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Reply to the reviewers

Manuscript number: RC-2025-03094

Corresponding author(s): Saurabh S. Kulkarni

1. General Statements

We thank the reviewers for their strong praise of the manuscript, highlighting its rigor, depth, and conceptual importance. They consistently described the study as a beautiful, fascinating, and conceptually strong piece of work that addresses a timely question in multiciliated cells. They also noted the high quality of the data, careful quantification, and the use of multiple genetic and pharmacological approaches, all of which improve the reproducibility and credibility of the findings. Importantly, they emphasized the novelty of discovering a direct mechanistic link between Piezo1-mediated mechanotransduction and Foxj1-driven transcriptional control of multiciliation, representing a significant breakthrough for both the cilia field and mechanobiology more broadly. Collectively, these strengths highlight the manuscript’s wide impact and make it highly suitable for publication in a high-impact journal.

2. Description of the planned revisions

Reviewer #1:

There are two experiments that would significantly strengthen these claims.

• First if their model is correct then even short term treatment with Yoda1 should induce the pathway and effect centriole numbers. While I appreciate the challenge of long term Yoda1 treatment its not clear to me why it would be needed if short term treatment is setting off the transcriptional cascade. Yoda is used throughout the paper to induce all the pathways but we don't know if it actually induces the phenotype. I think this should be addressed with either short term treatments or a dose response to find a dose that does not lead to skin pealing. It is hard to ignore this obvious deficiency.
• Second, the model predicts that all of this is to regulate Foxj1 levels to regulate the subtle balance between cell size and centriole number. If this is correct, then the overexpression of Foxj1 should have a profound effect on centriole number in multiciliated cells. This is such an easy experiment that would validate many of the claims. RESPONSE:

We recognize that the reviewer is asking us to test the sufficiency of the pathway with these comments: “If their model is correct, then they should be able to activate the pathway in one way or another to stimulate centriole number. This is a significant limitation to their overall model.” And “If this is correct, then the overexpression of Foxj1 should have a profound effect on centriole number in multiciliated cells.”

To address reviewers’ suggestions, we will perform the following experiments.

1. A brief exposure (15 and 30 mins) to Yoda1 and wait for 3 hours to examine changes in centriole amplification. This will avoid skin peeling from long-term exposure.
2. A brief exposure to Yoda1 (15 mins) followed by a 30-minute wait period, and the cycle repeats a total of 4 times for a total of 3 hours to examine centriole amplification.
3. The above two experiments will also be done in a constitutively active-Yap background to increase the probability that synergistic activation can lead to centriole amplification.
4. Although Foxj1 is essential for multiciliogenesis, it is not sufficient to induce multiciliogenesis, as shown by multiple previous studies. Therefore, we do not expect overexpression of Foxj1 to have a profound effect on centriole number. While we will conduct the experiments because we truly want to address the suggestions and gain insight into the answers ourselves, we respectfully ask the Reviewer to consider the following responses to their concern.

Yoda1 sufficiency: We agree that testing whether acute Yoda1 treatment can induce centriole amplification is an important question. We will conduct experiments with short-pulse and cyclic Yoda1 exposure, including in a constitutively active-YAP background (listed above), to address this possibility. However, several challenges complicate interpretation: (i) PIEZO1 adapts and desensitizes upon activation, (ii) transient signaling may be sufficient to cause secondary signaling but insufficient to drive stable transcriptional programs required for amplification, and (iii) centriole number is inherently variable, making modest effects difficult to resolve. However, we must recognize that failure to observe sufficiency under these conditions would not invalidate the model for two reasons: 1) absence of evidence is not evidence of absence, and thus, we may not have found the right experimental design. 2) PIEZO1–YAP is a necessary input but not sufficient on its own, as elaborated below. For both reasons, we are very careful about the interpretation of results in the manuscript, which shows that this pathway is necessary for centriole amplification using loss-of-function approaches.

Foxj1 overexpression: Foxj1 is a well-established regulator essential for motile and multiciliogenesis across species (Xenopus, zebrafish, mouse). Loss of Foxj1 reduces cilia number in MCCs, but its activation alone does not have a profound effect on ciliogenesis/cilia number in MCCs. This is because Foxj1 is a part of a larger network essential for multiciliogenesis. This parallels the behavior of other transcriptional regulators, such as Myb, where loss of function impairs centriole amplification, but overexpression does not drive the formation of supernumerary centrioles. Both studies are seminal discoveries in the field of ciliogenesis, but they did not demonstrate the sufficiency of these molecules/pathways. Thus, our results, demonstrating that Foxj1 is necessary to induce tension-dependent centriole amplification, are significant, as the reviewer mentioned. The lack of Foxj1 sufficiency to induce centriole amplification is not a deficiency of the study, but rather evidence that Foxj1 is a part of a larger network essential for tension-dependent centriole amplification.

Necessity versus sufficiency: We respectfully emphasize that sufficiency is not a prerequisite for demonstrating the significance of a pathway. Mechanochemical signaling is inherently complex, involving many mechanosensitive proteins and pathways. In our case, mechanical stretch increases centriole amplification, with PIEZO1–YAP signaling identified as a key mediator. However, we do not claim that PIEZO1–YAP alone is sufficient. Other pathways, including cadherin-mediated junctions, F-actin–myosin contractility, integrin–focal adhesion signaling, and nuclear mechanotransduction, likely contribute and may regulate unique downstream effectors that collectively promote centriole amplification. Therefore, PIEZO1–YAP should be regarded as one essential component within a larger network.

__TIMELINE: __We will perform these additional proposed experiments. Since the first author, a postdoctoral researcher on this manuscript, has started a new job and will be coming in on weekends to complete the experiments, we estimate it will take approximately 2-3 months to finish them.

Reviewer #2:

1. Considering the Yap-piezo mechanism of action, the authors' logic for the selection of myb, foxj, plk4 and ccno as transcriptional targets is clear, but the HCR-derived signal and the differences seen in the yap morphants are not very strong, notwithstanding the statistical significance. There appear to be distinct subgroups within the treated populations (in Figure S6B, although these data seem quite different in Fig. 7H, so a comment on the technical differences might be helpful), so that the extent to which Yap1 regulates (Myb-)Foxj1 expression in MCCs is not clearly demonstrated by this experiment. Related to this point, it is unclear why 20-25% of the yap1/ piezo1 MO-treated embryos do not show a decline in FOXj1 in Fig. 6, given the qualitative nature of the scoring. Assuming the KD penetrance would vary on a cell-to-cell basis, rather than an embryo-to-embryo basis, this may suggest that there are additional relevant targets (some of which are discussed by the authors). Single-cell analysis might be a way to address this; however, this is not a trivial experiment, it might be sufficient to include a caveat in the text. Furthermore, the conclusion that Foxj1 regulates centriole amplification in a tension-dependent manner is well-supported by the data.

RESPONSE: We appreciate the reviewer’s thoughtful observation. Differences in the expression of Foxj1 from experiment to experiment are possible due to a combination of factors, including heterogeneity in MCC development across embryos, slightly different embryonic stages, differences in embryo quality between fertilizations, and variability in morpholino delivery and knockdown penetrance, which can occur both across embryos and on a cell-to-cell basis within an embryo. We also note that technical aspects of HCR RNA-FISH, such as proteinase K treatment and washing steps, can affect signal intensity, potentially contributing to the appearance of distinct subgroups within treated populations.

We agree that single-cell analysis would be a powerful way to dissect these differences, but as the reviewer notes, this is not a trivial experiment and is beyond the scope of the present study. We have therefore added clarifications in the text and discussion to acknowledge these sources of variability and to highlight the possibility of parallel pathways regulating foxj1 expression.

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Controls for the knockdowns by the various MOs should be provided.

RESPONSE: We appreciate the reviewer’s comment. The piezo1 MO has been previously established in Kulkarni et al. (2021). Additionally, the current manuscript includes MO control experiments for both erk2 and yap1, through KD at the 1-cell stage using the MO oligonucleotide, followed by mosaic-rescue with the respective WT RNA constructs (mCherry-ERK2 and yap1-GFP) and a nuclear tracer molecule such as H2B-RFP (Fig. 5, E-H, Fig. S5, C&D, Fig. 3, D-F). The mosaic-rescue is a robust experiment that provides an internal control within the same embryo, thereby avoiding differences that may arise due to embryo-to-embryo variability, embryo quality, or differences in fertilization batches. This approach also serves as a valuable tool for detecting cell-autonomous effects, providing a clear readout against uninjected neighboring cells, as the injected cells are labeled with a tracer. We will perform a similar mosaic-rescue experiment for the foxj1 MO.

TIMELINE: We will conduct mosaic-rescue experiments for the foxj1 MO. We will need 1 month to complete the experiment.

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__Minor comments:

__

Autocorrection of ERK1/2 or MEK1/2 pathways to 1/2 should be avoided. – We are unclear on this comment. Can reviewer please clarify what they mean.

Reviewer # 3

Major concerns

1- The presented data do not yet establish a specific, direct pathway linking mechanotransduction to centriole number, because the molecular players tested (PIEZO1, Ca²⁺, PKC, ERK, YAP, Foxj1) are highly pleiotropic. As such, the observed centriole number phenotypes, and some of the major conclusions, could be indirect. It is therefore critical to test the specificity and causality of the proposed pathway. This could be done with the authors' own strategies and/or with the following potential approaches:

• Genetic dependency and sufficiency tests: It could be shown that Yoda1 has no effect in PIEZO1 loss-of-function MCCs, and that wild-type PIEZO1, but not conductance-ad PIEZO1 pore mutants restores Yoda1 responsiveness across centriole number, pERK, and YAP readouts. For example, PIEZO1 C terminus was shown to govern Ca²⁺ influx and ERK1/2 activation. Comparing full length PIEZO1 with a C terminal deletion in MCC restricted rescue; loss of rescue of centriole amplification and ERK/YAP activation with the C terminal deletion can provide a genetics anchored specificity test beyond broad inhibitors.

RESPONSE:

• To address the reviewer’s concern, we will test whether Yoda1 affects ERK and Yap activation when Piezo1 is depleted. We appreciate the reviewer’s thoughtful suggestion to employ genetic rescue experiments with Piezo1 mutants. Unfortunately, these are not technically feasible in Xenopus, as the Piezo1 coding sequence is exceptionally large (~7.5 kb)____, and repeated attempts by our group to generate and express stable, translatable transcripts have been unsuccessful. To address genetic dependency and specificity despite these technical barriers, we have employed a combination of orthogonal strategies that together provide strong genetic and mechanistic evidence:

• Mosaic loss-of-function experiments (Fig. 1) demonstrate that Piezo1 regulates centriole number in a cell-autonomous manner, ruling out global epithelial or indirect tissue-wide effects.

• Pharmacological activation/inhibition with Piezo1-specific agonist (Yoda1) and inhibitors (GSMTx4, gadolinium) produced consistent phenotypes, including activation of downstream ERK and YAP readouts. Notably, Yoda1 is a Piezo-specific agonist, not a broad pharmacological agent.
• Downstream pathway dissection (calcium chelation, PKC inhibition, ERK2 depletion, and YAP1 knockdown/rescue) consistently converges on the same phenotypes, reduced centriole amplification and altered Foxj1 expression, providing multiple independent lines of evidence that the Piezo1–Ca²⁺–PKC–ERK–YAP axis specifically controls centriole number.

• Positive feedback regulation of Piezo1 expression by YAP/Foxj1 (Fig. 7) further strengthens the argument for a pathway-specific role rather than pleiotropic, indirect effects. Taken together, while full-length Piezo1 rescue experiments are technically not possible in Xenopus due to gene size constraints, our data employ state-of-the-art genetic, pharmacological, and orthogonal functional assays to rigorously test pathway specificity. These complementary approaches provide compelling evidence for the causal role of Piezo1-mediated mechanotransduction in centriole number control in MCCs.

• Downstream bypass/rescue experiments: In PIEZO1 loss-of-function or BAPTA conditions, can enforcing MEK/ERK activation or YAP rescue centriole number defect? Conversely, can MEK inhibitors block Yoda1-induced effects.

RESPONSE: We appreciate the reviewer’s insightful questions.

• We will express CA Yap in the Piezo1 KD background to assess if we can rescue centriole number. We also note that the converse experiment has already been performed in our study: 1) PKC inhibition abolishes Yoda1-induced ERK phosphorylation and nuclear localization (Fig. 2), 2) both MEK inhibition and ERK2 depletion block Yoda1-induced Yap activation and nuclear entry (Figs. 4, S2). Thus, we have directly demonstrated that MEK inhibition prevents Yoda1-induced effects, satisfying this aspect of the reviewer’s concern.

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2- Image quantification and analysis must be described in greater detail in the Methods section, as they are central to the major conclusions of the manuscript. For example, the authors should explain how nuclear, cytoplasmic, and centriole segmentation were performed, and how relative protein levels in the nucleus versus the cytoplasm (e.g., YAP, volume- or area-based) were quantified. Specifically, the thresholds and segmentation criteria applied to different cellular structures under various conditions, as well as the use of Imaris and other software, should be clearly detailed.

RESPONSE: We will describe the methods in greater detail.

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3- PIEZO1 mRNA was shown to incrase in a Foxj1 linked feedback loop. Does this increase translate into an increase in total protein levels?

RESPONSE: If the reviewer is referring to Figure 7B, that is the Piezo1 antibody, so yes, the Piezo1 protein levels have increased.

If the reviewer is referring to Figure 7C and D, we show that loss of Foxj1 leads to a reduction in Piezo1 mRNA expression.

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4- Is the proposed signaling cascade active in mammalian multiciliated cells (e.g., airway epithelium). If possible, testing this by using one of the major players of the pathway as a readout such as as ERK phosphorylation, YAP nuclear localization in mammalian MCCs will reveal whether regulation of centriole number through this pathway is conserved and would strengthen the generality.

RESPONSE: We agree with the reviewer that testing conservation of this pathway in mammalian MCCs is of great interest. Indeed, another group is currently investigating the role of Yap in the mammalian airway epithelium; in their temporally controlled Yap knockout model (the global Yap KO being embryonic lethal), they observed that Yap loss led to a reduction in centriole number. To avoid overlap and direct competition with this ongoing work, we chose to focus our efforts on Xenopus.

Importantly, Xenopus has become a widely recognized and powerful system for MCC biology, enabling mechanistic dissection of centriole amplification and ciliogenesis. Several key discoveries in the field, including the identification of MCIDAS as a master regulator of MCC fate, were first made in Xenopus before being validated in mammals. Similarly, our study provides a mechanistic framework in Xenopus that can inform and guide ongoing studies in the mammalian airway.

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5- Throughout the results section, there are multiple times where authors raised specific hypothesis about their data (e.g. foxj1 regulation of number control, apical actin/YAP). However, they have not tested them. These hypothesis are very exciting and if possible, testing experimentally, would strengthen the conclusions associated with them.

RESPONSE: We are not sure what the reviewer means here by “authors raised specific hypothesis about their data (e.g., foxj1 regulation of number control, apical actin/YAP). However, they have not tested them”,

BECAUSE:

• Foxj1 regulation of centriole number: We demonstrate a clear reduction in centriole number upon Foxj1 depletion, and importantly, we extend this finding by showing that the reduction is tension-dependent (Fig. 6). We will perform a rescue assay to demonstrate the specificity.
• Foxj1 and YAP: We never claimed that Foxj1 regulates YAP expression, and this is not part of our proposed model. Instead, our data show that Piezo1–ERK–YAP signaling regulates Foxj1
• Foxj1 and apical actin: Foxj1 regulation of apical F-actin has already been established in prior work, and in our study, we clearly observe reduced apical actin intensity in Foxj1-depleted MCCs (Fig. 6). To further strengthen this conclusion, we will provide a quantitative analysis of apical actin intensity in Foxj1 morphants. ********************************************

__TIMELINE: __We will perform these additional proposed experiments. Since the first author, a postdoc on this manuscript, has started a new job and will be coming in on weekends to finish the experiments, we estimate it will take approximately 2-3 months to complete them.

Minor comments

MCC vs non MCC identification (Fig. 1): Clarify how non MCCs were distinguished from MCCs (e.g. markers/criteria). – Can the reviewer please clarify which panel or panels? Or provide more specific text that needs to be changed.

Add the Kintner group reference linking motile cilia number and centriole number in Xenopus MCCs.– Can the reviewer clarify where and which reference? Thank you.

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

Please insert a point-by-point reply describing the revisions that were already carried out and included in the transferred manuscript. If no revisions have been carried out yet, please leave this section empty.

Reviewer 2

Major comments:

1. It should be clarified whether the immunoblots and the related quantitations in Figs. 2 and S2 are all from separate blots/ exposures. If so, they are not useful as controls, and these blots should be repeated with the relevant samples analyzed in parallel. Size markers and labels should be included (2B, 2G; S2B and S2G). An increase in total ERK would alter the interpretation of the increase in nuclear pERK in the IF experiments. RESPONSE: We thank the reviewer for raising this important point regarding clarification of the immunoblots. All experimental groups were analyzed in parallel with their corresponding controls. Because the primary antibodies for pERK and ERK were both raised in rabbit, we optimized our workflow to prevent protein loss during stripping and to ensure accurate visualization. Specifically, lysates from each experimental group were loaded in duplicate on the same gel, separated by a molecular weight ladder that served as a reference point. After transfer, the blot was cut along the ladder, and the two halves were processed in parallel: one probed with anti-pERK and the other with anti-ERK. This strategy ensured that all samples from a single experiment (e.g., Control and Yoda1-treated groups) were analyzed under identical conditions, with staining and imaging performed together at the same exposure. To enhance clarity, we have provided this data as __uncut, full-length __as Supplemental Figure 7 (Figure S7) in the revised revision.

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Minor comments:

1. Reference list should be checked for completeness; some citations lack journal/ volume/ page/ year details. – We have corrected the references.
2. An 'overexposed' version of the image selected for centrioles in Figure 5F might be included with the Chibby-BFP at the same level as in the other figures. At present, the Yap KD cell in the image appears to have normal centrioles; this is potentially confusing, even though the authors clearly explain the matter in the text. – __We have added a new panel to Fig. 5F to avoid confusion.

__ 3. It might be clearer to present injected/ uninjected in the same orientation in Fig. 6A and B. – __Unfortunately, that is not possible because the injected and uninjected sides are left and right, and they cannot be in the same orientation.

__ 4. Figure 7B lacks the schematic described in the figure legend. – We have removed the Schematic sentence from the figure legend. That was an error on our side. Thank you for catching it.

Reviewer 3

1. Abstract: "how MCCs regulate centriole/cilia numbers remains a major knowledge gap" overstates the field; please soften to reflect recent advances (mechanics/apical area scaling; PIEZO1 implication). – We changed the text to “incompletely understood”.
2. GsMTx4 rationale: State that GsMTx4 is a spider venom peptide that inhibits cationic mechanosensitive channels (including PIEZO1) and justify its use alongside Yoda1.– GsMTx4 was used in the previous manuscript, and its use was justified there. Here, we are only comparing the results. However, we have added a sentence describing what GSMTx4 is. We have also included a sentence explaining the use of Yoda1. “GsMTx4, a spider venom peptide used in our previous study, inhibits cationic mechanosensitive channels, including Piezo1.”

“For this experiment, we used the Piezo1 channel-specific chemical agonist, Yoda1, to increase the sensitivity of Piezo1 and upregulate calcium entry into cells”

Timeline statement: "Centriole amplification to migration and apical docking takes ~4-5 h (personal observation)" is not appropriate; either cite time lapse literature or include your own time lapse data.– We have added a reference that showed imaging for 2 hours, but it was not enough to capture the entire process from intercalation to maturation, so we also kept “personal observation” still in the manuscript. We are unaware of any study that has done time-lapse imaging for 4 hours to capture the entire process of centriole amplification.

Redundancy: The description of Yoda1 as a channel specific agonist is repeated; keep only once.- Removed

"WT yap1 GFP construct previously used by Dr. Lance Davidson ..." should move construct description to Methods and keep only the citation in Results.– We moved it to Methods.

"(Unpublished data; Dr. Mahjoub)" should be removed unless data are shown.- Removed

Replace "as shown previously in our eLife paper" with "as we previously showed or shown previously (Kulkarni et al., 2021)".– We have made the change.

The two hypotheses for how Foxj1 could regulate number under tension (actin remodeling vs. transcriptional control of amplification genes) belong in the Discussion unless tested. Moreover, the part on the discussion on yap sequestration by apical actin and the two possibilities presented also should go do discussion. – We have moved both to the discussion section.

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

Please include a point-by-point response explaining why some of the requested data or additional analyses might not be necessary or cannot be provided within the scope of a revision. This can be due to time or resource limitations or in case of disagreement about the necessity of such additional data given the scope of the study. Please leave empty if not applicable.

Reviewer 3

1- The hypothesis about the centriole pool of Piezo as the mechnosensor for centriole number regulation is very exciting and novel. Can localization controlled variants be used to test whether a centriole associated pool directly senses tension for number control (for example, centrosome targeted PIEZO1 via a PACT tag). Alternatively, broad cellular Ca sensors (GcaMP) or centrosome proximal Ca sensors (e.g., PACT GCaMP) can be used detect local calcium microdomains during tethering or Yoda1 treatment.

RESPONSE: We appreciate the reviewer's curiosity and excitement; however, these experiments will not alter the conclusion of this paper and will be part of the next study, which aims to delve deeper into how different pools of Piezo1 at centrioles versus cell junctions function in MCCs. To that point, we had thought about these experiments. As mentioned earlier, the Piezo1 coding sequence is exceptionally large (~7.5 kb)____, and repeated attempts by our group to generate and express stable, translatable transcripts have been unsuccessful. Thus, the idea of centrosome-targeted PIEZO1 via a PACT is very exciting; however, it is not technically feasible. Beyond size, PIEZO1 is a trimeric, large plasma-membrane mechanosensitive channel that requires proper ER processing and bilayer incorporation. PACT localizes cargo to the centriole/pericentriolar material, not a membrane compartment; thus, a PACT-anchored PIEZO1 would be membrane-mismatched and almost certainly nonfunctional even if expressed/

Second, Centrosome-proximal GCaMP (PACT-GCaMP) would show correlation, not causation. This experiment does not address the question “centriole pool of Piezo as the mechanosensor for centriole number regulation”. It will only show if the Ca2+ influx is happening at the basal bodies, but not whether and how that Ca2+ is essential for centriole amplification. For this purpose, we will need to find a way to block Ca2+ influx specifically at basal bodies, rather than junctions, which will require extensive controls.

We do not claim that any specific Piezo1 or Ca2+ pool is critical for controlling centriole number and thus the suggested experiment would not alter the manuscript's conclusions. We therefore view the above as exciting future directions rather than prerequisites.

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2- Because the proposed pathway is tension-sensing and YAP pathway is tightly linked to the actin cytoskeleton, the role of actin cysoskeleton in the proposed pathway should be tested directly. The authors mention different hypothesis around actin but has not tested them in the manuscript. For example, actin-depedent sequestration of Yap at the apical surface is intriguing. Does actin polymerization induced by drugs release Yap from the apical surface?

RESPONSE: We would like to thank the reviewer for their suggestion. As per the reviewers' suggestion, we have moved this section to discussion, stating that “In the future, we plan to address this question by examining how Yap is sequestered by apical actin.”.

However, we appreciate the reviewer’s enthusiasm and would like to share some experiments we are thinking/planning of to test the hypothesis.

We plan to examine if the actin polymerization or contractility is responsible for Yap sequestration/release from the apical surface with the following experiments: 1) if the Yap is displaced by Jasplakinolide treatment, which stabilizes filamentous actin, 2) use of ROCK inhibitor to decrease contractility in the absence or presence of Yoda1, 3) Use genetic constructs such as Shroom3 to increase ROCK-mediated contractility to observe changes in Yap localization and dynamics.

Although these experiments are interesting, they do not alter the conclusion of the current manuscript, and they represent future directions for our research.

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Referee #3

Evidence, reproducibility and clarity

This manuscript investigates how mechanical tension is transduced into centriole amplification in Xenopus multiciliated cells (MCCs). Building on prior work that centriole number scales with MCC apical area and that this scaling depends on PIEZO1, the study proposes that MCCs repurpose a canonical mechanochemical axis-PIEZO1 → Ca²⁺/PKC → ERK1/2 → YAP → Foxj1-to regulate centriole number rather than mitosis. The authors use tethered vs. untetheredanimal cap explants to modulate tissue tension, combine pharmacologic perturbations with genetic loss of function and rescue, quantititative image analysis and present a model in which tension gated PIEZO1 activates ERK/YAP, influences Foxj1, and tunes centriole number in MCCs.

The manuscript tackles an important and timely problem with clear disease relevance. It major advance is their presented model that posits that post mitotic MCCs repurpose a canonical mechanotransduction module to regulate organelle number rather than proliferation. It is a conceptually strong study addressing an important problem with a clean mechanical paradigm. However, to support the central claim that centriole number control is a specific, direct consequence of the PIEZO1-Ca²⁺-ERK/YAP pathway within MCCs, the revision should establish specificity and causality and provide experimental data for some of the major conclusions as detailed below. Addressing these points are critical to support the mechanistic conclusions and impact.

Major concerns:

1) The presented data do not yet establish a specific, direct pathway linking mechanotransduction to centriole number, because the molecular players tested (PIEZO1, Ca²⁺, PKC, ERK, YAP, Foxj1) are highly pleiotropic. As such, the observed centriole number phenotypes, and some of the major conclusions, could be indirect. It is therefore critical to test the specificity and causality of the proposed pathway. This could be done with the authors' own strategies and/or with the following potential approaches:

• Genetic dependency and sufficiency tests: It could be shown that Yoda1 has no effect in PIEZO1 loss-of-function MCCs, and that wild-type PIEZO1, but not conductance-dead PIEZO1 pore mutants restores Yoda1 responsiveness across centriole number, pERK, and YAP readouts. For example, PIEZO1 C terminus was shown to govern Ca²⁺ influx and ERK1/2 activation. Comparing full length PIEZO1 with a C terminal deletion in MCC restricted rescue; loss of rescue of centriole amplification and ERK/YAP activation with the C terminal deletion can provide a genetics anchored specificity test beyond broad inhibitors.

• Downstream bypass/rescue experiments: In PIEZO1 loss-of-function or BAPTA conditions, can enforcing MEK/ERK activation or YAP rescue centriole number defect? Conversely, can MEK inhibitors block Yoda1-induced effects.

2) The hypothesis about the centriole pool of Piezo as the mechnosensor for centriole number regulation is very exciting and novel. Can localization controlled variants be used to test whether a centriole associated pool directly senses tension for number control (for example, centrosome targeted PIEZO1 via a PACT tag). Alternatively, broad cellular Ca sensors (GcaMP) or centrosome proximal Ca sensors (e.g., PACT GCaMP) can be used detect local calcium microdomains during tethering or Yoda1 treatment.

3) Because the proposed pathway is tension-sensing and YAP pathway is tightly linked to the actin cytoskeleton, the role of actin cysoskeleton in the proposed pathway should be tested directly. The authors mention different hypothesis around actin but has not tested them in the manuscript. For example, actin-depedent sequestration of Yap at the apical surface is intriguing. Does actin polymerization induced by drugs release Yap from the apical surface?

4) Image quantification and analysis must be described in greater detail in the Methods section, as they are central to the major conclusions of the manuscript. For example, the authors should explain how nuclear, cytoplasmic, and centriole segmentation were performed, and how relative protein levels in the nucleus versus the cytoplasm (e.g., YAP, volume- or area-based) were quantified. Specifically, the thresholds and segmentation criteria applied to different cellular structures under various conditions, as well as the use of Imaris and other software, should be clearly detailed.

5) PIEZO1 mRNA was shown to incrase in a Foxj1 linked feedback loop. Does this increase translate into an increase in total protein levels?

6) Is the proposed signaling cascade active in mammalian multiciliated cells (e.g., airway epithelium). If possible, testing this by using one of the major players of the pathway as a readout such as as ERK phosphorylation, YAP nuclear localization in mammalian MCCs will reveal whether regulation of centriole number through this pathway is conserved and would strengthen the generality.

7) Throughout the results section, there are multiple times where authors raised specific hypothesis about their data (e.g. foxj1 regulation of number control, apical actin/YAP). However, they have not tested them. These hypothesis are very exciting and if possible, testing experimentally, would strengthen the conclusions associated with them.

Minor concerns:

1) Abstract: "how MCCs regulate centriole/cilia numbers remains a major knowledge gap" overstates the field; please soften to reflect recent advances (mechanics/apical area scaling; PIEZO1 implication).

2) MCC vs non MCC identification (Fig. 1): Clarify how non MCCs were distinguished from MCCs (e.g. markers/criteria).

3) GsMTx4 rationale: State that GsMTx4 is a spider venom peptide that inhibits cationic mechanosensitive channels (including PIEZO1) and justify its use alongside Yoda1.

4) Timeline statement: "Centriole amplification to migration and apical docking takes ~4-5 h (personal observation)" is not appropriate; either cite time lapse literature or include your own time lapse data.

5) Redundancy: The description of Yoda1 as a channel specific agonist is repeated; keep only once.

6) "WT yap1 GFP construct previously used by Dr. Lance Davidson ..." should move construct description to Methods and keep only the citation in Results.

7) "(Unpublished data; Dr. Mahjoub)" should be removed unless data are shown.

8) Add the Kintner group reference linking motile cilia number and centriole number in Xenopus MCCs.

9) Replace "as shown previously in our eLife paper" with "as we previously showed or shown previously (Kulkarni et al., 2021)".

10) The two hypotheses for how Foxj1 could regulate number under tension (actin remodeling vs. transcriptional control of amplification genes) belong in the Discussion unless tested. Moreover, the part on the discussion on yap sequestration by apical actin and the two possibilities presented also should go do discussion.

Significance

This manuscirpt dissects Piezo1-mediated mechanotransduction to regulation of centriole number in Xenopus multiciliated cells (MCCs) via Ca²⁺, ERK/YAP, and Foxj1. While Piezo1 and its downstream effectors have been implicated broadly in mechanosensation, cellular tension responses, and transcriptional regulation, their specific role in centriole nubmer control in MCCs has been unknown By integrating pharmacological manipulation, genetic perturbation, and functional readouts, the authors demonstrate that this pathway directly influences centriole number.

The findings extend published knowledge in two main ways:

(1) they connect a mechanosensitive ion channel to the transcriptional program governing Foxj1 expression and multiciliation, a mechanistic link not previously defined, and

(2) they highlight the pleiotropic yet coordinated nature of Piezo1 signaling in organelle biogenesis. This work will be of broad interest to cell and developmental biologists studying ciliogenesis, epithelial differentiation, and mechanotransduction, as well as to biomedical researchers interested in multicilaited cells and ciliopathies. By situating a well-studied mechanosensor within the context of MCC biology, the study opens new directions for understanding how tissue-level forces shape organelle number control and function.

At the same time, the impact of the study is weakened by concerns regarding the causability and specificity of the pathway, since the signaling components examined are highly pleiotropic and it remains challenging to separate direct effects on centriole number from broader cellular consequences. The causal relationships among Piezo1 activity, downstream signaling, and Foxj1 expression require stronger substantiation, and the extent to which this pathway operates in mammalian multiciliated cells remains an open question. Addressing these limitations would strengthen the robustness, generality, and translational relevance of the conclusions.

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Referee #2

Evidence, reproducibility and clarity

Narayanan, Kulkami and colleagues here examine how the Piezo-Erk-Yap pathway is involved in centriole numerical control in multiciliated cells (MCCs). Using reverse genetic and pharmacological methods in Xenopus embryos, they show that Piezo-mediated ERK signalling through to Yap regulates tension-sensitive centriole number, through a mechanism that involves Foxj1, very likely acting as a transcription factor. The data are carefully controlled, robustly analysed and well presented. Statistical analyses are notably thorough.

Main points:

1. It should be clarified whether the immunoblots and the related quantitations in Figs. 2 and S2 are all from separate blots/ exposures. If so, they are not useful as controls, and these blots should be repeated with the relevant samples analysed in parallel. Size markers and labels should be included (2B, 2G; S2B and S2G). An increase in total ERK would alter the interpretation of the increase in nuclear pERK in the IF experiments.

2. Considering the Yap-piezo mechanism of action, the authors' logic for the selection of myb, foxj, plk4 and ccno as transcriptional targets is clear, but the HCR-derived signal and the differences seen in the yap morphants are not very strong, notwithstanding the statistical significance. There appear to be distinct subgroups within the treated populations (in Figure S6B, although these data seem quite different in Fig. 7H, so a comment on the technical differences might be helpful), so that the extent to which Yap1 regulates (Myb-)Foxj1 expression in MCCs is not clearly demonstrated by this experiment. Related to this point, it is unclear why 20-25% of the yap1/ piezo1 MO -treated embryos do not show a decline in FOXj1 in Fig. 6, given the qualitative nature of the scoring. Assuming the KD penetrance would vary on a cell-to-cell basis, rather than an embryo-to-embryo basis, this may suggest that there are additional relevant targets (some of which are discussed by the authors). Single-cell analysis might be a way to address this; however, this is not a trivial experiment, it might be sufficient to include a caveat in the text. Furthermore, the conclusion that Foxj1 regulates centriole amplification in a tension-dependent manner is well-supported by the data.

3. Controls for the knockdowns by the various MOs should be provided.

Minor points:

1. Autocorrection of ERK1/2 or MEK1/2 pathways to 1/2 should be avoided.

2. Reference list should be checked for completeness; some citations lack journal/ volume/ page/ year details.

3. An 'overexposed' version of the image selected for centrioles in Figure 5F might be included with the Chibby-BFP at the same level as in the other figures. At present, the Yap KD cell in the image appears to have the normal centrioles; this is potentially confusing, even though the authors clearly explain matters in the text.

4. It might be clearer to present injected/ uninjected in the same orientation in Fig. 6A and B.

5. Figure 7B lacks the schematic described in the figure legend.

Significance

This study presents novel insight into the developmentally important process of ciliogenesis in multiciliated cells that will be of specific interest to the fields of cilium biology and mechanobiology, with additional general interest in calcium signalling and cell biology.

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Referee #1

Evidence, reproducibility and clarity

The manuscript from Narayanan addresses the fascinating question of how Multiciliated cells regulate centriole number to scale with cell size. They have generated a tremendous amount of high quality data that supports a model in which mechanosensitive signaling via piezo1 leads to an increase in intracellular Ca++ that leads to an activation of the Erk pathway which in turn activates the Yap pathway that in turn regulates FoxJ1 levels which they propose regulates centriole number. This is complicated but they have strong quantifiable data that supports most of the claims. I think this is a beautiful study that adds significantly to the field. There is a lot of evidence that disrupting these pathways has a negative consequence on centriole number. What is lacking is a positive connection showing a role of these processes in fine tuning the centriole number as the title suggests. Several key experiments would significantly strengthen their claims.

• The data is presented in a way that proposes that the ultimate role of these pathways is to regulate Foxj1 levels to fine tune centriole number based on the level of tension. There are two experiments that would significantly strengthen these claims. First if their model is correct then even short term treatment with Yoda1 should induce the pathway and effect centriole numbers. While I appreciate the challenge of long term Yoda1 treatment its not clear to me why it would be needed if short term treatment is setting off the transcriptional cascade. Yoda is used throughout the paper to induce all the pathways but we don't know if it actually induces the phenotype. I think this should be addressed with either short term treatments or a dose response to find a dose that does not lead to skin pealing. It is hard to ignore this obvious deficiency. Second, the model predicts that all of this is to regulate Foxj1 levels to regulate the subtle balance between cell size and centriole number. If this is correct, then the overexpression of Foxj1 should have a profound effect on centriole number in multiciliated cells. This is such an easy experiment that would validate many of the claims.

