival, axonal regeneration and functional recovery after mammalian SCI. In this context, the potentially novel aspect of Lin et al. is the connection between microtubule-stabilizing treatment and preservation of ciliary structures specifically in ependymal cells and CSF-cNs. This represents an interesting conceptual and potentially mechanistic extension of the existing literature, although a direct demonstration that ciliary preservation in these populations contributes to recovery would be needed to fully establish that mechanistic advance.

References:

• Ribeiro A. et al. Foxj1a is expressed in ependymal precursors, controls central canal position and is activated in new ependymal cells during regeneration in zebrafish. Open Biology 7, 170139 (2017).

• Zhang R. et al. TTBK2-Driven Ciliogenesis Is Required for Intrinsic Neuronal Regeneration After Spinal Cord Injury. CNS Neuroscience & Therapeutics 32, e70763 (2026).

The work by Lin et al. will be of primary interest to a specialized basic-research audience working on spinal cord injury and regeneration, axon regeneration, cytoskeletal biology, ependymal cell biology, and cilia. The combination of pharmacological treatment with functional and cellular analyses also gives the study some translational relevance, particularly for researchers interested in therapeutic manipulation of the injured spinal cord. Beyond the SCI field, the proposed connection between microtubule stabilization and ciliary preservation may also be relevant to researchers studying cilia-dependent responses to CNS injury and tissue repair more broadly.

Field of expertise: spinal cord injury and regeneration; cellular and molecular mechanisms of tissue repair; axon regeneration; single-cell and spatial transcriptomics. My expertise is more limited with respect to pharmacokinetics, microtubule and cilia biology and the detailed structural pharmacology of microtubule-binding compounds. I therefore could not evaluate these aspects in depth.

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Reply to the reviewers

General Statements

We want to thank the Reviewers for both their positive comments and their constructive criticisms.

We are happy that Reviewer #1 found that “The manuscript examines very interesting topics - the molecular mechanism of action of Sephin1 as a potential therapeutic, its impact on autophagy, and a potential direct effect on the actin cytoskeleton” and that - “ *The authors performed numerous diverse experiments. “. *

Similarly, Reviewer #2 recognizes that “The study presents a large body of data and attempts to connect several major cellular pathways, including actin dynamics, Golgi organization, the integrated stress response, and mTORC1-TFEB signaling. “ and that “The topic is important and timely, particularly given the ongoing debate regarding the specificity and mode of action of sephin1 and related compounds.”

Indeed, they identified several flaws that we are more than willing to address along our revision.

Considering the additional experiments already performed plus the ones planned for the near future, we are confident that our manuscript will gain more support.

Description of the planned revisions

Reviewer #2

*Q: The data supporting a direct interaction between sephin1 and actin are not quantitatively documented, and the potential involvement of known actin-associated complexes, including PPP1R15 proteins and PP1c, is not addressed. *

A: Our department has recently acquired the WAVE system (Creoptix), an advanced technological platform allowing the determination of the affinity between a small molecule and its target. Thanks to such technology, we will test sephin1-actin affinity as requested.

Q: The analysis of Golgi organization is also limited. The use of GFP-based markers rather than established Golgi markers such as GM130 reduces confidence in the interpretation of Golgi morphology.

A: We will perform the experiment suggested : we will assess Golgi morphology upon sephin1 treatment by using Golgi markers. In the meantime, we invite the Reviewer to take in consideration our EM analysis. We showed the regular occurrence of massive Golgi alterations at the ultrastructural level by using samples quick frozen within milliseconds, thus, free of fixation artifacts. Formal quantification will be provided as a complement.

*Q: The evidence supporting modulation of mTORC1 signaling is not fully convincing. The quality of the 4EBP1 immunoblots is insufficient for reliable interpretation, and appropriate controls using established mTOR inhibitors such as rapamycin or Torin1 are missing. *

Additional readouts, including phosphorylation of S6, should be included.

A: We will complement our biochemical analyses as requested by the reviewer.

In the meantime, we have specifically verified that sephin1 increases lysosomal activity via TFEB by assessing DQ-BSA signals in the TFEB KO HeLa line described in (XX). The cells were previously incubated overnight with 10 μg/mL of DQTM Red BSA added in normal medium. Then we treated HeLa cells with sephin1 (100 μM, 2 hours). After the wash-out ( 8 hours) we processed the cells for imaging. In TFEB KO cells, sephin1 did not increase DQ-BSA signals, a proxy for lysosomal activity. These data further support our hypothesis that sephin1 triggers lysosomal activity via the mTOR-TFEB pathway. These results are included in the new Supplementary figure 12F-G and reported also here for Reviewer’s convenience (Rebuttal figure 6A-B).

Q: It remains unclear which events are primary and which are secondary consequences of cellular stress or cell death, in particular TFEB translocation, which should be shown with the endogenous protein.

A: We are more than willing to test TFEB translocation upon sephin1 treatment by staining the endogenous protein

Q: In addition, the study does not address the functional consequences of these pathways, such as the clearance of protein aggregates, which would be important to demonstrate, since it is the proposed model for the clinical application in which sephin 1 is tested as a therapeutic agent.

A: We will include new data from EM morphometry on human fibroblasts carrying the LRRK2 E193K mutation which provide strong indication for the therapeutic effect of sephin1. We have recently thoroughly characterized the autophagic impairment in this genotype. Among others, we observed the massive accumulation of any kind of autophagic and catabolic organelles in E193K cells under normal, steady state conditions [1]. In the present study, we treated E193K fibroblasts (and age-matched wild-type controls) with sephin1 (100 μM, 2 hours) and after 6 hours wash-out we documented ultrastructural patterns, including autophagy by EM. Sephin1 acute treatment induced subcellular alterations as documented in HeLa. Upon a 6 hours wash-out, we noticed also in those fibroblasts the disappearance of any waste-loaded, jammed catabolic organelles. Representative images are already included in the revised manuscript and (New supplementary figure 15A) and in this rebuttal (Rebuttal figure 11C), quantification is planned as well.

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

REVIEWER # 1

Q: 1. The cellular LC3 analyses are fraught with inconsistencies.

--Fig.1 shows that in response to Sephin1, LC3-I and LC3-II levels are similar; Fig.2 shows that LC3-I is more abundant than LC3-II; Fig.3 shows that LC3-II is way more abundant than LC3-I. This dramatic variability and inconsistencies make it impossible to draw solid conclusions about the effect of Sephin1 on LC3 lipidation or autophagy.

A: We are sorry for this inconvenience. However, it is well known that LC3 detection by western blotting is problematic due to the inherent susceptibility of microtubule-associated protein 1 light chain 3 to degradation and structural instability. LC3-I, for instance, may be detected with lower efficiency by some anti-LC3 antibodies and is intrinsically less stable than LC3-II (see for example Rebuttal Figure 10A). Accordingly, the guidelines report that LC3B-II levels, and not LC3B-I, correlated with elevated levels of autophagic vesicles monitored either by electron microscopy or rat GFP-LC3 transfection in response to autophagy-inducing stress, Furthermore, a key recommendation is that LC3-II levels should be normalized to a housekeeping protein such as actin or tubulin rather than to LC3-I [2, 3]. In all our experiments we included the proper internal control and we mainly relied on LC3B-II/tubulin values to draw our conclusions. Altogether, we are confident that our data support our hypothesis.

Q: In Fig.S1B, the LC3B blot has 8 lanes but the tubulin loading control shows 11 lanes. This also does not make sense.

A: We are sorry for that. It was merely a clerical error that occurred during the pictures handling. We replaced it with the right picture.

Q: LC3B is shown above and below a "23kDa" marker. But LC3-I should appear just above a 15kDa marker and LC3-II just below a 15kDa marker. In Fig.1A (and really, all the figures), LC3 species should not be >20kDa. Is the placement of the MW markers incorrect?

A: Indeed, the reviewer is right. We indicate now the proper marker ( 15 kDa)

Q: Why do Figs.S1E-F not show any actual data points? What are the bases of these curves? LC3-I and -II values are again all over the place in multiple supplemental data panels.

A: Supplementary figures 1E-F show the D/R curve describing sephin1 effect. The Y axis shows LC3-II/tubulin and LC3II/I levels, respectively, while the X axis reports sephin1 concentration, expressed as Log. We fitted the experimental data to the logarithmic variation of the Hill equation. New figures report now also the actual data points.

1. • The actin biochemistry assays involving Sephin1 are also problematic. --First, what does actin "precipitation" mean? Is actin misfolding and/or aggregating and therefore pelleting upon centrifugation? Or is it polymerizing and/or bundling and therefore pelleting upon centrifugation? Or (depending on the experiment) is it binding to beads that pellet upon centrifugation? This is all unclear.*

A: We experienced that actin does not remain soluble in the buffer even at 1g room temperature when exposed to sephin1, at least in vitro. “Protein precipitation” is a common laboratory term referring to any strategy to separate proteins from a liquid sample. Generally, it works by making proteins insoluble so they clump together and sink to the bottom of a test tube. Given our experimental setting, we do think that precipitation is an acceptable term to describe the phenomenon.

Coming to the other points raised by the Reviewer, we did try to characterize the nature of the actin found in the pellet by crystallography but we failed. Therefore we moved to a low resolution biochemical strategy , namely the limited proteolysis approach. Limited proteolysis is a technique where low amounts of proteases cleave only exposed and flexible peptide bonds in a native protein, leaving the core structure intact. It maps higher-order protein conformation, domain boundaries, and conformational changes upon ligand binding.

More in detail, 850 ng of human platelet non-muscle actin (Cytoskeleton Inc., APHL99-C) was incubated overnight with 350μM sephin1 or DMSO in the following actin buffer [5 mM Tris-HCl pH 8.0, 0.2 mM CaCl2, 0.2 mM ATP, 5% (w/v) sucrose, and 1% (w/v) dextran] in presence of Triton-X100 (0.01%). The following day the samples were preheated at 25°C for 10 minutes and then proteinase K (Bio Basic) was simultaneously applied to samples (enzyme: substrate at 1:100 mass ratio) that were subjected to a further incubation at 25°C for 5 minutes. Proteinase K activity was quenched by heating samples at 98°C for 5 minutes. After the addition of 5% sodium deoxycholate (Sigma Aldrich), samples were incubated at 98°C for 3 minutes and reduced by using 12 mM DTT at 37°C for 30 minutes. An alkylation step was performed using 40 mM IAA for 30 minutes in the dark. Next, proteins were digested with 0.5μg Lys-C (Wako Chemicals) at 37 °C for 4 hours. Subsequently, samples were diluted with 100 mM ammonium bicarbonate to obtain a final 1% concentration of sodium deoxycholate, then digested with 1μg of Trypsin (Thermo Scientific) at 37 °C overnight. The following addition of 1.5% formic acid and centrifugation at 16 000 rcf for 10 minutes provoked sodium deoxycholate precipitation. Digests were desalted on in-house–packed StageTips, lyophilized in a Speed-vac and resuspended in 20 μL of 0.1% formic acid for LC-MS/MS analysis. Peak intensities of peptides were transformed into log2 space and data were normalized by the average of peak abundance within each sample [4]. Log2 normalized intensities of single peptides were averaged through the replicates. By subtracting the averaged values of Actin- DMSO samples to Actin-sephin1 samples, the fold-change was calculated for each peptide. Significant abundance differences between conditions were determined using a t-test (two-tailed, two-sample unequal variance). Our low-resolution structural analysis suggests that sephin1 reduces the solvent accessibility of two peptides located in subdomain 1 and 3, respectively . The mapped binding site is relatively far from these peptides, indicating that this outcome may be due to a different structural organization of that region, rather than steric hindrance. In particular, our data nominated the peptide 7-18, encompassing the phosphate binding loop 1 and an hydrophobic sequence ( aa 297-312) in the subdomain 3. The P1 loop (amino acids 11–16) is a flexible segment that binds ATP. The hydrophobic loop in subdomain 3 and 4 is crucial for the stabilization of G-actin and supports the monomer addition in the growing actin filament. Existing literature does not suggest that the P1 loop may engage subdomain 3 in either lateral or longitudinal interactions [5]. As such, sephin1 may affect G-actin folding and trigger the formation of yet to be described supramolecular actin complexes involving P1 loop-subdomain 3 interaction. Our data suggest that such structures encompass at least 3 G-actin monomers, as they are recognised by phalloidin, and interact with Arp2/3. Furthermore, in vitro, such actin structures precipitate already at 16K g, while F-actin is classically sedimented at 100K g, suggesting the peculiar nature of the actin assembly induced by sephin1. We are still figuring out how to gain a more detailed understanding of actin folding upon sephin1 binding. We included in this rebuttal the data gathered so far (Rebuttal figure 10B-C).

Q: It is also unclear how the experiments in Fig.4 were performed, because the legend for Fig.4 is uninformative, and the methods sections for the actin experiments were fairly thin. Data-wise, the pulldown blots in Fig.4A and Fig.4F are inconsistent with one another. Is Sephin1 pulldown of actin dose-dependent or not? Where are the actual data points in Fig.4G? Is the dose of Sephin1 used in Fig.4H higher than that in Fig.4F?

A: We did our best to improve the description of the experiments and the relative figure legends.

Figure 4A shows a representative blot of an in vitro pull-down experiment. Briefly, we gathered protein samples from HeLa cells, exposed that to either naive sephin1 or biotinylated sephin1 (FG08) and then we immobilized biotinylated sephin1 and the potential interacting proteins on streptavidin agarose beads. Eventually, we resolved the interacting protein by SDS-PAGE. Figure 4F reports a completely different experiment, i.e. actin precipitation ( see the answer above) upon sephin1 exposure. Probably the reviewer meant Figure 4C. That is indeed a pull-down, but here we incubated either purified β- or ∝- actin with biotinylated sephin1. We now included the data point in figure 4G and we reported that actual concentration of sephin1 used for the experiment in Figure 4H (150 uM).

Q: CytoD binds to the + ends of actin filaments to prevent elongation and eventually promote depolymerization - what is the explanation for how this decreases the "precipitation" of actin in the presence of Sephin1 in Fig.4H-I?

A: Cytochalasin-D binds both G- and F-actin, albeit with largely different affinity (Kd F-actin: 2 nM; Kd G-actin 20 μM). Our molecular dynamics analysis suggests that the predicted sephin1 binding pocket on actin overlaps with binding sites reported for other actin ligands, including cytochalasin D (supplementary figure 5E), suggesting potential competition between cytochalasin D and sephin1 for β-actin binding 51–53. Consistent with this hypothesis, when we tested actin biochemical behavior in vitro by means of our precipitation assay, cytochalasin D significantly reduced β-actin precipitation induced by sephin1. We modified the relative result section to better convey our working hypothesis.

Q: The differences in actin "pulldown" by Sephin1-coated beads in Fig.S3D could possibly be explained by differences in input, and do not appear to be significantly outcompeted by soluble Sephin1.

A: The graph in Figure S3E reports the yield of actin recovery by pulldown expressed as bound /input. Therefore, any potential difference in the input level would not affect the final data.

Q: The amount of alpha-actin pulled down by Sephin1 appears to be proportional to the amount of albumin pulled down by the same beads in Fig.S4, showing that the proposed interaction of actin with Sephin1 is not specific. The complete absence of actin in lane 10 of Fig.S4 is difficult to reconcile with the amount in the pellets in lanes 4-5.

A: Figure S4 does not report the results of a pull-down experiment. Instead, it includes representative blots of sedimentation assays for ∝ actin and albumin. As such, we cannot comment further about the point raised by the Reviewer

Q: Fig.S6C/E appear to show pyrene-actin polymerization assays, but what do the different colored curves represent? What were the concentrations of Sephin1? Do the curves reach similar or different steady state levels of fluorescence? Does steady state occur at similar or different times? In other words, does Sephin1 increase or decrease the critical concentration of actin, polymerization rates, or other properties of actin?

A: We realised that graph labeling was poor: we are really sorry for that. Different colors show different experimental conditions, namely pyrene-actin polymerization assays run in presence of F-buffer, DMSO, or sephin1. Figure C and D show the outcome of sephin1 added at time 0, while figure E-F describe the kinetics of the polymerization of actin pre-incubated with sephin1.

In both cases, plateau levels are different, suggesting that sephin1 reduces the pool of g-actin.

Regarding the time to reach the plateau, we stopped our analyses after 3600 seconds. In our hands, 1 hour incubation was enough to reach a plateau only for the condition including F-buffer.

Q: The biological effects of Sephin1 on actin filaments in cells is unclear and inconsistent.

--Fig.5 relied on LifeAct overexpression, whereas preliminary data on the more important endogenous F-actin was relegated to the supplement. For the data with LifeAct in Fig.5B, what do the authors mean by "actin dots" (presumably LifeAct dots)? Examples of actin dots (with arrows and magnifications) should be highlighted in Fig.5A so the reader can understand what structures the authors are referring to.

A: In 2008 Riedl et. al. published LifeAct as a novel actin-binding probe. Lifeact is a 17 amino acid long peptide and binds preferentially to F-actin [6]. Since its publication, Lifeact has been fused to a variety of fluorescent proteins to label actin in vitro and in vivo [7]. It has been extensively demonstrated that transient expression of Lifeact in cell culture did not alter actin dynamics [8]. Super-resolution imaging of Lifeact and phalloidin in HeLa cells showed comparable results for imaging quality, filament thickness and length [9]. Accordingly, we consider LifeAct signal a reliable proxy for F-actin structures. As suggested, we included higher magnification insets with proper labelling.

Finally, please note that in Fig. 5 immuno-EM from cryofixed cells does show the subcellular localization of endogenous actin upon sephin1 treatment.

Q: --How does Sephin1 treatment quantitatively affect phalloidin staining of endogenous F-actin? Is this dose-dependent? This experiment is fundamental to understanding whether Sephin1 affects the cytoskeleton.

A: We now include data describing the impact of sephin1 50, 100, 200, and 250 µM (new supplementary figure 8C-D and Rebuttal figure 11A-B). Indeed we noticed a partial D/R effect. We did not quantify actin structures upon 250 uM, a condition where we noticed toxicity and a quite odd cytoskeletal organization.