Minor issues:

• The authors attempt to measure an effect of plk4 and ccno in the Yap MO experiment. However, the fact that they could not be scored means the experiment wasn't really performed. I think it is more appropriate to leave out rather than risk giving the impression that these genes were unaffected.

• The authors indicate that the foxj1 result suggests two alternatives, one that foxj1 regulates actin (pan 2007) and the other that it is a transcription factor. I think the evidence for foxj1 being a transcription factor is extremely well established and while it is possible for it to have an additional unrelated role my interpretation of the Pan paper is that the failed apical docking leads to disrupted actin which is also well established. I don't think there is a lot of evidence for foxj1 being anything other than a TF.

Significance

• This is a really beautiful paper that will be well appreciated by the cilia community but also should be appreciated by the broader cell biology community.

• The strengths of this paper are a high level of rigor in which they perform detailed quantification of a wide range of processes. For many experiments they have multiple methods for disrupting function which again adds to the rigor. They have successfully linked Piezo1, Erk, Yap and FoxJ1 function to proper centriole biogenesis, which is a significant advance.

• The limitation is that all their perturbations negatively effect centriole number which could be indirect. If their model is correct then they should be able to activate the pathway in one way or another to stimulate centriole number. This is a significant limitation to their overall model.

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Reply to the reviewers

Reviewer #1

Summary: The authors have previously published Mass-spectrometry data that demonstrates a physical interaction between Sall4 and the BAF chromatin complex in iPSC derived neurectodermal cells that are a precursor cell state to neural crest cells. The authors sought to understand the basis of this interaction and investigate the role of Sall4 and the BAF chromatin remodelling complex during neural crest cell specification. The authors first validate this interaction with a co-IP between ARID1B subunit and Sall4 confirming the mass spec data. The authors then utilise in silico modelling to identify the specific interaction between the BAF complex and Sall4, suggesting that this contact is mediated through the BAF complex member DPF2. To functionally validate the role of Sall4 during neural crest specification, the authors utilsie CRISPR-Cas9 to introduce a premature stop codon on one allele of Sall4 to generate iPSCs that are haploinsufficient for Sall4. Due to the reports of Sall4's role in pluripotency, the authors confirm that this model doesn't disrupt pluripotent stem cells and is viable to model the role of Sall4 during neural crest induction. The authors expand this assessment of Sall4 function further during their differentiation model to cranial neural crest cells, assessing Sall4 binding with Cut+Run sequencing, revealing that Sall4 binds to motifs that correspond to key genes in neural crest differentiation. Moreover, reduction in Sall4 expression also reduces the binding of the BAF complex, through Cut and Run for BRG1. Overall, the authors then propose a model by which Sall4 and BRG1 bind to and open enhancer regions in neurectodermal cells that enable complete differentiation to cranial neural crest cells.

Overall, the data is clear and reproducible and offers a unique insight into the role of chromatin remodellers during cell fate specification.

We thank the Reviewer for the nice words of appreciation of our manuscript.

However, I have some minor comments.

1- Using AlphaFold in silico modelling, he authors propose the interaction between the BAF complex with Sall4 is mediated by DPF2, but don't test it. Does a knockout, or knockdown of DPF2 prevent the interaction?

We agree with the Reviewer that we are not functionally validating our computational prediction that DPF2 is the specific BAF subunit directly linking SALL4 with BAF. We chose not to perform the validation experiment for two main reasons:

1) This would be outside of the scope of the paper. In fact, from a mechanistic point of view, we have confirmed via both Mass-spectrometry and co-IP with ARID1B that SALL4 and BAF interact in our system. Moreover, mechanistically we also extensively demonstrate that the interaction with SALL4 is required to recruit BAF at the neural crest induction enhancers and we further demonstrate that depletion of SALL4 impairs this. In our view, this was the focus of the manuscript. On the other hand, detecting with certainty which BAF subunit mediates the interaction with SALL4 would be outside the scope of the paper.

2) Moreover, after careful consideration, we don’t think that even a knock-out of DPF2 would provide a definite answer to which exact BAF subunit mediates the interaction with SALL4. In fact, knock out of DPF2 could potentially disrupt BAF assembly or stability, and this could result in a disruption of the interaction with SALL4 even if DPF2 is not the very subunit mediating it (in other words the experiment could provide a false positive result). In our opinion, the only effective experiment would be mutating the DPF2 residues that we computationally predicted as responsible for the interaction with SALL4, but again this would be very laborious and out of the scope.

That being said, we agree with the Reviewer that while the SALL4-BAF interaction was experimentally validated with robust approaches, the role of DPF2 in the interaction was only computationally predicted, which comes as a limitation of the study. We have now added a dedicated paragraph in the discussion to acknowledge such limitation.

2- OPTIONAL: Does knockout of DPF2 phenocopy the Sall4 ko? This would be very interesting to include in the manuscript, but it would perhaps be a larger body of work.

See point-1.

3- Figure 1, the day of IP is not clearly described until later in the test. please outline during in the figure.

We thank the Reviewer for pointing this out. This has been fixed.

3- What is the expression of Sall1 (and other Sall paralogs) during differentiation. The same with the protein levels of Sall4, does this remain at the below 50%, or is this just during pluripotency?

As Recommend by the Reviewer, we have performed time-course WB of SALL1 and SALL4. These experiments revealed that SALL1 remains very lowly expressed in wild-type conditions across time points and all the way through differentiation until CNCC (See updated supplementary Fig. S9). This is consistent with previous studies that demonstrated that SALL4, but not SALL1, is required for early mammalian development (see for example Miller et al. 2016, Development, and Koulle et al. 2025, Biorxiv). We performed the same time-course WB for SALL4 which revealed that SALL4 expression progressively decreases after day-5 (as expected) and it’s very low at CNCC stage (day-14), therefore we would expect the KO to remain at even lower level at this stage.

4- The authors hypothesise that Sall4 binds to enhancers- with the criteria for an enhancer being that these peaks > 1KB from the TSS are enhancers. Can this be reinforced by overlaying with other ChIP tracks that would give more confidence in this? There are several datasets from Joanna Wysocka's lab that also utilise this protocol which can give you more evidence to reinforce the claim and provide further detail as to the role of Sall4.

We thank the Reviewer for this great suggestion. As recommended, we have used publicly available ChIP-seq data generated by the Wysocka lab (H3K4me1, H3K4m3) and also generated new H3K27ac CHIP-seq data as well. These experiments and analyses confirmed that these regions are putative CNCC enhancers (and a minority of them putative promoters), decorated with H3K4me1 and with progressive increase in H3K27ac after CNCC induction (day-5). See new Supplementary Figure S6.

5- The authors state that cells fail to become cranial neural crest cells, however they do not propose what the cells do instead. do they become neural? Or they stay at pluriopotent, which is one option given the higher expression of Nanog, OCT4 and OTX2 that are all expressed in pluripotent stem cells.

We think that it is likely a mix of both. There is a mixed bag of expression of pluripotency markers, but also high expression of neuroectodermal markers. This suggests that most cells safely reach the neuroectodermal stage but fail to go beyond that, while some of the cells simply do not differentiate or regress back to pluripotency. We would rather refrain on overinterpreting what the KO-cells become, as it is likely an aberrant cell type, but following the Reviewer’s indication we have added a paragraph in the discussion to speculate on this.

6- In general, I would like to see the gating strategy and controls for the flow cytometry in a supplemental figure.

As Recommended by the Reviewer, we have added the gating strategy in the Supplementary Fig. S4.

7- For supplementary figure 1- please include the gene names in the main image panels rather than just the germ layer.

Done. The figure is now Supplementary Figure S3 since two supplementary figures were added before.

Reviewer #2

Summary In this manuscript, the authors build on their previous work (Pagliaroli et al., 2021) where they identified an interaction between the transcription factor SALL4 and the BAF chromatin remodeling complex at Day-5 of an iPSC to CNCC differentiation protocol. In their current work, the authors begin by exploring this interaction further, leveraging AlphaFold to predict interaction surfaces between SALL4 and BAF complex members, considering both SALL4 splice isoforms: a longer SALL4A (associated with developmental processes) and a shorter SALL4B (associated with pluripotency). They propose that SALL4A may interact with DPF2, a BAF complex member, in an isoform-dependent manner. The authors next explore the role of SALL4 in craniofacial development, motivated by patient heterozygous loss of function mutations, leveraging iPSC cells with an engineered SALL4 frameshift mutation (SALL4-het-KO). Using this model, the authors first demonstrate that a reduced expression of SALL4 does not impact the iPSC identity, perhaps due to compensation via upregulation of SALL1. Upon differentiation to neuroectoderm, SALL4 haploinsufficiency causes a reduction in newly accessible sites which are associated with a reduction in SALL4 binding and therefore a loss of BAF complex recruitment. Interestingly, however, there were few transcriptional changes at this stage. Later in the CNCC differentiation at Day-14 when the wildtype cells have switched expression of CNCC markers, the SALL4-het-KO cells fail to switch cadherin expression associated with a transition from epithelial to mesenchymal state, and fail to induce CNCC specification and post-migratory markers. Together the authors propose that SALL4 recruits BAF to CNCC enhancers as early as the neuroectodermal stage, and failure of BAF recruitment in SALL4-het-KO lines results in a loss of open chromatin at regulatory regions required later for induction of the CNCC programme. The failure of the later differentiation is compelling in the light of the early stages of the differentiation progressing normally, and the authors outline an interesting proposed mechanism whereby SALL4 recruits BAF to remodel chromatin ahead of CNCC enhancer activation, a model that can be tested further in future work. The link between SALL4 DNA binding and BAF recruitment is nicely argued, and very interesting as altered chromatin accessibility at Day 5 in the neuroectodermal stage is associated with only few changes in gene expression, while gene expression is greatly impacted later in the CNCC stage at Day 14. The in silico predictions of SALL4-BAF interaction interfaces are perhaps less convincing, requiring experimental follow-up outside the scope of this paper. Some of the associated figures could perhaps be moved to the supplement to enhance the focus on the later functional genomics experiments.

We thank the Reviewer for the nice words of appreciation of our manuscript.

Major comments

1. A lot of emphasis is placed on the AlphaFold predictions in Figure 1, however the predictions in Figure 1B appear to be mostly low or very low confidence scores (coloured yellow and orange). It is unclear how much weight can be placed on these predictions without functional follow-up, e.g. mutating certain residues and showing impact on the interaction by co-IP. The latter parts of the manuscript are much better supported experimentally, and therefore perhaps some of the Figure 1 could move to a Supplemental Figure (e.g. the right-hand part of 1B, and the lower part of Figure 1C showing SALL4B predicted interactions). The limitations of AlphaFold predictions should be acknowledged and the authors should discuss how these predicted interactions could be experimentally explored further in the future.

As recommended by the Reviewer, we have moved part of the AlphaFold predictions to Supplementary Figure S1, and we added a paragraph in the discussion to acknowledge the limitations of AlphaFold.

The authors only show data for one heterozygous knockout clone for SALL4. It is usual to have more than one clone to mitigate potential clonal effects. The authors should comment why they only have one clone and include any data for a second clone for key experiments if they already have this. Alternatively, the authors could provide any quality control information generated during production of this line, for example if any additional genotyping was performed.

We apologize for the confusion and for our lack of clarify on this. We have used two clones (one generated with a 11 bp deletion, one with a 19 bp deletion, both in exon-1, see also the point 6 of your minor points). The two clones were used as biological replicates, so for example the two ATAC-seq replicates performed in each time point were performed with the two different clones, and the three RNA-seq replicates were performed with two technical replicates of the clone with the 11bp deletion and one replicate with the clone with 19 bp deletion. We have clarified this in the methods section of the manuscript and added a Supplementary Figure (S2) showing the editing strategy for the two clones. Thank you for catching it.

The authors show all genomics data (ATAC-seq, CUT&RUN and ChIP-seq) as heatmaps and average profiles. It would be valuable to see some representative loci for the ATAC seq (perhaps along with SALL4 and BRG1 recruitment) at some representative and interesting loci.

As recommended by the Reviewer, we have added Genome Browser screenshots of representative loci in Fig. 6.

Figure 4A. The schematic could be improved by including brightfield or immunofluorescent images at the three stages of the differentiation. Are the iPS cells seeded as single cells, or passaged as colonies before starting the differentiation. Further details are required in the methods to clarify how the differentiation is performed, for example at what Day are the differentiating cells passaged, this is not shown on the schematic in Figure 4A.

As recommended, we added IF images in the Fig. 4A schematic, and added more details in the methods.

There is likely some heterogeneity of cell types in the differentiation at Day 5 and Day 14. Can the authors comment on this from previous publications or perhaps conduct some IF for markers to demonstrate what proportions of cells are neuroectoderm at Day 5 and CNCCs at Day 14.

The differentiation starts with single cells that aggregate to form neuroectodermal clusters, as per original protocol. The CNCCs that we obtain with this protocol homogeneously express CNCC markers, as shown by IF of SOX9 in Fig. 4A. For the day-5, as recommended we have added IF for PAX6 also showing homogeneous expression (Fig. 4A).

For the motif analysis for Day 5-specific SALL4 binding sites (Figure 4E), was de novo motif calling performed? Were any binding sites reminiscent of a SALL4 binding site observed (e.g. an AT-rich motif)? Could the authors comment on this in the text - if there is no SALL4 binding motif, does this suggest SALL4 is recruited indirectly to these sites via interaction with another transcription factor for example?

Similar to SALL4, SALL1 also recognizes AT-rich motifs. However, while we found AT-rich motifs as enriched in our day-5 motif analysis (in the regions that gain SALL4 binding upon differentiation), the enrichment is not particularly strong, and several other motifs are significantly more enriched, suggesting that, like the Reviewer mentioned, SALL4 might be recruited indirectly at these sites by other factors. We have added a paragraph on this in the discussion.

Does SALL1 remain upregulated at Day-5 and Day-14 of the differentiation for the SALL4-het-KO line? Are binding sites known for this TF and were they detected in the motif analysis performed? Further discussion of the impact of the overexpression of SALL1 on the phenotypes observed is warranted - e.g. for Figure 5F, could the sites associated with a gain of BRG1 peaks upon loss of SALL4 be associated with SALL1 being upregulated and 'hijacking' BAF recruitment to distinct sites associated with nervous system development? Is SALL1 still upregulated at Day 5?

As mentioned above, SALL1 also recognizes AT-rich motifs but similar to SALL4 also binds unspecifically, likely in cooperation with other TFs. Like the Reviewer suggested, it is certainly possible that some of the sites associated with a gain of BRG1 peaks upon loss of SALL4 could be associated with SALL1 being upregulated and 'hijacking' BAF recruitment to distinct sites. While this is speculative, we have added a paragraph on this in the discussion.

Related to the point above, SALL4A is proposed to have an isoform-specific interaction with the BAF complex. It would be valuable to plot SALL4A and SALL4B expression from the available RNA-seq data at Day 0, 5 and 14 to explore whether stage-specific isoform expression matches with the proposed role of SALL4A to interact with BAF at Day 5. It could be valuable to also look at expression of SALL1, 2 and 3 across the time course to see whether additional compensation mechanisms are at play during the differentiation.

Thanks for suggesting this. We performed a time course analysis of isoform specific gene expression, which showed that SALL4B expression remains low throughout differentiation, while SALLA4A expression increases upon differentiation cues and it remains at high levels until the end. We have added this to supplementary Fig. S9. Moreover, we have performed an additional experiment, using pomalidomide, which is a thalidomide derivative that selectively degrades SALL4A but not SALL4B. Notably, SALL4A degradation recapitulated the main findings obtained with the CRISPR-KO of SALL4, further supporting that SALL4A is the isoform involved in CNCC induction (see new Fig. 8).

At line 264, The authors state "SALL4 recruits the BAF complex at CNCC developmental enhancers to increase chromatin accessibility". Given that this analysis is performed at Day 5 of the differentiation, which is labelled as neuroectoderm what evidence do the authors have that these are specifically CNCC enhancers? Statements relating to enhancers should generally be re-phrased to putative enhancers (as no functional evidence is provided for enhancer activity), and further evidence could be provided to support that these are CNCC-specific regulatory elements, e.g. showing representative gene loci from CNCC-specific genes. Discussion of the RNA-seq presented in Supplementary Figure 2B may also be appropriate to introduce here given that large numbers of accessible chromatin sites are detected while the expression of very few genes is impacted, suggesting these sites may become active enhancers at a later developmental stage.

As also recommended by the other Reviewer, to further characterize these sites, we have used publicly available histone modification CHIP-seq data (H3K4me1, H3K4me3) generated by the Wysocka lab (H3K4me1, H3K4m3) and also generated new H3K27ac CHIP-seq data as well. These experiments and analyses confirmed that these regions are putative CNCC enhancers (and a minority of them putative promoters), all decorated with H3K4me1, and all showing progressive increase in H3K27ac after CNCC induction (day-5). See new Supplementary Figure S6.

1. Do any of the putative CNCC enhancers detected at Day 5 as being sensitive to SALL4 downregulation and loss of BAF recruitment overlap with previously tested VISTA enhancers (https://enhancer.lbl.gov/vista/)?

Yes, we have found examples of overlap and have included two of them in the updated Figure 6 as Genome Browser screenshots.

Minor comments

1. The authors are missing references in the introduction "a subpopulation of neural crest cells that migrate dorsolaterally to give rise to the cartilage and bones of the face and anterior skull, as well as cranial neurons and glia".

Fixed, thank you.

The discussion of congenital malformations associated with SALL4 haploinsufficiency is brief in the introduction. From OMIM, SALL4 heterozygous mutations are implicated with the condition Duane-radial ray syndrome (DRRS) with "upper limb anomalies, ocular anomalies, and, in some cases, renal anomalies... The ocular anomalies usually include Duane anomaly". That Duane anomaly is one phenotype among a number for patients with SALL4 haploinsufficiency could be clarified in the introduction. Of note, this is stated more clearly in the discussion but needs re-wording in the introduction.

Done, thank you.

The statements "show that the SALL4A isoform directly interacts with the BAF complex subunit DPF2 through its zinc-finger-3 domain" and "this interaction occurs between the zinc-finger-cluster-3 (ZFC3) domain of SALL4A and the plant homeodomains (PHDs) of DPF2" in the introduction appear overstated and should be toned down. To show this the authors would need to mutate or delete the proposed important zinc-finger domains from SALL4A, which is outside the scope of this work. Notably, this is less strongly-stated elsewhere in the manuscript, e.g "predict that this interaction is mediated by the BAF subunit DPF2", Line 162.

Done, thank you.

Could the authors clarify why 3 Alphafold output models are shown for SALL4B in Figure 1C, and only one output model for SALL4A?

AlphaFold3 produces five separate predicted models per protein combination (e.g., Model_1 … Model_4), each derived from slightly different network parameters or initializations. The final output prioritizes the model with the highest confidence score. This multi-model strategy enables the identification of the most robust conformation while providing a measure of structural uncertainty (as per GitHub documentation for AlphaFold3). wE have conducted the same analysis for SALL4A as we did for SALL4B. Specifically, SALL4A interacts with the AT-rich DNA in models 0, 1, and 2, therefore models 3 and 4 were excluded. When analysing models 1 and 2, we found a higher number of residues involved in the interaction (>800 instead of 396). Similarly to model 0, only the interactions between residues belonging to an annotated functional domain (ZFs and PHDs) were considered.

In Model 1: SALL4A and DPF2 interact mainly through ZF6 and 7, and not 5 as Model 0.

In Model 2: SALL4A and DPF2 interact mainly through ZF5 and 6, and not 7 as Models 0. In contrast, this model shows an interaction with ZF1 not shown in the other two models, but with a higher PAE (31 average compared to 25 to 27 average of the other two ZFs.

Therefore, we considered Model 0 as it is the model with higher confidence and representative of all significant models (includes ZF5, 6, and 7).

Line 121. The authors state "DPF2, a broadly expressed BAF subunit,", but don't show expression during their CNCC differentiation. It would be good to include expression of DPF2 in Figure 1E.

Done, thank you.

The text states "a 11 bp deletion within the 3'-terminus of exon 1 of SALL4", while the figure legend states, "Sanger sequencing confirming the 19 bp deletion in one allele of SALL4 is displayed". The authors should clarify this disparity and experimentally confirm the deletion, e.g. by TA-cloning the two alleles and sequencing these separately to show that one allele is wildtype and the other has a frameshift deletion.

We apologize for the confusion. As stated above (point-2 of the major comments), we have used two clones (one generated with a 11 bp deletion, one with a 19 bp deletion, both in exon-1, see also the point 6 of your minor points). The two clones were used as biological replicates (see response above for details). The deletion for both clones was experimentally confirmed by Sanger sequencing by the company that generated the lines for us (Synthego). The strategy for the two clones is now shown also in Supplementary Fig. S2.

The authors generate an 11-bp (or 19-bp?) deletion in exon-1 - it would be valuable to include a discussion whether patients have been identified with deletions and frame-shift mutations in this region of SALL4 exon-1. And also clarify, if not clearly stated in the text, that both SALL4A and SALL4B will be impacted by this mutation. Are there examples of patient mutations which only impact SALL4A?

As requested, we have added a discussion paragraph to discuss this. And, yes, both SALL4A and SALL4B are impacted by both deletions in both clones (11 bp and 19 bp deletion).

Regarding patient variants on exon-1 and patient variants that only impact SALL4A. We could only find one published pathogenic 170bp deletion in exon 1 (VCV000642045.7). The majority of the pathogenic or likely pathogenic variances are located on exon2. In particular, of the 63 reported pathogenic (or likely pathogenic) clinical variants, 42 were located on exon 2. Among these, 28 are located in the portion shared by both SALL4A and SALL4B, while the remaining 14 were SALL4A specific.

For the SALL4 blots in Figure 2B, is the antibody expected to detect both isoforms (SALL4A and SALL4B), and which isoform is shown? If two isoforms are detected, they should both be presented in the figure.

Yes, the antibody detects both isoforms, and we now present both in the figure 2, as recommended.

SALL4 expression should be shown for Figure 2C to see whether the >50% down-regulation of SALL4 at the protein level may be partially driven by transcriptional changes.

Done, thank you. As expected, we observed the SALL4 mRNA expression in the KO line is comparable to wild-type conditions, but still this results in a significant decrease of the SALL4 protein level likely because of autoregulatory mechanisms coupled with non-sense mediated decay of the mutated allele. Also, we note that SALL4 usually makes homodimers, therefore lack of sufficient amount of protein could also lead to degradation of the monomers.

The number of experimental replicates should be indicated in all figure legends where relevant. Raw data points should be plotted visibly over the violin plots (e.g. Figure 2C).

Done, thank you.

For Figure 3A, the images of the DAPI and NANOG/OCT4 staining should be shown separately in addition to the overlay.

Done, thank you.

The metric 'Corrected Total Cell Fluorescence (CTCF)' should be described in the methods. The number of images used for the quantification in Figure 3A should be

Done, thank you.

Figure 3C - what are the 114 differentially expressed genes? Some interesting genes could be labelled on the plot and the data used to generate this plot should be included as a Supplementary Table. Supplementary Tables should similarly be provided for Figure 6C, Day 14 and Supplementary Figure 2B, Day 5.

As recommended, we have highlighted some interesting genes in the volcano plot and also included all the expression data for all genes in Supplementary Table S3.

Figure 4B. The shared peaks are not shown. For completeness, it would be ideal to show these sites also.

Done, thank you.

Figure 4C is difficult to interpret. Why is the plot asymmetric to the left versus right? What does the axis represent - % of binding sites?

The asymmetry is due to the fact that there is a larger number of peaks that are downstream of the TSS than peaks that are upstream of TSS. This is consistent with the fact that many SALL4 peaks are in introns, likely representing intronic enhancers.

Line 224-225. What do n= 3,729 and n= 6,860 refer to? There appear to be many more binding sites indicated in Figure 4B, therefore these numbers cannot represent 86% and 97% of sites?

Thank you for pointing this out, we should have specified in the text. Those numbers refer to the genes whose TSS is closest to each SALL4 peak. Notably, multiple peaks can share the same closest TSS, hence the discrepancy between # of peaks and # of nearest genes.

Raw numbers:

• Day-0 RAW = 6,104 (peaks = 6,114);
• Day-5 RAW = 17,131 (peaks = 17,137). Now raw data reported in Supplementary Table 4.

Figure 4E. Several TFs mentioned in the text (Line 243) are not shown in the figure, it would be good to show all TFs motifs mentioned in the text in this figure. Again, there is no mention of whether a sequence-specific motif is detected for SALL4 (e.g. an AT-rich sequence) from this motif analysis.

Done, thank you. An AT-rich sequence, resembling the SALL4 motif, was detected in a small minority of sites (this is now shown in Supplementary Figure S5), suggesting that SALL4 engages chromatin in a broad manner, going beyond its preferred motif, possibly in cooperation with other TFs. This is consistent with many studies that in mESCs have shown that SALL4 binds at OCT4/NANOG/SOX2 target motifs. This is now discussed in a dedicated paragraph in the discussion.

Figure 4G. How was the ATAC-seq data normalized for the WT and SALL4-het-KO lines for this comparison? The background levels of accessibility seem quite different in Replicate 1.

The bigwigs used to make the heatmaps are normalized by sequencing depth using the Deeptools Suite (normalization by RPKM).

Figures 5B-C could be exchanged to flow better with the text. A Venn diagram could be included to show the overlap between the sites losing BRG1 in SALL4-het-KO (13,505 sites) and the Day5-specific SALL4 sites (17,137 sites).

Done, thank you.

At Day 5, the authors suggest a shift towards neural differentiation. It could be interesting for the authors to perform qRT-PCR at Day 5 for some neural markers or look in the Day 14 data for markers of neural differentiation at the expense of CNCC markers.

See updated Supplementary Fig. S8, where we show timecourse expression of several genes, including neural markers.

Is the data used to plot Figure 5D the same as Figure 4G. If so, why is only one replicate shown in Figure 5D?

Only one replicate was shown in the main figure purely for lack of space, but the experiment was replicated twice (with the two different clones), and the results were exactly the same. See plots below for your convenience:

Figure 6A. How many replicates are shown? If n=2, boxplots are not an appropriate to represent the distribution of the data. Please include n= X in the figure legend and plot the raw data points also.

Done, thank you, and as suggested we are no longer using boxplots for this panel.

Figure 6B. What is the significance of CD99 for CNCC differentiation?

Figure 6F. No error bars are shown, how many replicates were performed for this time couse? The linear regression line does not appear to add much value and could be removed.

As suggested, we have removed these plots and replaced them with individual genes plots, which include error bars. See updated Supplementary Figure S8.

At line 304, the authors state "while SALL4-het-KO showed a significant downregulation of these genes". Perhaps 'failed to induce these genes' may be more accurate unless they were expressed at Day 5 and downregulated at Day 14.

Done, thank you.

Lines 332-335. The genes selected for pluripotency, neural plate border, CNCC specification could be plotted separately in the Supplement to show individual gene expression dynamics.

Done, thank you, see point 24.

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Referee #2

Evidence, reproducibility and clarity

Summary

In this manuscript, the authors build on their previous work (Pagliaroli et al., 2021) where they identified an interaction between the transcription factor SALL4 and the BAF chromatin remodeling complex at Day-5 of an iPSC to CNCC differentiation protocol. In their current work, the authors begin by exploring this interaction further, leveraging AlphaFold to predict interaction surfaces between SALL4 and BAF complex members, considering both SALL4 splice isoforms: a longer SALL4A (associated with developmental processes) and a shorter SALL4B (associated with pluripotency). They propose that SALL4A may interact with DPF2, a BAF complex member, in an isoform-dependent manner. The authors next explore the role of SALL4 in craniofacial development, motivated by patient heterozygous loss of function mutations, leveraging iPSC cells with an engineered SALL4 frameshift mutation (SALL4-het-KO). Using this model, the authors first demonstrate that a reduced expression of SALL4 does not impact the iPSC identity, perhaps due to compensation via upregulation of SALL1. Upon differentiation to neuroectoderm, SALL4 haploinsufficiency causes a reduction in newly accessible sites which are associated with a reduction in SALL4 binding and therefore a loss of BAF complex recruitment. Interestingly, however, there were few transcriptional changes at this stage. Later in the CNCC differentiation at Day-14 when the wildtype cells have switched expression of CNCC markers, the SALL4-het-KO cells fail to switch cadherin expression associated with a transition from epithelial to mesenchymal state, and fail to induce CNCC specification and post-migratory markers. Together the authors propose that SALL4 recruits BAF to CNCC enhancers as early as the neuroectodermal stage, and failure of BAF recruitment in SALL4-het-KO lines results in a loss of open chromatin at regulatory regions required later for induction of the CNCC programme. The failure of the later differentiation is compelling in the light of the early stages of the differentiation progressing normally, and the authors outline an interesting proposed mechanism whereby SALL4 recruits BAF to remodel chromatin ahead of CNCC enhancer activation, a model that can be tested further in future work.

Major comments

The link between SALL4 DNA binding and BAF recruitment is nicely argued, and very interesting as altered chromatin accessibility at Day 5 in the neuroectodermal stage is associated with only few changes in gene expression, while gene expression is greatly impacted later in the CNCC stage at Day 14. The in silico predictions of SALL4-BAF interaction interfaces are perhaps less convincing, requiring experimental follow-up outside the scope of this paper. Some of the associated figures could perhaps be moved to the supplement to enhance the focus on the later functional genomics experiments.

1. A lot of emphasis is placed on the AlphaFold predictions in Figure 1, however the predictions in Figure 1B appear to be mostly low or very low confidence scores (coloured yellow and orange). It is unclear how much weight can be placed on these predictions without functional follow-up, e.g. mutating certain residues and showing impact on the interaction by co-IP. The latter parts of the manuscript are much better supported experimentally, and therefore perhaps some of the Figure 1 could move to a Supplemental Figure (e.g. the right-hand part of 1B, and the lower part of Figure 1C showing SALL4B predicted interactions). The limitations of AlphaFold predictions should be acknowledged and the authors should discuss how these predicted interactions could be experimentally explored further in the future.
2. The authors only show data for one heterozygous knockout clone for SALL4. It is usual to have more than one clone to mitigate potential clonal effects. The authors should comment why they only have one clone and include any data for a second clone for key experiments if they already have this. Alternatively, the authors could provide any quality control information generated during production of this line, for example if any additional genotyping was performed.
3. The authors show all genomics data (ATAC-seq, CUT&RUN and ChIP-seq) as heatmaps and average profiles. It would be valuable to see some representative loci for the ATAC seq (perhaps along with SALL4 and BRG1 recruitment) at some representative and interesting loci.
4. Figure 4A. The schematic could be improved by including brightfield or immunofluorescent images at the three stages of the differentiation. Are the iPS cells seeded as single cells, or passaged as colonies before starting the differentiation. Further details are required in the methods to clarify how the differentiation is performed, for example at what Day are the differentiating cells passaged, this is not shown on the schematic in Figure 4A.
5. There is likely some heterogeneity of cell types in the differentiation at Day 5 and Day 14. Can the authors comment on this from previous publications or perhaps conduct some IF for markers to demonstrate what proportions of cells are neuroectoderm at Day 5 and CNCCs at Day 14.
6. For the motif analysis for Day 5-specific SALL4 binding sites (Figure 4E), was de novo motif calling performed? Were any binding sites reminiscent of a SALL4 binding site observed (e.g. an AT-rich motif)? Could the authors comment on this in the text - if there is no SALL4 binding motif, does this suggest SALL4 is recruited indirectly to these sites via interaction with another transcription factor for example?
7. Does SALL1 remain upregulated at Day-5 and Day-14 of the differentiation for the SALL4-het-KO line? Are binding sites known for this TF and were they detected in the motif analysis performed? Further discussion of the impact of the overexpression of SALL1 on the phenotypes observed is warranted - e.g. for Figure 5F, could the sites associated with a gain of BRG1 peaks upon loss of SALL4 be associated with SALL1 being upregulated and 'hijacking' BAF recruitment to distinct sites associated with nervous system development? Is SALL1 still upregulated at Day 5?
8. Related to the point above, SALL4A is proposed to have an isoform-specific interaction with the BAF complex. It would be valuable to plot SALL4A and SALL4B expression from the available RNA-seq data at Day 0, 5 and 14 to explore whether stage-specific isoform expression matches with the proposed role of SALL4A to interact with BAF at Day 5. It could be valuable to also look at expression of SALL1, 2 and 3 across the time course to see whether additional compensation mechanisms are at play during the differentiation.
9. At line 264, The authors state "SALL4 recruits the BAF complex at CNCC developmental enhancers to increase chromatin accessibility". Given that this analysis is performed at Day 5 of the differentiation, which is labelled as neuroectoderm what evidence do the authors have that these are specifically CNCC enhancers? Statements relating to enhancers should generally be re-phrased to putative enhancers (as no functional evidence is provided for enhancer activity), and further evidence could be provided to support that these are CNCC-specific regulatory elements, e.g. showing representative gene loci from CNCC-specific genes. Discussion of the RNA-seq presented in Supplementary Figure 2B may also be appropriate to introduce here given that large numbers of accessible chromatin sites are detected while the expression of very few genes is impacted, suggesting these sites may become active enhancers at a later developmental stage.
10. Do any of the putative CNCC enhancers detected at Day 5 as being sensitive to SALL4 downregulation and loss of BAF recruitment overlap with previously tested VISTA enhancers (https://enhancer.lbl.gov/vista/)?

Minor comments

1. The authors are missing references in the introduction "a subpopulation of neural crest cells that migrate dorsolaterally to give rise to the cartilage and bones of the face and anterior skull, as well as cranial neurons and glia".
2. The discussion of congenital malformations associated with SALL4 haploinsufficiency is brief in the introduction. From OMIM, SALL4 heterozygous mutations are implicated with the condition Duane-radial ray syndrome (DRRS) with "upper limb anomalies, ocular anomalies, and, in some cases, renal anomalies... The ocular anomalies usually include Duane anomaly". That Duane anomaly is one phenotype among a number for patients with SALL4 haploinsufficiency could be clarified in the introduction. Of note, this is stated more clearly in the discussion but needs re-wording in the introduction.
3. The statements "show that the SALL4A isoform directly interacts with the BAF complex subunit DPF2 through its zinc-finger-3 domain" and "this interaction occurs between the zinc-finger-cluster-3 (ZFC3) domain of SALL4A and the plant homeodomains (PHDs) of DPF2" in the introduction appear overstated and should be toned down. To show this the authors would need to mutate or delete the proposed important zinc-finger domains from SALL4A, which is outside the scope of this work. Notably, this is less strongly-stated elsewhere in the manuscript, e.g "predict that this interaction is mediated by the BAF subunit DPF2", Line 162.
4. Could the authors clarify why 3 Alphafold output models are shown for SALL4B in Figure 1C, and only one output model for SALL4A?
5. Line 121. The authors state "DPF2, a broadly expressed BAF subunit,", but don't show expression during their CNCC differentiation. It would be good to include expression of DPF2 in Figure 1E.
6. The text states "a 11 bp deletion within the 3'-terminus of exon 1 of SALL4", while the figure legend states, "Sanger sequencing confirming the 19 bp deletion in one allele of SALL4 is displayed". The authors should clarify this disparity and experimentally confirm the deletion, e.g. by TA-cloning the two alleles and sequencing these separately to show that one allele is wildtype and the other has a frameshift deletion.
7. The authors generate an 11-bp (or 19-bp?) deletion in exon-1 - it would be valuable to include a discussion whether patients have been identified with deletions and frame-shift mutations in this region of SALL4 exon-1. And also clarify, if not clearly stated in the text, that both SALL4A and SALL4B will be impacted by this mutation. Are there examples of patient mutations which only impact SALL4A?
8. For the SALL4 blots in Figure 2B, is the antibody expected to detect both isoforms (SALL4A and SALL4B), and which isoform is shown? If two isoforms are detected, they should both be presented in the figure.
9. SALL4 expression should be shown for Figure 2C to see whether the >50% down-regulation of SALL4 at the protein level may be partially driven by transcriptional changes.
10. The number of experimental replicates should be indicated in all figure legends where relevant. Raw data points should be plotted visibly over the violin plots (e.g. Figure 2C).
11. For Figure 3A, the images of the DAPI and NANOG/OCT4 staining should be shown separately in addition to the overlay.
12. The metric 'Corrected Total Cell Fluorescence (CTCF)' should be described in the methods. The number of images used for the quantification in Figure 3A should be indicated in the legend, and error bars included if multiple images were quantified.
13. Figure 3C - what are the 114 differentially expressed genes? Some interesting genes could be labelled on the plot and the data used to generate this plot should be included as a Supplementary Table. Supplementary Tables should similarly be provided for Figure 6C, Day 14 and Supplementary Figure 2B, Day 5.
14. Figure 4B. The shared peaks are not shown. For completeness, it would be ideal to show these sites also.
15. Figure 4C is difficult to interpret. Why is the plot asymmetric to the left versus right? What does the axis represent - % of binding sites?
16. Line 224-225. What do n= 3,729 and n= 6,860 refer to? There appear to be many more binding sites indicated in Figure 4B, therefore these numbers cannot represent 86% and 97% of sites?
17. Figure 4E. Several TFs mentioned in the text (Line 243) are not shown in the figure, it would be good to show all TFs motifs mentioned in the text in this figure. Again, there is no mention of whether a sequence-specific motif is detected for SALL4 (e.g. an AT-rich sequence) from this motif analysis.
18. Figure 4G. How was the ATAC-seq data normalized for the WT and SALL4-het-KO lines for this comparison? The background levels of accessibility seem quite different in Replicate 1.
19. Figures 5B-C could be exchanged to flow better with the text. A Venn diagram could be included to show the overlap between the sites losing BRG1 in SALL4-het-KO (13,505 sites) and the Day5-specific SALL4 sites (17,137 sites).
20. At Day 5, the authors suggest a shift towards neural differentiation. It could be interesting for the authors to perform qRT-PCR at Day 5 for some neural markers or look in the Day 14 data for markers of neural differentiation at the expense of CNCC markers.
21. Is the data used to plot Figure 5D the same as Figure 4G. If so, why is only one replicate shown in Figure 5D?
22. Figure 6A. How many replicates are shown? If n=2, boxplots are not an appropriate to represent the distribution of the data. Please include n= X in the figure legend and plot the raw data points also.
23. Figure 6B. What is the significance of CD99 for CNCC differentiation?
24. Figure 6F. No error bars are shown, how many replicates were performed for this time couse? The linear regression line does not appear to add much value and could be removed.
25. At line 304, the authors state "while SALL4-het-KO showed a significant downregulation of these genes". Perhaps 'failed to induce these genes' may be more accurate unless they were expressed at Day 5 and downregulated at Day 14.
26. Lines 332-335. The genes selected for pluripotency, neural plate border, CNCC specification could be plotted separately in the Supplement to show individual gene expression dynamics.

Significance

This work provides a conceptual advance in understanding the aetiology of human SALL4-mediated craniofacial malformations in a cell-type specific manner. Leveraging an in vitro differentiation system, the authors define development timepoints and cell types impacted by altered SALL4 dosage. Additionally, the authors provide interesting mechanistic insights how the teratogen thalidomide may impact craniofacial development through proteasomal targeting and degradation of SALL4, and subsequent impact on neural crest differentiation progression.

Several audiences will be interested in this work: stem cell and developmental biologists (especially those interested in neural crest and facial development), and researchers interested in enhancer regulation, chromatin biology or gene regulatory mechanisms. Clinician scientists and geneticists will be interested in the proposed implications for mechanisms of disease.

Field of expertise: We have expertise in mechanisms of gene regulation and in vitro models of early development. We are not experts in modeling protein interactions in silico.

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Referee #1

Evidence, reproducibility and clarity

Summary: The authors have previously published Mass-spectrometry data that demonstrates a physical interaction between Sall4 and the BAF chromatin complex in iPSC derived neurectodermal cells that are a precursor cell state to neural crest cells. The authors sought to understand the basis of this interaction and investigate the role of Sall4 and the BAF chromatin remodelling complex during neural crest cell specification. The authors first validate this interaction with a co-IP between ARID1B subunit and Sall4 confirming the mass spec data. The authors then utilise in silico modelling to identify the specific interaction between the BAF complex and Sall4, suggesting that this contact is mediated through the BAF complex member DPF2. To functionally validate the role of Sall4 during neural crest specification, the authors utilsie CRISPR-Cas9 to introduce a premature stop codon on one allele of Sall4 to generate iPSCs that are haploinsufficient for Sall4. Due to the reports of Sall4's role in pluripotency, the authors confirm that this model doesn't disrupt pluripotent stem cells and is viable to model the role of Sall4 during neural crest induction. The authors expand this assessment of Sall4 function further during their differentiation model to cranial neural crest cells, assessing Sall4 binding with Cut+Run sequencing, revealing that Sall4 binds to motifs that correspond to key genes in neural crest differentiation. Moreover, reduction in Sall4 expression also reduces the binding of the BAF complex, through Cut and Run for BRG1. Overall, the authors then propose a model by which Sall4 and BRG1 bind to and open enhancer regions in neurectodermal cells that enable complete differentiation to cranial neural crest cells.

Overall, the data is clear and reproducible and offers a unique insight into the role of chromatin remodellers during cell fate specification.

However, I have some minor comments.

1. Using AlphaFold in silico modelling, he authors propose the interaction between the BAF complex with Sall4 is mediated by DPF2, but don't test it. Does a knockout, or knockdown of DPF2 prevent the interaction?
2. OPTIONAL: Does knockout of DPF2 phenocopy the Sall4 ko? This would be very interesting to include in the manuscript, but it would perhaps be a larger body of work.
3. Figure 1, the day of IP is not clearly described until later in the test. please outline during in the figure

3- What is the expression of Sal1 (and other Sall paralogs) during differentiation. The same with the protein levels of Sall4, does this remain at the below 50%, or is this just during pluripotency? 4. The authors hypothesise that Sall4 binds to enhancers- with the criteria for an enhancer being that these peaks > 1KB from the TSS are enhancers. Can this be reinforced by overlaying with other ChIP tracks that would give more confidence in this? There are several datasets from Joanna Wysocka's lab that also utilise this protocol which can give you more evidence to reinforce the claim and provide further detail as to the role of Sall4 5. The authors state that cells fail to become cranial neural crest cells, however they do not propose what the cells do instead. do they become neural? Or they stay at pluriopotent, which is one option given the higher expression of Nanog, OCT4 and OTX2 that are all expressed in pluripotent stem cells. 6. In general, I would like to see the gating strategy and controls for the flow cytometry in a supplemental figure. 7. For supplementary figure 1- please include the gene names in the main image panels rather than just the germ layer.

Significance

The strength of this study lies in its well-designed and clearly presented experiments and datasets. In particular, identifying the specific SALL4 isoform that interacts with the BAF complex-and further exploring the implications of this interaction-is a major highlight. The authors also make effective use of in silico modelling with AlphaFold, offering valuable mechanistic insight into how this interaction is mediated.

The topic should have appeal to researchers in developmental biology and epigenetics. This study represents a significant step forward in validating the interaction between SALL4 and the BAF complex, and it highlights the requirement of SALL4 for BAF-mediated chromatin remodelling during neural crest specification. These findings are likely to be of interest to those studying the gene regulatory mechanisms underlying craniofacial development.

However, while the authors outline the roles of SALL4 and the BAF complex in chromatin remodeling during neural crest development, the downstream effects on cell fate specification could be more thoroughly examined. Currently, Gene Ontology analysis is the primary method used to interpret these consequences, and additional functional validation would strengthen the conclusions.

Intended audience: Basic research, epigenetics in pluripotency and neural crest development.

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Reply to the reviewers

Response to reviewers

We thank the reviewers for their constructive feedback, which has greatly improved the clarity and rigor of our manuscript. We have carefully addressed each comment below, indicating changes made to the text, figures, or supplementary material where appropriate. References to line numbers correspond to the revised version of the manuscript.

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

* In this paper, the authors focus on the role of Reticulon-1C in concert with Spastin in response to axonal injury. In data mining, they find axonal mRNAs encoding for ER-associated proteins including Rtn-1. They establish a knockdown targeting both Rtn-1 isoforms Rtn-1A and Rtn-1C. They observe decreased beta-3-Tubulin levels in the soma while axonal protein levels are unchanged. In microfluidic devices, they characterise the effect of a compartment-specific Rtn-1 KD on axonal outgrowth in the axonal compartment. The authors quantify axonal outgrowth, seeing increased outgrowth in an axonal compartment-specific Rtn-1 KD, while the effect seems to be reversed when applying the KD construct in the somatic compartment. When focussing on the axonal growth cone, they find the Rtn-1 KD shows differences in several morphological features of the growth cone. They find an increase in Tubulin levels in an axonal compartment-specific, but a decrease in a somatic compartment-specific Rtn-1 KD. Colocalisation of Rtn-1C and Spastin is shown to be monolaterally increased following axotomy. Combining axotomy with the Rtn-1 KD shows increases in dynamic microtubule growth rates and track lengths. In another model system, neuron balls, they show Rtn1-C, but not Rtn1-A to be present in the axon. In a puro-PLA assay they also show it can be synthesised in the axonal compartment. To investigate the mechanism enabling the cooperation between Spastin and Rtn-1C, they move to a cell line model in which they see a correlating distribution between Spastin and Rtn-1C but not Rtn-1A. Finally, they use in silico modelling to speculate on binding between Spastin domains and Rtn-1 isoforms.*

Major comment:

The rationale behind the work is convincing, however some interpretations are presented as more robust than some data allow. Most notably, while the interaction between Rtn-1 and Spastin has been shown prior to this study, it is only presented here through in silico analysis. In figure 5, an increase in the growth rate of dynamic microtubules is observed in either a Rtn-1C KD or by using a Spastin-inhibitor. Due to a described increase in colocalisation between Rtn-1C and Spastin (5A), the increase in growth rate is displayed as caused by Rtn-1 promoting Spastin's severing ability. This result might however be correlative. Further in the injured samples, Spastin-levels seemingly increase (in the representative images) and it is thus not surprising that the level of Rtn-1C colocalising with Spastin increases as well. This might not be indicative of a cooperation and further experimental evidence are required.

R: We thank the reviewer for this thoughtful comment. We agree that our interpretation should be more cautious, and we have revised the Title, Results and Discussion sections accordingly. In particular:

1. Following yours and other reviewer comments, we have analyzed a new set of experiments regarding the STED images of non-injured and injured axons. To eliminate the risk of artifactual descriptions, we have avoided deconvolution and worked directly with raw STED images (Figure 5A). Under these conditions, the distribution of Spastin and its intensity in distal axons are not modified by injury, nor those of Rtn-1C and Spastin (Supplementary figure 4). We emphasize in the revised text that the in silico modeling we present is supportive, but not definitive, of a direct interaction. To address this concern, we clarify that our study builds on prior evidence of biochemical interaction between Rtn-1C and Spastin (Mannan et al., 2006), and that our own data demonstrate: i) compatible subcellular distribution in axons by super-resolution (STED microscopy, Figure 5A);ii) a potential functional interplay in axons (rescue of β3-tubulin levels by Spastin inhibition, Figure 5B), and iii) isoform-specific co-distribution with Spastin in heterologous cells that is associated with changes on microtubule integrity (see improved Figure 7). Together, these results go beyond correlative localization, but we acknowledge that they do not directly demonstrate a molecular complex in axons. Thus, we now indicate that "Although we did not directly test their molecular association, these results are consistent with Rtn-1C and Spastin sharing a similar subcellular localization, potentially enabling their functional interaction in distal axons" (lines 285-287)

We would like to clarify a possible misunderstanding: in our experiments, the increase in microtubule growth rate was observed after axonal Rtn-1 KD. Spastazoline (SPTZ) only prevented the reduction in β3-tubulin levels induced by Rtn-1 KD, while leaving the KD-driven increase in growth rate and track length unaffected (Figures 5B-E). Thus, our interpretation is that axonal Rtn-1 KD correlates with increased Spastin function. (lines 307-309)

Other comments:

• Generally, graphs would benefit from individual values plotted as well as the summary. Font sizes and types (but rarely) are sometimes inconsistent. Proteins should be consistently written (capitalised or not).

__R: __ We agree with the reviewer and thank for taking the time for noticing these inconsistencies as it significantly affects the quality of the work. We have improved several figures and added graphs plotting individual values (Figures: 2 C, 2E; 4 (A-E); 5E; 6D). We have reviewed the Font size and types more carefully and capitalized the proteins accordingly.

• *Table 1 and figure 1 present data collected from a vast amount of resources. It should be highlighted that datasets from which data was obtained includes many different models, different DIVs and neuronal cell types. Figure 1B may benefit from a different colour scheme. "Ex-vivo" should be "Ex vivo". For "ER mRNAs are a relevant category" it is not described what "relevant" would mean in this context. The title might remove this small part or describe it in the text. It should be described how it is decided that mRNAs are "common". *

• *

__R: __We have now highlighted in the result section the diverse origins of the analyzed samples; We removed the indicated part from the text and explained that common mRNAs were chosen based on the Benjamini-Hochberg (Ben) analysis. (Page 33, lines 1299-1304).

* - Figure 2: add description to y-axis to describe what fold change is displayed, applies to multiple figures. Will improve readability of the figures. In 2C, the ROI showing neuronal somata should be increased to show part of the axon and not cut off the soma.*

• *

__R: __We thank the reviewer for taking the time to highlight this. We have included this modification in figure 2 and throughout the article. We have also enlarged the indicated ROIs in figure 2C as requested. (Page 34)

• *Figure 3: Three out of four axonal compartments seem to be comprised of dying or damaged axons. Especially the axonal KD scrambled image. It should be ensured that neuronal cultures are healthy. *

• *

__R: __We completely agree with the reviewer that the selected images were not describing the general good health of axons which has been accredited by the lack of fragmentation and functional responsiveness shown in (Figure 4 and 5 B, C, E). Thus, we have now replaced the previous axonal fields by more representative ones (Figure 3). (page 36)

• *

Typo in "intersections". The schematic of 3B is a great addition to explain the graphs above. Perhaps it could be a bit refined as it is currently hard to see whether this is a neuron or a growth cone without context. Maybe show where the axon connects to the depicted growth cones and change the third icon which looks like it was crossed out. Small formatting issues: remove additional space bar before "Figure 3." And add after "Bar"

__R: __Many thanks for these great suggestions. We have now improved the figures as suggested and changed the indicated formatting issues. (page 36)

- Figure 4: If not misunderstanding what is depicted, in 4A and B, different lookup tables are used to depict the same signal. Only one of each images is necessary. Do the axons have more tiny branches in the Rtn-1 KD condition in 4A? Unclear why Rtn-1 levels are increased in the Rtn-1 KD (4C), please clarify.

• *

__R: __We thank the reviewer for these observations. The reviewer is correct that different lookup tables were initially applied to the same image. Our intention was to highlight the fine distribution of axonal Rtn-1, but since this aspect is already clearly shown in previous figures, we now retain only a single lookup table. The appearance of tiny branches in the Rtn-1 KD condition represents an isolated observation and does not reflect a consistent or robust phenotype associated with Rtn-1 KD.

As the reviewer points out, the increase of Rtn-1 in the cell bodies of injured neurons following axonal KD was initially surprising to us. However, this was a consistent phenomenon, as shown in the improved Figure 4. Of note, previous studies have reported that total Rtn-1C (but not Rtn-1A) levels increase in response to injury in cortical neurons(Fan et al., 2018). In our case, we interpret this as a compensatory somatic response triggered by the local reduction of Rtn-1 in injured axons. This interpretation is also consistent with the apparent lack of effect of siRNA on distal axonal Rtn-1 levels when applied locally after injury (while somatic application of the same siRNA does reduce axonal Rtn-1). Thus, after 24 hours of KD, the somatic upregulation of Rtn-1 may partially compensate for its expected local synthesis decrease. We have clarified this assumption in the revised text. (lines 247-251)

- Figure 5: It may be easier to understand what "axotomy" samples are if just referred to as "injured" as later in the same figure. The procedure could also very briefly be explained in the results. 5C should depict AUC in µm2 not µm. 5D Spastin is barely visible, brightness and contrast should be adjusted to enhance visibility.

• *

__R: __We thank the reviewer for these helpful suggestions and have implemented the requested changes in Figure 5. Specifically:

We now consistently refer to "axotomy" samples as "injured" throughout the figure and article. In addition, a brief explanation of the axotomy procedure has been added before Figure 2 and before figure 5, also the description has been clarified in Materials and methods. (lines 191-192) and (lines 289-290) and (lines 779-787)

To improve the reproducibility of our outgrowth measurements, we revised this analysis approach. Based on previous work from a co-autor (McCurdy et al., 2019), instead of reporting the "relative number of intersections," we now present the total counts obtained from Sholl analysis of binarized axons (see Methods). To this end, we took advantage of the NeuroAnatomy plugin of FIJI, which more precisely tracks axon trajectories and makes the measurement more independent of axon width. Also, this new approach avoids the conflict we had with what we considered the "first line" after the groove ends, which was a bit of arbitrary. Accordingly, the correct term is now "summation of intersections (sum.)" at different distance bins, as reflected in Figure 5D. (page 40)

For the former Figure 5D (now Figure 5B), we have improved the acquisition of representative images and applied a different set of lookup tables to enhance visibility. (page 40)

- Figure 6: It should be made clear why it is necessary to switch to another model system just for 6A, please indicate this in the text. PCR bands seem very pixelated, check the quality. It is unclear why soma genes/proteins were only tested with either PCR or WB others with both. Rtn-1C and Rtn1-A should be presented in the same order in the PCR and WB panel. Correct "Rtn1-1A" typo. In 6D, 1.5 dots per soma seems like a low number. When normalized to the area the soma vs the axon occupies, the compartmentalization does not work? Maybe it makes sense to refine analysis or apply puromycin in the somatic compartment and analyze the axonal compartment as comparison?

__R: __Many thanks for these observations. We have now included the following clarification in the text: "We sought to characterize the isoform expression of Rtn-1 mRNA and protein in both axons and cell bodies. Because microfluidic chambers yield only limited cellular material, we adopted an alternative culture approach using 'neuronballs.' This method enables the segregation of an axon-enriched fraction by mechanically separating axons from somato-dendritic structures" (lines 375-376).

The resolution of PCR bands has been improved in the revised figure. Note that because the amount of cellular material is relatively scarce, we did not obtain too strong bands.

The difference in the genes/proteins used for characterizing RNA and protein samples reflects our intention to treat both approaches as complementary. The PCR markers were primarily included to confirm sample purity, which also applies to the WB samples since they derive from the same preparation. In both assays, we used MAP2 as a dendritic marker to demonstrate axonal purity. While we acknowledge that the same genes could have been tested by both methods, we believe the results as presented adequately demonstrate the effective isolation of axons.

We have switched the order of Rtn-1C/1A for consistency across PCR and WB panels and corrected the indicated typo in Figure 6A.

We agree with the reviewer that an average of 1.5 puncta per soma initially appeared low. We have identified at least three reasons for this:

First, the signal derives from only a 15-minute puromycin pulse, which is a very short labeling window. Second, our puro-PLA assay is particularly stringent, as ligation relies directly on puromycin- and Rtn-1C-labeled primary antibodies, without the additional spacing normally introduced by secondary antibodies. In standard PLA, the critical distance for amplification is ~30-40 nm, whereas in our assay this distance is even more restrictive. Third, in our initial analysis we applied an overly cautious threshold to define "true" amplification. We have now refined this threshold using a baseline defined by the absence of puromycin stimulation. With this improved criterion, we now quantify an average of ~5 puncta per soma and ~10 puncta per 1000 µm² of axonal area (Figure 6D and Supplementary Figure 3D). Assuming a neuronal soma diameter of 15 µm (area ≈ 176.71 µm²), this yields ~0.028 puncta per µm² in soma. In comparison, axons display ~0.01 puncta per µm², approximately one-third of the soma value, which is compatible with the idea thar cell bodies dominate neuronal protein synthesis.

Following the reviewer's valuable suggestion, we performed additional quantifications in which puromycin was applied exclusively to the somatic compartment. Under these conditions, we still observed amplification in axons (~5 puncta per 1000 µm²), although this value was significantly lower than when puromycin was applied directly to axons. This analysis provided a novel appreciation of the puro-PLA technique in neurons: at least half of the signal originates in the axonal compartment, while a portion may reflect proteins synthesized in soma and transported anterogradely to the axon through yet-unknown mechanisms (potentially involving rapid anterograde transport) (Figure 6D). (page 42)

• Figure 7: 7A shows two images depicting the same information that may not be needed. Can probably be removed. In 7B there is no negative (or any) correlation between Spastin levels and Tubulin, however later it is mentioned that Rtn-1C transports Spastin thus causing a decrease in Tubulin at certain locations? It is nclear if Spastin levels vary intensely between different samples. Mean intensity of the somatic area may be beneficial to rule this out. 7B Tubulin on the right top panel seems to have a decrease in Tubulin levels which is not visible due to the Y axis of Tubulin being set to a different range than the middle and lower panel. The average of line scans from multiple cells may be helpful to determine whether there is indeed no colocalization between Rtn-1A and Spastin. The provided representative images seem to show similar degrees of colocalization between Spastin and Rtn-1A/C.

• *

__R: __We thank the reviewer for these valuable observations and acknowledge that Figure 7 may have caused confusion. We have eliminated the fluorescence line-scan traces, as they can be biased depending on the region of the cell analyzed. Although this may not have been sufficiently emphasized in the text, we had already performed a quantitative colocalization analysis across multiple cells and independent experiments, using Mander's coefficients (Figure 7B). These analyses showed higher colocalization between Rtn-1C and Spastin compared to Rtn-1A. Regarding the concerns about variability in Spastin levels or possible bias from Y-axis scaling, we have eliminated those traces by the risk of bias. Also, we had already quantified the total tubulin fluorescence intensity across all the z-stacks and from multiple cells from independent experiments as shown in Figure 7C. To further rule out artifacts caused by variable transfection efficiency, we quantified total fluorescence intensity in both RFP and GFP channels across conditions. As shown in Supplementary Figure 6, no significant differences were observed, suggesting that the changes in tubulin reflect specific effects of Spastin/Rtn-1C co-expression rather than variability in expression levels.

Results: - It would be helpful to reiterate the hypothesis at the start to ease the reading flow.

__ R: __Many thanks, we have introduced a line reiterating the hypothesis as suggested (lines 117-118)

- There seems to be minor redundancy in lines 132-138.

• *

__R: __Indeed, we have now removed the indicated phrase.

• There are several spellings, proof-reading is recommended. For example, in line 136 should be "promotes". 160 "localla", 192 should be "the actin cytoskeleton".,194 should be "we first examined", 195 should be "Different", 223 "using", 259 "axons".

__R: __We apologize for the spellings; we have now performed a careful proof-reading and introduced these corrections.

- 154-155: Unclear, why the lower MW Rtn-1C was seen as more important.

__R: __We apologize for not being clear enough. It is not necessarily more important, but we just took the Rtn-1C molecular weight as reference for the analysis considering that this isoform is the predominant in axons. In any case we have found a significant effect for both isoforms at least on siRNA 2 (data not shown), which is now expressed in the text (line 165-169) : "We also examined the 180 kDa band and found that siRNA 1 reduced expression to a mean of 0.41 relative to Scr, showing a strong trend that did not reach statistical significance (p = 0.05; N = 3; Wilcoxon test compared to 1, data not shown). In contrast, siRNA 2 further reduced expression to a mean of 0.29, which was statistically significant (p = 0.04; N = 3; Wilcoxon test compared to 1, data not shown)."

- 167 results of 2E not stated before interpreting them.

• *

__R: __We have corrected this mistake.

- 181 would suggest "outline" instead of "perimeter".

• *

__R: __We have considered this suggestion and included "outline", nevertheless the morphometric parameter is defined as perimeter, so we retained the term, but with the suggested clarification.

• *

- 183-184 "longest shortest path" is a confusing term.

__R: __We agree that it is a confusing term, thus have now introduced multiple clarifications for the term in the leyend of figure 3 (page 36), and with more detail in a new section of Materials and methods (lines 697-699).

• figure 4B should be referenced earlier in the sentence.

__R: __We have corrected the sentence in the text.

- 243-244 may be correlation. Rtn-1 and Spastin do not necessarily interact so that this result is achieved.

• *

__R: __Thanks for the clarification, we are aware that so far in the manuscript the conclusion is not correct, thus now we have stated at the end of the paragraph: "Together, these observations suggest that axonal Rtn-1 KD correlates with higher Spastin microtubule severing" (lines 307-309)

- 246: In figure 1 the KD seemed to influence both Rtn-1 isoforms, why not here anymore? 259 "axons". 284 "counteract" instead of "suppress"?

• *

__R: __We acknowledge the confusion at this point of the article because of measuring a specific isoform. We now indicate that we will focus on Rtn-1C because of previous evidence of the literature pointing to an interaction of Rtn-1C with Spastin (line 264-267). Later we show that Rtn-1C is the predominant isoform in axons (Figure 6). We have corrected all the suggestions in the manuscripts.

- 485: rephrase as the interaction between Rtn-1C with Spastin has not been shown directly in these experiments.

__R: __Many thanks for the relevant clarification. Now, we have corrected:" Here, we have described an emerging mechanism relating Rtn-1C with the activity of Spastin, which is the most frequently mutated isoform in HSP (Hazan et al., 1999; Mannan et al., 2006)." (line 632-634). * Methods: 535 "in PBS". 543 citation error. 689-699 is it necessary to add a gaussian blur?*

• *

__R: __We have corrected the words and removed the wrong reference. Regarding the use of Gaussian blur, it is a very important point. We used this approach because, in our experimental conditions, it was critical to highlight moving particles that otherwise would go unnoticed by the noise. This was particularly manifest for the seemingly more "unorganized" movements of axonal microtubules after injury.

References: Mannan, A U et al. appears twice in the citation list (36 and 44).

* *R: Many thanks for the observation. Now we have corrected it.

Reviewer #1 (Significance (Required)):

Overall, this manuscript describes novel fundings which will be interesting to the neuronal cell biology community and scientists working on the field of neuronal injury and regeneration. It is well structured, and the data are mostly well presented but sometimes conclusions are over-interpreted. However, several points need to be addressed in a more convincing way.

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

Axonal mRNA localization and localized translation support many neuronal functions and is an important determinant of the regenerative potential of axons after injury. How this works mechanistically remains unclear. The authors present a well performed and technically challenging study in which they identify RTN-1 as a regulator of axonal outgrowth after injury. They provide evidence using experiments in microfluidic chambers that RTN1 is locally synthesized in axons. Interestingly, they identify a (local) interplay between RTN1 and Spastin which affects microtubules and thereby regulates the outgrowth of cortical axons after injury. This study provides an interesting new link between a locally synthesized protein (RTN1) and a microtubule-regulating protein Spastin that is changed upon axon injury. This provides an advance in our understanding in axon regeneration after injury and provides the basis for new studies that can further investigate this interplay. Although interesting, I have several concerns that should be clarified and are needed to substantiate the findings and model presented in this study.

Major concerns:

2. In figure 1, the authors provide an analysis of overlapping axonal mRNAs. There are more axonal transcriptome studies and a recent study by von Kugelgen and Chekulaeva (2020; doi: 10.1002/wrna.1590) already performed such an analysis, which included more studies. It would be good to mention this. It can be perceived that studies were now chosen to get the outcome that Rtn-1 is present in all studies. For example, von Kugelgen finds mRNA coding for RTN3, another ER structural protein, as present in 16 out of 20 studies analyzed. That said, the authors present more reasons to look at Rtn-1, so the selection to continue with this protein remains valid but can be written up differently so not to present it as the 'sole' ER-shaping protein consistently present in axonal transcriptomes. __R: __We appreciate this important observation to enrich the article; we are aware that the transcriptome data can be even further expanded to more recent studies. Thus, we have now included this reference in the main text and highlighted the relevant finding of RTN3. However, Kugelgen and Chekulaeva used data from dendrites/axons (neurites). Thus, we indicate that "...On a similar approach, but combining data from dendrites and axons, it was found that Reticulon-3 *mRNA is present in 16 out of 20 studies, further suggesting a wider presence of other mRNAs coding for ER structural proteins in axons " (line 128-131)

3. The description of methods is currently insufficient and incomplete and does not allow for reproducibility of this study. For example, different Rtn-1 antibodies seem to be used in this study. Is the same antibody used for staining and WB? There is no listing of any of the antibodies used in the study and which one is used for which technique/experiment. This should be clarified and should be easy to do so in the methods section (antibody name, origin/company, dilution used) to enhance reproducibility of this study. This is not limited to primary antibodies and any information on secondary antibodies, including what was used for STED is completely missing.*

4. *

__R: __Thanks for these critical comments. First, we apologize for the former method version which was mistakenly not as accurate as it should. We have now revisited it and improved several points throughout this section. Regarding the use of primary and secondary antibodies, plasmids, siRNAs, and general reagents, they are all indicated in the Supplementary material, including company and dilution ("Reagent tables").

• The timeline of KD experiments in Figures 2 and 3 are unclear. For the Western blot KD is performed at DIV7 and collected 48 hours later. However, this is not specified for the stainings done in Figure 2C-E. Is this also at DIV7 and then for 48 hours? In figure 3 the siRNA is added at DIV8 (together with axotomy) and outgrowth is measured 24 hours later. Is 24 hours sufficient to achieve knockdown? Is this also what was done for stainings? Later on in Figure 5B, 48 hours of KD is again used. It is unclear what the rationale of these differing timepoints is. Why was this chosen? Is the timeline also the reason for the difference in segment lengths chosen? In Figure 3, there is a significant effect on outgrowth in the KD in the 'mid-range' which is not present in Figure 5.*

__R: __We regret the confusion, now all this information is explicitly clarified in the main text (lines 297-299) and the corresponding figure legends. We have strong reasons to have used these different time points. Figure 2 A-B is aimed at validating the siRNA against Rtn-1 thus we treated 7 DIV cultures for 48 hours to be sure of revealing a global effect by WB. In figure 2 C-D, we used the same 7 DIV cultures, but only for 24 hours. The reason for this is that, once the RNAi was validated, we explored its control on local synthesis in a shorter period based in previous literature supporting that axonal KD for 24 hours is sufficient for regulating axonal transcripts (Batista et al., 2017; Gracias et al., 2014; Lucci et al., 2020). We are also confident of using this time point based in the new supplementary figure 3D that shows a significant decrease on puro-PLA signal (indicative of Rtn-1C synthesis) 24 hours after axonal KD.

In figure 3, we performed axotomy thus we had to wait a longer period for axons to grow (8 DIV) before fully cut them out, in this case we performed axonal KD from 8 to 9 DIVs. This is the same period used for the staining and quantifications shown in figure 4. All this is properly clarified in the main text and figures.

In Figure 5 we performed a more challenging experiment that required to transfect cells with an EB3-GFP plasmid, then perform axotomy along with axonal KD as well as pharmacological treatment selectively in axonal compartment. First, we tried to measure microtubule dynamics under the same temporal frame of figure 3. Nevertheless, expression levels of EB3-GFP were not adequate for axonal measurements by live-cell imaging. Therefore, compared to figure 3, we increased the time frame after axotomy 24 hours (from 9 to 10 DIV) by this technical reason, but also to explore whether the changes on tubulin intensity might be revealed more clearly (which was the case, figure 5B). These considerations are now included in the main text

Regarding the significant effect on outgrowth in the KD in the 'mid-range' which is not present in Figure 5. Given that in figure 5D axons are left growing for two days instead of one, the number of intersections and the differences between conditions is modified compared to figure 3, while retaining the overall trends. Note that to improve the reproducibility of our outgrowth measurements, we revised this analysis approach. Based on previous work of a co-autor (McCurdy et al., 2019), instead of reporting the "relative number of intersections," we now present the total counts obtained from the Sholl analysis of binarized axons (see Materials and methods). To this end, we took advantage of the NeuroAnatomy plugin of FIJI, which precisely tracks axon trajectories and makes the measurements more independent of axon width segmentation. Also, this new approach avoids the conflict we had with what we considered the "first line" after the groove ends, which was a bit of arbitrary. Accordingly, the correct term is now "summation of intersections (sum.)" at different distance bins, as reflected in the new Figure 5D.

Could the authors provide a rescue condition for their siRNA (using a siRNA-resistant construct) to show that their siRNA is specific for RTN1. They nicely show the efficiency of the siRNA but not its specificity. This is crucial because if not specific, this will affect a large part of their study. They already have RTN1A and RTN1C constructs available. Such a rescue experiment should ideally also be performed for one or more of their phenotypic experiments, such as the one presented in Figure 3A or 5 to show that the phenotype is really RTN1 dependent. If done by re-expressing either RTN1A or RTN1C, this could provide insightful information on the relevant isoforms.

__R: __We agree with the reviewer that this is a critical point. A major challenge in demonstrating the functional role of axonally synthesized proteins using a KD approach is that the rescue may also need to occur locally. Since axonal Rtn-1 appears to play a distinct role compared to its somato-dendritic counterpart (Figure 3), a siRNA-resistant construct would ideally require an axon-targeting sequence to restore local synthesis. As this is technically demanding, we have not yet been able to perform such an experiment, but we are actively working on identifying the optimal sequence to direct Rtn-1C to axons. Importantly, studies performing axonal KD typically rely on at least two independent siRNA sequences, thereby minimizing the likelihood that a phenotype arises from off-target effects. Thus, we have now validated a third siRNA (siRNA 3), which selectively downregulates Rtn-1C. Then, following the same experimental frame of figure 3, we performed axonal Rtn-1 KD after injury and observed that siRNA 3 also significantly increases the outgrowth of injured axons (Supplementary figure 2). This suggests that, at least this phenotype, is not product of an off-target effect. Complementarily, pharmacological rescue with the Spastin inhibitor SPTZ mitigated both the reduction in distal axonal β3-tubulin and the increase on axon outgrowth, supporting that the observed phenotypes are unlikely to arise from off-target effects. If these effects were due to random interference with unrelated mRNA targets, inhibition of an ostensibly independent target such as Spastin would not be expected to yield such a consistent rescue. Accordingly, SPTZ treatment alone did not increase β3-tubulin, indicating that its action is specifically contingent upon Rtn-1 KD. Taken together, the pharmacological rescue in axons (Figure 5B) and the Rtn-1C/Spastin co-distribution in heterologous cells, which correlates with preserved microtubules (improved Figure 7), provide converging evidence to suggest that Rtn-1C-Spastin interplay may underly the observed phenotypes in axons.