Q: In Fig.S8, why do no phalloidin-stained actin "dots" appear in panel A, but several clumps of phalloidin-stained material appear in panel C? Panel B says n=8-10, but 8-10 what? Cells? Experiments? Experiments examining how many cells?

A: We now offer more representative pictures (see new supplementary figure 9A). The number (n) refers to the number of independent experiments, each one including at least 4 cells. We clarified this information in the material and method section. We now write “For imaging data, N reflects the number of independent biological replicates (coverslips), ensuring a minimum of 4–5 cells were sampled per experiment”

Q: As stated above, the jumping around on numerous pathways (e.g., autophagy, Golgi stress, GCN2 signaling, eIF2/PPP/CHOP, actin assembly, mTOR/TFEB signaling) throughout the figures was just too difficult to follow as currently written.

A: We improved the figures description.

Q: If the authors are specifically interested in following up on actin polymerization at the lysosome and mTOR signaling, they should begin with the Priya et al., 2023 Science Advances paper.

A: We now comment the paper suggested by the reviewer

REVIEWER # 2

Q: A central concern is the lack of robust and quantitative evidence supporting the regulation of autophagy. The use of sephin1 at concentrations up to 100 µM raises concerns about non-specific effects and cellular toxicity, especially in light of previous studies using substantially lower concentrations around 5 µM.

A:We have assessed cell viability upon 2 hours of sephin1 treatment at different concentrations. Our data indicate that 2 hours sephin1 is not overtly toxic at both 50 and 100 µM (Supplementary figure 1A). Instead, we registered slight toxicity at both 5 and 100 µM concentrations upon O/N incubation (Rebuttal figure 1A-B). By EM imaging of quick frozen samples, we did not notice toxicity upon sephin1 administration, considering global parameters such as cell density, membrane integrity, or organelle and nuclear morphology (Rebuttal figure 1C). In particular, the transient effects of 2 hours sephin1 treatment are less pronounced at 50 µM as compared to 100 µM. Longer incubation with 50 µM Sephin (4 hours and even overnight) did not visibly harm the cells either (Rebuttal figure 1C). We would like to remind here that in the original paper describing sephin1 [10], the authors performed several in vitro experiments using sephin1 at concentrations higher than 5 µM (as high as 50 µM, see for example the experiments included in figure S1 and S2).

Q2: The absence of dose-response and time-course analyses limits the interpretation of the observed effects. * Measurements of LC3 dynamics over time and across different concentrations are needed, together with analysis of established autophagy substrates such as p62 and NBR1.*

A: Dose-response and time-course analyses have been already included in the original submission. Please, see Supplementary figure 1B-F, where we explore D/R relationship and Supplementary figure 11A-I where we describe the time-course analyses of the molecular changes happening upon 100 µM Sephin1.

Furthermore, we tested the long term effect of a 2 hours pulse with sephin1 50 µM. In detail, we treated HeLa cells with sephin1 (50 μM, 2 hours). After the wash-out ( 8 hours) and the treatment with DMSO or bafilomycin (100 nM, 2 hours), we measured by western-blotting LC3-II. We did not notice a major effect on LC3-II, suggesting that the initial pulse at 50 µM is not sufficient to elicit subsequent autophagy. The output of such analysis is included in this rebuttal (New supplementary figure 14A-B and Rebuttal figure 2A-B ).

Prompted by Reviewer 2, we assessed the amount of p62. In particular, we analyzed the level of insoluble p62 in our experimental condition. In fact, the detergent insoluble fraction of p62 is a bona fide proxy for aggregated, polyubiquitinated protein complexes that eventually are cleared by selective autophagic clearance. More in detail, we treated HeLa cells with sephin1 (100 μM, 2 hours). After the wash-out ( 8 hours) and the treatment with DMSO or bafilomycin (100 nM, 2 hours), we solubilised the cells in a mild detergent buffer (1% Triton-X100, 50 mM Tris-HCl pH 7.4, 150 mM NaCl, 1 mM EDTA). Upon centrifugation (15K g, 4°C), we collected the pellet and measured by western-blotting p62 levels. As shown in Rebuttal figure 2C–D, sephin1 treatment did not induce the accumulation of insoluble p62-positive aggregates.

While p62 is a classic marker of autophagic flux under steady-state conditions, interpreting total p62 levels in our model is fundamentally confounded by transcriptional regulation. As we demonstrate in Figure 8D and Supplementary figure 13A–B, sephin1 strongly upregulates p62/SQSTM1 mRNA via TFEB (and likely ATF4/CHOP) during the washout phase. As highlighted in the autophagy guidelines [2, 3, 11], when p62 transcription is actively induced by cellular stress pathways, its protein levels cannot be reliably used as a readout for autophagic degradation, because de novo synthesis masks lysosomal turnover.

To overcome this, we relied on functional readouts of autophagic and lysosomal clearance capacity: (1) DQ-BSA dequenching (Figure 8E–F), (2) BafA1-sensitive LC3-II flux following the washout (Figure 9A–D), and (3) new ultrastructural data in human LRRK2 E193K fibroblasts (New Supplementary figure. 15A / Rebuttal figure 11C). These diseased fibroblasts suffer from massive baseline accumulation of jammed catabolic organelles; a sephin1 pulse followed by a 6-hour washout successfully clears this pathological waste, providing definitive morphometric proof of functionally enhanced autophagic clearance

Q: The study is largely restricted to HeLa cells, which are known to display particular features in their integrated stress response. This raises concerns about the general applicability of the findings.

A: Following the Reviewer’ s suggestions, we measured the impact of acute Sephin1 treatment (100 μM, 2 hours) in different cell lines, including human HEK293 and DIV14 primary murine neurons ( obtained from E15.5 C56BL/6 mice embryos). In both the models, acute sephin1 treatment induced LC3B-II accumulation. These results are included in the revised manuscript (new supplementary figure 2A-D) and in this rebuttal for the Reviewer convenience (Rebuttal figure 2E-H)

*Q: The lack of detectable increase in eIF2α phosphorylation in response to thapsigargin treatment is unexpected and should be clarified, as it may reflect suboptimal experimental conditions or timing. *

A: Indeed the choice of the exemplificative blot included in the original submission was poor. We apologize for this issue. However, the quantification did report that thapsigargin elicit eIF2 phosphorylation ( about 1.7 fold over control, see Figure 2D). We now include a more representative blot (new Figure 2B).

Q: The manuscript does not provide data on the expression or activity of PPP1R15A and PPP1R15B, despite their central role in regulating eIF2α phosphorylation and potentially Sephin's effect.

A: First, we apologize for a nomenclature error in the original Figure 3 legend. Sephin1's originally proposed specific target is PPP1R15A (GADD34). PPP1R15B (CReP) is the constitutive, sephin1-insensitive subunit. We ectopically overexpressed PPP1R15B as a genetic bypass to force constitutive eIF2α dephosphorylation even in the presence of sephin1. We have corrected the text and legends to reflect this. We have now included the western blots confirming that PPP1R15B overexpression effectively abolishes Ssphin1-induced eIF2α phosphorylation (New Figure 3D; Rebuttal figure 3C–D). We have also added qRT-PCR data showing that sephin1 induces PPP1R15A mRNA (a known ISR target) but not PPP1R15B mRNA (New Supplementary figure 2E–F).

Crucially, the Reviewer astutely points out the necessity of discussing the PPP1R15-PP1c-actin complex. The active eIF2α holophosphatase is a tripartite complex requiring G-actin for substrate specificity [12]. In the crystal structure of this holophosphatase (PDB: 4V0U), PPP1R15 binds G-actin directly at the hydrophobic cleft between subdomains 1 and 3. Remarkably, this is the exact same pocket where Cytochalasin D binds, and the very same interface where our PAL-MS and molecular docking localize Sephin1 binding (Figure 4B). We hypothesize that Sephin1 binding at the subdomain 1/3 cleft directly competes with or allosterically distorts the assembly of the active PPP1R15-PP1c-G-actin tripartite complex. During the revision, we will test the affinity of sephin1 to G-actin using the Creoptix WAVE platform, and we have expanded the Discussion to formally integrate the structural overlap between the sephin1 binding site and the holophosphatase G-actin interface.

Q: In particular in Figure 3, there is absolutely no demonstration provided, that the ectopic expression of PPP1R15B is sufficient to down-regulate or prevent eIF2 phosphorylation, while leaving LC3 processing intact.

A: We assessed eIF2 phosphorylation upon ectopic expression of PPP1R15B. As expected, PPP1R15B overexpression prevented sephin1 induced eIF2 phosphorylation. These data are included in the manuscript (new Figure 3D and Rebuttal figure 3C-D).

*Q: The specificity of GCN2 involvement is also not convincingly demonstrated, as other eIF2α kinases are not excluded experimentally. *

A: Indeed other pathways may link lysosome physiology and eIF2 phosphorylation. eIF2α phosphorylation acts as the central molecular switch that pauses general translation during lysosomal stress. For example, lysosomal membrane damage triggers the leakage of calcium from the punctured lysosomal lumen into the cytosol. This localized spike in calcium is sensed by the scaffolding protein ALIX. ALIX recruits and activates the kinase PKR. This physical sensor complex directly drives the phosphorylation of eIF2α. However, our data exclude lysosomal damage (Supplementary Figure 1G-H , plus ultrastructural observations) or any major role of Ca2+ (Supplementary Figure 12A-B). Another major pathway initiates on lysosomes. Lysosomal damage hampers the organelle's role as an amino acids recycling hub. Alteration in lysosome membrane potential slows down membrane transporters like SLC38A9, stopping the efflux of recycled amino acids into the cytosol. This scarcity reduces tRNAs loading with amino acids. The accumulation of uncharged tRNAs is intercepted by the metabolic sensor kinase GCN2. Upon activation, GCN2 phosphorylates eIF2α. To explore such a scenario, we monitored eIF2 phosphorylation and LC3-II accumulation in cells treated with sephin1 ( 2 hours, 100 μM ) and cultured in normal media or upon essential amino acids extra supplementation (5X). Noteworthy, essential amino acids supplementation did not prevent either sephin1 induced eIF2 phosphorylation or LC3II accumulation, suggesting another mechanism is involved. These data are included in the revised manuscript (New supplementary figure 2G-I and Rebuttal figure 3E-G). We deem that the minor/no role played by an hypothetical lysosomal damage or amino acids starvation , together with our pharmacological evidence of the implication of GCN2, strongly support our initial hypothesis that GCN2 senses actin cytoskeleton remodelling

Q: Although the manuscript emphasizes actin as a primary target of sephin 1, the supporting evidence remains incomplete. The proteomic analysis from FG08 pull-down experiments is not fully reported, and a comprehensive list of interacting proteins is missing.

A: To identify bona fide sephin1 interactors, we performed a pull-down followed by a SDS-PAGE. Upon silver stain, we selected the prominent band at ∼42kDa for the follow-up MS/MS analysis. Actin with more than 1370 identified peptides was by far the most abundant protein in the FG08 pull-down sample. We now added the full list of the identified proteins (New supplementary table 1).

Q: The imaging of actin structures could also be improved, as the observed punctate signals may correspond to focal adhesions or other actin-based structures that are not characterized here.

A: We agree with the reviewer that a characterization of the actin punctate signals was missing.

The actin cluster observed upon acute sephin1 treatment localized mainly in the perinuclear zone. Rather than focal adhesions ( that are normally present on the cell membrane), we focused on actin comet tails, an actin structure propelled by WHAMM protein and related to autophagosome biogenesis [13]. To this aim, we transfected HeLa cells with GFP-WHAMM (kindly provided by Campellone’ s lab). The day after, we treated cells with sephin1 (2 hours, 100 μM). Upon fixation, we processed the cells to visualize actin structure via phalloidin. We did not report an evident colocalization between actin cluster and GFP-WHAMM signal, suggesting that actin punctate signals nature is different from comet tails. These results are included in the new Supplementary figure 9D and reported also here for Reviewer’s convenience (Rebuttal figure 4A).

Q: Additional functional assays, such as analysis of actin repolymerization dynamics or cell migration, would help establish the relevance of the observed phenotypes.

A: We monitored the impact on cell migration by the wound healing assay. In particular, we grew HeLa at full confluency, then created a physical gap within the cell monolayer. We treated the cell for either vehicle or sephin1 2 hours and then we monitored cell migration into the gap by taking photos at different time points (6, 12, 18, 24, 30 hours). Interestingly, we noticed that the sephin1 pulse did not significantly alter cell migratory behaviour. These results are included in the new Supplementary figure 8E and reported also here for Reviewer’s convenience (Rebuttal figure 4B-C). Altogether, our data suggest that our treatment (sephin1 100 μM 2 hours) does not permanently affect actin dynamics.

Q: Quantitative analysis is lacking, and the mechanistic relationship between actin disruption and Golgi disorganization is not explored in depth. No experimental strategy to determine if protein secretion or glycosylation are affected by sephin1 was provided in the current manuscript. As a result, the connection between these observations and the proposed signaling cascade remains unclear.

A: As suggested we analysed the glycosylation pattern of Negr1, an adhesion protein that undergoes glycosylation in six different sites. By western-blotting, fully glycosylated Negr1 runs at the apparent MW of 50 kDa and the naive protein at 30 kDa [14]. We treated cells with sephin1 (2 hours and 6 hours, 100 μM), monensin (6 hours, 500 nM), and vehicle. To appreciate the extent of Negr1 glycosylation we computed the ratio between the isoforms at 50 and the one at 30 kDa. We found that sephin1 treatments did not overtly affect Negr1 glycosylation. These results are included in the Rebuttal figure 4D-E. Altogether, our data suggest that our treatment (sephin1 100 μM 2 hours) does not overtly affect Golgi physiology.

Q: The use of classical actin-polymerizing and -depolymerizing agents and genetic deletion of PERK has previously demonstrated that eIF2α phosphorylation can be modulated by the state of actin polymerization. In this context, the effects observed upon Sephin1 treatment on eIF2α could plausibly arise as a consequence of altered actin dynamics. Although the manuscript discusses a potential increase in globular actin levels, the functional consequences of this rise are not explored by direct experiments. Furthermore, while the discussion highlights the role of actin in Golgi organization and autophagosome formation, the study lacks a detailed and mechanistic analysis of these processes.

A: We did our best to clarify the connection among sephin1, actin cytoskeleton, Golgi integrity , and autophagy. In particular, we investigated more in detail the impact of the ARP2/3 inhibitor CK-666. In fact, we already showed that CK-666 (250 μM, 2 hours) prevents the acute effect of sephin1 in terms of formation of actin clusters (Figure 5A-C) and LC-3II accumulation (Figure 5D-F). However, it does not prevent Golgi fragmentation (Figure 5H and Rebuttal figure 5C ) nor TFEB translocation induced by sephin1 (Rebuttal figure 5A-B). Still, CK-66 co-administration prevented late stage autophagy (Figure 9). Actually, we found that the ARP2/3 inhibitor CK-666 ( 250 μM, 2 hours) by itself affects Golgi integrity (Rebuttal figure 5C), induces CHOP mRNA (Rebuttal figure 5D) and elicits TFEB translocation (Rebuttal figure 5A-B).

However, a pulse with only CK-666 ( 250 μM, 2 hours) is not sufficient to trigger late stage autophagy (Supplementary figure 14C-D and Rebuttal figure 5E-F).

Altogether, these data suggest that Golgi integrity signals directly to the mTOR-TFEB pathway, as recently suggested also by PMID: 42115886. Our new data clearly indicate that TFEB is instrumental for sephin1 driven increase in lysosomal activity (New supplementary figure 12F-G and Rebuttal figure 6A-B). Therefore, we deem that TFEB translocation associated with Golgi fragmentation is necessary but not sufficient to induce late stage autophagy. We included in this revision new data describing that the co-administration with Cytochalasin D (1 μM) and sephin1 (100 μM) prevents late-stage autophagy ( New supplementary figure 14E and Rebuttal figure 6C). Given that Cytochalasin D impairs sephin1 binding to actin (figure 4H-I), we are confident that the actin alterations observed upon acute sephin1 treatment play a major role in orchestrating a full autophagic response.

*Q: The evidence supporting modulation of mTORC1 signaling is not fully convincing. The quality of the 4EBP1 immunoblots is insufficient for reliable interpretation, and appropriate controls using established mTOR inhibitors such as rapamycin or Torin1 are missing. *

Additional readouts, including phosphorylation of S6, should be included.

A: We will complement our biochemical analyses as requested by the reviewer. Furthermore, we specifically verified that sephin1 increases lysosomal activity via TFEB by assessing DQ-BSA signals in the TFEB KO HeLa line described in [15]. The cells were previously incubated overnight with 10 μg/mL of DQTM Red BSA added in normal medium. Then we treated HeLa cells with sephin1 (100 μM, 2 hours). After the wash-out ( 8 hours) we processed the cells for imaging purposes. Sephin1 did not increase DQ-BSA signals, a proxy for lysosomal activity, in TFEB KO cells. These data further support our hypothesis that sephin1 triggers lysosomal activity via the mTOR-TFEB pathway. These results are included in the new Supplementary figure 12F-G and reported also here for Reviewer’s convenience (Rebuttal figure 6A-B).

Q: Finally, the manuscript does not sufficiently address the broader pharmacological context of sephin1. Given the ongoing discussion regarding the specificity of this class of compounds, it would be important to compare sephin1 with related molecules such as guanabenz or other derivatives (Raphin 1?).

A: Guanabenz acts as a highly potent α2-adrenergic receptor agonist, which confounds its cellular effects and limits its clinical utility due to severe hypotensive activity. To rigorously assess the structure-activity relationship (SAR) of this chemical class without adrenergic confounding, we synthesized three novel structural analogues of sephin1: DG161, EC190, and PF03 (Rebuttal Figure 7–9). Strikingly, these novel derivatives recapitulate the exact mechanism of sephin1—including actin cluster formation, CK-666-sensitive LC3-II accumulation, TFEB nuclear translocation, and enhanced lysosomal DQ-BSA activity—but achieve these effects at 4- to 20-fold lower concentrations (5 µM for DG161; 25 µM for EC190) compared to Sephin1 (100 µM). This analogue data definitively confirms that the MoA we describe is an on-target property of the pharmacophore, rather than a non-specific artifact of 100 µM dosing. These SAR data will form the basis of a follow-up manuscript, but we will gladly include a summarized discussion of this in the revised text to address the Reviewer's broader pharmacological question.