• I find the data presented in Figure 4A/B confusing. Axonal RTN-1 KD does not reduce axonal RTN1 levels, but somatic KD does. I understand that this implies most protein comes from the soma, and the authors indeed present an explanation that increased somatic RTN1 occurs after axonal KD as a compensation mechanism. However, this can also be interpreted that there is no axonal synthesis of RTN1 after injury and axonal KD has indirect or even aspecific effects. Their model depends on this difference. Their data in Figure 6 could provide supporting evidence if it shows RTN1 puro-PLA after injury. Along these same lines, in Figure 6, they nicely include a compartment control for puro-PLA. It therefore seems doable to include a somatic puromycin control for their axonal puro-PLA, to exclude and diffusion/transport of the newly synthesized peptides. This is especially considering two recent papers reporting on this possible phenomenon, although these studies were not performed in neurons.*

__R: __We consider the possibility that after injury there is no axonal Rtn-1 synthesis as a plausible and relevant appreciation. Unfortunately, we could not perform a puro-PLA experiment after injury, which would have provided a more definite answer. However, now we are more confident of regulating Rtn-1 synthesis before injury as supported by a new supplementary figure 3D that shows a significant decrease on puro-PLA signal (indicative of Rtn-1C synthesis) 24 hours after axonal KD. Thus, based on the similar phenotypes observed before and after injury, we consider our results are still compatible with Rtn-1 axonal synthesis being downregulated, but not absent after injury. First, axonal Rtn-1 KD decreased β3-tubulin levels before and after injury according to figure 5B and the improved statistical analysis performed on figure 2E. Similarly, axonal Rtn-1KD significantly increases microtubule growth rate before and after injury according to the current statistical comparisons (Figure 5E). Second, if β3-tubulin decrease was a merely unspecific siRNA targeting, it is unlikely that SPTZ treatment should increase and restore β3-tubulin levels only in the context of axonal Rtn-1 KD (Figure 5B). We have now included these considerations in the discussion (lines 537-543). Although on a different track, the mechanistic relationship between Rtn-1C and Spastin suggested in Figure 7 could make more plausible that a similar phenomenon regarding the control of tubulin levels may occur locally in axons.

Following the reviewer's valuable suggestion, we performed additional quantifications in which puromycin was applied exclusively to the somatic compartment. Under these conditions, we still observed amplification in axons (~4 puncta per 1000 µm²), although this value was significantly lower than when puromycin was applied directly to axons (~10 puncta per 1000 µm²). This analysis provided a novel appreciation of the puro-PLA technique in neurons: at least half of the signal originates in the axonal compartment, while a portion may reflect proteins synthesized in soma and transported anterogradely to the axon through yet-unknown mechanisms (potentially involving rapid anterograde transport). Note that we revised the criteria for detecting true amplification spots based in staining without puromycin, which increased true amplification numbers. Still, these seemingly low values are compatible with reflecting a limited amount of time (only 15´ of puromycin pulse) and the stringent conditions of this experiment in which secondary antibodies were avoided by directly labeling primary ones. This approach makes the classical 30-40nm distance for PLA even narrower, thus reducing signal. In any case, assuming a neuronal soma diameter of 15 µm (area ≈ 176.71 µm²), this yields ~0.028 puncta per µm² in somata. In comparison, axons display ~0.01 puncta per µm², approximately one-third of the soma value, which makes sense for the expected difference in ribosome density.

• In Figure 5A the authors find an increased co-localization (RTN1/Spastin) after axotomy. From their images, it seems that the amount of Spastin is hugely increased, which would by default increase the chance of (random) colocalization of RTN1 on Spastin. Could the authors comment on this?*

__R: __Thanks for this relevant and constructive critique. We formerly based our colocalization analysis on deconvolved images. However, after performing several quantifications through different deconvolution parameters, we were not convinced about the robustness of this finding and the performed staining. Thus, we performed a new set of experiments and found that non-deconvolved images from the STED microscope were more informative about the expected tubular morphology of the axonal ER. Thus, we improved figure 5A, and now the main conclusion is just that both proteins are closely distributed in distal axons before and after injury.

• In figure 5E and 5F, the condition of scr + SPTZ is omitted. What is the reason for this? The explanation of results in these figures is confusing. The authors report a 'clear trend' in increase in comet track length and lifetime upon addition of SPTZ to axonal RTN-1 KD. This is however not significant. The comparisons that are made afterwards are confusing (e.g. increase in comet lifetime of SPTZ in non-injured axons with RTN1 KD compared to Scr+DMSO and KD + DMSO in injured axons). Their conclusion is axonal RTN-1 synthesis in injured axons (see my concern in the points above on this) governs microtubules growth rate beyond Spastin activity yet blocking Spastin activity still completely blocks the effect of KD on outgrowth.*

* *__R: __We thank this observation and fully agree that the general description provided in figure 5 E wasn't satisfactory. We have re-organized the descriptions of these results and performed more relevant statistical comparisons (lines 338-359). Based on the reviewer observation, we now conclude: "Together, these results suggest that axonal Rtn-1 synthesis controls microtubule dynamics in both non-injured and injured axons, mostly independently of Spastin-mediated microtubule severing." (lines 357-359).

Other/minor concerns:

- The gene ontology analysis in Figure 1A contains the category 'Endoplasmic reticulum'. In this category are mainly ribosomal proteins. Although in a gene ontology analysis these proteins will be included in this category, it is misleading in this respect since they are just as likely to be coming from cytoplasmic ribosomes. Although it cannot be excluded that these are ER-bound ribosomes, not in the last place because a recent study (Koppers et al., 2024, doi: 10.1016/j.devcel.2024.05.005) found ribosomes attached to the ER in axons, I believe the category should be adapted or at the least clarified in the text.

• *

__R: __Many thanks for the suggestion, which is now included in the text. "Note that several of the identified transcripts in the category 'endoplasmic reticulum' code for cytoplasmic ribosomal components, which indeed can be attached to the axonal ER (Koppers et al., 2024) and be locally synthesized in axons (Shigeoka et al., 2019)." (lines 125-128)

- Is RTN-1C isoform still an ER-shaping protein or rather an ER protein with alternative functions? The final sentence in the abstract makes a statement that a locally synthesized ER-shaping protein lessens microtubule dynamics. Could the authors provide a clearer description and discussion of the evidence in literature for this? RTN1C has been suggested to perform alternative functions in which case the statement that the local synthesis of an ER-shaping protein is important for axonal outgrowth should be adapted.

R: We agree with the reviewer and are aware that some non-canonical roles of Rtn-1C may partially explain the observed phenotypes. Thus, we have rephrased the last statement of the abstract: "These findings uncover a mechanism by which axonal protein synthesis provides fine control over the microtubule cytoskeleton in response to injury.". Also, we have modified the discussion section introducing new references accordingly..." Some studies have pointed to a non-canonical role for Rtn-1C in the nucleus, including DNA binding and histone deacetylase inhibition (Nepravishta et al., 2010, 2012). It is tempting to speculate that these still emerging roles may also contribute to the observed phenotypes. Of note, different axonally synthesized proteins exert transcriptional control in response to injury or local cues (Twiss et al., 2016)." (lines 576-580).

• Is there a difference in RTN1 distribution or levels pre- and post-axotomy?

R: Thanks for the suggestion, with the new analysis we have only found slight reorganization of Rtn-1C and Spastin in distal axons (Figure 5A). We have also included now quantification of their levels and found no significant differences for both proteins (Supplementary figure 4)

- Line 100/101 states 'the interactome of the axonal ER provides...'. To my knowledge there has been no study looking at the interactome of the axonal ER specifically. Surely axonal ER proteins are known but there is a difference.

• *

__R: __We agree with the reviewer that the phrase was misleading, so we rephrased it in the introduction "...Different lines of evidence support that the protein components of the axonal ER may interact with proteins that regulate microtubule dynamics"

* - Typo line 160 'localla'*

• *

__R: __Thanks for taking the time, we have now corrected it.

- In Figure S1 B, please add the DIVs to make it clearer what each graph corresponds to. The legend of S1B states different distances from the cell body but the graph shows distances from the tip.

• *

__R: __We have now corrected the legend accordingly.

- Figure 2C, why does B3 tubulin decrease in soma, aspecific effect of siRNA?

• *

__R: __This was indeed an unexpected finding. However, we do not observe unspecific or global changes in β3-tubulin levels (see Figure 2A and Supplementary Figure 2). Considering our other results linking Rtn-1 to the regulation of the microtubule cytoskeleton, we interpret this decrease as an indirect effect of Rtn-1 depletion rather than an off-target action of the siRNA. Moreover, if the effect were unspecific, both proteins would likely be reduced in the cell body, given that the siRNA was specifically designed to target Rtn-1 as its primary sequence-specific target.

- What is the rationale on the opposite effect found in outgrowth in Figure 3?

• *

__R: __The apparent opposite outcomes observed in Figure 3 - where axonal versus somatic Rtn-1 knockdown leads to divergent effects on axonal outgrowth - can be explained by compartment-specific environments and isoform distribution. The siRNA targets the conserved RHD region, reducing both Rtn-1A and Rtn-1C. Axons are enriched in Rtn-1C. Thus, axonal KD preferentially reduces Rtn-1C. In contrast, somatic KD reduces both isoforms. Rtn-1A, predominant in cell bodies, may probably engage other signaling pathways (Kaya et al., 2013). Interestingly, it was reported by Nozumi et al. (2009b) that global Rtn-1 depletion reduces axonal outgrowth in developing cortical neurons. This aligns with the notion that somatic KD mimics a more global loss of function, whereas axonal KD reveals a compartmentalized, pro-regenerative effect due to local Rtn-1C regulation. (All the references indicated here are in the main manuscript). These considerations are now included in the discussion ( lines 581-593).

* - Missing word 'we' on line 194*

• *

__R: __ We have corrected it.

- Typo line 629 'witmn h', please proofread the entire manuscript carefully.

• *

__R: __ We apologize for the spellings, now we have carefully revised the manuscript.

- Could the authors comment on why, in Figure 7B/C, GFP only is colocalizing with Spastin-RFP? In general, GFP should be diffusive and not display punctate colocalization with Spastin.

• *

We appreciate the reviewer's comment. Under normal conditions, GFP displays a diffuse cytoplasmic distribution. However, in our experimental setup, we observed punctate GFP signals only in the context of co-expression with Spastin-RFP. This is consistent with prior reports showing that soluble GFP can occasionally be sequestered into late endosomal structures (Sahu et al., 2011), which are also known to harbor the M87 Spastin isoform (Allison et al., 2013; Allison et al., 2019). To rigorously exclude the possibility of unspecific fluorescence crosstalk, we independently acquired each fluorophore channel and confirmed that GFP puncta were genuine and not due to bleed-through (Supplementary Figure 5). Further, cells expressing only GFP or only Spastin-RFP did not show overlapping puncta, and co-expression of GFP with Rtn-1A-RFP did not produce any apparent overlap, indicating that the punctate GFP pattern is specifically associated with Spastin co-expression. Thus, the observed GFP colocalization with Spastin reflects a biological phenomenon potentially linked to the endosomal localization of M87 Spastin, and not an artifact of imaging or fluorophore bleed-through.

Reviewer #2 (Significance (Required)):

* Axonal mRNA localization and localized translation support many neuronal functions and is an important determinant of the regenerative potential of axons after injury. How this works mechanistically remains unclear. The authors present a well performed and technically challenging study in which they identify RTN-1 as a regulator of axonal outgrowth after injury. They provide evidence using experiments in microfluidic chambers that RTN1 is locally synthesized in axons. Interestingly, they identify a (local) interplay between RTN1 and Spastin which affects microtubules and thereby regulates the outgrowth of cortical axons after injury. This study provides an interesting new link between a locally synthesized protein (RTN1) and a microtubule-regulating protein Spastin that is changed upon axon injury. This provides an advance in our understanding in axon regeneration after injury and provides the basis for new studies that can further investigate this interplay. Although interesting, I have several concerns that should be clarified and are needed to substantiate the findings and model presented in this study.*

*

The audience for this study will be mainly basic research in the fields of both axonal protein synthesis and axon regeneration. My expertise is in the field of mRNA localization and local protein synthesis.*

Batista, A. F. R., Martínez, J. C., & Hengst, U. (2017). Intra-axonal synthesis of SNAP25 is required for the formation of presynaptic terminals. Cell Reports, 20(13), 3085. https://doi.org/10.1016/J.CELREP.2017.08.097

Fan, X. xuan, Hao, Y. ying, Guo, S. wen, Zhao, X. ping, Xiang, Y., Feng, F. xue, Liang, G. ting, & Dong, Y. wei. (2018). Knockdown of RTN1-C attenuates traumatic neuronal injury through regulating intracellular Ca2+ homeostasis. Neurochemistry International, 121, 19-25. https://doi.org/10.1016/J.NEUINT.2018.10.018

Gracias, N. G., Shirkey-Son, N. J., & Hengst, U. (2014). Local translation of TC10 is required for membrane expansion during axon outgrowth. Nature Communications 2014 5:1, 5(1), 1-13. https://doi.org/10.1038/ncomms4506

Lucci, C., Mesquita-Ribeiro, R., Rathbone, A., & Dajas-Bailador, F. (2020). Spatiotemporal regulation of GSK3β levels by miRNA-26a controls axon development in cortical neurons. Development (Cambridge), 147(3). https://doi.org/10.1242/DEV.180232,

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

This manuscript investigates the relationship between the endoplasmic reticulum morphogen reticulon-1 (Rtn-1) and the microtubule severing protein spastin in axons after injury. The main message and conclusion of the paper is that local axonal synthesis of Rtn-1 plays a role in regulating the microtubule severing activity of spastin by interacting with spastin and inhibiting its activity. This mechanism would be important after injury by regulating axonal growth.

* The conclusions of the paper are based on the following claims:*

* 1) Rtn-1 is synthesized locally in axons.*

* 2) Specific downregulation in Rtn-1 in axons using microfluidic chambers affects microtubules abundance (measured by beta-3 tubulin) and promotes axon growth after injury.*

* 3) Inhibition of spastin MT-severing activity with a specific drug rescues the growth effect induced by axonal downregulation of Rtn-1.*

* 4) Rtn-1c interacts with spastin-M87 to limit its MT-severing activity in a cellular system upon overexpression.*

*

*

Major comments:

1) Evidence that Rtn-1 is synthesized in axons comes from two experiments. Initially, the authors show that Rtn-1 siRNA transfection in the axonal compartment of microfluidic chambers reduces Rtn-1 levels in axons, suggesting that there is some local synthesis. Although this method is very attractive, I am concerned about the statistical analysis. The graphs show bars rather than individual data points from the average of many neurons (about 300). The plots also show the SEM instead of the SD, thus covering all the variability that is inherent in this type of experiment. The statistics are probably not performed on the 3 biological replicates, but consider the individual neurons as N. This is obviously not correct, since neurons in an experiment may all be affected by the same technical problem and are not independent replicates. For this reason, I am a bit skeptical about this quantification. Another problem is that the quantification of the fluorescence intensity of the sample does not take the nuclei into account. Are the nuclei removed for analysis? Are the images single planes? Addressing the quantification issues is crucial also for data in Figure 4, where the authors show a different effect of Rtn-1 axonal KD after injury.

* The second experiment is the Puro-PLA in Figure 6D. This experiment shows an average of 1.5 dots of signal per soma, which is a very low level of translation for this compartment where most of the synthesis should be taking place. In the axons, it is not clear how they calculate the axonal area. Again, the number of dots detected is very low and the physiological significance is questionable. A control with a known mRNA translated in axons would be important.*

* Finally, as an important control, the authors should show the presence of Rtn-1 mRNA by FISH in their experimental system.*

__R: __We appreciate the critical points addressed here as they moved us to improve the quality of the findings. We analyzed cells/axons as statistical units to increase statistical power given the subtle nature of these local changes. We agree with the reviewer that this approach may increase the risk of finding false positives. To address this point, i) we plotted the individual data points and colored them according with the different experimental dates (all the dates showed a similar trend) ii) We indicated SD instead of SEM iii) We analyzed our data using linear mixed-effects models, with experimental date included as a random effect. This approach allows to preserve the granularity and statistical power, while avoiding pseudoreplication. To exclude artifactual changes, we now analyzed the intensity fold change of total fluorescence normalized to Scr. Our former quantifications were based on the corrected fluorescence intensity used to construct the plot profiles, which could be adding some distortion to the measurements. These changes were applied throughout figures 2 and 4 (pages 34 and 38, respectively). After these new analyses the formerly presented results remain valid.

We thank the reviewer for raising concerns about the quantification of fluorescence intensity in cell bodies. We now specify in Materials and methods that fluorescence intensity analysis of distal axons (always isolated by the microfluidic chambers) and of cell bodies was performed using the wide-field configuration of the microscope. In all the cases, a single (epifluorescent) plane was analyzed to reflect the total fluorescence of a cell or axon. We did not exclude the nuclear region from the quantifications, as this would also remove cytoplasmic signal located above or below the nucleus.

We also understand the concerns about puro-PLA experiments. We agree with the reviewer that an average of 1.5 puncta per soma initially appeared low. We have identified at least three reasons for this. First, the signal derives from only a 15-minute puromycin pulse, which is a short labeling window. Second, our puro-PLA assay is particularly stringent, as ligation relied directly on puromycin- and Rtn-1C-labeled primary antibodies, without the additional spacing normally introduced by secondary antibodies. In standard PLA, the critical distance for amplification is ~30-40 nm, whereas in our assay this distance is even more restrictive. Third, in our initial analysis we applied an overly cautious threshold to define "true" amplification. We have now refined this threshold using a baseline defined by the absence of puromycin stimulation. With this improved criterion, we now quantify an average of ~5 puncta per soma and ~10 puncta per 1000 µm² of axonal area (Supplementary Figure 3D). As it is now included in methods, we calculated the axonal area by binarizing β3-tubulin staining and only counted the true amplification spots inside this region. Assuming a neuronal soma diameter of 15 µm (area ≈ 176.71 µm²), this yields ~0.028 puncta per µm² in somata. In comparison, axons display ~0.01 puncta per µm², approximately one-third of the soma value which seems more reasonable. This is also compatible with most of Rtn-1C synthesis comes from the cell body.

Unfortunately, we could not be able to perform puro-PLA of other axonally synthesized proteins. Nevertheless, to further validate our puro-PLA signal, we tested the specificity of the Rtn-1C antibody we used for this assay by WB, IF, and Rtn-1 KD (Supplementary figure 3 A-C). In addition, we performed axonal Rtn-1 KD in microfluidic chambers for twenty-four hours, which elicited a significant decrease in puro PLA signal compared to Scr (Supplementary figure 3D). Together, these results strongly indicate that the quantified signal reflects Rtn-1C synthesis. To prove that Rtn-1 mRNA is present in these conditions, we now included a RT-PCR performed on RNA isolated from the somato-dendritic and pure axonal fractions of 8 DIV microfluidic chambers (Supplementary figure 3D). Note that the presence of this mRNA in axons has been supported by several studies, one of them using cortical neurons of similar DIV and cultured in microfluidic chambers (Table I and figure 1).

2) The effects on tubulin following Rtn-1 downregulation in axons is potentially very interesting, but the authors should be careful because it could also mean that the axons are suffering. Can they also stain for other cytoskeletal markers?

R: Regarding this concern, we are aware that in the former Figure 3 we mistakenly selected axonal fields that did not display healthy axons, which was not the dominant trend. This is accredited by the lack of fragmentation and by the functional responsiveness (microtubule dynamics) shown in Figures 4 and 5B, C, E. We have now replaced the previous axonal fields in Figure 3 with more representative axons (healthy), devoid of varicosities and fragmentation (page 37)

3) The results using SPTZ are very interesting and implicate spastin microtubule severing activity in the observed phenotype. In my opinion these experiments however do not prove that "axonal Rtn-1 is indeed promoting the severing of microtubules by spastin", but simply that the blocking spastin activity prevents the appearance of the microtubular phenotype (which appears still with a mysterious mechanism). What happens if they try to stabilize the cytoskeleton by another mean (with taxol for example?). The authors should rephrase this conclusion.

__R: __We completely agree with the reviewer's appreciation. We now explicitly indicate in the main text that this is (so far in the manuscript) a still correlative phenomenon that suggests an interplay with Spastin activity "..Together, these results suggest that locally synthesized Rtn-1 normally acts to suppress the outgrowth of injured axons, a process that could involve the microtubule-severing activity of Spastin." (lines 321-323). Later in the article, with the improved Figure 7, we further propose that these findings may reflect a causal relationship, although this mechanism has not yet been directly demonstrated in axons.

4) The last experiment (Figure 7) that aims to connect Rtn-1 and spastin function is very artificial, since it is based on overexpression. Why should spastin M87 interact with an ER morphogen? Endogenously it is conceivable that spastin M1 which localizes to the ER would interact with Rtn-1. Moreover, this experiment needs further controls and quantifications. First, it is quite obvious from panel 7C that there is crossover of signal in the two fluorescence channels (see GFP and spastin). Controls need to be shown, where only one of the two fluorescent proteins is expressed, and the specificity of the laser is tested. This experiment is based on only 1 cell shown where co-localisation is detected based on a line that is placed in a specific area of the cell. The effects on the microtubular network needs quantification.

__R: __We have now improved Figure 7 and added the requested controls to rule out crosstalk as indicated in Supplementary Figure 5 and in the main text. We agree that under normal conditions GFP should display a diffuse cytoplasmic distribution. However, in our experimental setup, we observed punctate GFP signals only in the context of co-expression with Spastin-RFP. This is consistent with prior reports showing that soluble GFP can occasionally be sequestered into late endosomal structures (Sahu et al., 2011), which are also known to harbor the M87 Spastin isoform (Allison et al., 2013; Allison et al., 2019). To exclude the possibility of unspecific fluorescence crosstalk, we independently acquired each fluorophore channel and confirmed that GFP puncta were genuine and not due to bleed-through (Supplementary Figure 5). Further, cells expressing only GFP or only Spastin-RFP did not show overlapping puncta (arrowheads), and the co-expression of GFP with Rtn-1A-RFP did not produce any apparent overlap, indicating that the punctate pattern of GFP is specifically associated with Spastin co-expression. Thus, we consider that the observed GFP colocalization with Spastin potentially reflects a true phenomenon and not an artifact of imaging or fluorophore bleed-through.

We thank for these observations and apologize for the confusion in the outline of the former figure 7 and the lack of a better description. As the reviewer indicates, one interesting aspect of the M87 isoform is that lacks the ER morphogen domain (so is soluble or cytoplasmic in principle). However, it also harbors endosome and microtubule binding domains which according to previous literature (now included in the main text) may render it a punctate rather than a homogeneous pattern. Also, M87 is the most abundant isoform in the nervous system, particularly at early development. This is the reason why we selected this isoform to test our model. To clarify this point, we based our colocalization analysis in different cells and experimental dates and analyzed all the z-stacks for each cell (see new figure 7B and methods), the intensity plots (now removed) were only for graphical purposes. Similarly, we had already quantified the total tubulin intensity in COS cells based on many cells from different dates and included the sum projections of all the z-stacks from these cells (see new figure 7C). Thus, we removed the intensity profiles as they were clearly misleading (see new figure 7).

We agree that over-expressing constructs may force interactions or co-distribution of proteins. However, in this case, if the observed results were mainly due to over-expression, we should see a similar trend with isoform A as both constructs are under the control of the same strong promoter (CMV) and harbor the same ER morphogen domain (RHD). Nevertheless, the distribution of M87 tightly mirrors Rtn-1C, which is not the case for Rtn-1A. Only as a theoretical prediction, our molecular modeling suggests that Rtn-1C may be associated with Spastin through its microtubule binding domain (Figure 7E). This would suppose that Spastin "decorates" ER-tubules rather than being in the same ER membranous structure. This discrete pattern of Spastin is more coherent with the distribution of both proteins that is now more clearly observed in distal axons by STED super-resolution (new figure 5A). So, despite a bit unexpected, these results suggest a novel interaction mechanism between these two proteins that deserves further validation.

5) What is exactly the model proposed? The title implies that axonal synthesis of Rtn-1 is important during injury, but the data in the paper rather suggest that upon injury the majority of Rtn-1 is not locally synthesized. If the levels of Rtn-1 do not change, why the effect on the microtubules should be specific? Why would a siRNA against Rtn-1 in axons not affect the levels of Rtn-1, but those of tubulin? The authors should be careful, and test other control siRNAs, and Rtn-1 siRNAs, since it is well known even in more simple cellular systems that the toxicity of individual siRNAs can vary greatly.

We consider the possibility that after injury there is no axonal Rtn-1 synthesis as a plausible and relevant appreciation. Unfortunately, we could not perform a puro-PLA experiment after injury, which would have provided a more definite answer. However, now we are more confident of regulating Rtn-1 synthesis before injury as supported by a Supplementary figure 3D that shows a significant decrease on puro-PLA signal (indicative of Rtn-1C synthesis) 24 hours after axonal KD. Thus, based on some similar phenotypes before and after injury, we consider our results are still compatible with Rtn-1 axonal synthesis being downregulated, but not fully absent (the mRNA is still detected, as described by Taylor 2009). As such, axonal Rtn-1 KD decreased β3-tubulin levels before and after injury according to figure 5B and the improved statistical analysis performed on figure 2E. Similarly, axonal Rtn-1KD significantly increases microtubule growth rate before and after injury according to the current statistical comparisons (Figure 5E). in complement, if β3-tubulin decrease was merely due to unspecific siRNA targeting, it is unlikely that SPTZ treatment should restore β3-tubulin only in the context of axonal Rtn-1 KD (Figure 5B). Although on a different track, the mechanistic relationship between Rtn-1C and Spastin suggested in Figure 7 could make more plausible that a similar phenomenon regarding the control of tubulin levels could be occurring locally in axons. We have now included these considerations in the discussion (lines 535-543).

To discard off-targets effects, we have now validated a third siRNA sequence (siRNA 3) specifically designed against Rtn-1 and showed that it selectively downregulates Rtn-1C but not β3-tubulin in cultured cortical neurons. Then, following the same experimental frame of figure 3, we performed axonal Rtn-1 KD after injury and observed that siRNA 3 also significantly increases the outgrowth of injured axons (Supplementary figure 2). This suggests that, at least this phenotype, is not product of an off-target effect. Thus, the pharmacological rescue of β3-tubulin levels by SPTZ (Figure 5B) and the Rtn-1C/Spastin co-distribution in heterologous cells, which correlates with preserved microtubules (improved Figure 7), provide converging evidence to suggest that Rtn-1C-Spastin interplay may underly the observed phenotypes in axons.

Minor comments:

In Figure 5A, it would be helpful to indicate the border of the axon. The figure is not really convincing.

Following yours and other reviewer comments, we have analyzed a new set of experiments regarding the STED images of non-injured and injured axons. To eliminate the risk of artifactual descriptions, we have avoided deconvolution and worked directly with raw STED images (Figure 5A). Under these conditions, distribution of Spastin and its intensity in distal axons are not modified by injury, nor those of Rtn-1C and Spastin (Supplementary figure 4). Despite these results, data still supports that both proteins are restricted to similar domains subcellular domains before and after injury.

Reviewer #3 (Significance (Required)):

The manuscript uses complex methods to address an interesting cell biological question of relevance to understand axonal growth regulation upon injury. A limitation of the study is the statistical analysis, which triggers some doubts about the reproducibility of the data. Further experiments and the addition of controls would be important to support the claims of the authors.

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Referee #3

Evidence, reproducibility and clarity

This manuscript investigates the relationship between the endoplasmic reticulum morphogen reticulon-1 (Rtn-1) and the microtubule severing protein spastin in axons after injury. The main message and conclusion of the paper is that local axonal synthesis of Rtn-1 plays a role in regulating the microtubule severing activity of spastin by interacting with spastin and inhibiting its activity. This mechanism would be important after injury by regulating axonal growth.

The conclusions of the paper are based on the following claims:

1. Rtn-1 is synthesized locally in axons.
2. Specific downregulation in Rtn-1 in axons using microfluidic chambers affects microtubules abundance (measured by beta-3 tubulin) and promotes axon growth after injury.
3. Inhibition of spastin MT-severing activity with a specific drug rescues the growth effect induced by axonal downregulation of Rtn-1.
4. Rtn-1c interacts with spastin-M87 to limit its MT-severing activity in a cellular system upon overexpression.

Major comments:

1. Evidence that Rtn-1 is synthesized in axons comes from two experiments. Initially, the authors show that Rtn-1 siRNA transfection in the axonal compartment of microfluidic chambers reduces Rtn-1 levels in axons, suggesting that there is some local synthesis. Although this method is very attractive, I am concerned about the statistical analysis. The graphs show bars rather than individual data points from the average of a large number of neurons (about 300). The plots also show the SEM instead of the SD, thus covering all the variability that is inherent in this type of experiment. The statistics are probably not performed on the 3 biological replicates, but consider the individual neurons as N. This is obviously not correct, since neurons in an experiment may all be affected by the same technical problem and are not independent replicates. For this reason, I am a bit skeptical about this quantification. Another problem is that the quantification of the fluorescence intensity of the sample does not take the nuclei into account. Are the nuclei removed for analysis? Are the images single planes? Addressing the quantification issues is crucial also for data in Figure 4, where the authors show a different effect of Rtn-1 axonal KD after injury. The second experiment is the Puro-PLA in Figure 6D. This experiment shows an average of 1.5 dots of signal per soma, which is a very low level of translation for this compartment where most of the synthesis should be taking place. In the axons, it is not clear how they calculate the axonal area. Again, the number of dots detected is very low and the physiological significance is questionable. A control with a known mRNA translated in axons would be important. Finally, as an important control, the authors should show the presence of Rtn-1 mRNA by FISH in their experimental system.
2. The effects on tubulin following Rtn-1 downregulation in axons is potentially very interesting, but the authors should be careful because it could also mean that the axons are suffering. Can they also stain for other cytoskeletal markers?
3. The results using SPTZ are very interesting and implicate spastin microtubule severing activity in the observed phenotype. In my opinion these experiments however do not prove that "axonal Rtn-1 is indeed promoting the severing of microtubules by spastin", but simply that the blocking spastin activity prevents the appearance of the microtubular phenotype (which appears still with a mysterious mechanism). What happens if they try to stabilize the cytoskeleton by another mean (with taxol for example?). The authors should rephrase this conclusion.
4. The last experiment (Figure 7) that aims to connect Rtn-1 and spastin function is very artificial, since it is based on overexpression. Why should spastin M87 interact with an ER morphogen? Endogenously it is conceivable that spastin M1 which localizes to the ER would interact with Rtn-1. Moreover, this experiment needs further controls and quantifications. First, it is quite obvious from panel 7C that there is crossover of signal in the two fluorescence channels (see GFP and spastin). Controls need to be shown, where only one of the two fluorescent proteins is expressed and the specificity of the laser is tested. This experiment is based on only 1 cell shown where co-localisation is detected based on a line that is placed in a specific area of the cell. The effects on the microtubular network needs quantification.
5. What is exactly the model proposed? The title implies that axonal synthesis of Rtn-1 is important during injury, but the data in the paper rather suggest that upon injury the majority of Rtn-1 is not locally synthesized. If the levels of Rtn-1 do not change, why the effect on the microtubules should be specific? Why would a siRNA against Rtn-1 in axons not affect the levels of Rtn-1, but those of tubulin? The authors should be careful, and test other control siRNAs, and Rtn-1 siRNAs, since it is well known even in more simple cellular systems that the toxicity of individual siRNAs can vary greatly.

Minor comments:

In Figure 5A, it would be helpful to indicate the border of the axon. The figure is not really convincing.

Significance

The manuscript uses complex methods to address an interesting cell biological question of relevance to understand axonal growth regulation upon injury. A limitation of the study is the statistical analysis, which triggers some doubts about the reproducibility of the data. Further experiments and the addition of controls would be important to support the claims of the authors.

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Referee #2

Evidence, reproducibility and clarity

Axonal mRNA localization and localized translation supports many neuronal functions and is an important determinant of the regenerative potential of axons after injury. How this works mechanistically remains unclear. The authors present a well performed and technically challenging study in which they identify RTN-1 as a regulator of axonal outgrowth after injury. They provide evidence using experiments in microfluidic chambers that RTN1 is locally synthesized in axons. Interestingly, they identify a (local) interplay between RTN1 and Spastin which affects microtubules and thereby regulates the outgrowth of cortical axons after injury. This study provides an interesting new link between a locally synthesized protein (RTN1) and a microtubule-regulating protein Spastin that is changed upon axon injury. This provides an advance in our understanding in axon regeneration after injury and provides the basis for new studies that can further investigate this interplay. Although interesting, I have several concerns that should be clarified and are needed to substantiate the findings and model presented in this study.

Major concerns:

1. In figure 1, the authors provide an analysis of overlapping axonal mRNAs. There are more axonal transcriptome studies and a recent study by von Kugelgen and Chekulaeva (2020; doi: 10.1002/wrna.1590) already performed such an analysis, which included more studies. It would be good to mention this. It can be perceived that studies were now chosen to get the outcome that Rtn-1 is present in all studies. For example, von Kugelgen finds mRNA coding for RTN3, another ER structural protein, as present in 16 out of 20 studies analyzed. That said, the authors present more reasons to look at Rtn-1, so the selection to continue with this protein remains valid but can be written up differently so not to present it as the 'sole' ER-shaping protein consistently present in axonal transcriptomes.
2. The description of methods is currently insufficient and incomplete and does not allow for reproducibility of this study. For example, different Rtn-1 antibodies seem to be used in this study. Is the same antibody used for staining and WB? There is no listing of any of the antibodies used in the study and which one is used for which technique/experiment. This should be clarified and should be easy to do so in the methods section (antibody name, origin/company, dilution used) to enhance reproducibility of this study. This is not limited to primary antibodies and any information on secondary antibodies, including what was used for STED is completely missing.
3. The timeline of KD experiments in Figure 2 and 3 are unclear. For the Western blot KD is performed at DIV7 and collected 48 hours later. However, this is not specified for the stainings done in Figure 2C-E. Is this also at DIV7 and then for 48 hours? In figure 3 the siRNA is added at DIV8 (together with axotomy) and outgrowth is measured 24 hours later. Is 24 hours sufficient to achieve knockdown? Is this also what was done for stainings? Later on in Figure 5B, 48 hours of KD is again used. It is unclear what the rationale of these differing timepoints is. Why was this chosen? Is the timeline also the reason for the difference in segment lengths chosen? In Figure 3, there is a significant effect on outgrowth in the KD in the 'mid-range' which is not present in Figure 5.
4. Could the authors provide a rescue condition for their siRNA (using a siRNA-resistant construct) to show that their siRNA is specific for RTN1. They nicely show the efficiency of the siRNA but not its specificity. This is crucial because if not specific, this will affect a large part of their study. They already have RTN1A and RTN1C constructs available. Such a rescue experiment should ideally also be performed for one or more of their phenotypic experiments, such as the one presented in Figure 3A or 5 to show that the phenotype is really RTN1 dependent. If done by re-expressing either RTN1A or RTN1C, this could provide insightful information on the relevant isoforms.
5. I find the data presented in Figure 4A/B confusing. Axonal RTN-1 KD does not reduce axonal RTN1 levels but somatic KD does. I understand that this implies most protein comes from the soma and the authors indeed present an explanation that increased somatic RTN1 occurs after axonal KD as a compensation mechanism. However, this can also be interpreted that there is no axonal synthesis of RTN1 after injury and axonal KD has indirect or even aspecific effects. Their model depends on this difference. Their data in Figure 6 could provide supporting evidence if it shows RTN1 puro-PLA after injury. Along these same lines, in Figure 6, they nicely include a compartment control for puro-PLA. It therefore seems doable to include a somatic puromycin control for their axonal puro-PLA, to exclude and diffusion/transport of the newly synthesized peptides. This is especially in light of two recent papers reporting on this possible phenomenon, although these studies were not performed in neurons.
6. In Figure 5A the authors find an increased co-localization (RTN1/Spastin) after axotomy. From their images, it seems that the amount of Spastin is hugely increased, which would by default increase the chance of (random) colocalization of RTN1 on Spastin. Could the authors comment on this?
7. In figure 5E and 5F, the condition of scr + SPTZ is omitted. What is the reason for this? The explanation of results in these figures is confusing. The authors report a 'clear trend' in increase in comet track length and lifetime upon addition of SPTZ to axonal RTN-1 KD. This is however not significant. The comparisons that are made afterwards are confusing (e.g. increase in comet lifetime of SPTZ in non-injured axons with RTN1 KD compared to Scr+DMSO and KD + DMSO in injured axons). Their conclusion is axonal RTN-1 synthesis in injured axons (see my concern in the points above on this) governs microtubules growth rate beyond Spastin activity yet blocking Spastin activity still completely blocks the effect of KD on outgrowth.

Other/minor concerns:

• The gene ontology analysis in Figure 1A contains the category 'Endoplasmic reticulum'. In this category are mainly ribosomal proteins. Although in a gene ontology analysis these proteins will be included in this category, it is misleading in this respect since they are just as likely to be coming from cytoplasmic ribosomes. Although it cannot be excluded that these are ER-bound ribosomes, not in the last place because a recent study (Koppers et al., 2024, doi: 10.1016/j.devcel.2024.05.005) found ribosomes attached to the ER in axons, I believe the category should be adapted or at the least clarified in the text.
• Is RTN-1C isoform still an ER-shaping protein or rather an ER protein with alternative functions? The final sentence in the abstract makes a statement that a locally synthesized ER-shaping protein lessens microtubule dynamics. Could the authors provide a clearer description and discussion of the evidence in literature for this? RTN1C has been suggested to perform alternative functions in which case the statement that the local synthesis of an ER-shaping protein is important for axonal outgrowth should be adapted.
• Is there a difference in RTN1 distribution or levels pre- and post-axotomy?
• Line 100/101 states 'the interactome of the axonal ER provides...'. To my knowledge there has been no study looking at the interactome of the axonal ER specifically. Surely axonal ER proteins are known but there is a difference.
• Typo line 160 'localla'
• In Figure S1 B, please add the DIVs to make it more clear what each graph corresponds to. The legend of S1B states different distances from the cell body but the graph shows distances from the tip.
• Figure 2C, why does B3 tubulin decrease in soma, aspecific effect of siRNA?
• What is the rationale on the opposite effect found in outgrowth in Figure 3?
• Missing word 'we' on line 194
• Typo line 629 'witmn h', please proofread the entire manuscript carefully.
• Could the authors comment on why, in Figure 7B/C, GFP only is colocalizing with Spastin-RFP? In general, GFP should be diffusive and not display punctate colocalization with Spastin.

Significance

Axonal mRNA localization and localized translation supports many neuronal functions and is an important determinant of the regenerative potential of axons after injury. How this works mechanistically remains unclear. The authors present a well performed and technically challenging study in which they identify RTN-1 as a regulator of axonal outgrowth after injury. They provide evidence using experiments in microfluidic chambers that RTN1 is locally synthesized in axons. Interestingly, they identify a (local) interplay between RTN1 and Spastin which affects microtubules and thereby regulates the outgrowth of cortical axons after injury. This study provides an interesting new link between a locally synthesized protein (RTN1) and a microtubule-regulating protein Spastin that is changed upon axon injury. This provides an advance in our understanding in axon regeneration after injury and provides the basis for new studies that can further investigate this interplay. Although interesting, I have several concerns that should be clarified and are needed to substantiate the findings and model presented in this study.

The audience for this study will be mainly basic research in the fields of both axonal protein synthesis and axon regeneration. My expertise is in the field of mRNA localization and local protein synthesis.

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Referee #1

Evidence, reproducibility and clarity

In this paper, the authors focus on the role of Reticulon-1C in concert with Spastin in response to axonal injury. In data mining, they find axonal mRNAs encoding for ER-associated proteins including Rtn-1. They establish a knockdown targeting both Rtn-1 isoforms Rtn-1A and Rtn-1C. They observe decreased beta-3-Tubulin levels in the soma while axonal protein levels are unchanged. In microfluidic devices, they characterise the effect of a compartment-specific Rtn-1 KD on axonal outgrowth in the axonal compartment. The authors quantify axonal outgrowth, seeing increased outgrowth in an axonal compartment-specific Rtn-1 KD, while the effect seems to be reversed when applying the KD construct in the somatic compartment. When focussing on the axonal growth cone, they find the Rtn-1 KD shows differences in several morphological features of the growth cone. They find an increase in Tubulin levels in an axonal compartment-specific, but a decrease in a somatic compartment-specific Rtn-1 KD. Colocalisation of Rtn-1C and Spastin is shown to be monolaterally increased following axotomy. Combining axotomy with the Rtn-1 KD shows increases in dynamic microtubule growth rates and track lengths. In another model system, neuron balls, they show Rtn1-C, but not Rtn1-A to be present in the axon. In a puro-PL assay they also show it can be synthesised in the axonal compartment. To investigate the mechanism enabling the cooperation between Spastin and Rtn-1C, they move to a cell line model in which they see a correlating distribution between Spastin and Rtn-1C but not Rtn-1A. Finally, they use in silico modelling to speculate on binding between Spastin domains and Rtn-1 isoforms.

Major comment:

The rationale behind the work is convincing, however some interpretations are presented as more robust than some data allow. Most notably, while the interaction between Rtn-1 and Spastin has been shown prior to this study, it is only presented here through in silico analysis. In figure 5, an increase in the growth rate of dynamic microtubules is observed in either a Rtn-1C KD or by using a Spastin-inhibitor. Due to a described increase in colocalisation between Rtn-1C and Spastin (5A), the increase in growth rate is displayed as caused by Rtn-1 promoting Spastin's severing ability. This result might however be correlative. Further in the injured samples, Spastin-levels seemingly increase (in the representative images) and it is thus not surprising that the level of Rtn-1C colocalising with Spastin increases as well. This might not be indicative of a cooperation and further experimental evidence are required.

Other comments:

• Generally, graphs would benefit from individual values plotted as well as the summary. Font sizes and types (but rarely) are sometimes inconsistent. Proteins should be consistently written (capitalised or not).
• Table 1 and figure 1 present data collected from a vast amount of resources. It should be highlighted that datasets from which data was obtained includes many different models, different DIVs and neuronal cell types. Figure 1B may benefit from a different colour scheme. "Ex-vivo" should be "Ex vivo". For "ER mRNAs are a relevant category" it is not described what "relevant" would mean in this context. The title might remove this small part or describe it in the text. It should be described how it is decided that mRNAs are "common".
• Figure 2: add description to y-axis to describe what fold change is displayed, applies to multiple figures. Will improve readability of the figures. In 2C, the ROI showing neuronal somata should be increased to show part of the axon and not cut off the soma.
• Figure 3: Three out of four axonal compartments seem to be comprised of dying or damaged axons. Especially the axonal KD scrambled image. It should be ensured that neuronal cultures are healthy. Typo in "intersections". The schematic of 3B is a great addition to explain the graphs above. Perhaps it could be a bit refined as it is currently hard to see whether this is a neuron or a growth cone without context. Maybe show where the axon connects to the depicted growth cones and change the third icon which looks like it was crossed out. Small formatting issues: remove additional space bar before "Figure 3." And add after "Bar"
• Figure 4: If not misunderstanding what is depicted, in 4A and B, different lookup tables are used to depict the same signal. Only one of each images is necessary. Do the axons have more tiny branches in the Rtn-1 KD condition in 4A? Unclear why Rtn-1 levels are increased in the Rtn-1 KD (4C), please clarify.
• Figure 5: It may be easier to understand what "axotomy" samples are if just referred to as "injured" as later in the same figure. The procedure could also very briefly be explained in the results. 5C should depict AUC in µm2 not µm. 5D Spastin is barely visible, brightness and contrast should be adjusted to enhance visibility.
• Figure 6: It should be made clear why it is necessary to switch to another model system just for 6A, please indicate this in the text. PCR bands seem very pixelated, check the quality. It is unclear why soma genes/proteins were only tested with either PCR or WB others with both. Rtn-1C and Rtn1-A should be presented in the same order in the PCR and WB panel. Correct "Rtn1-1A" typo. In 6D, 1.5 dots per soma seems like a low number. When normalised to the area the soma vs the axon occupies, the compartmentalisation does not work? May be it make sense to refine analysis or apply puromycin in the somatic compartment and analyse the axonal compartment as comparison?
• Figure 7: 7A shows two images depicting the same information that may not be needed. Can probably be removed. In 7B there is no negative (or any) correlation between Spastin levels and Tubulin, however later it is mentioned that Rtn-1C transports Spastin thus causing a decrease in Tubulin at certain locations? It is nclear if Spastin levels vary intensely between different samples. Mean intensity of the somatic area may be beneficial to rule this out. 7B Tubulin on the right top panel seems to have a decrease in Tubulin levels which is not visible due to the Y axis of Tubulin being set to a different range than the middle and lower panel. The average of line scans from multiple cells may be helpful to determine whether there is indeed no colocalization between Rtn-1A and Spastin. The provided representative images seem to show similar degrees of colocalization between Spastin and Rtn-1A/C.

Results:

• It would be helpful to reiterate the hypothesis at the start to ease the reading flow.
• There seems to be minor redundancy in lines 132-138.
• There are several spellings, proof-reading is recommended. For example, in line 136 should be "promotes". 160 "localla", 192 should be "the actin cytoskeleton".,194 should be "we first examined", 195 should be "Different", 223 "using", 259 "axons". ...
• 154-155: Unclear, why the lower MW Rtn-1C was seen as more important.
• 167 results of 2E not stated before interpreting them.
• 181 would suggest "outline" instead of "perimeter".
• 183-184 "longest shortest path" is a confusing term.
• figure 4B should be referenced earlier in the sentence.
• 243-244 may be correlation. Rtn-1 and Spastin do not necessarily interact so that this result is achieved.
• 246: In figure 1 the KD seemed to have an effect on both Rtn-1 isoforms, why not here anymore? 259 "axons". 284 "counteract" instead of "suppress"?
• 485: rephrase as the interaction between Rtn-1C with Spastin has not been shown directly in these experiments.

Methods: 535 "in PBS". 543 citation error. 689-699 is it necessary to add a gaussian blur?

References: Mannan, A U et al. appears twice in the citation list (36 and 44).

Significance

Overall, this manuscript describes novel fundings which will be interesting to the neuronal cell biology community and scientists working on the field of neuronal injury and regeneration. It is well structured, and the data are mostly well presented but sometimes conclusions are over-interpreted. However, several points need to be addressed in a more convincing way.

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

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility and clarity):

This manuscript described the translational responses to single and combined BCAA shortages in mouse cell lines. Using Ribo-seq and RNA-seq analysis, the authors found selective ribosome pausing at codons that encode the depleted amino acids, where the pausing at valine codons was prominent at both a single and triple starvations whereas isoleucine codons showed pausing only under a single depletion. They analyzed the mechanisms of the unexpected selective pausing and proposed that the positional codon usage bias could shape the ribosome stalling and tRNA charging patterns across different amino acids. They also examined the stress responses and the changes in the protein expression levels under BCAA starvation.

The manuscript was well-written, and the findings are interesting, especially their model that positional codon usage bias could be a regulator of ribosome pausing and tRNA charging levels. Although different translational responses to distinct amino acid starvation have been widely documented, the positional codon usage bias is an interesting aspect. The manuscript's central message could have been made clearer. The authors may consider emphasizing this point more explicitly in the abstract. The rich multi-omics dataset in this work provides valuable resources for the translation field.

We thank the reviewer for the thoughtful and positive evaluation of our work.

Major comments

1. The abstract may need to be revised since it is hard to immediately catch the authors' main point. If the authors regard this work as a resource paper, the current version is fine. But it could be better to point out the positional codon usages the authors found, which is a strong point of the current manuscript.

Response: We thank the reviewer for highlighting the importance of positional codon usage, which indeed represents a key finding of our study. We revised the abstract, and we now emphasize this aspect more clearly. However, in response to review #2, we have framed the observed positional effects and the idea of an elongation bottleneck as one possible contributing mechanism among others and relate it specifically to the attenuation of isoleucine-specific stalling under triple starvation.

1. Page 18 "Beyond these tRNA dynamics, our data also highlight the importance of the codon positional context within mRNAs, indicating that where a codon is located within the CDS can influence both the extent of ribosomal stalling and overall translation efficiency during nutrient stress." This idea is interesting. To what extent the authors think this could be generalized? The authors may discuss whether they think their proposed model is specific to the different ribosome stalling patterns between valine and isoleucine codons or generalized to other codon combinations. For example, the positional codon usage bias will be different among different organisms, and are there any previous reports on ribosome behaviors that align with their model?

Response: We thank the reviewer for raising these important points. While our study primarily focuses on the differential stalling patterns of valine and isoleucine codons, we believe the underlying principle, that the position of codons within the CDS can modulate the extent of ribosome stalling, may under very specific circumstances extend beyond this amino acid pair. We expect this positional effect to be potentially relevant for combinations in which one amino acid has considerable enrichment near the 5′ end of coding sequences, coupled with starvation-sensitive tRNA isoacceptors, while the other does not. In our case, valine meets these criteria (see Fig. S11A and Fig. 6). In contrast, isoleucine and leucine codons, although also relatively frequent, show more variable positional distributions and are both decoded by isoacceptors that appear more resistant to starvation, as illustrated in Fig. 6 and reported for mammals and bacteria in Saikia et al. 2016; Darnell, Subramaniam, and O’Shea 2018; Elf et al. 2003; Dittmar et al. 2005. To explore the generalizability of this model, we have now included a transcriptome-wide analysis of codon position biases in mouse for all codons in the revised manuscript (Supplementary Figures 10 and 11). This analysis may serve as a basis to identify additional candidate codons for future studies. Furthermore, we now mention in the Discussion that amino acids with similar properties to valine regarding their positional distribution and tRNA isoacceptors, such as phenylalanine, and glutamine, whose tRNA isoacceptors are predicted to be fully deacylated under their respective starvation in bacteria (Elf et al. 2003), could be promising candidates for testing this model, in combination with amino acids, whose tRNAs are expected to remain partially charged under starvation or to be depleted at the start of the CDS such as i.e. His (Supplementary Fig.11C).

Even if the authors think this model can be applied to BCAA starvation, would it be possible to explain the different isoleucine codon responses between single and double starvation? The authors may discuss why the ribosome stalling at isoleucine AUU and AUC codons was slightly attenuated under double starvation. And how about the different leucine codon responses among single, double, and triple starvations, although the pausing is not as strong as isoleucine and valine codons?

Response: Regarding the attenuated isoleucine stalling under double starvation, we believe this is primarily due to stronger inhibition of the mTORC1 pathway when leucine is co-depleted (i.e., in the double starvation condition; Fig. 2D–F). This results in a more substantial suppression of global translation, reducing overall tRNA demand and thereby mitigating stalling (Darnell, 2018). A similar effect may explain the only mild leucine codon stalling observed under single leucine starvation, which also triggers strong mTORC1 inhibition and reduced initiation. In contrast, triple starvation does not suppress mTORC1 to the same extent, and thus reduced initiation alone cannot explain the absence of leucine codon stalling. Instead, we propose that additional features, such as the relative sensitivity of tRNA isoacceptors to starvation and their aminoacylation dynamics, must be considered. Valine tRNAs, for example, are known to be highly sensitive and become strongly deacylated under starvation in bacteria (Elf et al. 2003), a pattern that we also find in our own data (Fig. 6). Leucine tRNAs, by contrast, appear more resistant, possibly due to better amino acid recycling or isoacceptor-specific differences in charging kinetics, though further validation would be needed. However, combined with the strong stalling at 5′-enriched valine codons, this could reduce downstream ribosome traffic and limit exposure of leucine codons, thus preventing stalling. However, our new analysis of the positional relationship between valine and leucine codons within individual transcripts (now shown in Supplementary Figure 11B) did not reveal as strong a pattern as we observed for valine and isoleucine codons. We now discuss these points and their implications in the revised Discussion.

Experimental validation using artificial reporters carrying biased sequences may also be considered.

Response: We appreciate the reviewer’s suggestion. In fact, we explored this experimentally using a dual-fluorescent reporter system (GFP–RFP) (Juszkiewicz and Hegde 2017) containing consecutive Val or Ile codons. However, the constructs yielded variable and non-reproducible results under starvation conditions. In addition, testing the role of codon position would require placing the same codons at multiple defined positions within a single transcript and performing ribosome profiling directly on the reporter. This type of targeted experimental validation is technically challenging and falls beyond the scope of the current study. We now mention this explicitly in the revised Discussion as an interesting direction for future work.

1. Page 13 "Moreover, we noticed that DT changes extend beyond the ribosomal A-site, including the P-site, E-site, and even further positions (Supplementary Fig. 2A), consistent with other studies on single amino acid starvation 39 (Supplementary Fig. 2B-C)." Could the widespread DT changes be due to Ribo-DT pipeline they used or difficulties in offset determination? Indeed the authors showed that this feature was found in other datasets, but it seems that the datasets were processed and analyzed in the same way as their data. The original Ribo-DT paper (Gobet and Naef, 2022, Methods) also showed some widespread DT changes even from RNA-seq. Another analysis method like the codon subsequence abundant shift as a part of diricore analysis (Loayza-Puch et al., 2016, Nature) did not show that broad changed regions. The authors are encouraged to re-analyze the data sets using different methods.

Response: We agree with the reviewer that the fact that DT changes beyond the ribosomal A-site is puzzling, but this has already been seen in other papers using other approaches (Darnell, Subramaniam, and O’Shea 2018). To validate that this shift is not due to our A-site assignment, enrichment analysis, or DT method, we applied the Diricore pipeline to our Ribo-Seq data. The output of the pipeline provides either 5’-end ribosome density or “subsequence” analysis using an A-site offset for each read size based on the metagene profile at the start codon. Both analyses show the same enriched codons across the different conditions as in our analyses, and the broad shift is similar, with the maximum signal at E, -1 position (Fig. R1).

1. Page 13 "Intriguingly, only two of the three isoleucine codons (AUU and AUC) showed increased DTs upon Ile starvation (p < 0.01), while just one leucine codon (CUU) exhibited a modest but significant DT increase (p < 0.01) under Leu starvation (Figure 1A-B, Supplementary Figure 2A)." How can the authors explain the different strengths of ribosome pausing at Ile codons under Ile and double starvation? The AUA codon did not show any pausing under either of the starvation conditions. Throughout the manuscript, the authors mainly describe the difference between amino acids but it is desirable to discuss the codon-level difference as well.

Response: Thank you for raising this point. The observed differences in stalling between the isoleucine codons can likely be explained by differences in tRNA isoacceptor charging and positional bias within transcripts. The AUA codon is decoded by a distinct tRNAIle isoacceptor (tRNAIleUAU), which, according to our tRNA charging data (Fig. 6), remains largely charged during Ile starvation. This observation aligns with previous reports suggesting that this isoacceptor is more resistant to starvation-induced deacylation in mammalian cells and bacteria (Saikia et al. 2016; Elf et al. 2003). In contrast, the AUU and AUC codons are primarily decoded by the tRNAIleAAU isoacceptor, which we find to be strongly deacylated under Ile starvation, likely contributing to the observed codon-specific ribosome pausing. Additionally, we found that the AUA codons are relatively rare in general and particularly underrepresented near the 5′ ends of coding sequences. Our new spatial analysis (now included in Supplementary Figure 11B) confirms that AUA codons tend to occur downstream of AUU and AUC codons within transcripts. This potentially further reduces stalling on these codons and further diminishes their apparent DT increase under starvation. In order to better explain these important points, we have now expanded the codon-level discussion of these differences in the revised manuscript.

1. Page 13 "We examined the effects of single amino acid starvations (-Leu, -Ile and -Val), as well as combinations, including a double starvation of leucine and isoleucine (hereafter referred to as "double") and a starvation of leucine, isoleucine, and valine ("triple"), allowing us to identify potential non-additive effects." The different double starvations, isoleucine and valine, and leucine and valine, will further support their hypothesis on the effects of the positional codon usage bias on ribosome pausing and tRNA charging patterns. Although this could be beyond the scope of the current manuscript, the authors are encouraged to provide a rationale for the chosen combination.

Response: Our experimental design evolved stepwise: we initially focused on leucine and isoleucine depletion as we found that despite their structure similarity these had respectively short and long dwell times in our previous work in the mouse liver (Gobet et al. 2020). Valine was included at a later stage to cover all the BCAAs. At the time, we did not anticipate valine to yield particularly striking effects in cells, and therefore we did not include systematic pairwise depletions involving valine. However, the strong and unexpected stalling observed at valine codons, especially under triple starvation, became a central aspect of the study. Thus, we agree that additional combinations, such as Leu/Val or Val/Ile, could be informative and now mention this in the Discussion as a potential direction for future studies.

Minor comments

Page 16 "these results imply that BCAA deprivation lowers protein output through multiple pathways: a combination of reduced initiation, direct elongation blocks (stalling), and possibly an increased proteolysis" This conclusion is totally right but may be too general. Could the authors summarize BCAA-specific features of the events including reduced initiation, stalling, and proteolysis that all contribute to protein outputs? This is not well discussed in the latter sections including Discussion.

Response: We thank the reviewer for this helpful suggestion. We agree that the original statement was too general and have revised the relevant section to more clearly delineate the distinct responses observed under each BCAA starvation condition. Specifically, we now summarize that valine starvation is characterized by strong, positionally biased ribosome stalling; leucine starvation primarily impacts translation initiation, likely via mTORC1 repression; and isoleucine starvation shows a mixed phenotype, with features of both impaired initiation and codon-specific elongation delays. We also clarify that while protein stability or degradation may contribute to the observed changes in protein output, our current data do not allow for quantitative assessment of proteolytic effects (e.g., changes in protein half-life). Therefore, we refrain from making direct quantitative conclusions about the differential modulations of proteolysis and instead focus our discussion on the translational mechanisms supported by our data.

Reviewer #1 (Significance):

The manuscript was well-written, and the findings are interesting, especially their model that positional codon usage bias could be a regulator of ribosome pausing and tRNA charging levels. Although different translational responses to distinct amino acid starvation have been widely documented, the positional codon usage bias is an interesting aspect. The manuscript's central message could have been made clearer. The authors may consider emphasizing this point more explicitly in the abstract. The rich multi-omics dataset in this work provides valuable resources for the translation field.

We thank the reviewer for the encouraging comments and share the view that positional codon-usage bias is an important result; accordingly, we now underscore this point explicitly in the revised Abstract. We also emphasise that our other observations are, to our knowledge, novel: only a handful of multi-omics studies have combined ribosome-pausing profiles with direct tRNA-aminoacylation measurements, and none has systematically examined multiple amino-acid-deprivation conditions as presented here.

Reviewer #2 (Evidence, reproducibility and clarity):

This study examines the consequences of starvation for the BRCAAs, either singly, for Leu & Ile, or for all three simultaneously in HeLa cells on overall translation rates, decoding rates at each codon, and on ribosome density, protein expression, and distribution of ribosome stalling events across the CDS for each expressed gene. The single amino acid starvation regimes specifically reduce the cognate intracellular amino acid pool and lead to deacylation of at least a subset of the cognate tRNAs in a manner dependent on continuing protein synthesis. They also induce the ISR equally and decrease bulk protein synthesis equally in a manner that appears to occur largely at the initiation level for -Leu and -Val, judging by the decreased polysome:monsome ratio, but at both the initiation and elongation levels for -Ile-a distinction that remains unexplained. Only -Leu appears to down-regulate mTORC1 and TOP mRNA translation.There is a significant down-regulation of protein levels for 50-200 genes, which tend to be unstable in nutrient-replete cells, only a fraction of which are associated with reduced ribosome occupancies (RPFs measured by Ribo-Seq) on the corresponding mRNAs in the manner expected for reduced initiation, suggesting that delayed elongation is responsible for reduced protein levels for the remaining fraction of genes. All three single starvations lead to increased decoding times for a subset of the cognate "hungry" codons: CUU for -Leu, AUU and AUC for -Ile, and all of the Val codons, in a manner that is said to correspond largely to the particular tRNA isoacceptors that become deacylated, although this correspondence was not explained explicitly and might not be as simple as claimed. All three single starvations also evoke skewing of RPFs towards the 5' ends of many CDSs in a manner correlated with an enrichment within the early regions of the CDSs for one or more of the cognate codons that showed increased decoding times for -Ile (AUC codon) and -Val (GUU, GUC, and GUG), but not for -Leu-of which the latter was not accounted for. These last findings suggest that, at least for -Val and -Ile, delays in decoding N-terminal cognate codons cause elongating ribosomes to build-up early in the CDS. They go on to employ a peak calling algorithm to identify stalling sites in an unbiased way within the CDS, which are greatest in number for -Val, and find that Val codons are enriched in the A-sites (slightly) and adjacent 5' nucleotides (to a greater extent) for -Val starvation; and similarly for Ile codons in -Ile conditions, but not for -Leu starvation-again for unknown reasons. It's unclear why their called stalling sites have various other non-hungry codons present in the A sites with the cognate hungry codons being enriched further upstream, given that stalling should occur with the "hungry" cognate codon in the A site. The proteins showing down-regulation are enriched for stalling sites only in the case of the -Val starvation in the manner expected if stalling is contributing to reduced translation of the corresponding mRNA. It's unclear why this enrichment apparently does not extend to -Ile starvation which shows comparable skewing of RPFs towards the 5'ends, and this fact diminishes the claim that pausing generally contributes to reduced translation for genes with abundant hungry codons. All of the same analyses were carried out for the Double -Ile/-Leu and Triple starvations and yield unexpected results, particularly for the triple starvation wherein decoding times are increased only at Val codons, skewing of RPFs towards the 5' ends of CDSs is correlated only with an enrichment for Val codons within the early regions of the CDSs, and stall sites are enriched only for Val codons at nearly upstream sites, all consistent with the finding that only Val tRNAs become deacylated in the Triple regime. To explain why only Val tRNA charging is reduced despite the observed effective starvation for all three amino acids, they note first that stalling at Val codons is skewed towards the 5'ends of CDS for both -Val and triple starvations more so than observed for Ile or -Leu starvation, which they attribute to a greater frequency of Val codons vs Ile codons in the 5' ends of CDSs. As such, charged Val tRNAs are said to be consumed in translating the 5'ends of CDSs and the resulting stalling prevents ribosomes from reaching downstream Ile and Leu codons at the same frequencies and thus prevents deacylation of the cognate Ile and Leu tRNAs. It's unclear whether this explanation is adequate to explain the complete lack of Ile or Leu tRNA deacylation observed even when amino acid recycling by the proteasome is inhibited-a treatment shown to exacerbate deacylation of cognate tRNAs in the single amino acid starvations and of Val tRNA in the triple starvation. As such, the statement in the Abstract "Notably, we could show that isoleucine starvation-specific stalling largely diminished under triple starvation, likely due to early elongation bottlenecks at valine codons" might be too strong and the word "possibly" would be preferred over "likely". It's also unclear why the proteins that are down-regulated in the triple starvation are not significantly enriched for stalling sites (Fig. 5B) given that the degree of skewing is comparable or greater than for -Val. This last point seems to undermine their conclusion in the Abstract that "that many proteins downregulated under BCAA deprivation harbor stalling sites, suggesting that compromised elongation contributes to decreased protein output." In the case of the double -Ile/-Leu starvation, a related phenomenon occurs wherein decoding rates are decreased for only the AUU Ile codon and only the AAU Ile tRNA becomes deacylated; although in this case increased RPFs in the 5' ends are not correlated with enrichment for Ile or Leu codons and, although not presented, apparently stall sites are not associated with the Ile codon in the double starvation. In addition, stalling sites are not enriched in the proteins down-regulated by the double starvation. Moreover, because Ile codons are not enriched in the 5'ends of CDS, it doesn't seem possible to explain the selective deacylation of the single Ile tRNA observed in the double starvation by the same "bottleneck" mechanism proposed to explain selective deacylation of only Val tRNAs during the triple starvation. This is another reason for questioning their "bottleneck" mechanism.

We thank the reviewer for their deep assessment, exhaustive reading, and constructive feedback, which have greatly contributed to improving the clarity and contextualization of our manuscript. We would first like to clarify that all experiments in this study were conducted in NIH3T3 mouse fibroblasts, not HeLa cells; we assume this was a misunderstanding and have verified that the correct cell line is consistently indicated throughout the manuscript. We also clarify that our data show that -Leu, double starvation, and to a lesser extent -Ile, downregulate mTORC1 signaling and TOP mRNA translation, whereas valine -Val and triple starvation had minimal effects on these pathways. We agree that some of our conclusions and observed phenomena were not explained in sufficient detail in the original version. To address this, we have significantly reworked the discussion, added complementary figures and clarified key points throughout the text, to better convey the underlying rationale and biological interpretation of our findings. We address each of the reviewer’s points in detail in the point-by-point responses below.

Specific comments (some of which were mentioned above):

-The authors have treated cells with CHX in the Ribo-Seq experiments, which has been shown to cause artifacts in determining the locations of ribosome stalling in vivo owing to continued elongation in the presence of CHX (https://doi.org/10.1371/journal.pgen.1005732 ). The authors should comment on whether this artifact could be influencing some of their findings, particular the results in Fig. 5C where the hungry codons are often present upstream of the A sites of called stalling sites in the manner expected if elongation continued slowly following stalling in the presence of CHX.

Response: We thank the reviewer for raising this important concern. We would like to clarify that our ribosome profiling protocol did not include CHX pretreatment of live cells. CHX was added only during the brief PBS washes immediately before lysis and in the lysis buffer itself. This approach aligns with best practices aimed at minimizing post-lysis ribosome run-off, and is intended to prevent the downstream ribosome displacement artifacts described by Hussmann et al. 2015, which result from pre-incubation of live cells with CHX for several minutes before harvesting. Furthermore, recent studies have demonstrated that CHX-induced biases are species-specific. For instance, Sharma et al. 2021 found that human (and mice) ribosomes are not susceptible to conformational restrictions by CHX, nor does CHX distort gene-level measurements of ribosome occupancy. This suggests that the use of CHX in the lysis buffer, as performed in our protocol, is unlikely to introduce significant artifacts in our ribosome profiling data. To further support this, we reanalyzed data from Darnell, Subramaniam, and O’Shea 2018, where the ribosome profiling samples were prepared without any CHX pretreatment or CHX in the wash buffer, and still observed similar upstream enrichments in their stalling profiles (see Supplementary Figure 2B-C in our manuscript). Additionally, in our previous work (Gobet et al. 2020), we compared ribosome dwell times with and without CHX in the lysis buffer and found no significant differences, reinforcing the notion that CHX use during lysis does not substantially affect the measurement of ribosome stalling. Given these considerations, we believe that CHX-related artifacts, such as downstream ribosome movement, are unlikely to explain the enrichment of hungry codons upstream of identified stalling sites in our data. We have now adjusted the Methods section to clarify this point.

-p. 12: "These starvation-specific DT and ribosome density modulations were also evident at the individual transcript level, as exemplified by Col1a1, Col1a2, Aars, and Mki67 which showed persistent Val-codon-specific ribosome density increases but lost Ile-codon-specific increases under triple starvation (Supplementary Figure 3A-D). " This conclusion is hard to visualize for any but Val codons. It would help to annotate the relevant peaks of interest for -Ile starvation with arrows.

Response: We agree and thank the reviewer for this observation. We have now annotated exemplary peaks in Supplementary Figure 3A–D to highlight ribosome pileups over Ile codons. However, we agree that it is still hard to visualize in the given Figure. Therefore, we added scatter plots for each of the transcripts that show the RPM of each position in the Ctrl vs starvation to allow for a better illustration of the milder effects upon Ile starvation (Supplementary Figure 4).

-To better make the point that codon-specific stalling under BCAA starvation appears to be not driven by codon usage, rather than the analysis in Fig. 1H, wouldn't it be better to examine the correlation between increases in DT under the single amino acid starvation conditions and the codon frequencies across all codons?

Response: We appreciate the suggestion. We have now added an additional analysis correlating the change in DT with codon usage frequency for each starvation condition. This is included in Supplementary Figure 5A-D and supports our interpretation that codon frequency alone does not explain the observed stalling behavior.

-p. 13, entire paragraph beginning with "Our RNA-seq and Ribo-seq revealed a general activation of stress response pathways across all starvations..." It is difficult to glean any important conclusions from this lengthy analysis, and the results do not appear to be connected to the overall topic of the study. If there are important conclusions here that relate to the major findings then these connections should be made or noted later in the Discussion. If not, perhaps the analysis should be largely relegated to the Supplemental material.

Response: We thank the reviewer for this comment. The paragraph in question is intended to provide a global overview of transcriptional and translational responses across the starvation conditions. It serves both as a quality control (e.g., PCA clustering and global shifts in RPF/RNA-seq profiles), and to confirm that expected starvation-induced responses are among the strongest detectable signals separating the starved samples from the control. Indeed, these observations establish that the perturbations are effective and that hallmark nutrient stress responses are globally engaged across conditions. Importantly, very few studies to date have examined transcriptional and translational responses under single or combined branched-chain amino acid (BCAA) starvation conditions. It therefore remains unclear to what extent BCAA depletion broadly remodels gene expression and translation. Our analysis contributes to addressing this gap, revealing that while certain stress pathways are commonly induced, others show condition-specific patterns such as we observed for -Ile starvation. To maintain focus, we have kept the detailed pathway analyses and transcript-level enrichments in the Supplement and rewritten the corresponding text in a more compact manner, reducing it by more than one third.

-p. 15: "Together, these findings highlight that BCAA starvation triggers a combination of effects on initiation and elongation, with varying dynamics by amino acid starvation." I take issue with this statement as it appears that translation is reduced primarily at the initiation step for all conditions except -Ile. As noted above, these data are never menitioned in the DISCUSSION as to why only -Ile would show a marked elongation component to the inhibition whereas -Val gives the greatest amount of ribosome stalling.

Response: We acknowledge the reviewer’s point. While the polysome profiles (Figure 3F-H) directly indicate that most conditions repress initiation, codon- and condition-specific elongation defects can still contribute to reduced protein output, even if they are not always detectable as global polysome shifts. Polysome profiles reflect the combined outcome of reduced initiation (which decreases polysome numbers) and ribosome stalling (which can, but does not always have to, increase ribosome density on individual transcripts, potentially counteracting the effects of reduced initiation). For valine starvation strong stalling occurs very early in the CDS (Figure 5F). This bottleneck restricts overall ribosome movement to downstream regions. Thus, while elongation is profoundly impaired, the total number of ribosomes per transcript (which polysome signals largely reflect) may appear low due to reduced overall ribosome traffic. In contrast, isoleucine codon stalling tends to occur also further downstream on the transcript (Figure 5F), allowing ribosomes to accumulate in larger numbers on the mRNA, leading to a clearer "elongation signature" in polysome profiles (Figure 3F, H). Additionally, we observed slightly higher inter-replicate variance for isoleucine starvation (Supplementary Figure 6B), which may have reduced the number of statistically significant stalling sites extracted compared to valine. We have revised the main text and discussion to clarify these points.

-I cannot decipher Fig. 4D and more detail is required to indicate the identity of each column of data.

Response: We thank the reviewer for pointing this out. Figure 4D (now Figure 4E) presents an UpSet plot, which is a scalable alternative to Venn diagrams commonly used to visualize intersections across multiple sets. Briefly, each bar in the upper plot represents the number of transcripts with increased 5′ ribosome coverage (Δpi < -0.15; p < 0.05) shared across the conditions indicated in the dot matrix below. Each column in the dot matrix highlights the specific combination of conditions contributing to a given intersection (e.g., dots under “Val” and “Triple” show the overlap between these two). To improve clarity, we have expanded the figure legend accordingly and now refer to the UpSetR methodology in the main text.

-In Fig. 4E, one cannot determine what the P values actually are, which should be provided in the legend to confirm statistical significance.

Response: Thank you for pointing that out. The legend in Figure 4E (now Figure 4F) for the p-values was accidentally removed during figure editing. We have added the legend back, so that the statistical significance is clear.

-It's difficult to understand how the -Leu condition and the Double starvation can produce polarized RPFs (Fig. 4A) without evidence of stalling at the cognate hungry codons (Fig. 4E), despite showing later in Fig. 5A that the numbers of stall sites are comparable in those cases to that found for -Ile.