Description of analyses that authors prefer not to carry out

Reviewer 2

Q: Alternative mechanisms, including effects on protein folding activity of the ribosome of these compounds (https://doi.org/10.1021/cn5001588), which could directly impact ribosome collision leading to GCN2 and subsequent mTORC1 activation, are not explored experimentally. This limits the ability to assess whether the observed effects are specific to actin modulation or reflect a more general stress response.

A: The ribosome collision hypothesis is indeed intriguing, but technically challenging and far beyond the scope of this manuscript. Still, we deem that our existing data can partially address it . A direct effect on the ribosome causing translational stalling/collision would immediately halt global protein synthesis. However, our puromycin incorporation assay (Supplementary Figure 3A–B) shows no global translation elongation block at 2 hours. Furthermore, our time-course kinetics (Figure 6C–D, Supplementary Figure 11) demonstrate that robust actin clustering occurs within just 10 minutes of sephin1 exposure, whereas GCN2-dependent eIF2α phosphorylation does not peak until 120–240 minutes. This temporal hierarchy strongly positions cytoskeletal remodeling upstream of the ISR, rather than the reverse. Finally, treating cells with Cycloheximide—a classic translation inhibitor that stalls ribosomes—fails to induce the acute LC3-II accumulation (Supplementary Figure 3C–H) or the late TFEB-target transcription (Supplementary Figure 13D) seen with Sephin1.

References

1. Redl S, Zweydorf FV, Gloeckner CJ, et al (2025) The E193K LRRK2 mutation interferes with the autophagosome processing through the impairment of the LRRK2-Dynein-1 complex. Sci Rep 15:39117. https://doi.org/10.1038/s41598-025-26716-4
2. Klionsky DJ, Abdalla FC, Abeliovich H, et al (2012) Guidelines for the use and interpretation of assays for monitoring autophagy. Autophagy 8:445–544
3. Klionsky DJ, Abeliovich H, Agostinis P, et al (2008) Guidelines for the use and interpretation of assays for monitoring autophagy in higher eukaryotes. Autophagy 4:151–175. https://doi.org/10.4161/auto.5338
4. Aguilan JT, Kulej K, Sidoli S (2020) Guide for protein fold change and p-value calculation for non-experts in proteomics. Mol Omics 16:573–582. https://doi.org/10.1039/d0mo00087f
5. Goddette DW, Frieden C (1985) The binding of cytochalasin D to monomeric actin. Biochem Biophys Res Commun 128:1087–1092. https://doi.org/10.1016/0006-291x(85)91051-4
6. Riedl J, Crevenna AH, Kessenbrock K, et al (2008) Lifeact: a versatile marker to visualize F-actin. Nat Methods 5:605–607. https://doi.org/10.1038/nmeth.1220
7. Riedl J, Flynn KC, Raducanu A, et al (2010) Lifeact mice for studying F-actin dynamics. Nat Methods 7:168–169. https://doi.org/10.1038/nmeth0310-168
8. Kumari A, Kesarwani S, Javoor MG, et al (2020) Structural insights into actin filament recognition by commonly used cellular actin markers. EMBO J 39:e104006. https://doi.org/10.15252/embj.2019104006
9. Mazloom-Farsibaf H, Farzam F, Fazel M, et al (2021) Comparing lifeact and phalloidin for super-resolution imaging of actin in fixed cells. PLoS One 16:e0246138. https://doi.org/10.1371/journal.pone.0246138
10. Das I, Krzyzosiak A, Schneider K, et al (2015) Preventing proteostasis diseases by selective inhibition of a phosphatase regulatory subunit. Science 348:239–242. https://doi.org/10.1126/science.aaa4484
11. Klionsky DJ, Abdel-Aziz AK, Abdelfatah S, et al (2021) Guidelines for the use and interpretation of assays for monitoring autophagy (4th edition)1. Autophagy 17:1–382. https://doi.org/10.1080/15548627.2020.1797280
12. Chen R, Rato C, Yan Y, et al (2015) G-actin provides substrate-specificity to eukaryotic initiation factor 2α holophosphatases. Elife 4:e04871. https://doi.org/10.7554/eLife.04871
13. Kast DJ, Zajac AL, Holzbaur ELF, et al (2015) WHAMM Directs the Arp2/3 Complex to the ER for Autophagosome Biogenesis through an Actin Comet Tail Mechanism. Curr Biol 25:1791–1797. https://doi.org/10.1016/j.cub.2015.05.042
14. Sim G, Jeong M, Seo H, et al (2022) The Role of N-Glycosylation in the Intracellular Trafficking and Functionality of Neuronal Growth Regulator 1. Cells 11:1242. https://doi.org/10.3390/cells11071242
15. Li D, Shao R, Wang N, et al (2021) Sulforaphane Activates a lysosome-dependent transcriptional program to mitigate oxidative stress. Autophagy 17:872–887. https://doi.org/10.1080/15548627.2020.1739442

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Referee #2

Evidence, reproducibility and clarity

The study presents a large body of data and attempts to connect several major cellular pathways, including actin dynamics, Golgi organization, the integrated stress response, and mTORC1-TFEB signaling. While the proposed model is interesting, the current evidence does not sufficiently support the strength of the conclusions, and several aspects of the study require clarification and additional experimental support.

A central concern is the lack of robust and quantitative evidence supporting the regulation of autophagy. The use of sephin1 at concentrations up to 100 µM raises concerns about non-specific effects and cellular toxicity, especially in light of previous studies using substantially lower concentrations around 5 µM. The absence of dose-response and time-course analyses limits the interpretation of the observed effects. In addition, autophagic flux is not rigorously assessed. Measurements of LC3 dynamics over time and across different concentrations are needed, together with analysis of established autophagy substrates such as p62 and NBR1. Importantly, these experiments should be performed alongside careful assessment of cell viability in order to distinguish between bona fide autophagy induction and stress-related or cell death induction effects. The reliance on non-quantitative electron microscopy without complementary quantitative approaches further weakens the conclusions.

The study is largely restricted to HeLa cells, which are known to display particular features in their integrated stress response. This raises concerns about the general applicability of the findings. The lack of detectable increase in eIF2α phosphorylation in response to thapsigargin treatment is unexpected and should be clarified, as it may reflect suboptimal experimental conditions or timing. More generally, key components of the ISR pathway are not sufficiently characterized. The manuscript does not provide data on the expression or activity of PPP1R15A and PPP1R15B, despite their central role in regulating eIF2α phosphorylation and potentially Sephin's effect. In particular in Figure 3, there is absolutely no demonstration provided, that the ectopic expression of PPP1R15B is sufficient to down-regulate or prevent eIF2 phosphorylation, while leaving LC3 processing intact. The specificity of GCN2 involvement is also not convincingly demonstrated, as other eIF2α kinases are not excluded experimentally. Validation in additional cell models would be important to support the proposed mechanism.

Although the manuscript emphasizes actin as a primary target of sephin 1, the supporting evidence remains incomplete. The proteomic analysis from FG08 pull-down experiments is not fully reported, and a comprehensive list of interacting proteins is missing. The data supporting a direct interaction between sephin1 and actin are not quantitatively documented, and the potential involvement of known actin-associated complexes, including PPP1R15 proteins and PP1c, is not addressed. The imaging of actin structures could also be improved, as the observed punctate signals may correspond to focal adhesions or other actin-based structures that are not characterized here. Additional functional assays, such as analysis of actin repolymerization dynamics or cell migration, would help establish the relevance of the observed phenotypes.

The analysis of Golgi organization is also limited. The use of GFP-based markers rather than established Golgi markers such as GM130 reduces confidence in the interpretation of Golgi morphology. Quantitative analysis is lacking, and the mechanistic relationship between actin disruption and Golgi disorganization is not explored in depth. No experimental strategy to determine if protein secretion or glycosylation are affected by sephin1 was provided in the current manuscript. As a result, the connection between these observations and the proposed signaling cascade remains unclear.

The use of classical actin-polymerizing and -depolymerizing agents and genetic deletion of PERK has previously demonstrated that eIF2α phosphorylation can be modulated by the state of actin polymerization. In this context, the effects observed upon Sephin1 treatment on eIF2α could plausibly arise as a consequence of altered actin dynamics. Although the manuscript discusses a potential increase in globular actin levels, the functional consequences of this rise are not explored by direct experiments. Furthermore, while the discussion highlights the role of actin in Golgi organization and autophagosome formation, the study lacks a detailed and mechanistic analysis of these processes.

The evidence supporting modulation of mTORC1 signaling is not fully convincing. The quality of the 4EBP1 immunoblots is insufficient for reliable interpretation, and appropriate controls using established mTOR inhibitors such as rapamycin or Torin1 are missing. Additional readouts, including phosphorylation of S6, should be included.

Significance

This manuscript investigates the mechanism of action of sephin1 and proposes a model in which the compound rewires proteostasis through actin-dependent signaling, linking cytoskeletal perturbation to ISR activation and autophagy regulation. The topic is important and timely, particularly given the ongoing debate regarding the specificity and mode of action of sephin1 and related compounds.

More broadly, the manuscript proposes a complex signaling cascade linking actin perturbation, ISR activation, Golgi disorganization, and autophagy induction, but the temporal and causal relationships between these events are not clearly established. It remains unclear which events are primary and which are secondary consequences of cellular stress or cell death, in particular TFEB translocation, which should be show with the endogenous protein. In addition, the study does not address the functional consequences of these pathways, such as the clearance of protein aggregates, which would be important to demonstrate, since it is the proposed model for the clinical application in which sephin 1 is tested as a therapeutic agent.

Finally, the manuscript does not sufficiently address the broader pharmacological context of sephin1. Given the ongoing discussion regarding the specificity of this class of compounds, it would be important to compare sephin1 with related molecules such as guanabenz or other derivatives (Raphin 1?). Alternative mechanisms, including effects on protein folding activity of the ribosome of these compounds (https://doi.org/10.1021/cn5001588), which could directly impact ribosome collision leading to GCN2 and subsequent mTORC1 activation, are not explored experimentally. This limits the ability to assess whether the observed effects are specific to actin modulation or reflect a more general stress response.

In its current form, the manuscript presents an interesting but insufficiently supported model. Additional quantitative analyses, improved experimental controls, validation in multiple systems, and focused mechanistic insight will be required to substantiate the proposed conclusions.

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Referee #1

Evidence, reproducibility and clarity

This manuscript by Frapporti et al. explores the effects of the small molecule Sephin1 on the actin cytoskeleton, autophagosome-lysosome system, and other endomembrane compartments and signaling pathways. The manuscript examines very interesting topics - the molecular mechanism of action of Sephin1 as a potential therapeutic, its impact on autophagy, and a potential direct effect on the actin cytoskeleton. The authors performed numerous diverse experiments. However, the text is very difficult to follow, and the transitions between experiments lack a logical flow. Moreover, the data seem to be very variable both within figures and from figure-to-figure. Most specifically from my perspective, the authors' conclusions about LC3 phenotypes and actin binding/polymerization are not supported by well-articulated methods or clear/convincing data.

For simplicity, I will comment here only on the LC3 and actin phenotypes (and not their relationships to autophagic flux, Golgi organization, kinase signaling cascades, or other processes, because those connections are difficult to make in light of the challenges in interpreting the basic data cited below).

1. The cellular LC3 analyses are fraught with inconsistencies.
   • Fig.1 shows that in response to Sephin1, LC3-I and LC3-II levels are similar; Fig.2 shows that LC3-I is more abundant than LC3-II; Fig.3 shows that LC3-II is way more abundant than LC3-I. This dramatic variability and inconsistencies make it impossible to draw solid conclusions about the effect of Sephin1 on LC3 lipidation or autophagy.
   • As a more specific example, in Fig.2L-M, for the Sephin1-treated samples, why are the LC3-II values and LC3-II:LC3-I ratios vastly different from those in Fig.1B (10-15-fold different)?
   • Also, an LC3 II:I ratio of ~20:1 for the Sephin1-treated quantification in Fig.2M makes no sense, as the blot in Fig.2K clearly shows more LC3-I than LC3-II in those samples.
   • In Fig.S1B, the LC3B blot has 8 lanes but the tubulin loading control shows 11 lanes. This also does not make sense.
   • LC3B is shown above and below a "23kDa" marker. But LC3-I should appear just above a 15kDa marker and LC3-II just below a 15kDa marker. In Fig.1A (and really, all the figures), LC3 species should not be >20kDa. Is the placement of the MW markers incorrect?
   • Why do Figs.S1E-F not show any actual data points? What are the bases of these curves? LC3-I and -II values are again all over the place in multiple supplemental data panels.
2. The actin biochemistry assays involving Sephin1 are also problematic.
   • First, what does actin "precipitation" mean? Is actin misfolding and/or aggregating and therefore pelleting upon centrifugation? Or is it polymerizing and/or bundling and therefore pelleting upon centrifugation? Or (depending on the experiment) is it binding to beads that pellet upon centrifugation? This is all unclear.
   • It is also unclear how the experiments in Fig.4 were performed, because the legend for Fig.4 is uninformative, and the methods sections for the actin experiments were fairly thin. Data-wise, the pulldown blots in Fig.4A and Fig.4F are inconsistent with one another. Is Sephin1 pulldown of actin dose-dependent or not? Where are the actual data points in Fig.4G? Is the dose of Sephin1 used in Fig.4H higher than that in Fig.4F?
   • CytoD binds to the + ends of actin filaments to prevent elongation and eventually promote depolymerization - what is the explanation for how this decreases the "precipitation" of actin in the presence of Sephin1 in Fig.4H-I?
   • The differences in actin "pulldown" by Sephin1-coated beads in Fig.S3D could possibly be explained by differences in input, and do not appear to be significantly outcompeted by soluble Sephin1.
   • The amount of alpha-actin pulled down by Sephin1 appears to be proportional to the amount of albumin pulled down by the same beads in Fig.S4, showing that the proposed interaction of actin with Sephin1 is not specific. The complete absence of actin in lane 10 of Fig.S4 is difficult to reconcile with the amount in the pellets in lanes 4-5.
   • Fig.S6C/E appear to show pyrene-actin polymerization assays, but what do the different colored curves represent? What were the concentrations of Sephin1? Do the curves reach similar or different steady state levels of fluorescence? Does steady state occur at similar or different times? In other words, does Sephin1 increase or decrease the critical concentration of actin, polymerization rates, or other properties of actin?
3. The biological effects of Sephin1 on actin filaments in cells is unclear and inconsistent.
   • Fig.5 relied on LifeAct overexpression, whereas preliminary data on the more important endogenous F-actin was relegated to the supplement. For the data with LifeAct in Fig.5B, what do the authors mean by "actin dots" (presumably LifeAct dots)? Examples of actin dots (with arrows and magnifications) should be highlighted in Fig.5A so the reader can understand what structures the authors are referring to.
   • How does Sephin1 treatment quantitatively affect phalloidin staining of endogenous F-actin? Is this dose-dependent? This experiment is fundamental to understanding whether Sephin1 affects the cytoskeleton.
   • In Fig.S8, why do no phalloidin-stained actin "dots" appear in panel A, but several clumps of phalloidin-stained material appear in panel C? Panel B says n=8-10, but 8-10 what? Cells? Experiments? Experiments examining how many cells?
4. As stated above, the jumping around on numerous pathways (e.g., autophagy, Golgi stress, GCN2 signaling, eIF2/PPP/CHOP, actin assembly, mTOR/TFEB signaling) throughout the figures was just too difficult to follow as currently written.

Minor

1. If the authors are specifically interested in following up on actin polymerization at the lysosome and mTOR signaling, they should begin with the Priya et al., 2023 Science Advances paper.
2. What does it mean to "jeopardize" a cellular process?

Significance

All of my comments appear in the above panel. It is difficult to comment on significance if the unclear methods and highly variable data do not lead to straightforward conclusions. If the drug directly binds/affects actin, then that would be interesting and significant, but the experimental evidence for this so far is very weak.

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Reply to the reviewers

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

Summary:

In this manuscript, Sherman Foo and Buzz Baum report the development of a tryptophan auxotrophy-based selection system in S. acidocaldarius. Using classical pop-in and pop-out methodology, the authors isolated a strain ΔtrpBA using a rich medium BDN medium (Brock medium supplemented with NZ-amine, Sucrose and uracil and an uracil auxotroph. To get stringent selection, they developed a defined medium BDN, based on analysis of amino acid composition of NZ-amine A and other related substrates. They then analyzed the possibility to use 5-FAA for counterselection and found that 5-FAA did not appear to function as an effective counterselection agent. Next, they successfully constructed a tryptophan complementation system using the pSVAara plasmid backbone, replacing the pyrEF cassette with the trpBAD genes from Saccharolobus solfataricus (sso0888 -sso0890).

Exploiting both uracil and tryptophan auxotrophies, the authors further demonstrated the use of this system by dual-plasmid co-transformation and co-expression of the surface layer proteins and a dominant-negative mutant of the AAA-ATPase Vps4 and confirmed that the accumulation of surface layer lattice forming protein SlaA at the midzone of division-arrested cells together with its membrane anchor SlaB. The localization of SlaA and SlaB at the midcell was in agreement with the observations previously reported by the same group.

This is a good summary of our paper.

Major comments:

1) The dual plasmids differ only at the selection markers, pryEF and trpBA. The stability of them in one cell needs to be addressed.

Thank you for raising this point. We have now addressed plasmid stability by following the maintenance of both plasmids during growth under selective and non-selective conditions. As shown in our new figure Fig. S4C, a strain carrying both plasmids was first grown in selective BCS medium and subsequently transferred to BCS, BCS ura+, BCS trp+, or BCS ura+ trp+. Cultures were sampled after 10 and 20 generations and plated on selective medium to quantify plasmid maintenance.

As expected, the two plasmid were efficiently maintained under selection. When selection for either plasmid was relaxed by supplementation, plasmid loss increased progressively with the number of generations as expected. After 20 generations, approximately 5% of the initial CFU remained under BCS ura+, approximately 21% under BCS trp+, and approximately 14% under BCS ura+ trp+. Thus, both plasmids can be maintained together under selection, while their maintenance is reduced at a similar rate only when the corresponding selective pressure is removed. The presence or loss of one plasmid does not appear to affect the stability of the other.

2) Relevant to the above, the authors should test the plasmid stability after culture with reasonable generations. Is it possible to construct a stably transmitted dural plasmid with different ori?

We agree that an alternative plasmid architecture with a different origin of replication could potentially improve long-term plasmid maintenance. However, constructing and validating such a system would require the identification and testing of additional compatible origins of replication, including screening of available native or cryptic plasmids, followed by construction and characterization of new plasmid backbones in S. acidocaldarius. This would constitute a substantial plasmid-development study beyond the scope of the present work.

Importantly, the dual-plasmid experiment was intended primarily as a proof-of-concept demonstrating that the two selection systems can be combined in the same cell, rather than as a requirement for all applications of the toolbox. Where long-term maintenance of both selectable markers is required, an alternative strategy would be to incorporate the second selection marker stably into the genome. This is addressed in the discussion. We have therefore focused the present study on demonstrating the functionality and compatibility of the two selection systems, while experimentally characterizing the stability of the dual-plasmid configuration under selective and relaxed selection conditions (Fig. S4C).

3) Lines 214-223, I am curious why the authors used ΔtrpAB as the auxotroph instead of using ΔtrpF directly, because the latter could be easily subject to 5-FAA counter selection test.

Thank you for this question. As described earlier in the Results (revised manuscript line 120), we initially selected trpBA as the deletion target because we wanted to establish tryptophan auxotrophy without disrupting the production of upstream metabolic intermediates generated by other genes in the tryptophan biosynthetic pathway, such as trpF, trpE and trpD. In particular, indole-3-glycerol phosphate and other intermediates of this pathway can serve as precursors for the biosynthesis of secondary metabolites, including benzoxazinones and indole diterpene alkaloids.

More generally, the principle of the selection system is not restricted to trpBA or trpF. Other genes in an amino acid biosynthetic pathway could in principle be targeted, provided that the selected gene is non-redundant and its deletion produces the desired auxotrophic phenotype.

Minor comments:

1) Lines 71-84, please add an important reference, Zhao et al., Rational design of unrestricted pRN1 derivatives and their application in the construction of a dual plasmid vector system for Saccharolobus islandicus, 2024.

We thank the reviewer for this excellent suggestion. We agree that this study is highly relevant to our discussion of archaeal genetic tool development. We have now included this reference in the indicated section, highlighting the recent development and of a second stably maintained vector system for Sc. islandicus.

2) In the title, the spatial organization of S-layer assembly during cytokinesis has already been reported by the authors previously. The title could be improved by slight modification.

We have now updated the title to avoid overstating this aspect as a completely novel finding and to shift the focus to the selection system instead.

Reviewer #1 (Significance (Required)):

Archaea of the order Sulfolobales are model microbes for studying the biology of archaea and the origin and evolution of eukaryotic-like characteristics. Lack of sufficient selection markers has been a limitation for genetic analysis of these organisms. Although dual selection system has been developed in Saccharolobus islandicus, another model archaeon of Sulfolobales, there is no such system for Sulfolobus acidocaldarius.

The study by Foo and Baum explored a method for the formulation of defined Brock-based dropout medium, which enables stringent selection not only for trypan auxotrophic selection, but also will be potentially useful for other amino acid-based selection in general. Therefore, this study expanded the genetic toolkit available for S. acidocaldarius and provided additional evidence for spatial regulation of S-layer assembly during archaeal cytokinesis. The dual selection system was based the same plasmid backbone which could have problem in plasmid stability. Use of different compatible plasmid could improve the dual selection system. In general, the developed system will facilitate the study of cell biology and molecular biology using the model archaeon Sulfolobus acidocaldarius.

We appreciate the reviewer's clear summary and are glad that this new selection method will be a valuable asset to the archaeal cell biology community.

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

In this manuscript, the authors develop a new selection method in the model thermoacidophilic archaeon S. acidocaldarius that allows the simultaneous expression of two proteins of interest. Namely, they expressed either the S-layer proteins SlaA or SlaB fused to an HA tag simultaneously with a dominant negative Vps4 protein point mutant tagged with a His6 tag that allows cell cycle arrest. Using this technique, they go on to show that S-layer proteins accumulate at division site in dividing cells. The paper is well written, the data well presented, and the novel selection method will likely be a useful new tool in this model species for archaeal cell biology. However, a few points should be addressed to further support some of the claims made, convince readers of the usefulness of the new strain, and increase the overall clarity of the manuscript.

Thank you for this summary of our results. Below, we address each of the specific points raised to further support our claims and enhance the manuscript's overall clarity and utility.

Major points: - Line 115: Was any RT-qPCR or transcriptomics done to confirm that the expression of the downstream genes in the operon remained the same? - Line 227: Why express the trpBAD cassette if you only deleted trpBA? Does this mean you disrupted the expression of the downstream trpD gene (saci_1423) in the tryptophan biosynthesis operon?

To address both points, yes, RT-qPCR was performed to test the expression of the downstream trpD gene. We have now included this result in Fig. S3D.

We found that trpD expression was reduced but not abolished in the ΔtrpBA strain when compared to the wild-type strain DSM639. However, we also note that this is similar to the commonly used MW001 (ΔpyrE) strain, where the downstream pyrF gene expression was reduced compared to the wild-type strain. In both cases, complementation with the corresponding Sa. solfataricus gene(s) and the downstream gene (trpD or pyrF) was used to rescue its auxotrophic phenotype.

• Line 227: Why did you choose to complement with the genes from Sa. solfataricus instead of using the native genes from S. acidocaldarius? Please clarify.

This was done to minimize the risk of unwanted homologous recombination events between the expression vector and the host genome. Because the trpB 5’ UTR and trpD sequences are present on the plasmid backbone, using the native S. acidocaldarius sequence could lead to unintended recombination at these genomic flanking regions, destabilizing the system. We have now included this information in the text at line 230.

• Line 236: Why is the promoter so much leakier on pSF251-SlaA-HA vs. pSVAaraFX-SlaA-HA? pSF251 is a derivative of pSVAaraFX-HA so it seems strange that the promoter would behave so differently on the two plasmids. While the arabinose promoter is somewhat leaky, it should not be this leaky according to reference 22 and in comparison to the non-induced controls of pSVAaraFX-SlaA-HA. The high level of expression in the non-induced control suggests the slaA-HA gene is being constitutively expressed. This could potentially be driven by the promoter of trpBAD cassette you introduced if you did not add a transcription terminator downstream.
• Line 238: Why is the expression of SlaA-HA so much higher in BDM when using the pSF251-SlaA-HA plasmid vs. the pSVAara-Fx-SlaA-HA plasmid? It appears to express just as well as SlaA-HA did in BSN media when expressed on pSVAara-Fx-SlaA-HA. Do you think the promoter controlling the trpBAD casette is somehow driving stronger and more constitutive expression of genes downstream trpBAD?
• Line 243: The authors may want to re qualify this. While the system can support inducible protein expression, the existing plasmid seems to express genes constitutively even when they are placed under inducible promoters. While the expression does increase upon induction, it goes from "high" to "very high" rather than "low" to "high" which may not be readily useful in typical applications of inducible promoters.

Thank you for these comments. We have repeated and re-quantified the SlaA-HA expression experiments and believe that the apparent difference between pSF251-SlaA-HA and the parental pSVAaraFX-SlaA-HA construct is partly due to differences in Western blot presentation in the original manuscript.

Firstly, pSF251 is progressively lost when cells are propagated in the absence of the corresponding selection in BNS. This is also supported by our observation in Fig. S4C, following supplementation of tryptophan in BCS. Thus, reduced SlaA-HA signal in both the uninduced and induced BNS samples in Fig. 3D is likely to reflect loss of the pSF251 plasmid rather than intrinsically low expression from the construct.

Secondly, direct visual comparison of the original Fig. 3D with Fig. S2C is complicated by differences in Western blot exposure and contrast. In particular, the presentation of Fig. 3D was adjusted to make the relatively weak BNS signal visible, due to the point raised above. This more saturated presentation results in the impression that uninduced SlaA-HA expression with pSF251 in BDM may seem much higher than it actually is.

We therefore consider the quantified values to provide a more appropriate comparison than direct visual comparison of band intensities between the two figures. To further support this, we have now included re-quantified data using triplicate experiments to show the quantified relative expression with means ±SD indicated in Fig. 3D and S2C. The re-quantified data show that SlaA-HA expression from pSF251 increases approximately two-fold following arabinose induction, confirming that the construct remains arabinose responsive. Furthermore, the blot in Figure 3D has been replaced with a more representative image featuring lower saturation levels.

We also note that the magnitude of basal expression and the induction response can depend on the gene of interest and the properties of the encoded protein. The LacS protein used in previous characterization of the arabinose-inducible system is distinct from SlaA and may differ substantially in abundance and stability. A demonstration of this effect can be found in Fig. S4D, where the expression of SlaA and SlaB are significantly different, despite being expressed from the same plasmid. We have therefore avoided interpreting the basal expression observed with SlaA-HA as a universal property of the promoter system.

With respect to the possibility of transcriptional read-through from the introduced S. solfataricus trpBAD cassette, we did not include a transcriptional terminator downstream of the cassette and therefore cannot exclude a contribution from transcription originating at the trpBAD promoter. However, we have not directly tested this mechanism and have therefore avoided attributing the observed basal expression specifically to trpBAD promoter read-through.

Importantly, the primary purpose of pSF251 in this study is to introduce trpBAD as an alternative selectable marker, rather than to systematically characterize or optimize the arabinose-inducible promoter. Our data demonstrate that the resulting vector retains arabinose-responsive expression, while also highlighting that basal expression can be substantial and should be considered when selecting and optimizing constructs for individual applications. Alternative regulatory systems, including copper-, maltose- or xylose-responsive promoters, may provide additional options where tighter regulation is required, but systematic comparison of promoter systems is beyond the scope of this study. This caveat has now been included in the discussion.

We have therefore edited the relevant text to state that pSF251 supports arabinose-responsive protein expression, rather than implying that it provides a tightly regulated low-to-high induction system.

• Line 275: Since both plasmids have the same replication strategy as well as possessing extended regions of homology, one could wonder whether there are any issues with plasmids undergoing recombination with one another? Or if there are any issues with inheritance of the plasmids? While we certainly see cells that are positive for both proteins being expressed (an HA tagged S-layer protein and a His6 tagged Vsp4 protein), what is the percentage of cells that are positive for both? And how stable is this?

This concern was also raised by Reviewer 1. We have now included new data in Fig. S4C to show the co-maintenance of both plasmids under selective and non-selective conditions. These experiments demonstrate that both plasmids can be maintained together under selection, while plasmid loss occurs progressively when the corresponding selective pressure is relaxed. Please see our response to Reviewer 1 above for a detailed description of these experiments.

We have also examined simultaneous protein expression from the two plasmids at the single-cell level by flow cytometry. Specifically, we analysed strains overexpressing either SlaA-HA or SlaB-HA together with Vps4WkB-His6 (Fig. S4D). These experiments demonstrate that proteins encoded by the two plasmids can be expressed simultaneously in individual cells. However, the proportion of cells expressing each protein is dependent on the particular gene of interest. For example, SlaA expression is readily detected in the SlaA-HA/Vps4WkB-His6 strain, whereas SlaB expression is substantially lower in the corresponding SlaB-HA/Vps4WkB-His6 strain. Thus, the proportion of double-positive cells reflects gene-specific expression properties and cannot be considered a general characteristic of the dual-plasmid system.

Importantly, the flow cytometry measurements report protein expression at the single-cell level and do not directly establish the presence or integrity of both plasmids in each individual cell. We therefore consider the plasmid stability experiment in Fig. S4C to be the appropriate assay for assessing inheritance of the two plasmids, while the flow cytometry and Western blotting experiments (Fig. S4D, Fig 4A) demonstrate that simultaneous expression from the two plasmids is possible in individual cells.

• Line 379: Figure 3D actually shows the contrary (cells start to lose the pSF plasmid if grown in BSN). Please correct accordingly.

Thank you for pointing this out. Indeed in the original Results (line 238), we also explicitly noted that lower expression levels were observed in BNS, potentially due to loss of the pSF251 vector in the presence of tryptophan in the rich medium, which relieves selection pressure. This limitation is further clarified with the addition of the plasmid stability data in Fig. S4C.

Our intention in the statement at line 379 was not to suggest that pSF251 plasmids can be stably maintained during prolonged growth in BNS without selection. Rather, we intended to highlight the flexibility provided by having independent trpBAD and pyrEF selection systems. For example, the trpBAD marker can be used to select for genome-engineering events, while a pyrEF-based plasmid can subsequently be used for plasmid-based overexpression under conditions where higher protein yields are required. Conversely, the two selection systems can also be combined where simultaneous selection for a genomic modification and plasmid-borne construct is desirable.

To avoid confusion, we have now edited this section to, “The availability of independent trpBAD and pyrEF selection systems provides flexibility for combining genome engineering and plasmid-based approaches. For example, auxotrophic strains can first be selected under defined conditions using trpBAD, while pyrEF-based plasmids can subsequently be used for overexpression experiments requiring higher protein yields. The two selection systems can also be combined to enable simultaneous selection of genomic modifications and plasmid-borne constructs.”

• Line 407: How does SlaB contribute to the recruitment or stabilization of SlaA if SlaA is also enriched in the portion of the extended division bridge that SlaB is absent from? Please discuss.

We agree that our original wording could be interpreted as implying that SlaB is required for recruitment or stabilization of SlaA at the division midzone, which is not directly supported by our observations.

Our data show enrichment of SlaA or SlaB at the division midzone in division-arrested cells, consistent with the possibility that SlaB contributes to SlaA recruitment or stabilization, as suggested previously by the accumulation of exogenously added SlaA at the division bridge (Foo et al., 2025). However, as the reviewer points out, SlaA remains enriched within portions of extended division bridges where SlaB signal is reduced. Thus, SlaB is unlikely to be the sole determinant of SlaA localization at the division midzone.

One possibility is that SlaB is dynamically remodelled during division-bridge maturation. In cells with extended division bridges, SlaB signal appears reduced at the bridge midzone but enriched at the flanking regions, while SlaA remains enriched within the bridge. Alternatively, additional S-layer anchoring components, including Saci_1846 identified previously (Foo et al., 2025), could contribute to SlaA retention or organization independently of SlaB. Distinguishing between these possibilities will require further experiments.

We have therefore revised the text to present the contribution of SlaB to SlaA localization as a model rather than an established mechanism, and to acknowledge the possibility of additional or dynamically regulated S-layer anchoring mechanisms in the discussion.

Foo, Sherman, Ido Caspy, Alice Cezanne, Tanmay A. M. Bharat, and Buzz Baum. “A Self-Assembling Surface Layer Flattens the Cytokinetic Furrow to Aid Cell Division in an Archaeon.” Proceedings of the National Academy of Sciences 122, no. 25 (2025): e2501044122. https://doi.org/10.1073/pnas.2501044122.

-Figure 4: It is unclear what the sample size is for microscopy. If only N=10 cells were imaged in one single experiment for each strain, then this does not fit standard criteria for scientific reproducibility. Unless N=10 cells were imaged across multiple independent experiments (e.g. 3 or 4 cells in three independent experiments)? Either way, one would expect that more cells could be imaged and added to this analysis, especially given that the authors enriched for dividing cells in their assays. It is also important that cells be selected in a blinded fashion.

Thank you for raising this point. We have repeated the microscopy analysis and increased the sample size to 25 cells per strain, with three independent experiments performed. The revised analysis and corresponding figure have been updated accordingly.

Because the purpose of this analysis was specifically to examine S-layer organization at the division site, dividing cells were selected according to its morphology. Importantly, cells were first identified and selected using an the independent channel (ConA staining) without assessing SlaA/SlaB localization. Only after the cells had been selected were the SlaA/SlaB fluorescence channels examined and quantified. Thus, selection of cells for analysis was based on an independent marker of cell morphology rather than the S-layer localization phenotype being quantified. This approach also resulted in inclusion of cells with both short and extended division bridges. Consequently, the midzone enrichment of SlaB is less distinct in the population-level profile shown in Fig. 4E than for SlaA, reflecting heterogeneity in division-bridge morphology rather than selection based on the S-layer localization phenotype.

We have clarified this procedure in the revised Materials and Methods.

• Figure 4: "endogenous S-layer at the midzone": Here the authors image the localization of tagged, overexpressed copies of SlaA and SlaB, not endogenous proteins. Please correct.

We have now edited this phrase accordingly.

Minor points: - Line 145: While the cells clearly grow in the absence of added tryptophan, it appears that they have a more severe/noticeable growth defect when grown on solid vs. liquid media. Is there a reason why this might be so?

The more pronounced growth defect observed on solid media compared to liquid media may be due to differences in pH between the two cultivation formats, dictated by technical constraints in solid media preparation. Gelrite, the gelling agent used, fails to polymerize at the acidic pH of 3.0 at high temperatures, and is thus kept at a pH of 5.0, which imposes an additional stress on Sulfolobus cells.

• Line 153: have been > has been

We have corrected this typo accordingly.

• Line 216: Would 5-FAA not be expected to just abiotically isomerize into the product of trpF under the acidic media conditions?

This is an interesting hypothesis. However, the literature and our experimental data demonstrate that this is unlikely to be occurring.

Firstly, an older study has shown that anthranilic acid derivatives do not undergo spontaneous skeletal or positional isomerization in acidic environments. At highly acidic values (approximating pH 2), anthranilic acids are remarkably stable against complex structural modifications (Stevens et al., 1952). The introduction of a highly electronegative fluorine atom at the C-5 position is expected to further exert a powerful electron-withdrawing inductive effect on the benzene ring, protecting the aromatic ring against the electrophilic intermediates required for skeletal or positional rearrangements.