Response: We appreciate this comment, which points to an important property of RPF profiles under nutrient stress. As shown in Figure 4A, all starvation conditions induce a degree of 5′ ribosome footprint polarization, a pattern that can be observed under various stress conditions and perturbations (Allen et al. 2021; Hwang and Buskirk 2017; Li et al. 2023). This general 5′ bias likely reflects a combination of slowed elongation and altered ribosome dynamics and is not necessarily linked to codon-specific stalling. However, Val and Triple starvation show a much stronger and more asymmetric polarization, characterized by pronounced 5′ accumulation and 3′ depletion of ribosome density. To better illustrate this, we have updated the visualization of polarity scores and added a new bar chart summarizing the number of transcripts showing strong 5′ polarization under each condition. This quantification highlights that the effect is markedly more prevalent under Val and Triple conditions than under Leu or Double starvation. In addition, Figure 4F demonstrates that this polarity is codon-specific under Val and Triple starvation. We clarify that this analysis tests for enrichment of specific codons near the start codon among the polarized transcripts and does not directly assess stalling. The observed enrichment of Val codons in the 5′ regions of polarized transcripts supports the interpretation that early elongation delays contribute to the RPF shift. In contrast, no such enrichment is observed for Leu starvation, reinforcing that Leu-induced polarity is not driven by stalling at Leu codons. While Figure 5 shows a similar number of peak-called stalling sites in -Leu, -Ile, and Double starvation, we note that Ribo-seq signal variability under Ile starvation was higher, which may have limited statistical power for detecting stalling sites, even though clear dwell time increases were observed at specific codons. Additionally, we have improved the metagene plots depicting total ribosome footprint density in Figure 4A. The previous version incorrectly showed sharp drops at CDS boundaries due to binning artifacts. The updated version more accurately reflects the density distribution and further highlights the stronger polarization in Val and Triple conditions. Together, these clarifications and improvements within the main text now more clearly distinguish between general polarity effects and codon-specific stalling.

-Fig. 5B: the P values should be given for all five columns, and it should be explained here or in the Discussion why the authors conclude that stalling is an important determinant for reduced translation when a significant correlation seems to exist only for the -Val condition and not even for the Triple condition.

Response: We thank the reviewer for this important observation. In response, we have revised both the text and the figures to provide a clearer and biologically more meaningful representation of the relationship between ribosome stalling and reduced protein output. Specifically, we have replaced the previous Figure 5B with a new analysis that stratifies transcripts based on the number of identified stalling sites. This updated analysis, now shown in Figure 5B, reveals that under Val and Triple starvation conditions, proteins that are downregulated tend to originate from transcripts with multiple stalling sites. Importantly, the corresponding p-values for all five conditions are now explicitly shown in the figure (as red lines). As the reviewer correctly notes, only the Val condition shows a statistically significant enrichment when considering overall overlap. Triple starvation shows a similarly high proportion of overlap (72.3%) but does not reach statistical significance, likely due to the more complex background composition under combined starvation, which increases the expected overlap and reduces statistical power. By stratifying transcripts by the number of stalling sites, we uncover that transcripts with ≥2 stalling sites are enriched among downregulated proteins specifically under Val and Triple conditions, providing a more robust indication of the link between stalling and translation repression under Valine deprivations. We believe this refined approach, prompted by the reviewer’s comment, offers a clearer and biologically more relevant perspective on the role of ribosome stalling. The original analysis previously shown in Figure 5B is now provided as Supplemental Figure 10C for transparency and comparison. We have clarified this in the revised text and now interpret the relationship more cautiously.

-p. 17: "Of note, in cases where valine or isoleucine codons were present just upstream (rather than at) the stalling position, we noted a strong bias for GAG (E), GAA (E), GAU (D), GAC (D), AAG (K), CAG (Q), GUG (V) and GGA (G) (Val starvation) and AAC (N), GAC (D), CUG (L), GAG (E), GCC (A), CAG (Q), GAA (E) and AAG (K) (Ile starvation) at the stalling site (Supplementary Figure 7B)." The authors fail to explain why these codons would be present in the A sites at stalling sites rather than the hungry codons themselves, especially since it is the decoding times of the hungry codons that are increased according to Fig. 1A-E. As suggested above, is this a CHX artifact?

Response: We agree that the observation that the listed codons are enriched at identified stalling positions (now Supplementary Figure 10C), while the depleted amino acid codon is located upstream, is a finding that needs more detailed explanation. Importantly, this phenomenon is not attributable to CHX artifacts, as our Ribo-seq protocol employs CHX solely during brief washes and lysis to prevent post-lysis ribosome run-off, rather than live-cell pre-treatment. Instead, we propose two hypotheses to explain this pattern: Firstly, many of these enriched codons are already inherently slow-decoded with longer DTs even under control conditions (Supplementary Figure 5H, newly added). Together with the upstream hungry codons they might form a challenging consecutive decoding environment, which results in an attenuated ribosome slowdown downstream after the hungry codon. Second, ribosome queuing may further explain this pattern. When a ribosome encounters a critically hungry codon and stalls, subsequent ribosomes can form a queue. The codon within the A-site of the queued ribosome would be (more or less) independent of the identity of the hungry codon itself that caused the initial stall. Since the listed codons have a high frequency within the transcriptome (Supp. Fig 5B), they therefore have an increased likelihood of appearing at this “stalling site”. Importantly, both of these phenomena are not necessarily represented by a general increase of DT on all of the listed codons and would therefore only be captured by the direct extraction of stalling sites but might be averaged out in the global dwell time analysis. We mention this phenomenon now in the Discussion.

-Fig. 5D: P values for the significance, or lack thereof, of the different overlaps should be provided.

Response: Thanks for pointing out this omission. We have now computed hypergeometric p-values for comparisons shown in Figure 5D and Figure 5E, and report them directly in the main text. As described, the overlap in stalling sites between Val and triple starvation is highly significant (2522 positions, p < 2.2×10⁻¹⁶), while overlaps involving Ile-specific stalling positions are smaller but still statistically robust (e.g., 149 positions for Ile – Triple, p = 1.77×10⁻⁵²). Notably, we also calculated p-values at the transcript level and found that a large fraction of transcripts with Ile-specific stalling under single starvation also stall under triple starvation, though often at different positions (1806 transcripts, p = 1.78×10⁻⁵⁸). These values are now included in the revised results section to support the interpretation of these overlaps.

-p. 17: "Nonetheless, when we examined entire transcripts rather than single positions, many transcripts that exhibited isoleucine-related stalling under Ile starvation also stalled under triple starvation, but at different sites along the CDS (Figure 5E). This finding is particularly intriguing, as it suggests that while Ile-starvation-specific stalling sites may shift under triple starvation, the overall tendency of these transcripts to stall remains." The authors never come back to account for this unexpected result.

Response: Thank you for highlighting this point. We've incorporated this finding as part of the proposed "bottleneck" scenario. While the isoleucine-specific stalling sites identified under Ile starvation do shift or disappear under triple starvation, we've observed that the same transcripts still tend to exhibit stalling. However, this now primarily occurs at upstream valine codons. We interpret this as a consequence of early elongation stalling caused by strong pausing at Val codons. This restriction on ribosome progression effectively prevents ribosomes from reaching the original Ile stalling sites. Therefore, the stalling sites identified under triple starvation are largely explained by the Val codons, reflecting a redistribution of stalling rather than its loss. To further clarify this crucial point, we've now explicitly mentioned Figure 5D-E again in the subsequent paragraph, which introduces the bottleneck theory.

-It seems very difficult to reconcile the results in Fig. 5F with those in Fig. 4A, where similar polarities in RPFs are observed for -Ile and -Val in Fig, 4A but dramatically different distributions of stalling sites in Fig. 5F. More discussion of these discrepancies is required.

Response: Thank you for pointing this out. The apparent discrepancy between the RPF profiles shown in Figure 4A and the stalling site distributions in Figure 5F likely reflects the fact that RPF polarization includes both general (unspecific) and codon-specific components. Figure 4A displays total ribosome footprint density, capturing both broad stress-induced effects and codon-specific contributions, whereas Figure 5F focuses specifically on peak-called stalling sites, representing localized and statistically significant pauses. Importantly, we would like to emphasise that Fig 4 shows that -Val and -Ile starvation exhibit different responses and not the same patterns. To make these differences even clearer, we have now updated the visualizations in Figure 4, including improved polarity plots and a new bar chart summarizing the number of transcripts with strong 5′ polarization. These additions highlight that the RPF profiles under -Val starvation are more pronounced and asymmetric, particularly due to 3′ depletion, while the polarity under -Ile is milder and a distinct, much smaller subset of transcripts appears to show polarity score shifts. We believe the updated figures and accompanying explanations now make these distinctions clearer.

• p. 18: " These isoacceptor-specific patterns correlate largely with the particular subsets of leucine and isoleucine codons that stalled (Figure 1A)." This correlation needs to be addressed for each codon-anticodon pair for all of the codons showing stalling in Fig. 1A.

Response: We thank the reviewer for this important comment. In the revised manuscript, we have expanded the relevant sections to address codon–anticodon relationships more thoroughly. We now explicitly match codons that exhibited increased dwell times under starvation to the corresponding tRNA isoacceptors whose charging was affected, and we provide a clearer discussion of the caveats involved. As noted by the reviewer, this correlation is not straightforward, as it is complicated by wobble base pairing, anticodon modifications, and the fact that multiple codons can be decoded by more than one isoacceptor, and vice versa. Moreover, in our qPCR-based tRNA charging assay, certain isoacceptors cannot be distinguished due to highly similar sequences (e.g., LeuAAG and LeuUAG, and LeuCAA and LeuCAG), which limits resolution for exact pairing. In addition, we did not assess absolute tRNA abundance, which may further influence decoding capacity. Nevertheless, where resolution is possible, the patterns align well: All tRNAVal isoacceptors became uncharged under Val and triple starvation, matching the consistent dwell time increases across all Val codons. Only tRNAIleAAU (decoding AUU and AUC) was deacylated, matching to these codons showing increased dwell times, while AUA (decoded by still-charged tRNAIleUAU) did not. Only CUU (decoded by uncharged tRNALeuGAA) showed increased dwell time. A mild deacylation of the other Leu isoacceptors was observed, but isoacceptor-level resolution is limited by assay constraints. However, these rather minimal tRNA and DT changes were consistent with more dominant initiation repression rather than elongation stalls. To support this analysis, we included an illustrative figure (now in Supplementary Figure 12F) summarizing the codon–anticodon matches.

-p. 19: "For instance, in our double starvation condition, unchanged tRNA charging levels (Figure 6E) may result from a pronounced downregulation of global translation initiation, likely driven by the activation of stress responses (Figure 2), subsequently lowering the demand for charged tRNAs as it has been observed previously for Leu starvation 39.” This seems at odds with the comparable down-regulation of protein synthesis for the Double starvation and -Leu and -Ile single starvations shown in Fig. 3C. Also, in the current study, Leu starvation does lower charging of certain Leu tRNAs.

Response: We thank the reviewer for raising this important point. In the revised manuscript, we have clarified this section and now offer a more refined interpretation of the tRNA charging patterns observed under double starvation. While Figure 3C shows a comparable reduction in global protein synthesis across the -Leu, -Ile, and double starvation conditions, it needs to be considered that the OPP assay has limited sensitivity. It operates in a relatively low fluorescence intensity range and is subject to background signal, which may obscure subtle differences between conditions. Moreover, other factors such as changes in protein stability or turnover could also contribute to the observed differences. Therefore, inter-condition differences in translation repression should be interpreted with caution. However, based on our stress response analysis (Figure 2), mTORC1 inactivation appears strongest under double starvation, likely leading to more profound suppression of translation initiation. This would reduce the overall demand for charged tRNAs and could explain why no detectable tRNA deacylation was observed under double starvation, even though mild uncharging of Leu isoacceptors occurred under -Leu, which exhibited a milder stress response. This distinction is consistent with the observed mild dwell time increases for one Leu codon under -Leu, but not in the double condition. Similarly, the absence of Ile codon stalling and tRNA deacylation under double starvation may be attributed to stress-driven reductions in elongation demand, preventing the tRNA depletion and codon-specific delays observed under single Ile starvation. A more direct clarification is now included in the revised manuscript.

Reviewer #2 (Significance):

The results here are significant in showing that starvation for a single amino acid does not lead to deacylation of all isoacceptors for that amino acid and in revealing that starvation for one amino acid can prevent deacylation of tRNAs for other amino acids, as shown most dramatically for the selective deacylation of only Val tRNAs in the triple BRCAA starvation condition. For the various reasons indicated above, however, I'm not convinced that their "bottleneck" mechanism is adequate to explain this phenomenon, especially in the case of the selective deacylation of Ile vs Leu tRNA in the Double starvation regime. It's also significant that deacylation leads to ribosome build-up near the 5'ends of CDS, which seems to be associated with an enrichment for the hungry codons in the case of Val and Ile starvation, but inexplicably, not for Leu or the Double starvations. This last discrepancy makes it hard to understand how the -Leu and Double starvations produce RPF buildups near the 5 ends of CDSs. In addition, the claim in the Discussion that "our data also highlight the importance of the codon positional context within mRNAs, indicating that where a codon is located within the CDS can influence both the extent of ribosomal stalling and overall translation efficiency during nutrient stress" overstates the strength of evidence that the stalling events lead to substantial decreases in translational efficiencies for the affected mRNAs, as the stalling frequency and decreased protein output are significantly correlated only for the -Val starvation, and the data in Fig. 3 D-H suggest that the reductions in protein synthesis generally occur at the level of initiation, even for -Val starvation, with a contribution from slow elongation only for -Ile-which is in itself difficult to understand considering that stalling frequencies are highest in -Val. Thus, while many of the results are very intriguing and will be of considerable interest to the translation field, it is my opinion that a number of results have been overinterpreted and that important inconsistencies and complexities have been overlooked in concluding that a significant component of the translational inhibition arises from the increased decoding times at hungry codons during elongation and that the selective deacylation of Val tRNAs in the Triple starvation can be explained by the "bottleneck" mechanism. The complexities and limitations of the data and their intepretations should be discussed much more thoroughly in the Discussion, which currently is devoted mostly to other phenomena often of tangential importance to the current findings. A suitably revised manuscript would clearly state the limitations and caveats of the proposed mechanisms and consider other possible explanations as well.

Again, we thank the reviewer for the valuable insights and constructive critiques. We believe that the concerns regarding potential overinterpretation and inconsistencies have now been addressed through clearer explanations and more cautious interpretation throughout the revised manuscript. We also agree that the original Discussion included aspects that, while interesting, were of secondary importance. In light of the reviewer’s suggestions, we have restructured and rebalanced the Discussion to focus more directly on the key findings and their implications. Importantly, we wish to clarify that we do not propose the elongation bottleneck model as a general mechanism across all conditions. In particular, for double (Leu/Ile) starvation, we attribute the observed effects primarily to stress response–mediated translational repression, and not to codon-specific stalling or tRNA depletion. We believe that this distinction is now more clearly conveyed in the revised manuscript.

Reviewer #3 (Evidence, reproducibility and clarity):

Summary

Worpenberg and colleagues investigated the translational consequences of branched-chain amino acid (BCAA) starvation in mouse cells. Limitation of individual BCAAs has been reported to cause codon-specific and global translational repression. In this paper, the authors use RNA-seq, ribosome profiling (Ribo-seq), proteomics, and tRNA charging assays to characterize the impacts of individual and combined depletion of leucine, isoleucine, and valine on translation. They find that BCAA starvation increases codon-specific ribosome dwell times, activates global translational stress responses and reduces global protein synthesis. They infer that this effect is due to decreased translation initiation and codon-specific translational stalling. They find that the effects of simultaneous depletion are non-additive. In valine and triple (valine, leucine, and isoleucine) depletion, they show that affected transcripts have a high density of valine codons early in their coding sequences, creating an "elongation bottleneck" that obscures the impact of starvation of other amino acids. Finally, they identify isoacceptor-specific differences in tRNA charging that help explain the codon-specific effects that they observe.

We find the major findings convincing and clear. We find that some results are incompletely explained. We suggest an additional experiment and also have some minor comments that we hope will improve clarity and rigor.

We thank the reviewer for the thorough and constructive feedback. We appreciate the recognition of our main findings and the helpful suggestions for improving the manuscript. Below we address each point in detail.

Major comments

Figure 3O: In this figure and the associated text, the authors try to determine whether differences in protein degradation can explain why some proteins have higher ribosome density but lower proteomic expression. However, since this analysis relies on published protein half-lives from non-starvation conditions and on the assumption that protein synthesis has entirely stopped, we are not convinced it is informative for this experimental context. It does not distinguish between a model in which protein synthesis has been reduced by stalling and a model in which both protein synthesis and degradation rate have increased, which are both consistent with their Ribo-seq and proteomic data. To address this issue, the authors should either perform protein half-life measurements under their starvation conditions, or more clearly explain these two models in the text and acknowledge that they cannot distinguish between them.

Response: We agree with the reviewer that our current analysis, which is based on protein half-lives obtained under non-starvation conditions, can not definitively separate the effects of reduced translation from those of increased protein degradation. We have revised the relevant section in the manuscript to more clearly state that this analysis is correlative in nature and serves only to explore one possible explanation for the observed disconnect between ribosome density and protein levels. We now also explicitly acknowledge that our dataset does not allow us to distinguish between a model in which protein output is reduced due to stalling and one in which both translation and degradation rates are altered. However, the observed log2FC in the proteomics data are often milder than expected based on complete-medium condition half-life alone, which would be difficult to reconcile with a dominant contribution from global protein destabilization. That said, we also acknowledge that protein degradation is highly context- and protein-specific, and that proteolytic regulation might still play a role. Performing a direct protein half-life measurement under our starvation conditions would indeed be required to rigorously test this, but such an experiment is outside the scope of this study. We now highlight this as a limitation and a valuable direction for future work, and we have softened any interpretations in the main text to reflect the uncertainty regarding the contribution of protein stability changes.

Minor comments

Figure 1G: Why does intracellular valine seem to be less depleted under starvation conditions than intracellular leucine or isoleucine? Are the limits of detections different for different amino acids? The authors should acknowledge this discrepancy and comment on whether it has any implications for interpretation of their results.

Response: We thank the reviewer for this important point. While valine appears slightly less depleted than leucine or isoleucine in Figure 1G, the fold changes and absolute reductions are strong for all three BCAAs, including valine. To further illustrate this, we have added a supplementary bar chart showing the measured intracellular concentrations in µmol/L, including mean and variance across five biological replicates (Supplementary Figure 5A). We believe that the variation may reflect technical factors, such as differences in detection sensitivity or ionization efficiency between amino acids in the targeted metabolomics assay and, therefore, that the observed difference does not have a meaningful impact on the interpretation of our results. We now directly acknowledge these differences in the main text.

Figure 1H: These data do not appear to meet the assumptions for linear regression. We suggest either reporting a Spearman R correlation (as the data appears linear in rank but not absolute value), or remove it entirely - we think the plot without statistics is sufficient.

Response: We thank the reviewer for the suggestion. In the revised manuscript, we removed the statistical annotation and retained only the trend line to illustrate the general pattern. We agree that this visualization alone is sufficient to support the qualitative point we aimed to convey.

Figure 2B: The in-text description of this figure states that "most" ISR genes show a "robust induction," but only three genes are shown in the figure, two of which are upregulated. The authors should instead specify that 2 out of the 3 genes profiled were robustly induced.

Response: We have rephrased the sentence to say “two of the three genes profiled…” for precision and consistency with the data shown.

Figure 2D: Please include the full, uncropped blots in the supplementary materials.

Response: We have now added the full, uncropped western blots to the supplementary material (Supplementary Figure 8).

Figure 2E: Swap the positions of the RPS6 and 4E-BP1 plots so they line up with their respective blots to make these figures easier to interpret. Authors should consider doing a one-way ANOVA and post-hoc analysis, if we correctly understand that they are making a conclusion about the difference between multiple groups in aggregate.

Response: We thank the reviewer for the suggestion. The alignment of the RPS6 and 4E-BP1 plots with their respective blots has been corrected. As this panel focuses on comparisons to the control condition only, we have retained the original presentation.

Figure 4B: Panel A in this figure is very convincing, and these plots don't add additional information. The authors could consider removing them. If this panel stays in, we suggest removing the "mid index" plot, since it is never referenced in the text and doesn't seem relevant to the message of the figure.

Response: We appreciate the feedback. While we considered removing panel B as suggested, we decided to retain it because it provides a useful summary of panel A. To improve clarity and visual interpretation, we replaced the original boxplot with a bar plot displaying mean values and SEM error bars. We believe the bar plot now nicely illustrates that Val and Triple starvation lead to stronger effects, especially in the reduction of the 3′ index. The “mid index” plot, which was not referenced in the text and did not contribute to the central message, has been removed as suggested.

Figure 4E: Why is there a reduction in frequency of a Leu and a Val codon under Ile starvation?

Response: Thank you for highlighting this observation. The reduction in the frequency of a specific Leu and Val codon under Ile starvation in Figure 4F (former Figure 4E) is indeed intriguing. This figure reflects codon usage in the first 20% of the CDSs among the subset of transcripts that exhibit a footprint polarization under each starvation condition. As such, the observed depletion likely arises from the specific transcript composition of the polarized subset under -Ile, which differs from that under -Val or other conditions. Importantly, this pattern is not consistently observed when analyzing the full transcripts (another Leu codon is affected), indicating that it is not a systematic depletion of these codons. One possibility is that an increased frequency of Ile codons (AUC) within the constrained region may lead to a relative underrepresentation of other codons, such as Leu and Val. Alternatively, this may reflect non-random codon co-occurrence patterns within specific transcripts. While our current data do not allow us to investigate this further, we acknowledge these as speculative explanations and now mention this point in the Discussion as a potential avenue for future study.

Figure 5G: There appears to be one Val codon early in the Hint1 transcript without much stalling under triple or valine starvation conditions. The authors should acknowledge this and comment on why this may be.

Response: We thank the reviewer for pointing this out. While the Hint1 transcript indeed contains a valine codon early in its CDS, no clear stalling peak was observed at that position under valine or triple starvation. Several factors may contribute to this: local sequence context can influence ribosome pausing, and not all cognate codons necessarily lead to detectable stalling even under amino acid starvation. Additionally, coverage at the 5′ end of Hint1 is relatively sparse in our dataset, and potential mappability limitations, such as regions with low complexity or repetitive elements, may further reduce resolution at specific sites. We now briefly mention this in the manuscript to clarify the possible causes.

Figure 5B: In the text referencing this figure, the authors state that "a high number of downregulated proteins with associated ribosome stalling sites did not show an overall decreased mean RPF count...as it would be expected from translation initiation defects, linking these stalling sites directly to proteomic changes." However, RPF is affected both by stalling (increases RPF) and initiation defects (decreases RPF). A gene with both stalling and decreased initiation may appear to have no RPF change. The data does suggest a contribution from stalling, but the authors should also acknowledge that reduced initiation may also be playing a role.

Response: We agree with the reviewer comment. Our cited statement should indeed be more nuanced. The reviewer correctly points out that RPFs are influenced by both increased ribosome density due to stalling and decreased ribosome density due to reduced initiation. Therefore, a gene experiencing both stalling and reduced initiation might appear to have no net change in RPF, or even a slight increase if stalling is dominant. Thus, while the presence of stalling sites strongly suggests a contribution from compromised elongation to reduced protein output, we cannot definitively rule out a concurrent role for reduced initiation, even in cases where RPF counts are not globally decreased. We revised this section in the manuscript to acknowledge this interplay.

Figure 5E: the black text on dark brown in the center of the Venn diagram is difficult to read. The diagram should either have a different color scheme, or the text in the center should be white instead of black for higher contrast.

Response: We have adjusted the text color for better contrast and improved readability.

Supplementary Figure 1C: The ribosome dwell time data in this study is described as "highly correlated" with another published dwell time dataset, but the P and E site data do not seem strongly correlated. The authors should remove the word "highly."

Response: We have removed the word “highly” to have a more cautious interpretation in the text.

Supplementary Figure 3E: Not all of the highlighted codons in this figure are ones with prolonged dwell times. To clarify the point that dwell time change is not related to codon frequency, this figure should only highlight codons that have a significantly prolonged dwell time in at least one starvation condition.

Response: We thank the reviewer for pointing this out. To improve clarity, we have revised the figure and now specifically highlight codons with significantly prolonged dwell times with stars.

Supplementary Figure 5C: The gene Chop is mentioned in the main text when referencing this figure, but is absent from the heatmap.

Response: We thank the reviewer for noting this. The gene Chop is annotated under its alternative name Ddit3 in the current version of the heatmap and is indeed present. To avoid confusion, we have now updated the label in the figure to display Chop (Ddit3) directly.

Supplementary Figure 7A: The authors could clarify this figure by adding additional language to either the figure panel or the figure legend specifying that the RPM metric being used comes from Ribo-seq.

Response: We have updated the legend to explicitly state that the RPM values shown are derived from Ribo-seq data.

Supplementary Figure 7D: The metric used to describe the spatial relationship between the first valine and isoleucine codons in transcripts in this figure seems to be describing something conceptually similar to the stalling sites in Figure 5G, but uses a different metric. These figures would be easier to interpret if these spatial relationships were presented in a consistent way throughout the manuscript.

Response: We thank the reviewer for this helpful observation. Supplementary Figure 7D (now Supplementary Figure 11B) originally used a gene-length-normalized metric to describe codon spacing, whereas Figure 5G depicted absolute nucleotide distances to stalling sites. To ensure consistency across the manuscript, we have now updated Supplementary Figure 11B to also use absolute distances. We believe this adjustment improves clarity and allows for a more direct comparison between spatial codon patterns and stalling events.

Discussion:

Reader understanding would be improved if the relevance of paragraphs were established in the first sentence. For instance, in the paragraphs about adaptive misacylation and posttranscriptional modifications, it is unclear until the end of the paragraph how these topics are relevant. Introducing the relevant aspects of the study (the fact that some starvation conditions have less severe effects and the observation about m6A-related mRNAs) at the beginning of these paragraphs would improve clarity.

Response: We thank the reviewer for this helpful comment. We agree that the flow and clarity of the Discussion can be improved by making the relevance of each paragraph clearer from the outset. In the revised manuscript, we have restructured these sections to better highlight the connection between each topic and our main findings. These changes also align with suggestions from Reviewer 2, and we believe they help to focus the Discussion more tightly around the core insights of our study.

The authors should provide more information and speculation about possible physiological relevance of their findings, particularly about the way that the effects of triple starvation are highly valine-dependent. Are there physiological conditions under which starvation of all three BCAAs is more likely than starvation of one or two of them? If so, are there any reasons why a valine-based bottleneck might be advantageous?

Response: We appreciate the reviewer's insightful question regarding the physiological relevance of our findings, particularly the valine-dependent bottleneck observed under triple BCAA starvation. This prompts a crucial discussion on the broader biological context of our work.

While complete starvation of all three BCAAs might be less frequent than individual deficiencies, such conditions are physiologically relevant in several contexts. In prolonged fasting, starvation, or severe cachectic states associated with chronic diseases (e.g., advanced cancer, critical illness), systemic amino acid pools, including BCAAs, can become significantly depleted due to increased catabolism and insufficient intake (Yu et al. 2021). Moreover, certain specialized diets or therapeutic strategies aim to modulate BCAA levels. For instance, in some Maple Syrup Urine Disease (MSUD) management protocols, BCAA intake is severely restricted to prevent the accumulation of toxic BCAA metabolites (Mann et al. 2021). Similarly, emerging cancer therapies sometimes explore nutrient deprivation strategies to selectively target tumor cells, which could involve broad BCAA reduction (e.g. Sheen et al. 2011; Xiao et al. 2016).

In these contexts, a valine-based bottleneck, as we describe, could indeed represent an adaptive strategy. If valine-tRNAs are particularly susceptible to deacylation and valine codons are strategically enriched at the 5' end of transcripts, stalling at these early positions could serve as a rapid "gatekeeper" for global translation. This early-stage inhibition would conserve cellular energy and available amino acids by quickly reducing the overall demand for charged tRNAs. Such a mechanism could potentially prioritize the translation of a subset of proteins that might have different codon usage biases or are translated via alternative, less valine-dependent mechanisms. This aligns with the concept of a multi-layered translational control where global initiation repression (as reflected in mTORC1 inhibition and polysome profiles) is complemented by specific elongation checkpoints, allowing for a more nuanced and adaptive response to severe nutrient stress.

Reviewer #3 (Significance):

Nature and significance of the advance

The main contribution of this work is to demonstrate that depletion of multiple amino acids simultaneously impacts translation elongation in ways that are not necessarily additive. These impacts can depend on the distribution of codons in a transcript. It adds to a growing body of work showing that essential amino acid starvation can cause codon-specific ribosome stalling. The authors suggest that the position-dependent stalling they observe could be a novel regulatory mechanism to alleviate the effects of multi-amino acid starvation. However, it is not fully clear from the paper what the significance of a valine-based regulatory adaptation to BCAA starvation is, or whether simultaneous starvation of all three BCAAs is of particular physiological relevance. The paper's primary contribution is mainly focused on the similarity between valine and triple BCAA starvation, and it provides limited insight into the effects of combined depletion of two BCAAs.

Context of existing literature

Although ribosome profiling does not distinguish between actively-elongating and stalled ribosomes, sites with higher read coverage, and thereby higher inferred dwell time, can be used to infer ribosome stalling (Ingolia 2011). Various downstream effects of essential amino acid depletion have been documented, such as leucine deficiency being sensed by mTORC1 via leucyl-tRNA synthetase (Dittmar 2005, Han 2012), and shared transcriptional responses among many amino acid depletion conditions (Tang 2015). These authors have previously measured the translational effects of nutrient stress using ribosome profiling (e.g., Gobet 2020), as have others (Darnell 2018, Kochavi et al. 2024). The present work represents the first study (to our knowledge) combining BCAA depletions, representing an incremental and useful contribution to our understanding of translational responses to stress conditions.

Audience

This work is of interest to investigators studying the response of human cells in stress conditions, such as in human disease, as well as investigators studying the basic biology of eukaryotic translational control.

Reviewer expertise: mRNA decay and translation regulation in bacteria.

We hope the authors have found our comments thoughtful and useful. We welcome further discussion or clarification via email: Juliana Stanley (julianst@mit.edu) and Hannah LeBlanc (leblanch@mit.edu).

We sincerely thank the reviewers for their thoughtful and constructive feedback, as well as for their careful and thorough reading of our manuscript. We also gratefully acknowledge the invitation for further discussion and would be happy to engage in future correspondence.

References

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Darnell, Alicia M., Arvind R. Subramaniam, and Erin K. O’Shea. 2018. “Translational Control through Differential Ribosome Pausing during Amino Acid Limitation in Mammalian Cells.” Molecular Cell 71 (2): 229-243.e11. https://doi.org/10.1016/j.molcel.2018.06.041.

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Referee #3

Evidence, reproducibility and clarity

Summary

Worpenberg and colleagues investigated the translational consequences of branched-chain amino acid (BCAA) starvation in mouse cells. Limitation of individual BCAAs has been reported to cause codon-specific and global translational repression. In this paper, the authors use RNA-seq, ribosome profiling (Ribo-seq), proteomics, and tRNA charging assays to characterize the impacts of individual and combined depletion of leucine, isoleucine, and valine on translation. They find that BCAA starvation increases codon-specific ribosome dwell times, activates global translational stress responses and reduces global protein synthesis. They infer that this effect is due to decreased translation initiation and codon-specific translational stalling. They find that the effects of simultaneous depletion are non-additive. In valine and triple (valine, leucine, and isoleucine) depletion, they show that affected transcripts have a high density of valine codons early in their coding sequences, creating an "elongation bottleneck" that obscures the impact of starvation of other amino acids. Finally, they identify isoacceptor-specific differences in tRNA charging that help explain the codon-specific effects that they observe.

We find the major findings convincing and clear. We find that some results are incompletely explained. We suggest an additional experiment and also have some minor comments that we hope will improve clarity and rigor.

Major comments

Figure 3O: In this figure and the associated text, the authors try to determine whether differences in protein degradation can explain why some proteins have higher ribosome density but lower proteomic expression. However, since this analysis relies on published protein half-lives from non-starvation conditions and on the assumption that protein synthesis has entirely stopped, we are not convinced it is informative for this experimental context. It does not distinguish between a model in which protein synthesis has been reduced by stalling and a model in which both protein synthesis and degradation rate have increased, which are both consistent with their Ribo-seq and proteomic data. To address this issue, the authors should either perform protein half-life measurements under their starvation conditions, or more clearly explain these two models in the text and acknowledge that they cannot distinguish between them.

Minor comments

Figure 1G: Why does intracellular valine seem to be less depleted under starvation conditions than intracellular leucine or isoleucine? Are the limits of detections different for different amino acids? The authors should acknowledge this discrepancy and comment on whether it has any implications for interpretation of their results.

Figure 1H: These data do not appear to meet the assumptions for linear regression. We suggest either reporting a Spearman R correlation (as the data appears linear in rank but not absolute value), or remove it entirely - we think the plot without statistics is sufficient.

Figure 2B: The in-text description of this figure states that "most" ISR genes show a "robust induction," but only three genes are shown in the figure, two of which are upregulated. The authors should instead specify that 2 out of the 3 genes profiled were robustly induced.

Figure 2D: Please include the full, uncropped blots in the supplementary materials.

Figure 2E: Swap the positions of the RPS6 and 4E-BP1 plots so they line up with their respective blots to make these figures easier to interpret. Authors should consider doing a one-way ANOVA and post-hoc analysis, if we correctly understand that they are making a conclusion about the difference between multiple groups in aggregate.

Figure 4B: Panel A in this figure is very convincing, and these plots don't add additional information. The authors could consider removing them. If this panel stays in, we suggest removing the "mid index" plot, since it is never referenced in the text and doesn't seem relevant to the message of the figure.

Figure 4E: Why is there a reduction in frequency of a Leu and a Val codon under Ile starvation?

Figure 5G: There appears to be one Val codon early in the Hint1 transcript without much stalling under triple or valine starvation conditions. The authors should acknowledge this and comment on why this may be.

Figure 5B: In the text referencing this figure, the authors state that "a high number of downregulated proteins with associated ribosome stalling sites did not show an overall decreased mean RPF count...as it would be expected from translation initiation defects, linking these stalling sites directly to proteomic changes." However, RPF is affected both by stalling (increases RPF) and initiation defects (decreases RPF). A gene with both stalling and decreased initiation may appear to have no RPF change. The data does suggest a contribution from stalling, but the authors should also acknowledge that reduced initiation may also be playing a role.

Figure 5E: the black text on dark brown in the center of the Venn diagram is difficult to read. The diagram should either have a different color scheme, or the text in the center should be white instead of black for higher contrast.

Supplementary Figure 1C: The ribosome dwell time data in this study is described as "highly correlated" with another published dwell time dataset, but the P and E site data do not seem strongly correlated. The authors should remove the word "highly."

Supplementary Figure 3E: Not all of the highlighted codons in this figure are ones with prolonged dwell times. To clarify the point that dwell time change is not related to codon frequency, this figure should only highlight codons that have a significantly prolonged dwell time in at least one starvation condition.

Supplementary Figure 5C: The gene Chop is mentioned in the main text when referencing this figure, but is absent from the heatmap.

Supplementary Figure 7A: The authors could clarify this figure by adding additional language to either the figure panel or the figure legend specifying that the RPM metric being used comes from Ribo-seq.

Supplementary Figure 7D: The metric used to describe the spatial relationship between the first valine and isoleucine codons in transcripts in this figure seems to be describing something conceptually similar to the stalling sites in Figure 5G, but uses a different metric. These figures would be easier to interpret if these spatial relationships were presented in a consistent way throughout the manuscript.