Second and more importantly, if 5-FAA were abiotically converting into a functional downstream tryptophan intermediate, this shortcut would bypass the genetic block in our ΔtrpF strain, rescuing its growth. Instead, we observe that 5-FAA is uniformly toxic to both the wild-type and the ΔtrpF strain (Fig. S3C). This lethality rules out abiotic conversion into a tryptophan intermediate or thermal degradation of 5-FAA. Instead, it indicates that 5-FAA possesses a toxicity mechanism in S. acidocaldarius that operates independently of the TrpF pathway. This phenomenon is precedented in hyperthermophilic archaea; for example, in Pyrococcus furiosus, deletion of downstream tryptophan biosynthesis genes similarly failed to yield 5-FAA resistance (Farkas et al., 2012).

Stevens, W. H., J. M. Pepper, and M. Lounsbury. “The Decarboxylation of Anthranilic Acid.” Canadian Journal of Chemistry 30, no. 7 (1952): 529–40. https://doi.org/10.1139/v52-065.

Farkas, Joel, Karen Stirrett, Gina L. Lipscomb, et al. “Recombinogenic Properties of Pyrococcus Furiosus Strain COM1 Enable Rapid Selection of Targeted Mutants.” Applied and Environmental Microbiology 78, no. 13 (2012): 4669–76. https://doi.org/10.1128/AEM.00936-12.

• Line 228: Was a transcription terminator added downstream of sso0890?

No. Please see above for the full response regarding transcriptional read-through and protein expression levels.

• Line 375: This is only true for one of the two plasmids. The expression is quite high on your pSF plasmid.

We agree that the original statement was too broad. We have rephrased the sentence to clarify that the response to arabinose induction is lower, rather than total expression levels.

Reviewer #2 (Significance (Required)):

S. acidocaldarius has previously been made accessible to genetic manipulation including in-frame markerless gene deletion and exogenous expression of proteins of interest from an expression vector, pSVA-AraFX, under the control of inducible promoters (arabinose, xylose, sucrose) that allow the timely expression of target proteins in the cell. Existing tools rely on uracil auxotrophy (i.e. the parental strain is deficient for uracil synthesis, and exogenous plasmid DNA carries the missing uracil synthesis gene, allowing selection of transformants). Here, the authors develop a tryptophan auxotrophy-based selection system in S. acidocaldarius by deleting the genes trpBA. They then modified the pSVA-AraFX plasmid by replacing the uracil synthesis genes pyrEF by the tryptophan synthesis genes trpBA, allowing double expression of proteins in S. acidocaldarius. The technique is used in the present work to show localization of S-layer proteins in dividing cells as a proof on concept. This novel selection method will likely be a useful new tool for archaeal cell biologists.

We thank the reviewer for their positive assessment and for recognizing the value of our tryptophan auxotrophy-based selection system.

---

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

The manuscript written by Foo and Baum describes the development of a tryptophan auxotrophy-based selection system for the archaeal model organism Sulfolobus acidocaldarius. The authors formulated a defined Brock-based dropout medium and demonstrated its use for tryptophan-based selection. They further combined this system with the established pyrEF marker to co-express two plasmid-borne constructs and used this approach to examine the localization of S-layer proteins in division-arrested cells.

The development of an additional selectable marker in S. acidocaldarius has great potential for sophisticated genetic analyses, including chromosomal marker exchange, simultaneous gene expression and complementation, and so on. I believe that this work is a valuable contribution to the Sulfolobus research community. Overall, the manuscript is clearly written, the experiments are generally well designed, and the results are clearly presented and discussed. I have several comments that I hope will help the authors strengthen the manuscript.

This is an accurate summary of our results.

Major concerns 1.The dual-plasmid system is one of the major advances claimed in this study. However, the two plasmids appear to share the same backbone and differ mainly in their selection markers. The compatibility and stability of the two plasmids within the same cells have not been adequately validated. The authors should evaluate the dual-transformation efficiency and plasmid retention over multiple generations under dual-selection conditions. Plasmid-specific analyses are also needed to confirm that both plasmids remain intact and to exclude potential recombination or rearrangement.

Thank you for the comment, this point was also raised by reviewers 1 and 2. We have now included new data in Fig. S4C to show the co-maintenance of both plasmids under selective and non-selective conditions. These experiments demonstrate that both plasmids can be maintained together under selection, while plasmid loss occurs progressively only when the corresponding selective pressure is relaxed. Please see our response to Reviewer 1 above for a more detailed description of these experiments.

2.I am not fully convinced that the current data support the authors' claim of stringent tryptophan-based selection. The spot assays do demonstrate that an established ΔtrpBA culture cannot grow on BDM without tryptophan. However, in Sulfolobus transformation, a spot assay is not equivalent to a transformation plating assay and does not directly demonstrate the performance of the selection marker during transformation. Although the authors present this approach as a further development of the S. acidocaldarius genetic system, they do not show representative transformation plates or report transformation efficiency, background colony formation, or false-positive frequency. These data are needed to establish the stringency and practical utility of the proposed selection system.

Thank you for raising this important point. We agree that the spot assays alone do not directly assess the performance of the trpBAD selection marker during transformation. We have therefore performed transformation plating assays and subsequently genotyped individual colonies to directly assess the stringency of tryptophan-based selection.

Specifically, we performed three independent transformations of and genotyped 15 colonies from each transformation. This was done for the case of single (trpBAD) and double (trpBAD and pyrEF) transformations, plated on BDM or BCS. These analyses allowed us to directly determine the frequency of genuine transformants among colonies recovered. We have now included the resulting false-positive frequencies in the revised manuscript (lines 234, 281 and 294). These results demonstrate that background colony formation under the selection conditions is low and provide direct evidence for the stringency and practical utility of the trpBAD selection system during transformation.

We have not presented CFU per µg DNA as a general transformation-efficiency metric. Although we recorded the number of colonies recovered following transformation, this value reflects not only DNA uptake but also recovery during the outgrowth period post electroporation and subsequent growth under selection. In addition, constructs containing different genes of interest can differ in plasmid size and in their effects on plasmid replication, copy number, gene expression, cellular fitness and recovery. Consequently, CFU per µg DNA would not provide a directly comparable measure of transformation efficiency across different constructs.

Instead, we have focused on the frequency of genuine transformants among colonies recovered under selection, determined by genotyping independent colonies. We believe this provides a more direct assessment of the parameter relevant to the reviewer’s concern, namely the stringency and specificity of the proposed tryptophan-based selection system.

Specific comments 1.The S-layer localization experiments provide a useful demonstration of the dual-selection system. However, the authors should clarify that SlaA and SlaB were examined separately in Vps4E209Q-arrested cells rather than simultaneously during unperturbed cytokinesis. Accordingly, terms such as "co-enrichment," "endogenous S-layer," and "spatial regulation" should be used with appropriate caution.

We have combed through the manuscript text and updated the terms accordingly to more accurately reflect the conditions and results presented in the paper.

2.The authors should provide additional information about key reagents, including the manufacturers and catalog numbers for casamino acids, tryptophan, Gelrite, and L-arabinose. This information is important for reproducing the defined and selective media, particularly because the composition of complex products such as casamino acids may vary among suppliers.

This information is now included in the Materials and Methods.

3.Plasmid sequences, annotated maps, primer sequences, and the complete BDM recipe should be deposited in a stable repository or provided as supplementary files. The statement that "all data are available in the manuscript" is not sufficient to ensure the reproducibility of a newly developed genetic system.

We have now included the annotated plasmid map and sequence of pSF251, and primer sequences used as supplementary files. The full BDM recipe can be found in the Materials and Methods, which we have now updated to include the full recipe for Brock media.

4.The sentence "The deletion of the arginine decarboxylase have been described" should be corrected to "Deletion of the arginine decarboxylase has been described."

We have edited this typo accordingly.

5.Figure S4C reports the percentages of HA-positive and His6-positive cells, but the gating strategy and negative controls used to establish the thresholds are not shown. Appropriate uninduced and single-expression controls should be included or described.

We appreciate the reviewer's request for clarity on the gating approach. Because the data are presented as a scatter plot, the boundary thresholds for HA-positive and His6-positive populations were established as a horizontal gate on the Y-axis, set directly above the wild-type parental control population. As noted earlier in the manuscript, the uninduced sample exhibits a degree of leaky/basal expression rather than a completely silent state. Because of this, the uninduced population displays a significant shift in fluorescence compared to the negative wild-type control. This is highly dependent on the protein of interest as can be clearly observed between the expression of the soluble SlaA-HA vs the membrane protein HA-SlaB (Fig. S4D).

As such, we chose to use the wild-type control to demonstrate the presence of the proteins of interest in this proof-of concept work. This Y-axis gate was positioned such that fewer than 5% of the negative wild-type control cells fall above the line. Because the fully induced populations exhibit an unambiguous upward shift in fluorescence intensity along the Y-axis, this clear boundary provides a highly reproducible separation between baseline cellular autofluorescence and protein overexpression.

We have added a statement to the Materials and Methods section to explicitly clarify this gating threshold rationale in light of the basal expression levels.

6.In line 227 and Figure 3A, why trpD was introduced into pSF251?

This point was raised by reviewer 2 as well, please see above for our full response. In short, RT-qPCR analysis (Fig. S3D) revealed that our ΔtrpBA deletion reduced downstream trpD expression. This was similar to what we found in the MW001 background strain where, pyrF expression was reduced following deletion of pyrE. In both cases, complementation was carried out with the corresponding Sa. solfataricus gene + the downstream gene (trpD or pyrF)

7.In line 268, I am not sure if "results not shown" should be allowed to use. The authors may need to rephrase these sentences or provide supporting data.

We have revised this section to remove the statement regarding reduced protein expression, which was not directly supported by data presented in the manuscript. In addition, we now provide direct evidence that the ΔtrpBA mutant can be efficiently selected in BCS as well (line 294).

Reviewer #3 (Significance (Required)):

Sulfolobus acidocaldarius is an emerging model archaeon for studying fundamental cellular processes. However, the limited availability of selectable markers restricts more sophisticated genetic analyses in this organism. The development of an additional selectable marker should facilitate chromosomal gene exchange and recombination, simultaneous gene expression and complementation, and experiments combining genetic perturbations with reporter constructs. This work therefore represents a valuable technical contribution to the Sulfolobus research community and may enable more advanced genetic and cell-biological studies in this important archaeal model.

We appreciate this supportive assessment of our work's significance.

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Referee #3

Evidence, reproducibility and clarity

The manuscript written by Foo and Baum describes the development of a tryptophan auxotrophy-based selection system for the archaeal model organism Sulfolobus acidocaldarius. The authors formulated a defined Brock-based dropout medium and demonstrated its use for tryptophan-based selection. They further combined this system with the established pyrEF marker to co-express two plasmid-borne constructs and used this approach to examine the localization of S-layer proteins in division-arrested cells.

The development of an additional selectable marker in S. acidocaldarius has great potential for sophisticated genetic analyses, including chromosomal marker exchange, simultaneous gene expression and complementation, and so on. I believe that this work is a valuable contribution to the Sulfolobus research community. Overall, the manuscript is clearly written, the experiments are generally well designed, and the results are clearly presented and discussed. I have several comments that I hope will help the authors strengthen the manuscript.

Major concerns

1.The dual-plasmid system is one of the major advances claimed in this study. However, the two plasmids appear to share the same backbone and differ mainly in their selection markers. The compatibility and stability of the two plasmids within the same cells have not been adequately validated. The authors should evaluate the dual-transformation efficiency and plasmid retention over multiple generations under dual-selection conditions. Plasmid-specific analyses are also needed to confirm that both plasmids remain intact and to exclude potential recombination or rearrangement. 2.I am not fully convinced that the current data support the authors' claim of stringent tryptophan-based selection. The spot assays do demonstrate that an established ΔtrpBA culture cannot grow on BDM without tryptophan. However, in Sulfolobus transformation, a spot assay is not equivalent to a transformation plating assay and does not directly demonstrate the performance of the selection marker during transformation. Although the authors present this approach as a further development of the S. acidocaldarius genetic system, they do not show representative transformation plates or report transformation efficiency, background colony formation, or false-positive frequency. These data are needed to establish the stringency and practical utility of the proposed selection system.

Specific comments

1. The S-layer localization experiments provide a useful demonstration of the dual-selection system. However, the authors should clarify that SlaA and SlaB were examined separately in Vps4E209Q-arrested cells rather than simultaneously during unperturbed cytokinesis. Accordingly, terms such as "co-enrichment," "endogenous S-layer," and "spatial regulation" should be used with appropriate caution.
2. The authors should provide additional information about key reagents, including the manufacturers and catalog numbers for casamino acids, tryptophan, Gelrite, and L-arabinose. This information is important for reproducing the defined and selective media, particularly because the composition of complex products such as casamino acids may vary among suppliers.
3. Plasmid sequences, annotated maps, primer sequences, and the complete BDM recipe should be deposited in a stable repository or provided as supplementary files. The statement that "all data are available in the manuscript" is not sufficient to ensure the reproducibility of a newly developed genetic system.
4. The sentence "The deletion of the arginine decarboxylase have been described" should be corrected to "Deletion of the arginine decarboxylase has been described."
5. Figure S4C reports the percentages of HA-positive and His6-positive cells, but the gating strategy and negative controls used to establish the thresholds are not shown. Appropriate uninduced and single-expression controls should be included or described.
6. In line 227 and Figure 3A, why trpD was introduced into pSF251?
7. In line 268, I am not sure if "results not shown" should be allowed to use. The authors may need to rephrase these sentences or provide supporting data.

Significance

Sulfolobus acidocaldarius is an emerging model archaeon for studying fundamental cellular processes. However, the limited availability of selectable markers restricts more sophisticated genetic analyses in this organism. The development of an additional selectable marker should facilitate chromosomal gene exchange and recombination, simultaneous gene expression and complementation, and experiments combining genetic perturbations with reporter constructs. This work therefore represents a valuable technical contribution to the Sulfolobus research community and may enable more advanced genetic and cell-biological studies in this important archaeal model.

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

In this manuscript, the authors develop a new selection method in the model thermoacidophilic archaeon S. acidocaldarius that allows the simultaneous expression of two proteins of interest. Namely, they expressed either the S-layer proteins SlaA or SlaB fused to an HA tag simultaneously with a dominant negative Vps4 protein point mutant tagged with a His6 tag that allows cell cycle arrest. Using this technique, they go on to show that S-layer proteins accumulate at division site in dividing cells. The paper is well written, the data well presented, and the novel selection method will likely be a useful new tool in this model species for archaeal cell biology. However, a few points should be addressed to further support some of the claims made, convince readers of the usefulness of the new strain, and increase the overall clarity of the manuscript.

Major points:

• Line 115: Was any RT-qPCR or transcriptomics done to confirm that the expression of the downstream genes in the operon remained the same?
• Line 227: Why express the trpBAD cassette if you only deleted trpBA? Does this mean you disrupted the expression of the downstream trpD gene (saci_1423) in the tryptophan biosynthesis operon?
• Line 227: Why did you choose to complement with the genes from Sa. solfataricus instead of using the native genes from S. acidocaldarius? Please clarify.
• Line 236: Why is the promoter so much leakier on pSF251-SlaA-HA vs. pSVAaraFX-SlaA-HA? pSF251 is a derivative of pSVAaraFX-HA so it seems strange that the promoter would behave so differently on the two plasmids. While the arabinose promoter is somewhat leaky, it should not be this leaky according to reference 22 and in comparison to the non-induced controls of pSVAaraFX-SlaA-HA. The high level of expression in the non-induced control suggests the slaA-HA gene is being constitutively expressed. This could potentially be driven by the promoter of trpBAD cassette you introduced if you did not add a transcription terminator downstream.
• Line 238: Why is the expression of SlaA-HA so much higher in BDM when using the pSF251-SlaA-HA plasmid vs. the pSVAara-Fx-SlaA-HA plasmid? It appears to express just as well as SlaA-HA did in BSN media when expressed on pSVAara-Fx-SlaA-HA. Do you think the promoter controlling the trpBAD casette is somehow driving stronger and more constitutive expression of genes downstream trpBAD?
• Line 243: The authors may want to re qualify this. While the system can support inducible protein expression, the existing plasmid seems to express genes constitutively even when they are placed under inducible promoters. While the expression does increase upon induction, it goes from "high" to "very high" rather than "low" to "high" which may not be readily useful in typical applications of inducible promoters.
• Line 275: Since both plasmids have the same replication strategy as well as possessing extended regions of homology, one could wonder whether there are any issues with plasmids undergoing recombination with one another? Or if there are any issues with inheritance of the plasmids? While we certainly see cells that are positive for both proteins being expressed (an HA tagged S-layer protein and a His6 tagged Vsp4 protein), what is the percentage of cells that are positive for both? And how stable is this?
• Line 379: Figure 3D actually shows the contrary (cells start to lose the pSF plasmid if grown in BSN). Please correct accordingly.
• Line 407: How does SlaB contribute to the recruitment or stabilization of SlaA if SlaA is also enriched in the portion of the extended division bridge that SlaB is absent from? Please discuss. -Figure 4: It is unclear what the sample size is for microscopy. If only N=10 cells were imaged in one single experiment for each strain, then this does not fit standard criteria for scientific reproducibility. Unless N=10 cells were imaged across multiple independent experiments (e.g. 3 or 4 cells in three independent experiments)? Either way, one would expect that more cells could be imaged and added to this analysis, especially given that the authors enriched for dividing cells in their assays. It is also important that cells be selected in a blinded fashion.
• Figure 4: "endogenous S-layer at the midzone": Here the authors image the localization of tagged, overexpressed copies of SlaA and SlaB, not endogenous proteins. Please correct.

Minor points:

• Line 145: While the cells clearly grow in the absence of added tryptophan, it appears that they have a more severe/noticeable growth defect when grown on solid vs. liquid media. Is there a reason why this might be so?
• Line 153: have been > has been
• Line 216: Would 5-FAA not be expected to just abiotically isomerize into the product of trpF under the acidic media conditions?
• Line 228: Was a transcription terminator added downstream of sso0890?
• Line 375: This is only true for one of the two plasmids. The expression is quite high on your pSF plasmid.