Discussion:

Reader understanding would be improved if the relevance of paragraphs were established in the first sentence. For instance, in the paragraphs about adaptive misacylation and posttranscriptional modifications, it is unclear until the end of the paragraph how these topics are relevant. Introducing the relevant aspects of the study (the fact that some starvation conditions have less severe effects and the observation about m6A-related mRNAs) at the beginning of these paragraphs would improve clarity.<br /> The authors should provide more information and speculation about possible physiological relevance of their findings, particularly about the way that the effects of triple starvation are highly valine-dependent. Are there physiological conditions under which starvation of all three BCAAs is more likely than starvation of one or two of them? If so, are there any reasons why a valine-based bottleneck might be advantageous?

We hope the authors have found our comments thoughtful and useful. We welcome further discussion or clarification via email: Juliana Stanley (julianst@mit.edu) and Hannah LeBlanc (leblanch@mit.edu).

Significance

Nature and significance of the advance

The main contribution of this work is to demonstrate that depletion of multiple amino acids simultaneously impacts translation elongation in ways that are not necessarily additive. These impacts can depend on the distribution of codons in a transcript. It adds to a growing body of work showing that essential amino acid starvation can cause codon-specific ribosome stalling. The authors suggest that the position-dependent stalling they observe could be a novel regulatory mechanism to alleviate the effects of multi-amino acid starvation. However, it is not fully clear from the paper what the significance of a valine-based regulatory adaptation to BCAA starvation is, or whether simultaneous starvation of all three BCAAs is of particular physiological relevance. The paper's primary contribution is mainly focused on the similarity between valine and triple BCAA starvation, and it provides limited insight into the effects of combined depletion of two BCAAs.

Context of existing literature

Although ribosome profiling does not distinguish between actively-elongating and stalled ribosomes, sites with higher read coverage, and thereby higher inferred dwell time, can be used to infer ribosome stalling (Ingolia 2011). Various downstream effects of essential amino acid depletion have been documented, such as leucine deficiency being sensed by mTORC1 via leucyl-tRNA synthetase (Dittmar 2005, Han 2012), and shared transcriptional responses among many amino acid depletion conditions (Tang 2015). These authors have previously measured the translational effects of nutrient stress using ribosome profiling (e.g., Gobet 2020), as have others (Darnell 2018, Kochavi et al. 2024). The present work represents the first study (to our knowledge) combining BCAA depletions, representing an incremental and useful contribution to our understanding of translational responses to stress conditions.

Audience

This work is of interest to investigators studying the response of human cells in stress conditions, such as in human disease, as well as investigators studying the basic biology of eukaryotic translational control.

Reviewer expertise: mRNA decay and translation regulation in bacteria.

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Referee #2

Evidence, reproducibility and clarity

Summary and General Critique:

This study examines the consequences of starvation for the BRCAAs, either singly, for Leu & Ile, or for all three simultaneously in HeLa cells on overall translation rates, decoding rates at each codon, and on ribosome density, protein expression, and distribution of ribosome stalling events across the CDS for each expressed gene. The single amino acid starvation regimes specifically reduce the cognate intracellular amino acid pool and lead to deacylation of at least a subset of the cognate tRNAs in a manner dependent on continuing protein synthesis. They also induce the ISR equally and decrease bulk protein synthesis equally in a manner that appears to occur largely at the initiation level for -Leu and -Val, judging by the decreased polysome:monsome ratio, but at both the initiation and elongation levels for -Ile-a distinction that remains unexplained. Only -Leu appears to down-regulate mTORC1 and TOP mRNA translation. There is a significant down-regulation of protein levels for 50-200 genes, which tend to be unstable in nutrient-replete cells, only a fraction of which are associated with reduced ribosome occupancies (RPFs measured by Ribo-Seq) on the corresponding mRNAs in the manner expected for reduced initiation, suggesting that delayed elongation is responsible for reduced protein levels for the remaining fraction of genes. All three single starvations lead to increased decoding times for a subset of the cognate "hungry" codons: CUU for -Leu, AUU and AUC for -Ile, and all of the Val codons, in a manner that is said to correspond largely to the particular tRNA isoacceptors that become deacylated, although this correspondence was not explained explicitly and might not be as simple as claimed. All three single starvations also evoke skewing of RPFs towards the 5' ends of many CDSs in a manner correlated with an enrichment within the early regions of the CDSs for one or more of the cognate codons that showed increased decoding times for -Ile (AUC codon) and -Val (GUU, GUC, and GUG), but not for -Leu-of which the latter was not accounted for. These last findings suggest that, at least for -Val and -Ile, delays in decoding N-terminal cognate codons cause elongating ribosomes to build-up early in the CDS. They go on to employ a peak calling algorithm to identify stalling sites in an unbiased way within the CDS, which are greatest in number for -Val, and find that Val codons are enriched in the A-sites (slightly) and adjacent 5' nucleotides (to a greater extent) for -Val starvation; and similarly for Ile codons in -Ile conditions, but not for -Leu starvation-again for unknown reasons. It's unclear why their called stalling sites have various other non-hungry codons present in the A sites with the cognate hungry codons being enriched further upstream, given that stalling should occur with the "hungry" cognate codon in the A site. The proteins showing down-regulation are enriched for stalling sites only in the case of the -Val starvation in the manner expected if stalling is contributing to reduced translation of the corresponding mRNA. It's unclear why this enrichment apparently does not extend to -Ile starvation which shows comparable skewing of RPFs towards the 5'ends, and this fact diminishes the claim that pausing generally contributes to reduced translation for genes with abundant hungry codons.<br /> All of the same analyses were carried out for the Double -Ile/-Leu and Triple starvations and yield unexpected results, particularly for the triple starvation wherein decoding times are increased only at Val codons, skewing of RPFs towards the 5' ends of CDSs is correlated only with an enrichment for Val codons within the early regions of the CDSs, and stall sites are enriched only for Val codons at nearly upstream sites, all consistent with the finding that only Val tRNAs become deacylated in the Triple regime. To explain why only Val tRNA charging is reduced despite the observed effective starvation for all three amino acids, they note first that stalling at Val codons is skewed towards the 5'ends of CDS for both -Val and triple starvations more so than observed for Ile or -Leu starvation, which they attribute to a greater frequency of Val codons vs Ile codons in the 5' ends of CDSs. As such, charged Val tRNAs are said to be consumed in translating the 5'ends of CDSs and the resulting stalling prevents ribosomes from reaching downstream Ile and Leu codons at the same frequencies and thus prevents deacylation of the cognate Ile and Leu tRNAs. It's unclear whether this explanation is adequate to explain the complete lack of Ile or Leu tRNA deacylation observed even when amino acid recycling by the proteasome is inhibited-a treatment shown to exacerbate deacylation of cognate tRNAs in the single amino acid starvations and of Val tRNA in the triple starvation. As such, the statement in the Abstract "Notably, we could show that isoleucine starvation-specific stalling largely diminished under triple starvation, likely due to early elongation bottlenecks at valine codons" might be too strong and the word "possibly" would be preferred over "likely". It's also unclear why the proteins that are down-regulated in the triple starvation are not significantly enriched for stalling sites (Fig. 5B) given that the degree of skewing is comparable or greater than for -Val. This last point seems to undermine their conclusion in the Abstract that "that many proteins downregulated under BCAA deprivation harbor stalling sites, suggesting that compromised elongation contributes to decreased protein output."<br /> In the case of the double -Ile/-Leu starvation, a related phenomenon occurs wherein decoding rates are decreased for only the AUU Ile codon and only the AAU Ile tRNA becomes deacylated; although in this case increased RPFs in the 5' ends are not correlated with enrichment for Ile or Leu codons and, although not presented, apparently stall sites are not associated with the Ile codon in the double starvation. In addition, stalling sites are not enriched in the proteins down-regulated by the double starvation. Moreover, because Ile codons are not enriched in the 5'ends of CDS, it doesn't seem possible to explain the selective deacylation of the single Ile tRNA observed in the double starvation by the same "bottleneck" mechanism proposed to explain selective deacylation of only Val tRNAs during the triple starvation. This is another reason for questioning their "bottleneck" mechanism.

Specific comments (some of which were mentioned above):

• The authors have treated cells with CHX in the Ribo-Seq experiments, which has been shown to cause artifacts in determining the locations of ribosome stalling in vivo owing to continued elongation in the presence of CHX (https://doi.org/10.1371/journal.pgen.1005732 ). The authors should comment on whether this artifact could be influencing some of their findings, particular the results in Fig. 5C where the hungry codons are often present upstream of the A sites of called stalling sites in the manner expected if elongation continued slowly following stalling in the presence of CHX.
• p. 12: "These starvation-specific DT and ribosome density modulations were also evident at the individual transcript level, as exemplified by Col1a1, Col1a2, Aars, and Mki67 which showed persistent Val-codon-specific ribosome density increases but lost Ile-codon-specific increases under triple starvation (Supplementary Figure 3A-D). " This conclusion is hard to visualize for any but Val codons. It would help to annotate the relevant peaks of interest for -Ile starvation with arrows.
• To better make the point that codon-specific stalling under BCAA starvation appears to be not driven by codon usage, rather than the analysis in Fig. 1H, wouldn't it be better to examine the correlation between increases in DT under the single amino acid starvation conditions and the codon frequencies across all codons?
• p. 13, entire paragraph beginning with "Our RNA-seq and Ribo-seq revealed a general activation of stress response pathways across all starvations..." It is difficult to glean any important conclusions from this lengthy analysis, and the results do not appear to be connected to the overall topic of the study. If there are important conclusions here that relate to the major findings then these connections should be made or noted later in the Discussion. If not, perhaps the analysis should be largely relegated to the Supplemental material.
• p. 15: "Together, these findings highlight that BCAA starvation triggers a combination of effects on initiation and elongation, with varying dynamics by amino acid starvation." I take issue with this statement as it appears that translation is reduced primarily at the initiation step for all conditions except -Ile. As noted above, these data are never menitioned in the DISCUSSION as to why only -Ile would show a marked elongation component to the inhibition whereas -Val gives the greatest amount of ribosome stalling.
• I cannot decipher Fig. 4D and more detail is required to indicate the identify of each column of data.
• In Fig. 4E, one cannot determine what the P values actually are, which should be provided in the legend to confirm statistical significance.
• It's difficult to understand how the -Leu condition and the Double starvation can produce polarized RPFs (Fig. 4A) without evidence of stalling at the cognate hungry codons (Fig. 4E), despite showing later in Fig. 5A that the numbers of stall sites are comparable in those cases to that found for -Ile.
• Fig. 5B: the P values should be given for all five columns, and it should be explained here or in the Discussion why the authors conclude that stalling is an important determinant for reduced translation when a significant correlation seems to exist only for the -Val condition and not even for the Triple condition.
• p. 17: "Of note, in cases where valine or isoleucine codons were present just upstream (rather than at) the stalling position, we noted a strong bias for GAG (E), GAA (E), GAU (D), GAC (D), AAG (K), CAG (Q), GUG (V) and GGA (G) (Val starvation) and AAC (N), GAC (D), CUG (L), GAG (E), GCC (A), CAG (Q), GAA (E) and AAG (K) (Ile starvation) at the stalling site (Supplementary Figure 7B)." The authors fail to explain why these codons would be present in the A sites at stalling sites rather than the hungry codons themselves, especially since it is the decoding times of the hungry codons that are increased according to Fig. 1A-E. As suggested above, is this a CHX artifact?
• Fig. 5D: P values for the significance, or lack thereof, of the different overlaps should be provided.
• p. 17: "Nonetheless, when we examined entire transcripts rather than single positions, many transcripts that exhibited isoleucine-related stalling under Ile starvation also stalled under triple starvation, but at different sites along the CDS (Figure 5E). This finding is particularly intriguing, as it suggests that while Ile-starvation-specific stalling sites may shift under triple starvation, the overall tendency of these transcripts to stall remains." The authors never come back to account for this unexpected result.
• It seems very difficult to reconcile the results in Fig. 5F with those in Fig. 4A, where similar polarities in RPFs are observed for -Ile and -Val in Fig, 4A but dramatically different distributions of stalling sites in Fig. 5F. More discussion of these discrepancies is required.
• p. 18: " These isoacceptor-specific patterns correlate largely with the particular subsets of leucine and isoleucine codons that stalled (Figure 1A)." This correlation needs to be addressed for each codon-anticodon pair for all of the codons showing stalling in Fig. 1A.
• p. 19: "For instance, in our double starvation condition, unchanged tRNA charging levels (Figure 6E) may result from a pronounced downregulation of global translation initiation, likely driven by the activation of stress responses (Figure 2), subsequently lowering the demand for charged tRNAs as it has been observed previously for Leu starvation 39. This seems at odds with the comparable down-regulation of protein synthesis for the Double starvation and -Leu and -Ile single starvations shown in Fig. 3C. Also, in the current study, Leu starvation does lower charging of certain Leu tRNAs.

Significance

The results here are significant in showing that starvation for a single amino acid does not lead to deacylation of all isoacceptors for that amino acid and in revealing that starvation for one amino acid can prevent deacylation of tRNAs for other amino acids, as shown most dramatically for the selective deacylation of only Val tRNAs in the triple BRCAA starvation condition. For the various reasons indicated above, however, I'm not convinced that their "bottleneck" mechanism is adequate to explain this phenomenon, especially in the case of the selective deacylation of Ile vs Leu tRNA in the Double starvation regime. It's also significant that deacylation leads to ribosome build-up near the 5'ends of CDS, which seems to be associated with an enrichment for the hungry codons in the case of Val and Ile starvation, but inexplicably, not for Leu or the Double starvations. This last discrepancy makes it hard to understand how the -Leu and Double starvations produce RPF buildups near the 5 ends of CDSs. In addition, the claim in the Discussion that "our data also highlight the importance of the codon positional context within mRNAs, indicating that where a codon is located within the CDS can influence both the extent of ribosomal stalling and overall translation efficiency during nutrient stress" overstates the strength of evidence that the stalling events lead to substantial decreases in translational efficiencies for the affected mRNAs, as the stalling frequency and decreased protein output are significantly correlated only for the -Val starvation, and the data in Fig. 3 D-H suggest that the reductions in protein synthesis generally occur at the level of initiation, even for -Val starvation, with a contribution from slow elongation only for -Ile-which is in itself difficult to understand considering that stalling frequencies are highest in -Val. Thus, while many of the results are very intriguing and will be of considerable interest to the translation field, it is my opinion that a number of results have been overinterpreted and that important inconsistencies and complexities have been overlooked in concluding that a significant component of the translational inhibition arises from the increased decoding times at hungry codons during elongation and that the selective deacylation of Val tRNAs in the Triple starvation can be explained by the "bottleneck" mechanism. The complexities and limitations of the data and their intepretations should be discussed much more thoroughly in the Discussion, which currently is devoted mostly to other phenomena often of tangential importance to the current findings. A suitably revised manuscript would clearly state the limitations and caveats of the proposed mechanisms and consider other possible explanations as well.

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Referee #1

Evidence, reproducibility and clarity

This manuscript described the translational responses to single and combined BCAA shortages in mouse cell lines. Using Ribo-seq and RNA-seq analysis, the authors found selective ribosome pausing at codons that encode the depleted amino acids, where the pausing at valine codons was prominent at both a single and triple starvations whereas isoleucine codons showed pausing only under a single depletion. They analyzed the mechanisms of the unexpected selective pausing and proposed that the positional codon usage bias could shape the ribosome stalling and tRNA charging patterns across different amino acids. They also examined the stress responses and the changes in the protein expression levels under BCAA starvation.

The manuscript was well-written, and the findings are interesting, especially their model that positional codon usage bias could be a regulator of ribosome pausing and tRNA charging levels. Although different translational responses to distinct amino acid starvation have been widely documented, the positional codon usage bias is an interesting aspect. The manuscript's central message could have been made clearer. The authors may consider emphasizing this point more explicitly in the abstract. The rich multi-omics dataset in this work provides valuable resources for the translation field.

Major comments

1. The abstract may need to be revised since it is hard to immediately catch the authors' main point. If the authors regard this work as a resource paper, the current version is fine. But it could be better to point out the positional codon usages the authors found, which is a strong point of the current manuscript.
2. Page 18 "Beyond these tRNA dynamics, our data also highlight the importance of the codon positional context within mRNAs, indicating that where a codon is located within the CDS can influence both the extent of ribosomal stalling and overall translation efficiency during nutrient stress."<br /> This idea is interesting. To what extent the authors think this could be generalized? The authors may discuss whether they think their proposed model is specific to the different ribosome stalling patterns between valine and isoleucine codons or generalized to other codon combinations. For example, the positional codon usage bias will be different among different organisms, and are there any previous reports on ribosome behaviors that align with their model? Even if the authors think this model can be applied to BCAA starvation, would it be possible to explain the different isoleucine codon responses between single and double starvation? The authors may discuss why the ribosome stalling at isoleucine AUU and AUC codons was slightly attenuated under double starvation. And how about the different leucine codon responses among single, double, and triple starvations, although the pausing is not as strong as isoleucine and valine codons? Experimental validation using artificial reporters carrying biased sequences may also be considered.
3. Page 13 "Moreover, we noticed that DT changes extend beyond the ribosomal A-site, including the P-site, E-site, and even further positions (Supplementary Fig. 2A), consistent with other studies on single amino acid starvation 39 (Supplementary Fig. 2B-C)." Could the widespread DT changes be due to Ribo-DT pipeline they used or difficulties in offset determination? Indeed the authors showed that this feature was found in other datasets, but it seems that the datasets were processed and analyzed in the same way as their data. The original Ribo-DT paper (Gobet and Naef, 2022, Methods) also showed some widespread DT changes even from RNA-seq. Another analysis method like the codon subsequence abundant shift as a part of diricore analysis (Loayza-Puch et al., 2016, Nature) did not show that broad changed regions. The authors are encouraged to re-analyze the data sets using different methods.
4. Page 13 "Intriguingly, only two of the three isoleucine codons (AUU and AUC) showed increased DTs upon Ile starvation (p < 0.01), while just one leucine codon (CUU) exhibited a modest but significant DT increase (p < 0.01) under Leu starvation (Figure 1A-B, Supplementary Figure 2A)." How can the authors explain the different strengths of ribosome pausing at Ile codons under Ile and double starvation? The AUA codon did not show any pausing under either of the starvation conditions. Throughout the manuscript, the authors mainly describe the difference between amino acids but it is desirable to discuss the codon-level difference as well.
5. Page 13 "We examined the effects of single amino acid starvations (-Leu, -Ile and -Val), as well as combinations, including a double starvation of leucine and isoleucine (hereafter referred to as "double") and a starvation of leucine, isoleucine, and valine ("triple"), allowing us to identify potential non-additive effects." The different double starvations, isoleucine and valine, and leucine and valiene, will further support their hypothesis on the effects of the positional codon usage bias on ribosome pausing and tRNA charging patterns. Although this could be beyond the scope of the current manuscript, the authors are encouraged to provide a rationale for the chosen combination.

Minor comments

Page 16 "these results imply that BCAA deprivation lowers protein output through multiple pathways: a combination of reduced initiation, direct elongation blocks (stalling), and possibly an increased proteolysis" This conclusion is totally right but may be too general. Could the authors summarize BCAA-specific features of the events including reduced initiation, stalling, and proteolysis that all contribute to protein outputs? This is not well discussed in the latter sections including Discussion.

Significance

The manuscript was well-written, and the findings are interesting, especially their model that positional codon usage bias could be a regulator of ribosome pausing and tRNA charging levels. Although different translational responses to distinct amino acid starvation have been widely documented, the positional codon usage bias is an interesting aspect. The manuscript's central message could have been made clearer. The authors may consider emphasizing this point more explicitly in the abstract. The rich multi-omics dataset in this work provides valuable resources for the translation field.

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Reply to the reviewers

Prior to the point-by-point response to the reviewer, we would like to sincerely thank all the peer reviewers for their overwhelmingly positive comments and helpful suggestions. The recommendations have undoubtedly improved our initial submission, and we have done our best to incorporate as many of the suggestions as possible.

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

*Jones et al. have submitted a manuscript detailing the role of Coenzyme A in the regulation of macrophage polarization. Overall, the manuscript is well designed, and the conclusions are well supported by the data. I find no major or minor deficiencies that need to be corrected. *

* Reviewer #1 (Significance (Required)): *

For decades the immunology community has boldly stated that mitochondrial metabolism not only provides the bioenergetics for cell expansion but also dictates cell fate. This has been especially true for fatty acid beta oxidation. Macrophage, T-cell and B-cell polarization have all been shown to require FAO for their polarization, but all based on one inhibitor. NONE of these observations hold up with more rigorous experimentation. The Divakaruni group has previously suggested that intracellular CoA homeostasis was the driver of macrophage differentiation as they could reverse the inhibitory effects by providing heroic levels of CoA extracellularly. Here, they have clarified the role of CoA. Intracellular CoA does not affect macrophage polarization/differentiation. This was done with cleaver manipulation of the CoA pools. Rather, extracellular CoA can act as a weak TLR4 ligand. This work nicely clarifies their previous work and further demonstrates a role for this metabolite as an endogenous activator of type 1 macrophages.

We are thrilled by the positive comments about our work, and we are grateful the reviewer found our submission to be clarifying for the field and significant in the larger context of immunometabolism research.

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

*This is a fairly straightforward manuscript that indicated CoA acts as a "weak" TLR4 agonist and primes macrophages for alternative activation. Overall, the experiments are well done and clear enough. There are two major issues that need to be addressed: *

We thank the reviewer for their positive comments regarding the quality and clarity of our work.

1. *Previous work has shown the following pathway: LPS>IL10>STAT3>IL4Ra>>>increased responsiveness to IL4/IL13 and increased expression of M2 associated markers (please note, this pathway does not apply to Arg1, often erroneously associated with M2 macrophages - LPS induces Arg1 far more than IL4 and this is independent of the STAT6 pathway - Dichtl et al., Science Advances and El Kasmi et al. Nature Immunology, and others). This pathway was first described in Lang et al. 2002 J. Immunol. Subsequently, other groups showed IL6 (Jens Brüning) and OSM (Carl Richards) do the same thing, which is not surprising given that they are STAT3 activators. Thus, Il4ra is a STAT3 target gene; this also makes sense in the kinetic evolution of macrophages from inflammatory to tissue reparative (if they survive). In my view, the authors have most likely found the same pathway. In Jones, expression of the IL4Ra was not quantified. Thus, the pathway described above needs to be accounted for. It may not apply here but seems the easiest explanation of the data. *

This is an excellent and important experiment suggested by the reviewer, and we address this in our revised Supplemental Figure 5. To determine whether the effect of CoA can be explained simply by a STAT3-mediated effect on the IL-4 receptor, we treated cells with the well-characterized STAT3 inhibitor Napabucasin and measured whether CoA could enhance the macrophage IL-4 response. Two results are clear from the data:

• Treatment with Napabucasin reduced the expression of IL-4-linked cell surface markers and the IL-4 target gene Ccl8. This serves as an important control consistent with the Il4ra gene being a STAT3 target that increases IL-4 responsiveness.
• Despite STAT3 inhibition and a reduced IL-4 response, CoA provision still augmented the IL-4-induced expression of Ccl8 and the percentage of CD206+/CD301+ cells, indicating a STAT3-independent mechanism. The result aligns with our ATAC-Seq data in Figure 6 that shows broad changes in chromatin accessibility that cannot be completely explained by expression-level changes in the IL-4 receptor.

*Can the authors come up with a meaningful in vivo experiment to corroborate their data. Pantothenate-deficient mice have many phenotypes (not fully explored at all - PMID 31918006, for example) and pantothenate metabolism can be manipulated in different ways. Obviously, a complex in vivo experiment is not feasible here. But this should be discussed. What happens in human macrophages, where "polarization" is a completely different beast? *

We thank the reviewer for these thoughtful comments, and address the questions regarding in vivo proof-of-concept and polarization of human macrophages separately:

• Regarding the question of whether CoA can enhance the phenotype of IL-4-activated human macrophages, this is an excellent suggestion and we have added the data as Figure 1h. Indeed, Coenzyme A dramatically amplifies expression of the human IL-4 responsive genes CCL17, TGM2, and PDCD1LG2 (similarly to mouse macrophages). The result substantially expands the significance of our work by showing the phenotype is reproducible in both mouse and human macrophages – unlike many immunometabolic phenotypes – and we thank the reviewer again for suggesting this experiment.
• With respect to an in vivo experiment to corroborate our data, we entirely agree with the reviewer regarding both the importance, but also the difficulty in interpretation, of an experiment genetically manipulating CoA synthesis in vivo. As they have suggested, we raise these issues in the discussion on Lines 370-377 of the revised manuscript. Here, we note the following points:
• Wherever possible/appropriate (e.g. Figures 1g, 3f&g, 5g&h), we have sought to corroborate our in vitro findings with in vivo/ex vivo proofs-of-concept.
• Studying immune phenotypes in pantothenate-deficient mice would be an exciting experiment in principle, but difficult to interpret if conducted. As noted by the reviewer in the work from Drs. Rock and Jackowski, knockout of one of four isoforms of pantothenate kinase (PANK) shows mild phenotypes consistent with compensation across isoforms for CoA provision. Global double knockout of PANK1 and PANK2, however, is postnatally lethal. Regardless, a tissue-specific double knockout in myeloid cells is unlikely to show a phenotype given our results showing that manipulating intracellular CoA levels in BMDMs does not alter the IL-4 response (Figs. 2h-j).
• Given the established role of CoA in postnatal development, it would be difficult to attribute any immunologic phenotypes in genetically modified mice to direct effects of CoA as a metabolic DAMP as opposed to indirect effects from a chronically altered immune system.

Reviewer #2 (Significance (Required)): *This is a fairly straightforward manuscript that indicated CoA acts as a "weak" TLR4 agonist and primes macrophages for alternative activation. Overall, the experiments are well done and clear enough.

*

We reiterate our gratitude for the comments on the quality and clarity of our work.

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

Summary: In this manuscript on enhancement of mIL-4 polarization by exogenous CoA, the authors follow up on their previous studies that had shown a correlation between Etomoxir-driven block in mIL-4 and a reduction of intracellular CoA levels. The results obtained (lack of enhancement of IL-4-induced changes in oxidative phosphorylation and glycolysis; lack of impact of pharmacological decrease/increase of intracellular CoA levels) led them to discard their initial hypothesis. Instead, the presence of a proinflammatory gene signature in macrophages treated with IL-4+CoA triggered experiments testing the involvement of TLR-Myd88 signaling and the identification of CoA as a weak agonist for TLR4 (which is consistent with a preprint manuscript posted in 2022 by others and showing induction of proinflammatory gene express in a TLR2/4-dependent manner).

• Significance: Overall, these results are novel and interesting, although the use of yeast-derived CoA preparations raises a question about the contribution of contaminants that is only partially controlled by data obtained with a synthetic CoA. Regarding a biological role for CoA in macrophage biology in vivo, the authors propose that CoA may act as a DAMP upon release from dying/dead cells and thereby modify transcriptional polarization of m(IL-4). I have several comments related to specific experimental conditions and interpretation that should be addressed. Most importantly, the key findings of the manuscript should be demonstrated using synthetic CoA as described in comment #5. *

We are heartened that the reviewer found our initial submission to be novel and interesting, and are grateful for their suggestions to reinforce our existing data with more studies comparing yeast-derived and synthetically-derived Coenzyme A. We have done our best to address each of the individual questions below:

Major comments:

1. *Increasing/decreasing intracellular CoA levels does not alter IL-4-induced CD206 expression (Fig. 2i/j. However, the impact of CoA addition to mIL-4 is stronger for Ccl8 and Mgl2 mRNA (Fig. 1a) than for the CD206+ cell fraction (Fig. 1d). Therefore, it would be better (higher sensitivity) to include expression of these genes as readout after CPCA/PZ-2891 treatment. *

This is a helpful suggestion, and we have now conducted gene expression studies to complement our flow cytometry and mass spectrometry studies while manipulating the intracellular CoA pool. In line with our previous work, neither CPCA (which decreases intracellular free CoA) or PZ-2891 (which increases intracellular free CoA) meaningfully alter expression of IL-4-linked genes including Ccl8 or Mgl2. In fact, the only (statistically insignificant) trend refutes the hypothesis, as gene expression with CPCA leads to marginally increased gene expression. These results are now included in Supplemental Figure S2f. We thank the reviewer for this helpful suggestion, as it has strengthened our conclusion that intracellular CoA levels do not adjust the macrophage IL-4 response.

• The CoA-induced proinflammatory gene expression in Fig. 3c is relatively weak (e.g. compared to LPS). The authors use CoA throughout the manuscript at a concentration of 1 mM, and we do not know how much of it is required to cause an effect at all. Therefore, dose-response curves for the stimulation of macrophages with titrated amounts of CoA should be provided. In addition, *

We thank the reviewer for bringing up this point so we could clarify and add to our existing data. We should note that Supplemental Figures 1b&c of our previous submission (and resubmitted manuscript) detail a concentration-response curve showing that at little as 62.5 mM CoA – the lowest concentration tested – was sufficient to enhance IL-4 cell surface marker expression.

However, it is an excellent suggestion as the reviewer notes, to conduct a similar concentration-response to determine if this lines up with CoA inducing a pro-inflammatory response. The full data set is presented in the answer to reviewer question 4 (comparing CoA purchased from Sigma vs. Avanti Polar Lipids), though we now show in Supplemental Figure S3 that 62.5 mM CoA is sufficient to elicit a pro-inflammatory response. Though it is indeed a weak effect as noted by the reviewer, our data suggest that the relatively mild stimulus is crucial for the effect. Given the results with the TLR3 agonist Poly I:C (Figure 5), which engages a Type 1 interferon response, strong TLR4 agonists that engage the TRIF/Type I interferon arm of the TLR4 response are likely to blunt or block the IL-4 response.

• Related question: we are informed that the concentration of CoA in the mitochondrial matrix is 5mM, whereas cytosol contains 100µM. For CoA to act as DAMP, I would like to know the concentration of it in supernatants of cell cultures (live vs. dying/dead cells) and from tissues. *

This is an important point brought up by the reviewer, and we agree that the implicit issue raised (i.e. “do the concentrations of CoA required to see an effect reconcile with a physiological role as a DAMP?”) should be more thoroughly addressed in the manuscript. Tissue concentrations of free CoA (in ng/mg tissue) are well established for mice and range from >100 nmol/g tissue (liver, heart, brown adipose tissue) to Nonetheless, the reviewer’s larger point is very well reasoned, and we address it in the following ways in the discussion on __Lines 378-391. __

• In light of the reviewer’s comment, we now mention specific instances in the discussion where CoA acting as a DAMP may reasonably play a physiological role (e.g. acetaminophen-induced acute liver injury or other forms of sterile liver injury given that DAMPs are known to be important factors and liver tissue contains relatively high concentrations of CoA).
• Although cytoplasmic concentrations of CoA may only be 50-100 mM, our work establishes a framework for how ubiquitous metabolic co-factors can activate pattern recognition receptors. Put another way, although CoA itself may not be a physiologically relevant DAMP, discovering this pathway could inform how other nucleotide or nucleoside analogs (e.g. adenine- or adenosine-containing molecules present at millimolar concentrations) exert their effects on innate immunity.
• Our newly obtained data with HMDMs (Figure 1h) shows that the CoA response in human macrophages – boosting IL-4-linked gene expression by 10-100X – may be much stronger than the 1.5-5X effect observed in mouse BMDMs. As such, it is exciting to speculate that CoA may have a more potent effect on the IL-4 response in humans relative to mice. We trust the reviewer understands the limitations of obtaining human macrophages that preclude conducting a thorough concentration-response analysis given the restrictions of a manuscript revision.

• It is very good that the authors validate the findings obtained using the yeast-derived CoA with the synthetic molecule. It is very conceivable that the 15% contaminating substances in the yeast CoA could be causing the observed changes in m(IL-4). The fact that synthetic CoA has higher activity in proinflammatory gene expression by BMM (Suppl. Fig. S3) is reassuring, however, it raises the question why this is the case. One possibility is that the concentrations of the different CoA preps cannot directly be compared. Therefore, dose response curves should also be provided for synthetic CoA. *

This is an astute observation by the reviewer and we thank them for reading our manuscript with such detailed attention to pick this up. We are reassured that the reviewer shares our interpretation that the effect of CoA is not due to a contaminating TLR4 agonist in the yeast-derived preparation (from Sigma-Aldrich; ~85% pure) given a negative Limulus Test (Supplemental Figure S4b). Moreover, the synthetically-derived preparation (from Avanti Polar Lipids; ~99% pure) yields a stronger TLR4 response.

An exploration of the follow-on question regarding why the effect is greater than 15% is presented below. These experiments have been added to Supplemental Figure S4c&d. The summary of our data suggests the individual concentrations indeed cannot be compared – matched concentrations of synthetic Avanti CoA have greater than a 15% effect than yeast-derived Sigma CoA. There are likely multiple factors that could explain this, some of which are listed below.

• The physiological effect of a TLR agonist need not be linear with its concentration, as demonstrated by the sigmoidal calibration curves for the TLR-expressing HEK-blue cells (Figures 4b, S4a). This likely does not explain the dramatic difference between the two CoA preparations but is worth noting.
• While we have determined that the 15% contaminating substances in the yeast-derived CoA are not causing the observed changes in the IL-4 response, it is formally possible that there are contaminating substances blunting the pro-inflammatory response and therefore limiting the effect of CoA purchased from Sigma-Aldrich relative to that from Avanti Polar Lipids. Importantly, however, our data in response to Reviewer Question #5 show there is no difference in amplifying the IL-4 response between the yeast- and synthetically-derived CoA.

• The difference in activity of yeast and synth. CoA could also be caused by the additional biologically active molecules in the yeast CoA. Therefore, it is important to show that the key findings in the paper (enhancement of m(IL-4) associated gene expression and CD206+ upregulation in vitro and in vivo) are also induced by synth. CoA. This is even more important in the context of the Myd88-independence of CD206+ upregulation in BMM treated with CoA (Suppl. Fig. S4). The experiment should be repeated with synth. CoA. If the enhancement of CD206+ cells induced by CoA is indeed unchanged in Myd88 KO BMM, then the title of the manuscript "CoA enhances alternative macrophage activation via Myd88" would not be supported by the data and needed to be changed. Activation of the TLR4 reporter cell line should also be tested using the synth. CoA molecule.*

We are grateful for this suggestion by the reviewer to further cement the idea that our observation of CoA enhancing the macrophage IL-4 response was not due to a contaminant in the Sigma-Aldrich CoA preparation. The reviewer makes a few points in this question which we address individually here.

• The suggestion to confirm that the CoA-induced enhancement of M(IL-4) is not due to a contaminating substance in the Sigma-Aldrich CoA is excellent and necessary. Here we show that synthetically derived CoA (99% pure, purchased from Avanti Polar Lipids) quantitatively reproduces the effect from yeast-derived CoA from Sigma-Aldrich in Supplemental Figure S4e. The response is noteworthy because synthetic CoA has profoundly stronger pro-inflammatory response than yeast-derived CoA, yet both have a similar effect on augmenting M(IL-4). This suggests that any appropriate pro-inflammatory response – irrespective of the relative strength or weakness – is sufficient to maximize the effect. This can also be observed with the range of MyD88-linked TLR agonists used in Figures 5 and S6a.
• Similarly, we also conducted experiments to show that the effect of synthetic CoA on M(IL-4) is independent of MyD88 similarly to yeast-derived CoA. These data are present in Supplemental Figure S6b&c. Here again, we should note that the effect of synthetic CoA is quantitatively similar to the effect of yeast CoA and Imiquimod (Supplemental Figure S6a).
• Activation of the TLR4 reporter cell line is available in Supplemental Figure S4c.
• Regarding the title of the manuscript, we acknowledge that we struggled a bit with how to frame our findings. Importantly, our findings support a model where (i) CoA provision enhances the IL-4 response not via metabolic changes but rather by acting as a mild pro-inflammatory stimulus, and (ii) MyD88 signaling augments the IL-4 response. We should also note that our findings simply show that CoA does not exclusively enhance the IL-4 response via MyD88 signaling, and there may be other redundant pathways (similarly to MyD88 agonist imiquimod but unlike the MyD88 agonists Pam3-CSK4 and low concentrations of LPS). We are open to working journal editors to strike the right balance of scientific accuracy and representation of the work when deciding on a final title.