Significance

S. acidocaldarius has previously been made accessible to genetic manipulation including in-frame markerless gene deletion and exogenous expression of proteins of interest from an expression vector, pSVA-AraFX, under the control of inducible promoters (arabinose, xylose, sucrose) that allow the timely expression of target proteins in the cell. Existing tools rely on uracil auxotrophy (i.e. the parental strain is deficient for uracil synthesis, and exogenous plasmid DNA carries the missing uracil synthesis gene, allowing selection of transformants). Here, the authors develop a tryptophane auxotrophy-based selection system in S. acidocaldarius by deleting the genes trpBA. They then modified the pSVA-AraFX plasmid by replacing the uracil synthesis genes pyrEF by the tryptophan synthesis genes trpBA, allowing double expression of proteins in S. acidocaldarius. The technique is used in the present work to show localization of S-layer proteins in dividing cells as a proof on concept. This novel selection method will likely be a useful new tool for archaeal cell biologists.

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:

In this manuscript, Sherman Foo and Buzz Baum report the development of a tryptophan auxotrophy-based selection system in S. acidocaldarius. Using classical pop-in and pop-out methodology, the authors isolated a strain ΔtrpBA using a rich medium BDN medium (Brock medium supplemented with NZ-amine, Sucrose and uracil and an uracil auxotroph. To get stringent selection, they developed a defined medium BDN, based on analysis of amino acid composition of NZ-amine A and other related substrates. They then analyzed the possibility to use 5-FAA for counterselection and found that 5-FAA did not appear to function as an effective counterselection agent. Next, they successfully constructed a tryptophan complementation system using the pSVAara plasmid backbone, replacing the pyrEF cassette with the trpBAD genes from Saccharolobus solfataricus (sso0888 -sso0890).

Exploiting both uracil and tryptophan auxotrophies, the authors further demonstrated the use of this system by dual-plasmid co-transformation and co-expression of the surface layer proteins and a dominant-negative mutant of the AAA-ATPase Vps4 and confirmed that the accumulation of surface layer lattice forming protein SlaA at the midzone of division-arrested cells together with its membrane anchor SlaB. The localization of SlaA and SlaB at the midcell was in agreement with the observations previously reported by the same group.

Major comments:

1. The dural plasmids differ only at the selection markers, pryEF and trpBA. The stability of them in one cell needs to be addressed.
2. Relevant to the above, the authors should test the plasmid stability after culture with reasonable generations. Is it possible to construct a stably transmitted dural plasmid with different ori?
3. Lines 214-223, I am curious why the authors useed ΔtrpAB as the auxotroph instead of using ΔtrpF directly, because the latter could be easily subject to 5-FAA counter selection test.

Minor comments:

1. Lines 71-84, please add an important reference, Zhao et al., Rational design of unrestricted pRN1 derivatives and their application in the construction of a dual plasmid vector system for Saccharolobus islandicus, 2024.
2. In the title, the spatial organization of S-layer assembly during cytokinesis has already been reported by the authors previously. The title could be improved by slight modification

Significance

Archaea of the order Sulfolobales are model microbes for studying the biology of archaea and the origin and evolution of eukaryotic-like characteristics. Lack of sufficient selection markers has been a limitation for genetic analysis of these organisms. Although dual selection system has been developed in Saccharolobus islandicus, another model archaeon of Sulfolobales, there is no such system for Sulfolobus acidocaldarius.

The study by Foo and Baum explored a method for the formulation of defined Brock-based dropout medium, which enables stringent selection not only for trypan auxotrophic selection, but also will be potentially useful for other amino acid-based selection in general. Therefore, this study expanded the genetic toolkit available for S. acidocaldarius and provided additional evidence for spatial regulation of S-layer assembly during archaeal cytokinesis. The dual selection system was based the same plasmid backbone which could have problem in plasmid stability. Use of different compatible plasmid could improve the dual selection system. In general, the developed system will facilitate the study of cell biology and molecular biology using the the model archaeon Sulfolobus acidocaldarius.

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Reply to the reviewers

Reviewer 1

Point 1. Cas-Tuner of Xist also represses Tsix (Supp Fig 3b). This was mentioned, but was not elaborated on in great detail. Was expression of the first exons of Tsix tested to see if this was simply transcriptional interference? If not, would this imply some more complex feedback?

*A central experiment in the manuscript is the observation that Xist knock-down leads to a reduction of H3K9me3 at the Xist locus, suggesting a functional role of Xist transcription in heterochromatin formation. As pointed out by the reviewer the knock-down strategy used resulted also in a reduction of Tsix, the antisense transcript of Xist. This is unlikely to reflect transcriptional interference between Xist and Tsix, because then a Xist knock-down should result in increased Tsix level, while we observe the opposite. It is more likely a direct effect of the CRISPRi system used for the knock-down, which recruits a repressor complex to the last exon of Tsix and might therefore interfere with proper termination or processing. *

Point 2. It was surprising that targeting an HDAC with Cas-Tuner leads to reduced K9me3, and transiently inducing Xist expression actually leads to increased silencing of that allele (Fig 3h). These were very exciting results. However, this seems inconsistent with the X-linked gene expression (supp 3d), where you would expect inverted expression patterns, but it's at 50%. What explains this? I know the authors mentioned the discrepancy between 1day vs 2 days of Dox induction, but nevertheless, I would have expected a stronger effect.

*In Fig. 3f-k and Suppl. Fig. 3d we show that transient Xist induction from one allele (B6) primes this allele to become the Xist-silent allele later on (Day 4). While we observed a clear skewing for Xist expression towards the Cast allele at day 4 (Fig. 3h), the effect on X-linked gene expression is much smaller and only observed for the 1 day Dox treatment (Suppl. Fig. 3d). We believe that two effects contribute to this difference: (1) Also Xist-negative cells, which are a considerable subpopulation (Fig. 3k), express the tested X-linked genes (50% Cast, 50% B6) and thus contribute to the pool of total RNA measured by pyrosequencing, while Xist is not expressed in these cells, resulting in a stronger skewing observed for Xist RNA levels. (2) X-linked gene silencing (and reactivation) occurs with a delay relative to changes in the Xist expression pattern, such that gene reactivation from the B6 allele might not yet be complete at day 4, in particular, in the 2-day Dox treated population, and silencing at the Cast allele might not yet be complete, resulting in a mixed / weak effect on X-linked gene expression. *

Point 3. Is it possible the ZFP proteins (281 and 36L1) are partially redundant? Moreover, could these be the mysterious targets of RNF12? I presume these are ideas that have occurred to the authors, and potentially want to save them for future studies?

We have performed a comparative analysis of how ZFP281, ZFP36L1 and RNF12 affect the genome-wide H3K9me3 distribution. This analysis revealed only a minor overlap of the affected regions beyond Xist, and thus suggested that the RNF12 does not function by targeting the ZFP proteins. This analysis also does not support the idea that the ZFP proteins exhibit redundant functions.

__Point 4. __The model in Figure 6 seems to hinge on transient silencing of RNF12. Could this be tested by inducible RNF12 expression?

In principle, this is an intriguing suggestion, which would address the question of how the Xist-transcription dependent H3K9me3 deposition and the RNF12 dependent reduction of the mark interact. However, manipulating RNF12 expression will also alter Xist transcription through the REX1 pathway, which is independent of the H3K9me3-effect, making it again difficult to disentangle the contributions of these two pathways.

Point 5. I enjoyed the discussion of possible mechanisms by which Tsix contributes to robust Xist silencing. I found both of them compelling, and I hope future work will test them!

We thank the reviewer for these encouraging words.

Minor Points

Point 6. Odd to introduce RITS concept from Pombe (page 11), where I believe has never been demonstrated in mice, with perhaps an exception being piRNAs in the male germline. In other words, this would be a huge paradigm shift. There is a study showing that dsRNAs from hypomethylated ESCs can form "endosiRNAs", but these are proposed to act post-transcriptionally. That's a long way of saying, it's probably best to remove it.

We will remove this notion from the revised version of the manuscript.

Point 7. Supp 5h: there does appear to be a subtle effect on exit of naive pluripotency in Zic3KD, even if at the edge of statistical significance. Text should be reworded. Also, Supp 5 appears cited in the following order: a, b, c, f, h, d, e (realizing they cite the whole figure in the beginning of the section, but this is not really standard practice).

*We agree with the suggested changes and will implement them in a revised version of the manuscript. *

Reviewer 2

Point 1. In Figure 3, is it possible that CasTuner-mediated recruitment of HDAC4 could change the spectrum of epigenetic modifications naturally found at RE57 -- is that a reason why H3K9me3 levels would change?

With the current data set we indeed cannot fully exclude that the CasTuner-mediated Xist knock-down might not affect H3K9me3 independently of Xist transcription. However, the fact that Xist overexpression can recruit H3K9me3 (Fig. 4e), makes it likely that the knock-down effect is also mediated by Xist-dependent H3K9me3 recruitment.

Point 2. Relatedly, in the experiment outlined in Figure 3F, can the authors explain how/why in the absence of doxcycline, the system results in a 50:50 ratio of Xist selection over the four day timecourse? I might have thought that Xist expression from the TetO-containing B6 allele would require dox to be expressed, and that in the absence of dox, expression from the Cast allele would dominate at Day 4. The results are striking but my concern is that they are being influenced by an unusual property of the TetO that is not related to natural regulation of Xist.

*In the TX1072 cell line used in this study, insertion of the Dox-inducible promoter does not prevent Xist upregulation in the absence of Doxycycline. In our Dox-inducible allele, which was originally generated by Anton Wutz in the Jaenisch lab (Wutz et al, Nat Gen, 2002), a TetO array is inserted directly upstream of the Xist TSS, leaving the core promoter and endogenous regulation largely intact. We have characterized the dynamics of random XCI (in the absence of Dox) in this line extensively in a previous publication (Pacini et al, Nat Comm, 2021). *

Point 3. Do the authors have access to a wild-type female B6/Cast ESC line? If so, the prediction based on the authors model would be that the B6 version of Xist is expressed more highly prior to differentiation, because in these hybrids, B6 is the allele that is typically inactivated after differentiation. Alternatively, if the Xist promoter has been substantially modified on the B6 allele in TX1072, can the authors perform a reciprocal Xist upregulation, by targeting a dCas9-activator to the wild-type Cast allele (which would presumably not upregulate Xist on the TetO-driven B6 allele)?

*The notion that differential timing of Xist upregulation might differ between mouse strains, which could then contribute to the often observed skewing in hybrid mice (e.g. in a B6xCast cross), is very interesting and would be worth following up in future studies. *

Reviewer 2, Point 4. Lastly, the authors show that Rnf12 deletion increases H3K9me3, but abolishes Xist expression. Am I correct to interpret that this result is the opposite of what would be predicted by the TetO and CasTuner experiments: the less Xist that is expressed, the lower the H3K9me3?

With the available data we cannot distinguish whether the RNF12- and the Xist-pathway are independent or in some way dependent on each other. This is technically difficult to disentangle because Rnf12 and Xist modulate each other.

Minor Points

Point 5. Am I correct in interpreting that TX1072 ESCs have a dox-inducible promoter driving Xist on the B6 allele? If so, for accuracy and ease of interpretation, the TetO should somehow be denoted in where X-B6 or Xist-B6 is shown in Figure 2, and this piece of information should be delivered when the TX1072 ESC line is first introduced in the manuscript.

The TX1072 ESCs indeed have a Dox-inducible promoter inserted upstream of the Xist TSS, which however does not affect the random choice of the active allele in the absence of Doxycycline.

Point 6. The clarity of the section describing the data in Figure 4 could be increased (modestly) if the title of the section and the figure were edited to distinguish the effects in undifferentiated cells from differentiated ones. The authors nicely show that Tsix transcription is not required for Xist-dependent H3K9me3 deposition at RE57 in undifferentiated cells, but is required for its maintenance in differentiated cells.

We will clarify this point in future versions of the manuscript.

Point 7. The data in Figure 5 are described in separate sections in the manuscript, entitled "Xist activator RNF12 counteracts heterochromatin formation at Xist" and "RNF12 regulates heterochromatin independently of REX1". This is within the authors discretion, but it may make sense from an organizational standpoint to split Figure 5 into two figures, to match with the way that the data are described in the manuscript. A split into two would also enable the supplemental data associated with Figure 5 to be shown in the main figure as well. As a final small suggestion for the authors, I might consider renaming the title of the final section to one that is more specific, such as "RNF12 counteracts heterochromatin at Xist and sites across the genome independently of REX1" etc. The term "regulates" does not indicate in what direction the primary regulation occurs.

*We will consider this suggestion for future versions of the manuscript. *

__Reviewer 3 __

Point 1. The H3K9me3 CUT&Tag profiles presented in this manuscript appear substantially different from those reported by Almeida et al. (2026; PMID: 41957023). This difference may in part reflect the use of different H3K9me3 antibodies, however, this raises some concern regarding the specificity of the H3K9me3 profiling performed here. The authors should provide validation of the H3K9me3 antibody used in this study, e.g. by including the KMetStat panel in a suitable control line during CUT&Tag. Validation of the specificity of the H3K9me3 antibody used here would help facilitate the interpretation of the differences in H3K9me3 profiles reported in the two studies.

The H3K9me3 profiles along the Xist gene are indeed somewhat different between the two studies. In particular Almeida et al do not observe the H3K9me3 accumulation that we see at RE57 at the Xist promoter-proximal region, but instead a much broader domain that extends over the Xist gene body. This RE57-centric pattern is however also observed in ChIP-seq data from a different study (Bleckwehl et al, 2021, PMID: 34599190), which we had re-analyzed previously (Gjaltema et al, 2022). Nevertheless, we welcome the suggestion to verify antibody specificity.

Point 2. A limitation of Figures 3-5 is that the Xist, Tsix, and Rnf12 perturbation experiments appear to have been performed in bulk populations of hybrid XX cells undergoing random X-inactivation rather than the TX-Maged1-2tag fluorescent reporter system employed in Figure 2, which permits separation of cells according to which X chromosome is inactive. The experiments in Figures 3-5 use the CasTuner cell line, which is described as hybrid, but not indicated to be XX∆XIC-B6 (i.e. not undergoing biased X-inactivation) in the text or methods of the paper. Perturbations of Xist, Tsix, and Rnf12 could affect the active- and inactive-X chromosomes differently, whereas the bulk H3K9me3 CUT&Tag measurements in Figures 3-5 represent aggregate signal from both X chromosomes in a mixed population of cells that are undergoing random X-inactivation. Thus, a change in bulk H3K9me3 does not establish whether the change occurs specifically on the Xist-silent allele, the Xist-expressing allele, or both. Understanding the dynamics of H3K9me3 on both X chromosomes would help clarify the authors' proposed model, in which it is still unclear how H3K9me3 ultimately preferentially accumulates on the Xist-silent allele. Ideally, key perturbation experiments should be repeated in the TX-Maged1-2tag system to enable allele-specific quantification of changes to Xist expression and H3K9me3 accumulation on the active- vs. inactive-X chromosomes.

For example, in Figure 4H, Xist RNA expression is increased following Tsix knockdown during differentiation. Tsix is required for maintenance of Xist repression on the active-X chromosome (PMID: 25981039), therefore, the upregulation of Xist RNA could reflect a de-repression of Xist on the active-X. Ideally, the authors would quantify Xist expression from the active- vs. inactive-X chromosomes using allele-specific RNA-seq. As an alternative to allele-specific RNA-seq, the authors could determine whether Xist RNA upregulation following Tsix knockdown reflects increased expression of Xist from the active-X, inactive-X, or both, using allele-specific fluorescent in situ hybridization (FISH). However, discerning whether H3K9me3 changes on the active- vs. inactive-X upon Tsix knockdown is arguably more critical to the model, and would require use of the CasTuner system in the TX-Maged1-2tag fluorescent reporter line.

*While indeed the majority of experiments use bulk cell populations, we contend that it is still possible to draw conclusions about which allele is affected by a perturbation. In particular in those experiments where we observe a reduction of H3K9me3 (Xist-KD, Tsix-KD), we can attribute this to the Xist-silent allele, because we show in Fig. 2 that the mark is nearly exclusively present at that allele. *

Point 3. We suggest that the authors soften their description of H3K9me3 as having a role in the "initiation of X-inactivation". Conventionally, initiation of X-inactivation refers to the initiation and upregulation of Xist RNA expression, whereas the authors' data suggest that Xist transcription precedes and promotes H3K9me3 deposition at the Xist locus. The authors' findings therefore appear more directly relevant to the establishment of Xist allele-specific repression on the active-X, and perhaps more accurately the "establishment" of X-inactivation, rather than initiation of X-inactivation itself.

We will consider this suggestion in future versions of the manuscript.

Point 4. Figure 3K shows a strikingly low frequency of Xist-expressing cells at day 4 of differentiation in both the "no dox" and "dox" conditions. Approximately 50% of no dox cells and 25% of dox-treated cells show Xist RNA coating at day 4 of differentiation. These data, particularly the no dox condition, contrast with Figure 2, in which nearly 100% of WT XX cells exhibit Xist RNA coating at day 4 of differentiation. Can the authors clarify the reason for the notable difference in Xist induction efficiency between the control cells (WT XX and no-dox) shown in Figures 2 and 3? Presumably, the reduced number of Xist-expressing cells in the dox-treated condition reflect a higher proportion of cells in which both Xist loci were silenced by H3K9me3 accumulation through Xist overexpression. The authors can directly test this experimentally.

*In Fig. 2c the cells were sorted according to their Xist expression pattern, generating pure populations of Xist-positive cells. Therefore the Xist-positive fraction is much higher than in unsorted cells shown in Fig. 3k. The two experiments are actually very comparable when analyzing the unsorted cells (Supplementary Fig. 2f vs Fig. 3k). *

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Referee #3

Evidence, reproducibility and clarity

Summary Here, the authors investigate the role of tri-methylation at histone H3 lysine 9 (H3K9me3) in the regulation of Xist during the initiation and establishment of random X chromosome inactivation. Previous work from the authors (PMID: 34932975) identified a regulatory element within the first exon of Xist, termed RE57, that exhibits differential H3K9me3 levels in female cells harboring a single X chromosome (XO) relative to XX female cells during early differentiation. In addition, a CRISPR screen by the authors (PMID: 41053217) identified the H3K9 methyltransferase SETDB1 as a potential repressor of Xist RNA expression. Recent work (PMID: 41957023) further implicates SETDB1 in the accumulation of H3K9me3 across the Xist gene body during differentiation of XX female embryonic stem cells (ESCs) to neural progenitor cells (NPCs), potentially through an interaction between SETDB1, the HUSH complex, and the Xist RNA. Building on these observations, here, the authors examine the establishment and maintenance of H3K9me3 at the Xist promoter-proximal region and its relationship to Xist transcription and known regulators of X-inactivation.

Using hybrid XX ESCs to enable allele specific analyses, the authors showed that H3K9me3 preferentially accumulates in the RE57 region of the Xist allele of the active X chromosome (the "Xist-silent" allele) during the onset of random X-inactivation.  Knockdown of Xist using the CasTuner dCas9-HDAC4 fusion system in undifferentiated and differentiating XX and XO ESCs unexpectedly revealed that Xist transcription contributes to the accumulation of H3K9me3 at the RE57 region.  The authors further show that Xist-dependent H3K9me3 deposition at the RE57 region is independent of Tsix, although Tsix somewhat contributes to the maintenance of H3K9me3 during cellular differentiation.  Finally, the authors investigate the role of X-linked Xist activator RNF12 and show that loss of RNF12 promotes the accumulation of H3K9me3 at the RE57 region through a mechanism that they propose is independent of REX1 targeting.  From these findings, the authors propose a model in which transient Xist transcription promotes initial H3K9me3 deposition at the RE57 region of the future active-X, which is maintained in part by Tsix on the active-X and counteracted by RNF12 on the future inactive-X through an undefined mechanism.

These data are intriguing and provide evidence for a relationship between Xist transcription and H3K9me3 deposition at the RE57 region.  However, the mechanistic interpretation of these findings is limited by the use of bulk populations of cells undergoing random X-inactivation in many of the perturbation experiments, which makes it difficult to determine the consequences of altered Xist, Tsix, or Rnf12 expression on the active- vs. inactive-X chromosomes.  In addition, several aspects of the proposed temporal relationship between Xist transcription, H3K9me3 deposition, and subsequent Xist silencing remain unresolved - particularly how the Xist-expressing inactive-X avoids accumulation of and silencing by H3K9me3.

Major Points

1. The H3K9me3 CUT&Tag profiles presented in this manuscript appear substantially different from those reported by Almeida et al. (2026; PMID: 41957023). This difference may in part reflect the use of different H3K9me3 antibodies, however, this raises some concern regarding the specificity of the H3K9me3 profiling performed here. The authors should provide validation of the H3K9me3 antibody used in this study, e.g. by including the KMetStat panel in a suitable control line during CUT&Tag. Validation of the specificity of the H3K9me3 antibody used here would help facilitate the interpretation of the differences in H3K9me3 profiles reported in the two studies.

2. A limitation of Figures 3-5 is that the Xist, Tsix, and Rnf12 perturbation experiments appear to have been performed in bulk populations of hybrid XX cells undergoing random X-inactivation rather than the TX-Maged1-2tag fluorescent reporter system employed in Figure 2, which permits separation of cells according to which X chromosome is inactive. The experiments in Figures 3-5 use the CasTuner cell line, which is described as hybrid, but not indicated to be XX∆XIC-B6 (i.e. not undergoing biased X-inactivation) in the text or methods of the paper. Perturbations of Xist, Tsix, and Rnf12 could affect the active- and inactive-X chromosomes differently, whereas the bulk H3K9me3 CUT&Tag measurements in Figures 3-5 represent aggregate signal from both X chromosomes in a mixed population of cells that are undergoing random X-inactivation. Thus, a change in bulk H3K9me3 does not establish whether the change occurs specifically on the Xist-silent allele, the Xist-expressing allele, or both. Understanding the dynamics of H3K9me3 on both X chromosomes would help clarify the authors' proposed model, in which it is still unclear how H3K9me3 ultimately preferentially accumulates on the Xist-silent allele. Ideally, key perturbation experiments should be repeated in the TX-Maged1-2tag system to enable allele-specific quantification of changes to Xist expression and H3K9me3 accumulation on the active- vs. inactive-X chromosomes.

For example, in Figure 4H, Xist RNA expression is increased following Tsix knockdown during differentiation. Tsix is required for maintenance of Xist repression on the active-X chromosome (PMID: 25981039), therefore, the upregulation of Xist RNA could reflect a de-repression of Xist on the active-X. Ideally, the authors would quantify Xist expression from the active- vs. inactive-X chromosomes using allele-specific RNA-seq. As an alternative to allele-specific RNA-seq, the authors could determine whether Xist RNA upregulation following Tsix knockdown reflects increased expression of Xist from the active-X, inactive-X, or both, using allele-specific fluorescent in situ hybridization (FISH). However, discerning whether H3K9me3 changes on the active- vs. inactive-X upon Tsix knockdown is arguably more critical to the model, and would require use of the CasTuner system in the TX-Maged1-2tag fluorescent reporter line.

Minor Points

1. We suggest that the authors soften their description of H3K9me3 as having a role in the "initiation of X-inactivation". Conventionally, initiation of X-inactivation refers to the initiation and upregulation of Xist RNA expression, whereas the authors' data suggest that Xist transcription precedes and promotes H3K9me3 deposition at the Xist locus. The authors' findings therefore appear more directly relevant to the establishment of Xist allele-specific repression on the active-X, and perhaps more accurately the "establishment" of X-inactivation, rather than initiation of X-inactivation itself.

2. Figure 3K shows a strikingly low frequency of Xist-expressing cells at day 4 of differentiation in both the "no dox" and "dox" conditions. Approximately 50% of no dox cells and 25% of dox-treated cells show Xist RNA coating at day 4 of differentiation. These data, particularly the no dox condition, contrast with Figure 2, in which nearly 100% of WT XX cells exhibit Xist RNA coating at day 4 of differentiation. Can the authors clarify the reason for the notable difference in Xist induction efficiency between the control cells (WT XX and no-dox) shown in Figures 2 and 3? Presumably, the reduced number of Xist-expressing cells in the dox-treated condition reflect a higher proportion of cells in which both Xist loci were silenced by H3K9me3 accumulation through Xist overexpression. The authors can directly test this experimentally.

Significance

The manuscript seeks to address how one of the two X chromosomes in cells of eutherian females does NOT undergo X-inactivation. This is an important question to address, since it gets at the heart of how the two Xs become transcriptionally divergent despite sharing the same or similar sequences. The question, however, isn't adequately addressed via experimentation, as detailed above.

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Referee #2

Evidence, reproducibility and clarity

Summary

Kanata and collegues present an interesting follow-up of a study published by the Schulz lab in 2022, which discovered a domain of H3K9me3 and DNA methylation deposited on the Xist promoter during differentiation of mouse embryonic stem cells. Kanata et al. demonstrate in this manuscript that the H3K9me3 and DNA methylation modifications are deposited on the Xist allele that is ultimately silenced during differentiation. Intriguingly, they present results that suggest Xist overexpression from one allele increases H3K9me3 and DNA methylation and primes that allele to be selected for ultimate silencing. They further show in the final figures of the manuscript that Tsix modulates the levels of H3K9me3 in differentiated cells, and that Rnf12 has a REX1-independent role in reducing the accumulation of H3K9me3 surrounding the RE57 element.

Overall the study was well controlled, well written, and the conclusions were supported by the data. From a visual presentation standpoint, the Figures were exceptionally clear. I enjoyed reading the manuscript.

Major questions:

My main questions revolve around the somewhat non-intuitive observation that higher Xist expression prior to differentiation results in preferential silencing of the more highly expressed allele after differentiation. I am wondering if the authors can rule out that the relationship that they observe between higher Xist expression and higher H3K9me3 levels is a natural phenomenon and not due to genetic manipulation of the Xist locus? Asking because the key data suggesting the relationship were acquired using genetic modifications of the Xist locus (in Figure 4), whereas the data in Figure 5 (by my interpretation) suggest the opposite result, that the lower the levels of Xist, the higher the levels of H3K9me3.

1) In Figure 3, is it possible that CasTuner-mediated recruitment of HDAC4 could change the spectrum of epigentic modifications naturally found at RE57 -- is that a reason why H3K9me3 levels would change?

2) Relatedly, in the experiment outlined in Figure 3F, can the authors explain how/why in the absence of doxcycline, the system results in a 50:50 ratio of Xist selection over the four day timecourse? I might have thought that Xist expression from the TetO-containing B6 allele would require dox to be expressed, and that in the absence of dox, expression from the Cast allele would dominate at Day 4. The results are striking but my concern is that they are being influenced by an unusual property of the TetO that is not related to natural regulation of Xist.

3) Do the authors have access to a wild-type female B6/Cast ESC line? If so, the prediction based on the authors model would be that the B6 version of Xist is expressed more highly prior to differentiation, because in these hybrids, B6 is the allele that is typically inactivated after differnetiation. Alternatively, if the Xist promoter has been substantially modified on the B6 allele in TX1072, can the authors perform a reciprocal Xist upregulation, by targeting a dCas9-activator to the wild-type Cast allele (which would presumably not upregulate Xist on the TetO-driven B6 allele)?

4) Lastly, the authors show that Rnf12 deletion increases H3K9me3, but abolishes Xist expression. Am I correct to interpret that this result is the opposite of what would be predicted by the TetO and CasTuner experiments: the less Xist that is expressed, the lower the H3K9me3?

Minor comments:

5) Am I correct in interpeting that TX1072 ESCs have a dox-inducible promoter driving Xist on the B6 allele? If so, for accuracy and ease of interpretation, the TetO should somehow be denoted in where X-B6 or Xist-B6 is shown in Figure 2, and this peice of information should be delivered when the TX1072 ESC line is first introduced in the manuscript.

6) The clarity of the section describing the data in Figure 4 could be increased (modestly) if the title of the section and the figure were edited to distinguish the effects in undifferentiated cells from differentiated ones. The authors nicely show that Tsix transcription is not required for Xist-dependent H3K9me3 deposition at RE57 in undifferentiated cells, but is required for its maintenance in differentiated cells.

7) The data in Figure 5 are described in separate sections in the manuscript, entitled "Xist activator RNF12 counteracts heterochromatin formation at Xist" and "RNF12 regulates heterochromatin independently of REX1". This is within the authors discretion, but it may make sense from an organizational standpoint to split Figure 5 into two figures, to match with the way that the data are described in the manuscript. A split into two would also enable the supplemental data associated with Figure 5 to be shown in the main figure as well. As a final small suggestion for the authors, I might consider renaming the title of the final section to one that is more specific, such as "RNF12 counteracts heterochromatin at Xist and sites across the gennome independently of REX1" etc. The term "regulates" does not indicate in what direction the primary regulation occurs.

Significance

Significance

The significance of this work, in my opinion, is its investigation into the dynamics of H3K9me3 deposition surrounding Xist promoter following differentiation and the data showing that Rnf12 has an REX1-independent function in counteracting the deposition of H3K9me3 at Xist and at other sites across the genome. The putative link between Xist expression and H3K9me3 is intriguing, but as described above, I do not quite see how it is consisent between the data described in Figure 3 and the data described in Figure 5.

If clarity about the relationship between Xist expression and H3K9me3 deposition were obtained during revision, I would describe the study as providing a mechanistic advance that is important from a basic research standpoint.

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Referee #1

Evidence, reproducibility and clarity

In early mammalian development, the cells in female embryos silence one of their two X chromosomes in a random manner. After this initial choice, there is robust epigenetic memory, such that the silent X chromosome remains silent throughout life. There has been a decades-long intense effort to investigate this phenomenon, and a great deal is known about dynamics, mechanism and implications in development and disease. Nevertheless, one of the most interesting facets of this process-how this random choice is made to begin with-remains nebulous. In this study from Kanata and colleagues, they do not resolve this quandary, but they do make important insights. Briefly, X chromosome silencing requires the cis action of the non-coding RNA Xist. This RNA contains a regulatory region called RE57 (previously characterized by the lab) that becomes enriched for the heterochromatic mark H3K9me3, associated with the silent form of Xist. In other words, the H3K9me3 at RE57 is associated with the active X chromosome. Here, in a set of elegant genetic assays performed in mouse ESCs, the authors show that transient expression of Xist is counterintuitively required for deposition of H3K9me3. The well-characterized antagonist ncRNA of Xist, Tsix, is not required for this initial deposition, but instead helps maintain and reinforce the RE57 heterochromatin, which involves accumulation of DNA methylation. The authors then went on to investigate candidate trans regulators of Xist silencing. They made the novel finding that RNF12 counteracts H3K9me3 through an REX1-independent function, adding a new dimension to Xist regulation. While they did not show the mechanism, per se, this should be fodder for future studies.

Below are some questions and comments.

• Cas-Tuner of Xist also represses Tsix (Supp Fig 3b). This was mentioned, but was not elaborated on in great detail. Was expression of the first exons of Tsix tested to see if this was simply transcriptional interference? If not, would this imply some more complex feedback?

• It was surprising that targeting an HDAC with Cas-Tuner leads to reduced K9me3, and transiently inducing Xist expression actually leads to increased silencing of that allele (Fig 3h). These were very exciting results. However, this seems inconsistent with the X-linked gene expression (supp 3d), where you would expect inverted expression patterns, but it's at 50%. What explains this? I know the authors mentioned the discrepancy between 1day vs 2 days of Dox induction, but nevertheless, I would have expected a stronger effect.

• Is it possible the ZFP proteins (281 and 36L1) are partially redundant? Moreover, could these be the mysterious targets of RNF12? I presume these are ideas that have occurred to the authors, and potentially want to save them for future studies?

-The model in Figure 6 seems to hinge on transient silencing of RNF12. Could this be tested by inducible RNF12 expression?

• I enjoyed the discussion of possible mechanisms by which Tsix contributes to robust Xist silencing. I found both of them compelling, and I hope future work will test them!

Minor

• Odd to introduce RITS concept from Pombe (page 11), where I believe has never been demonstrated in mice, with perhaps an exception being piRNAs in the male germline. In other words, this would be a huge paradigm shift. There is a study showing that dsRNAs from hypomethylated ESCs can form "endosiRNAs", but these are proposed to act post-transcriptionally. That's a long way of saying, it's probably best to remove it.

• Supp 5h: there does appear to be a subtle effect on exit of naive pluripotency in Zic3KD, even if at the edge of statstical significance. Text should be reworded. Also, Supp 5 appears cited in the following order: a, b, c, f, h, d, e (realizing they cite the whole figure in he beginning of the section, but this is not really standard practice).

Significance

All told, I found this to be a fantastically executed study. The authors made great use of a bevy of X-chromosome-specific genetic tools, as well as implementation of their Cas-Tuner system developed by the group. While the gene networks at play can be complex-as well as having to keep track of simultaneous, asymmetric regulation occurring on the two X homologs-the authors assist the reader with clear descriptions and helpful models throughout. I also appreciated the thoughtful discussion, drawing links with the biallelic Xist expression in mice with what is known in other mammals (humans and rabbits). Of course, the study begs the question: if Xist expression leads to K9me3 enrichment, how does the cell choose which allele to activate? But it was not trivial to reach this question, and I am excited for future work to unravel this conundrum.

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Referee #3

Evidence, reproducibility and clarity

Summary:

This study characterizes the localization of Rootletin, the major molecular component of the ciliary rootlet, in radial glial cells (RGCs) of the developing cortex. The authors show that in addition to connecting the two centrioles, Rootlet also forms a ring-like structure in RGCs while their apical endfeet constrict (Fig 1-2). This ring-like structure is also observed when delamination and neuronal differentiation are forced by overexpressing Lzts1 and Ngn2 in RGCs (Fig 3-4). Finally, the authors characterize the interaction between the rootlet and the Zika virus protein NS5 (Fig 5).

Major comments:

(1) It is difficult to extract the information on the actual function of Rootletin from this manuscript. There is no data demonstrating its active function in RGCs. All figures are descriptive, illustrating where Rootletin localizes and showing that its intensity increases during apical endfoot constriction. Most major claims are unsupported by data. For example:

i) Which specific data support the claim that the Rootletin "shapes neuroepithelial architecture"? There is no such data. Most figures in the manuscript point to a single conclusion: Rootletin intensity increases at the apical endfeet concurrently with the shrinkage of the apical surface area. Does Rootletin actively drive apical surface constriction, or does the constriction of the apical endfeet cause the now one-end-free rootlet fiber to passively coil into a circular structure? It seems that the latter explanation is more plausible.

ii) How does the Zika virus protein NS5 "hijack" the rootlet to trigger premature neuronal delamination. The data in Figure 5 attempt to show colocalization between GFP-Rootletin and NS5; no functional data demonstrate how the "hijacking" work. In addition, the claimed co-localization is not unconvincing either.

Overall, the manuscript is crammed with data, but none of the data support the major claim.

(2) Most images are oversaturated and over-processed; the only acceptable figure is Figure 2F. The remaining figures lack sufficient detail, and could be artifacts from excessive image processing. Due to this overall low quality, the conclusions drawn from these images could be misleading. For example:

i) The pattern in Fig 2I is typical image processing artifact, and may not represent the true biological structure.

ii) Most of the GFP-Rootlet images in Figures 3 and 5 are oversaturated and over-processed, obscuring the details of the true endogenous structure.

iii) Images in these figures are low quality and does not contain the necessary details to support the conclusion: Figure 3I-K, 4F-P.

(3) Most conclusions are made from over-expression of GFP-Rootletin. However, the GFP-Rootletin does not resemble endogenous Rootlet: in FigEV3H, Rootletin antibody does not recognize electroplated GFP-Rootletin; In fig EV3A-F, none of the endogenous Rootlet show the rim-like structure that is observed in GFP-Rootletin. Therefore, most data on over-expressed GFP-Rootletin could be overexpression artifacts.

(4) Other critical stuctures appear to be inaccurately represented. For instance, at the apical endfeet, acetylated-tubulin staining typically highlights a wheel-like structure with a circular ring and radial spokes (Kasioulis et al., 2017 eLife). However, this structure is not observed in Figures 3G-N.

Also in Figures 3G-N, the claimed primary cilium does not represent ciliary structure. Another non-microtubule marker is needed to label primary cilia in these neuroepithelial cells.

The Drebrin staining in Figure3Q is also different from what is usually observed (such as in Kasioulis et al., 2017 eLife). The model showing that it localizes to the corner is misleading.

These issues reinforce the concern that images in this manuscript are either overprocessed or of insufficient quality to accurately resolve true biological structures.

Minor comments:

Some quantification does not make sense: for example, Figure 3B: The majority of the data points are clustered in the left corner of the plot. Given this distribution, it is statistically unsound to infer a negative correlation based on a few sporadic outliers residing from the main cluster. The same is true for Figure 4G and 4Q.

Significance

The topic addressed in this manuscript is significant and of general interest. However, there are serious concerns regarding the methodology, data quality, and interpretation of the results. There is a serious disconnect between the presented data and the authors' major claims.

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Referee #2

Evidence, reproducibility and clarity

Summary:

During CNS development, neuroepithelial (NE) cells committed to neural differentiation detach from the ventricular surface. This detachment involves dynamic cytoskeleton and membrane remodelling including downregulation of adherens junction proteins, actomyosin contractility and microtubules reorganisation at the apical end-foot of the NE cell. Infection by the Zica virus induces premature apical constriction and NE cells delamination, which could explain the microcephaly observed in embryos from mothers infected by the virus. Saade et al. (2020) previously identified Rootletin, a component of the ciliary rootlet involved in cilium stability, as an interactor of Zica NS5 protein.<br /> Here, the authors investigate the dynamics of rootletin subcellular localisation and remodelling during NE cells delamination using the surface epithelium of the developing chick neural tube electroporated to express GFP-Rootletin as a model. They describe several Rootletin organisation pattern, suggesting that Rootletin fibres are dynamic structures. In mitotic cells, GFP-Rootletin associates with either one or both spindle poles. While in interphase NE cells GFP-Rootletin fibres present an extended apico-basal organisation that reorganises into a rim-like structure at the apical foot before and during delamination of NE cell. They show that this rim-like rearrangement precedes apical foot constriction and investigate the connection between cytoskeleton and Rootletin remodelling. This leads the authors to propose a model of sequential spatiotemporal reorganisation of Rootletin, microtubule and acto-myosin cytoskeleton during apical foot contraction. Importantly, this Rootletin fibre organisation is also observed in embryonic mouse neural tube, human 3D neural organoids. Last, the authors investigate how Zika-NS5 and GFP-Rootletin dynamically interact during NE cell delamination.

Major comments:

Are the claims and the conclusions supported by the data or do they require additional experiments or analyses to support them?

1.. The first part of this manuscript consists in the description of rootletin organisation in NE cells, mainly on fixed tissues. Although the authors present endogenous localisation in the mouse embryonic neural tube and in human neural organoid, the anti rootletin staining of the chicken neural tube is very noisy and hence difficult to interpret (EV3). This, and the aim to study the dynamics of Root organisation, led the authors to use mis-expression of GFP-Root in the chicken neural epithelium as a model. A validation that the ectopic expression of GFP-Root is not inducing artificial Root structures is missing. Specifically, the manuscript relies on the observation that Rootletin adopts several organisations from inter-centriolar, basally directed, fibres to fibres oriented in the apical plane first in a "coma" shape and then adopting a rim-like structure. Although en face imaging of the embryonic mouse neural tube are shown, these rootletin patterns are not studied. This would however constitute a validation that the GFP-Rootletin structures described are not artificially induced by their ectopic GFP-Root expression. Alternatively, the use of another anti Rootletin antibody with less background noise in the chicken neural epithelium could be used. (Of note, the "co-localisation" of GFP-Root and "endogenous" Root labelled with the antibody presented in EV3 only shows that the anti rootletin recognises the GFP-Root, unless the epitope was mutated, which should then be mentioned). 2. There is an overall lack of quantification. There is no indication of the number at which the different Root patterns are observed. Again, the whole work relies on these static observations to propose that Rootletin fibres reorganise before and during apical constriction of the NE cells. Indications of the frequency of these events, and the number of independent biological replicates used to obtain these data, is thus mandatory to support the model. This concerns particularly the events described in Figure 1C, 1H, 2A-F, 3C-E, I-K, Q-R. If indeed root forms a rim before apical constriction, this should be supported by quantifications. Also, in GFP-root expressing cells, is there an apical foot area below which root forms a rim, but is still not constricted by the apical foot perimeter? That information is not present with the different ratios integrated by the authors (SAM, AE) and should be analysed (see comment below) to better describe the process. 3. the authors aim to determine if rootletin remodelling precedes neuronal delamination by inducing differentiation or constriction with ectopic expression of respectively Neurog2 and Lzts1. As far as I understand, this section only shows that i) neurog2 induces apical constriction and neuronal differentiation as previously published (panels B, E), premature accumulation of Lzts1 (panel J-L), which surprisingly does not lead to apical constriction in all cells since there is a population of cells with large apical surface areas and Lzts1 while in control condition such population is not found (4L black dots and 3F). But this experiment is not detailed enough to provide information regarding rootletin organisation. Quantification in 4G does not differ from 3F in the distribution of cell population with low or high rootletin occupancy. A relevant information would be to analyse if the cells that have a large apical area and Lzts1 also present rooteltin as a rim or not. If not, that would show that Lzts1 expression is not sufficient to trigger root reorganisation, nor is neurog2 induction, and that Root reorganisation is controlled by a different, potentially earlier, mechanism. Similarly, Lzts1 mis-expression only shows that it can induce apical foot constriction independently of cell differentiation to neuronal fate. Again, one should look at the shape of root fibres in the "not natural" population, ie large apical surface with Lzts1. Unless this specific population presents a different behaviour of Root fibres than large apical surface cells without Lzts1, I do not see the point of this part. Dynamics of root fibres organisation with respect to apical foot surface already suggest that remodelling precedes delamination. This could be further supported if remodelling could be triggered independently of differentiation and induce apical foot constriction. With this in mind, does mis-expression of GFP-Root trigger more apical constriction than mis-expression of a mock GFP construct? Going back to the point, does mis-expression of GFP-Root artfectualy trigger GFP-Root shapes? 4. In a previous work (Saade 2020), the authors showed that mis-expression of Zika virus NS5 protein localises at the centriole and nuclei of E cells and promotes their delamination. They had further identified Root as an interactor of ZikV-NS5 and showed that upon ZikV-NS5 mis-expression in human cells, cilia associated pool of endogenous Rootletin decreases. Here, the authors aim to further characterise ZikV-NS5 Rootelin interaction, with the idea to propose a model for ZikV behaviour. However, they did not describe any lagging localisation for ZikV-NS5 basal to the centriole, as shown in Figure 5C-G, in their previous work. This raises the question whether the observed localisation here could be an artefact due to the mis expression of GFP-Root itself. Same mis-expression experiments using a GFP mock plasmid in place of GFP-Root is necessary to verify that the observed localization is not a consequence of GFP-Root mis-expression triggering ectopic localisation of ZikV-NS3 but a real "hacking" of the rootletin. More, they show here an accumulation of GFP-Root at the apical foot of NE cells, in contradiction with previous work showing a decrease of Root centriolar localisation. It is surprising that such accumulation has not been observed before. To exclude any artefact due to GFP-Root misexpression, endogenous Root should be monitored.

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

Are the data and the methods presented in such a way that they can be reproduced?

yes, except that the type of image shown in the figures is not specified: single confocal plane versus Z projection should be mentioned when relevant. As well the line along which plots were drawn in figures 1 and 2 are missing and should be shown.

Are the experiments adequately replicated and statistical analysis adequate?

there is no information regarding numbers of events analysed for Rootletin localisation pattern, nor about biological replicates. these should be added or when necessary biological replicates performed.

Minor comments:

Specific experimental issues that are easily addressable.

1. Lines 143-146 : live imaging of GFP-Root "fibres" revealing a movement "reminiscent of interkinetic nuclear migration". As H2B-RFP was co electroporated with Root-GFP, showing nuclei could be informative as this would show if the rootletin structure is connected to and moves together with nuclei or has independent movements.
2. In several figures, co-stainings are necessary to support the claims regarding localisation patterns. As well IF stainings are often saturated, which deteriorates the analysis. Please improve the image quality

a. Figure 1F: showing ZO1 (membrane label) and centrin (centriole) in the same colour is confusing, especially since one of the staining seems dotty. Show centrioles and membrane in two different colours as in Fig 2A-F.

b. Figure 1T,V: add a centrin label to support the claim of intercentriolar localisation of Rootletin

c. Figure 3G: Acetylated tubulin staining saturated. Image should be improved. As well, a costaining, with Arl13B for example, is necessary to identify the presence of cilia. 3. Figure 3G-M: the panels with Acetylated tubulin staining are not convincing. The stainings are saturated and, based on the text, it seems that they correspond to z-projection of several focal planes (Fig 3G: there is a mention of "basally oriented bundles"). If so, this should me mentioned in the figure legend. Otherwise, how can you decipher bundles in the plane of the epithelium from basally oriented? New images should be provided to better support the microtubules rearrangements. Again here, there is a need for quantification of number of events observed.

Are prior studies referenced appropriately?

yes

Are the text and figures clear and accurate?

The text is overall clear however some sentences are over-interpretations and should be either removed or rephrased.

1. Lines 155-160 "In some apical end-feet, Rootletin is exclusively localized at the centrosome (Figs. 1H, I (upper), J (left)). In others, Rootletin appears as a rim-like structure, extending from the centrosome towards, and aligning partially with, the apical junction, where the adherens junctions (AJs), tight junctions (TJs)- and the polarity complex are localised (Figs. 1 H, I (lower), J (right), K)" this centrosome localisation could in fact be fibres with an apico-basal orientation, as shown in fig 1C. This part should be modified to propose this alternative.
2. Lines 261-263: there are no evidence of a mechanical contribution of Rootletin to apical constriction. the sentence "likely playing a mechanical role in apical constriction...morphogenesis" should be either removed or clearly presented as a hypothesis of the authors.
3. Lines 283-293: with fig 2 A-F and Fig 3C-E, the authors show that Rootletin fibre remodelling occurs before apical constriction and Lzts1 accumulation since rim-like structures are observed in not-constricted apical foot with no Lzts1 staining. However, there are no data showing that once Rootletin forms a rim, it always leads to apical constriction. Conclusion on a tight association between remodelling and constriction should thus be removed.
4. Lines 333-336: the "uniform" distribution of debrin in constricted apical feet could be the consequence of tricellular junctions being very close to each other and not resolved with the imaging set used here. Hence the mention (line 364) that Debrin "redistributes" along apical endfoot cortex seems to be an overinterpretation of the observation.

Figures

1. As a general comment, IF stainings are saturated, which deteriorates the analysis. Please improve the image quality. Specifically Fig. 3I-K.
2. Figure 1J,W,X: show the region/ line used to generate these profiles.
3. Figure 2H-I: quality of image very degraded. provide better images to support measure of Root length.
4. Figure 4L and 3B should be shown in the same orientation for comparison purposes. Same for 3F,4G and 4Q
5. Figure legends: We lack necessary information regarding the imaging modalities, specifically to conclude on apico-distal localisation. Are the images shown Z-projections? How are cell outlined?

Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

1. the authors aim to quantify the Rootletin reorganisation using two read-outs: the ratio between root fibre length and cell membrane periphery (SAM) and the ratio between Root area and apical foot area (AE). These read-outs are not fully convincing. First, measure of Root fibre length appears subject to high variability due to the precision of the images and the way Root fibres seem to coil as apical foot surface reduces. Second, these read-outs do not account for the formation of rim-like structures preceding the constriction of the apical foot surface. Analysing the categories of root structure for different surface coverage (AE) could be more informative.

Significance

General assessment:

this work provides a description of Root dynamics of localisation, as reconstructed mainly from still images, but also with the support of a few movies. It shows that Root fibres are dynamics and actively reorganise during apical constriction and NE cells delamination. This work however lacks quantification of the events described to strongly support the model proposed. As well, this work is grounded on mis expression of GFP-Root. The model proposed could benefit from a similar description of the reorganisation of endogenous rootletin fibres during apical foot constriction in mouse neural tube.

Advance:

Until know, Rootletin fibres have been considered as a static structure providing mechanical resistance to ciliated cells. A recent work based on Cryo ET has shown that Rootlet is constituted of flexible fibres. Here, the authors show that Rootletin fibres change shape during a dynamic cellular process using still and live images. As such, it provides a conceptual advance that a structure often considered as static might be dynamic, at least in some cellular contexts, and could thus mediate other cellular functions than mechanical support.

Audience:

this work will be of interest for a specialized audience in the neurodevelopment field but also in the field of ciliogenesis. It will open a new perspective on a structure often seen as a static anchor of the cilium.

Please define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.

I am expert in ciliogenesis, with a strong background in genetics and imaging. Regarding the analysis of the quantified data (length or area of Rootletin, Lzts1 intensity) in relation with area of the apical foot, I lack expertise in the correlation analysis but I am surprised that correlations with a R2 below 0.4 come as biologicaly relevant.

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Referee #1

Evidence, reproducibility and clarity

In this manuscript, based on previous observations from their own and other groups, Wilmerding and collaborators attempt a thorough description of the dynamic localization, as well as possible interactions and functional roles, of the cilia-associated protein Rootletin during the process of neurogenesis in the early chick embryo neural tube. Through a combination of electroporation of constructs containing fluorescent reporters and immunostaining, the authors show, mainly in the chick embryo but also in mouse embryos and in human ESC-derived organoids, that Rootletin localization is highly dynamic in relation to the neuroepithelial cells cell cycle, and particularly, in correlation with neurogenic apical abscission events. All the observations are supported by labeling with several other cell markers, especially those highlighting the structure and dynamics of NE cells apical processes, by time-lapse in vivo imaging of the neurogenic NE, and by extensive quantifications. They reinforce the initially observed correlation by inducing apical abscission by overexpression of the transcription factor Neurogenin2 (that induces neurogenesis) and the microtubule-associated protein Lzts1 (that induces apical detachment but not neurogenesis). Lastly, they demonstrate a partial but very suggestive co-localization of the Zika virus NS5 protein with Rootletin during the process of apical abscission, a process that is known to be accelerated by viral infection.

I have comments only on minor issues that are listed below with no particular order (except of appearance in the manuscript):

1. A general issue has to do with figure accessibility to visually impaired persons (these are suggestions only):

a- Some figures, particularly Fig. 1, and to a lesser extent Fig. 3, are huge, with a lot of images and letters that, when compressed to fit a pdf page, will result too small. If possible, please consider dividing these figures in two (this is very straightforward in the case of Fig. 1, which is already composed of 2 easily divided parts: chick on one side, mammals on the other).

b- Colors: although many microscopy images are fine, there are some others using red in fluorescence, which should always be avoided considering color-blind persons. There is a possibility of choosing color-blind friendly palettes as plugins for Fiji (see for example https://github.com/bruvellu/color-blind-luts). 2. Line 95: What is the "surface epithelium of the developing chick NT"? Maybe you meant "the apical surface of the epithelium..."? NE cells in chick are a simple layer of cells, forming a pseudostratified epithelium but with all cells contacting apical and basal surfaces. 3. Abbreviation of "electroporation" to "EP". The whole term is first mentioned in line 126, and there is a sudden switch to the abbreviation from line 382. The explanation to abbreviation only appears at Fig. 1 legend, please clarify this earlier in the main text. 4. Lines 483-485: It is claimed that "...apically accumulated ZIKV-NS5 actively recruit Rootletin fibers...". This seems to be an assumption based on a partial co-localization of the overexpressed proteins in the apical process, hence a correlation that gives no causal evidence. Please revise. 5. Figure 1C legend, an error repeated in several similar cases in most figure legends: Where it reads "...transversal view of the apical process of electroporated NE cells...", the authors probably mean something like "... view of the apical process...on a transverse section of the NT...". The cell, and the process, are actually shown in a longitudinal view, what is transversal is the section of the neural tube. 6. Fig. 1D legend: Correct duplication of "(AU)". 7. Fig. 1D and J legend, and repeated in other cases, two comments:

a- More important (and very often seen in the figure legends): Fluorescence intensity is shown with a statistical analysis, which is excellent. However, many times it is not clarified if the central line means "average/mean" (most probably) or another parameter. And, in most cases SEM is shown instead SD. Is there a reason for choosing SEM? Since variability in these data are most probably due to biological diversity than to experimental error, would it not be better to show the SD to convey a better idea of this (expected) intrinsic variability?

b- Although very minor, it could help the reader if the authors draw a line on the example images to illustrate where fluorescence intensity was measured. 8. Fig. 1P legend: What is illustrated with the lines on the graph; mean/average, median? 9. Fig. 2G legend: Where it reads "L1 and L2 parameters were used to measure ... SAM...", the authors probably meant "... to calculate..."? 10. Fig. 2M legend: I am slightly confused by what is shown in the graphs. Rather than "SAM occupancy", which is a calculated percent, is it not directly shown the extension of the Rootletin signal as an outline? And in the case of the "Apical area", is it not the "apical outline" as well? 11. Fig. 3F: Where it reads "...they show stronger correlation...", I suggest writing "stronger negative correlation". 12. Fig. 4C: What are the parameters shown? What is the "n"? 13. Fig. 4L: The "white arrow" is cyan. 14. Fig. EV3: Since the images are from NE at the same developmental stage, why is it that in A,B Rootletin immunodetection is only seen at the centriolar liker and in B,C along the ciliary rootlet fibers extended inside the apical processes? Is it a matter of signal intensity and different microscopy settings? Something else? This should be clarified. 15. Fig. EV3E: Why "orthogonal views"? According to the outlines drawn by the authors, it would look like these are "oblique views", since we can see the apical surface and the end of the apical processes inside the NE.

Significance

The observations are novel and very interesting for the field of neural development, addressing a process that is still little understood at the cellular and molecular level: how neural progenitor/early neuronal cells eventually detach from a surface (in this case, the apical neuroepithelial surface) to begin differentiation. The results are in general well analyzed and support the conclusions. The manuscript is very well written and organized, in a way that can be readily understood by a wide readership.