• The results from the tumor model in Fig. 5 are presented to show a stronger tumor-promoting effect of m(IL-4) stimulated with Pam3. However, the variability of the data is high and 2 out of 6 mice in the +Pam3 group appear to actually have a lower tumor weight than the control mice. Therefore, these data are quite superficial and preliminary, and would benefit from a replicate experiment. Furthermore, for the evaluation of CoA as a biologically relevant DAMP, it would be important to know whether CoA-treated m(IL-4) show the same tumor-promoting effect in vivo as Pam3. *

We thank the reviewer for their comment, and agree that our in vivo work is indeed preliminary. Our goal with this report was to focus on the initial discovery of this molecular pathway and its first, broad characterization using a range of techniques (e.g. in vivo outcomes, ATAC-Seq, etc.), many of which can spur more detailed follow-up studies for future papers. As detailed in the manuscript discussion (Lines 415-419), future work beyond our initial discovery is warranted to thoroughly explore the physiological outcomes of CoA as a metabolic DAMP in relevant model systems such as acute liver injury. As an initial proof-of-concept to show that MyD88 signaling can enhance alternative activation, however, we believe our two discrete experiments (sterile inflammation and tumor formation) are sufficient to indicate the phenotype is likely relevant in animal models. In vivo syngeneic tumor models display natural variability in tumor size due to differences in implantation efficiency, host immune responses, and tumor-intrinsic growth kinetics. Nonetheless, our statistical analysis demonstrates that, with high confidence, that the observed differences are reproducible and not attributable to random variation.

Minor comments:

1. • Fig. 1b: where the gates for CD206/CD301 set based on isotype control stainings? *

We thank the reviewer for pointing out this oversight in our methods. The gates were indeed set on isotype control stains, and this is now mentioned in Lines 519-521 of the revised manuscript.

The formatting not cohesive m(IL-4) vs. M(IL-4)

Again, this is an embarrassing oversight on our part and we have done our very best to copy edit the piece and remove any inconsistencies and errors.

*Methods: primer sequences are not shown. They should be provided. *

We thank the reviewer for pointing this out, and now include all primer sequences used in Supplemental Table 1 of the revised manuscript.

Description of flowcytometry (L/D staining after surface? No washing steps after addition of L/D staining)

We thank the reviewer for pointing out another oversight in our methods, and have provided a more detailed description of the flow cytometric analysis in Lines 509-521 of the revised manuscript.

Statistics: the methods section states that variability is indicated by SD, but the Figure legends always mention SEM. Please correct.

We are grateful for the reviewer’s helpful attention to detail, and have corrected the methods to line up with the figure legends.

*A multitude of typos and editorial inconsistencies (e.g. spelling of m(IL-4), punctation and capitalization) should be corrected/streamlined. *

We are grateful for the reviewer’s helpful attention to detail, and have done our best to copy edit the manuscript prior to resubmission.

Reviewer #3 (Significance (Required)):

strengths: I like that the authors follow up their previous work on Etomoxir and CoA, now finding again an unexpected twist in how the effect on m(IL-4) is brought about. This makes the story more complicated, but is important to get to a more precise and realistic understanding of metabolic and transcriptomic regulation and how they are interconnected (or not). In addition, the use of a relatively broad set of methods including ATACseq and mass spectrometry is a strength.

weakness: the use of the not very pure yeast derived CoA prep, which is controlled for induction of proinflammatory cytokines by one experiment with synth. CoA. This validation needs to be expanded (see comments above) to substantiate the main message of the manuscript.

The scope of the manuscript is quite focussed on the mechanism of CoA enhanced m(IL-4). The finding that CoA appears not to act by changing intracellular macrophage metabolism but instead after its release by activation TLR4 widens the scope and suggests a new function for CoA as DAMP. This aspect would need to be further substantiated to be convincing.

Audience: scientists working at the intersection between metabolism and innate immunity will be interested in the results.

We thank the reviewer for their kind comments regarding the precision, credibility, and breadth of our manuscript. We hope they find our revised manuscript an improvement over our previous submission regarding both the new experiments and modified text. The comments have undoubtedly improved our manuscript and we are grateful to the reviewer for the considerable effort they put into reading our submission.

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

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Referee #3

Evidence, reproducibility and clarity

Summary:

In this manuscript on enhancement of mIL-4 polarization by exogenous CoA, the authors follow up on their previous studies that had shown a correlation between Etomoxir-driven block in mIL-4 and a reduction of intracellular CoA levels. The results obtained (lack of enhancement of IL-4-induced changes in oxidative phosphorylation and glycolysis; lack of impact of pharmacological decrease/increase of intracellular CoA levels) led them to discard their initial hypothesis. Instead, the presence of a proinflammatory gene signature in macrophages treated with IL-4+CoA triggered experiments testing the involvement of TLR-Myd88 signaling and the identification of CoA as a weak agonist for TLR4 (which is consistent with a preprint manuscript posted in 2022 by others and showing induction of proinflammatory gene express in a TLR2/4-dependent manner).

Significance:

Overall, these results are novel and interesting, although the use of yeast-derived CoA preparations raises a question about the contribution of contaminants that is only partially controlled by data obtained with a synthetic CoA. Regarding a biological role for CoA in macrophage biology in vivo, the authors propose that CoA may act as a DAMP upon release from dying/dead cells and thereby modify transcriptional polarization of m(IL-4). I have several comments related to specific experimental conditions and interpretation that should be addressed. Most importantly, the key findings of the manuscript should be demonstrated using synthetic CoA as described in comment #5.

Major comments:

1. Increasing/decreasing intracellular CoA levels does not alter IL-4-induced CD206 expression (Fig. 2i/j. However, the impact of CoA addition to mIL-4 is stronger for Ccl8 and Mgl2 mRNA (Fig. 1a) than for the CD206+ cell fraction (Fig. 1d). Therefore, it would be better (higher sensitivity) to include expression of these genes as readout after CPCA/PZ-2891 treatment.
2. The CoA-induced proinflammatory gene expression in Fig. 3c is relatively weak (e.g. compared to LPS). The authors use CoA throughout the manuscript at a concentration of 1 mM, and we do not know how much of it is required to cause an effect at all. Therefore, dose-response curves for the stimulation of macrophages with titrated amounts of CoA should be provided. In addition,
3. Related question: we are informed that the concentration of CoA in the mitochondrial matrix is 5mM, whereas cytosol contains 100µM. For CoA to act as DAMP, I would like to know the concentration of it in supernatants of cell cultures (live vs. dying/dead cells) and from tissues.
4. It is very good that the authors validate the findings obtained using the yeast-derived CoA with the synthetic molecule. It is very conceivable that the 15% contaminating substances in the yeast CoA could be causing the observed changes in m(IL-4). The fact that synthetic CoA has higher activity in proinflammatory gene expression by BMM (Suppl. Fig. S3) is reassuring, however, it raises the question why this is the case. One possibility is that the concentrations of the different CoA preps cannot directly be compared. Therefore, dose response curves should also be provided for synthetic CoA.
5. The difference in activity of yeast and synth. CoA could also be caused by the additional biologically active molecules in the yeast CoA. Therefore, it is important to show that the key findings in the paper (enhancement of m(IL-4) associated gene expression and CD206+ upregulation in vitro and in vivo) are also induced by synth. CoA. This is even more important in the context of the Myd88-independence of CD206+ upregulation in BMM treated with CoA (Suppl. Fig. S4). The experiment should be repeated with synth. CoA. If the enhancement of CD206+ cells induced by CoA is indeed unchanged in Myd88 KO BMM, then the title of the manuscript "CoA enhances alternative macrophage activation via Myd88" would not be supported by the data and needed to be changed. Activation of the TLR4 reporter cell line should also be tested using the synth. CoA molecule.
6. The results from the tumor model in Fig. 5 are presented to show a stronger tumor-promoting effect of m(IL-4) stimulated with Pam3. However, the variability of the data is high and 2 out of 6 mice in the +Pam3 group appear to actually have a lower tumor weight than the control mice. Therefore, these data are quite superficial and preliminary, and would benefit from a replicate experiment. Furthermore, for the evaluation of CoA as a biologically relevant DAMP, it would be important to know whether CoA-treated m(IL-4) show the same tumor-promoting effect in vivo as Pam3.

Minor comments:

1. Fig. 1b: where the gates for CD206/CD301 set based on isotype control stainings?
2. The formatting not cohesive m(IL-4) vs. M(IL-4)
3. Methods: primer sequences are not shown. They should be provided.
4. Description of flowcytometry (L/D staining after surface? No washing steps after addition of L/D staining)
5. Statistics: the methods section states that variability is indicated by SD, but the Figure legends always mention SEM. Please correct.
6. A multitude of typos and editorial inconsistencies (e.g. spelling of m(IL-4), punctation and capitalization) should be corrected/streamlined.

Significance

Strengths: I like that the authors follow up their previous work on Etomoxir and CoA, now finding again an unexpected twist in how the effect on m(IL-4) is brought about. This makes the story more complicated, but is important to get to a more precise and realistic understanding of metabolic and transcriptomic regulation and how they are interconnected (or not). In addition, the use of a relatively broad set of methods including ATACseq and mass spectrometry is a strength.

Weakness: the use of the not very pure yeast derived CoA prep, which is controlled for induction of proinflammatory cytokines by one experiment with synth. CoA. This validation needs to be expanded (see comments above) to substantiate the main message of the manuscript.

The scope of the manuscript is quite focussed on the mechanism of CoA enhanced m(IL-4). The finding that CoA appears not to act by changing intracellular macrophage metabolism but instead after its release by activation TLR4 widens the scope and suggests a new function for CoA as DAMP. This aspect would need to be further substantiated to be convincing.

Audience: scientists working at the intersection between metabolism and innate immunity will be interested in the results.

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

This is a fairly straightforward manuscript that indicated CoA acts as a "weak" TLR4 agonist and primes macrophages for alternative activation. Overall, the experiments are well done and clear enough. There are two major issues that need to be addressed:

1. Previous work has shown the following pathway: LPS>IL10>STAT3>IL4Ra>>>increased responsiveness to IL4/IL13 and increased expression of M2 associated markers (please note, this pathway does not apply to Arg1, often erroneously associated with M2 macrophages - LPS induces Arg1 far more than IL4 and this is independent of the STAT6 pathway - Dichtl et al., Science Advances and El Kasmi et al. Nature Immunology, and others). This pathway was first described in Lang et al. 2002 J. Immunol. Subsequently, other groups showed IL6 (Jens Brüning) and OSM (Carl Richards) do the same thing, which is not surprising given that they are STAT3 activators. Thus, Il4ra is a STAT3 target gene; this also makes sense in the kinetic evolution of macrophages from inflammatory to tissue reparative (if they survive). In my view, the authors have most likely found the same pathway. In Jones, expression of the IL4Ra was not quantified. Thus, the pathway described above needs to be accounted for. It may not apply here but seems the easiest explanation of the data.
2. Can the authors come up with a meaningful in vivo experiment to corroborate their data. Pantothenate-deficient mice have many phenotypes (not fully explored at all - PMID 31918006, for example) and pantothenate metabolism can be manipulated in different ways. Obviously, a complex in vivo experiment is not feasible here. But this should be discussed. What happens in human macrophages, where "polarization" is a completely different beast?

Significance

This is a fairly straightforward manuscript that indicated CoA acts as a "weak" TLR4 agonist and primes macrophages for alternative activation. Overall, the experiments are well done and clear enough.

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

Jones et al. have submitted a manuscript detailing the role of Coenzyme A in the regulation of macrophage polarization. Overall, the manuscript is well designed, and the conclusions are well supported by the data. I find no major or minor deficiencies that need to be corrected.

Significance

For decades the immunology community has boldly stated that mitochondrial metabolism not only provides the bioenergetics for cell expansion but also dictates cell fate. This has been especially true for fatty acid beta oxidation. Macrophage, T-cell and B-cell polarization have all been shown to require FAO for their polarization, but all based on one inhibitor. NONE of these observations hold up with more rigorous experimentation. The Divakaruni group has previously suggested that intracellular CoA homeostasis was the driver of macrophage differentiation as they could reverse the inhibitory effects by providing heroic levels of CoA extracellularly. Here, they have clarified the role of CoA. Intracellular CoA does not affect macrophage polarization/differentiation. This was done with cleaver manipulation of the CoA pools. Rather, extracellular CoA can act as a weak TLR4 ligand. This work nicely clarifies their previous work and further demonstrates a role for this metabolite as an endogenous activator of type 1 macrophages.

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-2025-02922

Corresponding author(s): Christian Specht

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1. General Statements [optional]

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We thank the reviewers for their thorough and constructive evaluation of our work. We have revised the manuscript carefully and addressed all the criticisms raised, in particular the issues mentioned by several of the reviewers (see point-by-point response below). We have also added a number of explanations in the text for the sake of clarity, while trying to keep the manuscript as concise as possible.

• *

In our view, the novelty of our research is two-fold. From a neurobiological point of view, we provide conclusive evidence for the existence of glycine receptors (GlyRs) at inhibitory synapses in various brain regions including the hippocampus, dentate gyrus and sub-regions of the striatum. This solves several open questions and has fundamental implications for our understanding of the organisation and function of inhibitory synapses in the telencephalon. Secondly, our study makes use of the unique sensitivity of single molecule localisation microscopy (SMLM) to identify low protein copy numbers. This is a new way to think about SMLM as it goes beyond a mere structural characterisation and towards a quantitative assessment of synaptic protein assemblies.

2. Point-by-point description of the revisions

This section is mandatory. *Please insert a point-by-point reply describing the revisions that were already carried out and included in the transferred manuscript. *

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__Reviewer #1 (Evidence, reproducibility and clarity (Required)): __

In this manuscript, the authors investigate the nanoscopic distribution of glycine receptor subunits in the hippocampus, dorsal striatum, and ventral striatum of the mouse brain using single-molecule localization microscopy (SMLM). They demonstrate that only a small number of glycine receptors are localized at hippocampal inhibitory synapses. Using dual-color SMLM, they further show that clusters of glycine receptors are predominantly localized within gephyrin-positive synapses. A comparison between the dorsal and ventral striatum reveals that the ventral striatum contains approximately eight times more glycine receptors and this finding is consistent with electrophysiological data on postsynaptic inhibitory currents. Finally, using cultured hippocampal neurons, they examine the differential synaptic localization of glycine receptor subunits (α1, α2, and β). This study is significant as it provides insights into the nanoscopic localization patterns of glycine receptors in brain regions where this protein is expressed at low levels. Additionally, the study demonstrates the different localization patterns of GlyR in distinct striatal regions and its physiological relevance using SMLM and electrophysiological experiments. However, several concerns should be addressed.

The following are specific comments:

1. Colocalization analysis in Figure 1A. The colocalization between Sylite and mEos-GlyRβ appears to be quite low. It is essential to assess whether the observed colocalization is not due to random overlap. The authors should consider quantifying colocalization using statistical methods, such as a pixel shift analysis, to determine whether colocalization frequencies remain similar after artificially displacing one of the channels. *Following the suggestion of reviewer 1, we re-analysed CA3 images of Glrbeos/eos hippocampal slices by applying a pixel-shift type of control, in which the Sylite channel (in far red) was horizontally flipped relative to the mEos4b-GlyRβ channel (in green, see Methods). As expected, the number of mEos4b-GlyRβ detections per gephyrin cluster was markedly reduced compared to the original analysis (revised__ Fig. 1B__), confirming that the synaptic mEos4b detections exceed chance levels (see page 5). *

Inconsistency between Figure 3A and 3B. While Figure 3B indicates an ~8-fold difference in the number of mEos4b-GlyRβ detections per synapse between the dorsal and ventral striatum, Figure 3A does not appear to show a pronounced difference in the localization of mEos4b-GlyRβ on Sylite puncta between these two regions. If the images presented in Figure 3A are not representative, the authors should consider replacing them with more representative examples or providing an expanded images with multiple representative examples. Alternatively, if this inconsistency can be explained by differences in spot density within clusters, the authors should explain that.

*The pointillist images in Fig. 3A are essentially binary (red-black). Therefore, the density of detections at synapses cannot be easily judged by eye. For clarity, the original images in Fig. 3A have been replaced with two other examples that better reflect the different detection numbers in the dorsal and ventral striatum. *

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Quantification in Figure 5. It is recommended that the authors provide quantitative data on cluster formation and colocalization with Sylite puncta in Figure 5 to support their qualitative observations.

*This is an important point that was also raised by the other reviewers. We have performed additional experiments to increase the data volume for analysis. For quantification, we used two approaches. First, we counted the percentage of infected cells in which synaptic localisation of the recombinant receptor subunit was observed (Fig. 5C). We found that mEos4b-GlyRa1 consistently localises at synapses, indicating that all cells express endogenous GlyRb. When neurons were infected with mEos4b-GlyRb, fewer cells had synaptic clusters, meaning that indeed, GlyR alpha subunits are the limiting factor for synaptic targeting. In cultures infected with mEos4b-GlyRa2, only very few neurons displayed synaptic localisation (as judged by epifluorescence imaging). We think this shows that GlyRa2 is less capable of forming heteromeric complexes than GlyRa1, in line with our previous interpretation (see pp. 9-10, 13). *

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Secondly, we quantified the total intensity of each subunit at gephyrin-positive domains, both in infected neurons as well as non-infected control cultures (Fig. 5D). We observed that mEos4b-GlyRa1 intensity at gephyrin puncta was higher than that of the other subunits, again pointing to efficient synaptic targeting of GlyRa1. Gephyrin cluster intensities (Sylite labelling) were not significantly different in GlyRb and GlyRa2 expressing neurons compared to the uninfected control, indicating that the lentiviral expression of recombinant subunits does not fundamentally alter the size of mixed inhibitory synapses in hippocampal neurons. Interestingly, gephyrin levels were slightly higher in hippocampal neurons expressing mEos4b-GlyRa1. In our view, this comes from an enhanced expression and synaptic targeting of mEos4b-GlyRa1 heteromers with endogenous GlyRb, pointing to a structural role of GlyRa1/b in hippocampal synapses (pp. 10, 13).

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The new data and analyses have been described and illustrated in the relevant sections of the manuscript.

Potential for pseudo replication. It's not clear whether they're performing stats tests across biological replica, images, or even synapses. They often quote mean +/- SEM with n = 1000s, and so does that mean they're doing tests on those 1000s? Need to clarify.

All experiments were repeated at least twice to ensure reproducibility (N independent experiments). Statistical tests were performed on pooled data across the biological replicates; n denotes the number of data points used for testing (e.g., number of synaptic clusters, detections, cells, as specified in each case). We have systematically given these numbers in the revised manuscript (n, N, and other experimental parameters such as the number of animals used, coverslips, images or cells). Data are generally given as mean +/- SEM or as mean +/- SD as indicated.

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Does mEoS effect expression levels or function of the protein? Can't see any experiments done to confirm this. Could suggest WB on homogenate, or mass spec?

The Glrbeos/eos knock-in mouse line has been characterised previously and does not to display any ultrastructural or functional deficits at inhibitory synapses (Maynard et al. 2021 eLife). GlyRβ expression and glycine-evoked responses were not significantly different to those of the wild-type. The synaptic localisation of mEos4b-GlyRb in KI animals demonstrates correct assembly of heteromeric GlyRs and synaptic targeting. Accordingly, the animals do not display any obvious phenotype. We have clarified this in the manuscript (p. 4). In the case of cultured neurons, long-term expression of fluorescent receptor subunits with lentivirus has proven ideal to achieve efficient synaptic targeting. The low and continuous supply of recombinant receptors ensures assembly with endogenous subunits to form heteropentameric receptor complexes (e.g. [Patrizio et al. 2017 Sci Rep]). In the present study, lentivirus infection did not induce any obvious differences in the number or size of inhibitory synapses compared to control neurons, as judged by Sylite labelling of synaptic gephyrin puncta (new__ Fig. 5D__).

Quantification of protein numbers is challenging with SMLM. Issues include i) some of FP not correctly folded/mature, and ii) dependence of localisation rate on instrument, excitation/illumination intensities, and also the thresholds used in analysis. Can the authors compare with another protein that has known expression levels- e.g. PSD95? This is quite an ask, but if they could show copy number of something known to compare with, it would be useful.

We agree that absolute quantification with SMLM is challenging, since the number of detections depends on fluorophore maturation, photophysics, imaging conditions, and analysis thresholds (discussed in Patrizio & Specht 2016, Neurophotonics). For this reason, only very few datasets provide reliable copy numbers, even for well-studied proteins such as PSD-95. One notable exception is the study by Maynard et al. (eLife 2021) that quantified endogenous GlyRb-containing receptors in spinal cord synapses using SMLM combined with correlative electron microscopy. The strength of this work was the use of a KI mouse strain, which ensures that mEos4b-GlyRb expression follows intrinsic regional and temporal profiles. The authors reported a stereotypic density of ~2,000 GlyRs/µm² at synapses, corresponding to ~120 receptors per synapse in the dorsal horn and ~240 in the ventral horn, taking into account various parameters including receptor stoichiometry and the functionality of the fluorophore. These values are very close to our own calculations of GlyR numbers at spinal cord synapses that were obtained slightly differently in terms of sample preparation, microscope setup, imaging conditions, and data analysis, lending support to our experimental approach. Nevertheless, the obtained GlyR copy numbers at hippocampal synapses clearly have to be taken as estimates rather than precise figures, because the number of detections from a single mEos4b fluorophore can vary substantially, meaning that the fluorophores are not represented equally in pointillist images. This can affect the copy number calculation for a specific synapse, in particular when the numbers are low (e.g. in hippocampus), however, it should not alter the average number of detections (Fig. 1B) or the (median) molecule numbers of the entire population of synapses (Fig. 1C). We have discussed the limitations of our approach (p. 11).

Rationale for doing nanobody dSTORM not clear at all. They don't explain the reason for doing the dSTORM experiments. Why not just rely on PALM for coincidence measurements, rather than tagging mEoS with a nanobody, and then doing dSTORM with that? Can they explain? Is it to get extra localisations- i.e. multiple per nanobody? If so, localising same FP multiple times wouldn't improve resolution. Also, no controls for nanobody dSTORM experiments- what about non-spec nb, or use on WT sections?

*As discussed above (point 6), the detection of fluorophores with SMLM is influenced by many parameters, not least the noise produced by emitting molecules other than the fluorophore used for labelling. Our study is exceptional in that it attempts to identify extremely low molecule numbers (down to 1). To verify that the detections obtained with PALM correspond to mEos4b, we conducted robust control experiments (including pixel-shift as suggested by the reviewer, see point 1, revised__ Fig. 1B__). The rationale for the nanobody-based dSTORM experiments was twofold: (1) to have an independent readout of the presence of low-copy GlyRs at inhibitory synapses and (2) to analyse the nanoscale organisation of GlyRs relative to the synaptic gephyrin scaffold using dual-colour dSTORM with spectral demixing (see p. 6). The organic fluorophores used in dSTORM (AF647, CF680) ensure high photon counts, essential for reliable co-localisation and distance analysis. PALM and dSTORM cannot be combined in dual-colour mode, as they require different buffers and imaging conditions. *

The specificity of the anti-Eos nanobody was demonstrated by immunohistochemistry in spinal cord cultures expressing mEos4b-GlyRb and wildtype control tissue (Fig. S3). In response to the reviewer's remarks, we also performed a negative control experiment in Glrbeos/eos slices (dSTORM), in which the nanobody was omitted (new__ Fig. S4F,G__). Under these conditions, spectral demixing produced a single peak corresponding to CF680 (gephyrin) without any AF647 contribution (Fig. S4F). The background detection of "false" AF647 detections at synapses was significantly lower than in the slices labelled with the nanobody. We conclude that the fluorescence signal observed in our dual-colour dSTORM experiments arises from the specific detection of mEos4b-GlyRb by the nanobody, rather than from background, cross-reactivity or wrong attribution of colour during spectral demixing. We have added these data and explanations in the results (p. 7) and in the figure legend of Fig. S4F,G.

What resolutions/precisions were obtained in SMLM experiments? Should perform Fourier Ring Correlation (FRC) on SR images to state resolutions obtained (particularly useful for when they're presenting distance histograms, as this will be dependent on resolution). Likewise for precision, what was mean precision? Can they show histograms of localisation precision.

This is an interesting question in the context of our experiments with low-copy GlyRs, since the spatial resolution of SMLM is limited also by the density of molecules, i.e. the sampling of the structure in question (Nyquist-Shannon criterion). Accordingly, the priority of the PALM experiments was to improve the sensibility of SMLM for the identification of mEos4b-GlyRb subunits, rather than to maximize the spatial resolution. The mean localisation precision in PALM was 33 +/- 12 nm, as calculated from the fitting parameters of each detection (Zeiss, ZEN software), which ultimately result from their signal-to-noise ratio. This is a relatively low precision for SMLM, which can be explained by the low brightness of mEos4b compared to organic fluorophores together with the elevated fluorescence background in tissue slices.

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In the case of dSTORM, the aim was to study the relative distribution of GlyRs within the synaptic scaffold, for which a higher localisation precision was required (p. 6). Therefore, detections with a precision ≥ 25 nm were filtered during analysis with NEO software (Abbelight). The retained detections had a mean localisation precision of 12 +/- 5 for CF680 (Sylite) and 11 +/- 4 for AF647 (nanobody). These values are given in the revised manuscript (pp. 18, 22).

Why were DBSCAN parameters selected? How can they rule out multiple localisations per fluor? If low copy numbers (

Multiple detections of the same fluorophore are intrinsic to dSTORM imaging and have not been eliminated from the analysis. Small clusters of detections likely represent individual molecules (e.g. single receptors in the extrasynaptic regions, Fig. 2A). DBSCAN is a robust clustering method that is quite insensitive to minor changes in the choice of parameters. For dSTORM of synaptic gephyrin clusters (CF680), a relatively low length (80 nm radius) together with a high number of detections (≥ 50 neighbours) were chosen to reconstruct the postsynaptic domain with high spatial resolution (see point 8). In the case of the GlyR (nanobody-AF647), the clustering was done mostly for practical reasons, as it provided the coordinates of the centre of mass of the detections. The low stringency of this clustering (200 nm radius, ≥ 5 neighbours) effectively filters single detections that can result from background noise or incorrect demixing. An additional reference explaining the use of DBSCAN including the choice of parameters is given on p. 22 (see also R2 point 4).

For microscopy experiment methods, state power densities, not % or "nominal power".

*Done. We now report the irradiance (laser power density) instead of nominal power (pp. 18, 21). *

In general, not much data presented. Any SI file with extra images etc.?

*The original submission included four supplementary figures with additional data and representative images that should have been available to the reviewer (Figs. S1-S4). The SI file has been updated during revision (new Fig. S4E-G). *

Clarification of the discussion on GlyR expression and synaptic localization: The discussion on GlyR expression, complex formation, and synaptic localization is sometimes unclear, and needs terminological distinctions between "expression level", "complex formation" and "synaptic localization". For example, the authors state:"What then is the reason for the low protein expression of GlyRβ? One possibility is that the assembly of mature heteropentameric GlyR complexes depends critically on the expression of endogenous GlyR α subunits." Does this mean that GlyRβ proteins that fail to form complexes with GlyRα subunits are unstable and subject to rapid degradation? If so, the authors should clarify this point. The statement "This raises the interesting possibility that synaptic GlyRs may depend specifically on the concomitant expression of both α1 and β transcripts." suggests a dependency on α1 and β transcripts. However, is the authors' focus on synaptic localization or overall protein expression levels? If this means synaptic localization, it would be beneficial to state this explicitly to avoid confusion. To improve clarity, the authors should carefully distinguish between these different aspects of GlyR biology throughout the discussion. Additionally, a schematic diagram illustrating these processes would be highly beneficial for readers.

We thank the reviewer to point this out. We are dealing with several processes; protein expression that determines subunit availability and the assembly of pentameric GlyRs complexes, surface expression, membrane diffusion and accumulation of GlyRb-containing receptor complexes at inhibitory synapses. We have edited the manuscript, particularly the discussion and tried to be as clear as possible in our wording.

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We chose not to add a schematic illustration for the time being, because any graphical representation is necessarily a simplification. Instead, we preferred to summarise the main numbers in tabular form (Table 1). We are of course open to any other suggestions.

Interpretation of GlyR localization in the context of nanodomains. The distribution of GlyR molecules on inhibitory synapses appears to be non-homogeneous, instead forming nanoclusters or nanodomains, similar to many other synaptic proteins. It is important to interpret GlyR localization in the context of nanodomain organization.

The dSTORM images in Fig. 2 are pointillist representations that show individual detections rather than molecules. Small clusters of detections are likely to originate from a single AF647 fluorophore (in the case of nanobody labelling) and therefore represent single GlyRb subunits. Since GlyR copy numbers are so low at hippocampal synapses (≤ 5), the notion of nanodomain is not directly applicable. Our analysis therefore focused on the integration of GlyRs within the postsynaptic scaffold, rather than attempting to define nanodomain structures (see also response to point 8 of R1). A clarification has been added in the revised manuscript (p. 6).

__Reviewer #1 (Significance (Required)): __

The paper presents biological and technical advances. The biological insights revolve mostly on the documentation of Glycine receptors in particular synapses in forebrain, where they are typically expressed at very low levels. The authors provide compelling data indicating that the expression is of physiological significance. The authors have done a nice job of combining genetically-tagged mice with advanced microscopy methods to tackle the question of distributions of synaptic proteins. Overall these advances are more incremental than groundbreaking.

We thank the reviewer for acknowledging both the technical and biological advances of our study. While we recognize that our work builds upon established models, we consider that it also addresses important unresolved questions, namely that GlyRs are present and specifically anchored at inhibitory synapses in telencephalic regions, such as the hippocampus and striatum. From a methodological point of view, our study demonstrates that SMLM can be applied not only for structural analysis of highly abundant proteins, but also to reliably detect proteins present at very low copy numbers. This ability to identify and quantify sparse molecule populations adds a new dimension to SMLM applications, which we believe increases the overall impact of our study beyond the field of synaptic neuroscience.

__Reviewer #2 (Evidence, reproducibility and clarity (Required)): __

In their manuscript "Single molecule counting detects low-copy glycine receptors in hippocampal and striatal synapses" Camuso and colleagues apply single molecule localization microscopy (SMLM) methods to visualize low copy numbers of GlyRs at inhibitory synapses in the hippocampal formation and the striatum. SMLM analysis revealed higher copy numbers in striatum compared to hippocampal inhibitory synapses. They further provide evidence that these low copy numbers are tightly linked to post-synaptic scaffolding protein gephyrin at inhibitory synapses. Their approach profits from the high sensitivity and resolution of SMLM and challenges the controversial view on the presence of GlyRs in these formations although there are reports (electrophysiology) on the presence of GlyRs in these particular brain regions. These new datasets in the current manuscript may certainly assist in understanding the complexity of fundamental building blocks of inhibitory synapses.

However I have some minor points that the authors may address for clarification:

1) In Figure 1 the authors apply PALM imaging of mEos4b-GlyRß (knockin) and here the corresponding Sylite label seems to be recorded in widefield, it is not clearly stated in the figure legend if it is widefield or super-resolved. In Fig 1 A - is the scale bar 5 µm? Some Sylite spots appear to be sized around 1 µm, especially the brighter spots, but maybe this is due to the lower resolution of widefield imaging? Regarding the statistical comparison: what method was chosen to test for normality distribution, I think this point is missing in the methods section.

*This is correct; the apparent size of the Sylite spots does not reflect the real size of the synaptic gephyrin domain due to the limited resolution of widefield imaging including the detection of out-of-focus light. We have clarified in the legend of Fig. 1A that Sylite labelling was with classic epifluorescence microscopy. The scale bar in Fig. 1A corresponds to 5 µm. Since the data were not normally distributed, nonparametric tests (Kruskal- Wallis one-way ANOVA with Dunn’s multiple comparison test or Mann-Whitney U-test for pairwise comparisons) were used (p. 23). *

Moreover I would appreciate a clarification and/or citation that the knockin model results in no structural and physiological changes at inhibitory synapses, I believe this model has been applied in previous studies and corresponding clarification can be provided.

The Glrbeos/eos mouse model has been described previously and does not exhibit any structural or physiological phenotypes (Maynard et al. 2021 eLife). The issue was also raised by reviewer R1 (point 5) and has been clarified in the revised manuscript (p. 4).

2) In the next set of experiments the authors switch to demixing dSTORM experiments - an explanation why this is performed is missing in the text - I guess better resolution to perform more detailed distance measurements? For these experiments: which region of the hippocampus did the authors select, I cannot find this information in legend or main text.

Yes, the dSTORM experiments enable dual-colour structural analysis at high spatial resolution (see response to R1 point 7). An explanation has been added (p. 6).

3) Regarding parameters of demixing experiments: the number of frames (10.000) seems quite low and the exposure time higher than expected for Alexa 647. Can the authors explain the reason for chosing these particular parameters (low expression profile of the target - so better separation?, less fluorophores on label and shorter collection time?) or is there a reference that can be cited? The laser power is given in the methods in percentage of maximal output power, but for better comparison and reproducibility I recommend to provide the values of a power meter (kW/cm2) as lasers may change their maximum output power during their lifetime.

Acquisition parameters (laser power, exposure time) for dSTORM were chosen to obtain a good localisation precision (~12 nm; see R1 point 8). The number of frames is adequate to obtain well sampled gephyrin scaffolds in the CF680 channel. In the case of the GlyR (nanobody-AF647), the concept of spatial resolution does not really apply due to the low number of targets (see R1, point 13). Power density (irradiance) values have now been given (pp. 18, 21).

4) For analysis of subsynaptic distribution: how did the authors decide to choose the parameters in the NEO software for DBSCAN clustering - was a series of parameters tested to find optimal conditions and did the analysis start with an initial test if data is indeed clustered (K-ripley) or is there a reference in literature that can be provided?

DBSCAN parameters were optimised manually, by testing different values. Identification of dense and well-delimited gephyrin clusters (CF680) was achieved with a small radius and a high number of detections (80 nm, ≥ 50 neighbours), whereas filtering of low-density background in the AF647 channel (GlyRs) required less stringent parameters (200 nm, ≥ 5) due to the low number of target molecules. Similar parameters were used in a previous publication (Khayenko et al. 2022, Angewandte Chemie). The reference has been provided on p. 22 (see also R1 point 9).

5) A conclusion/discussion of the results presented in Figure 5 is missing in the text/discussion.

*This part of the manuscript has been completely overhauled. It includes new experimental data, quantification of the data (new Fig.5), as well as the discussion and interpretation of our findings (see also R1, point 3). In agreement with our earlier interpretation, the data confirm that low availability of GlyRa1 subunits limits the expression and synaptic targeting of GlyRa1/b heteropentamers. The observation that GlyRa1 overexpression with lentivirus increases the size of the postsynaptic gephyrin domain further points to a structural role, whereby GlyRs can enhance the stability (and size) of inhibitory synapses in hippocampal neurons, even at low copy numbers (pp. 13-14). *

6) in line 552 "suspension" is misleading, better use "solution"

Done.

__Reviewer #2 (Significance (Required)): __

Significance: The manuscript provides new insights to presence of low-copy numbers by visualizing them via SMLM. This is the first report that visualizes GlyR optically in the brain applying the knock-in model of mEOS4b tagged GlyRß and quantifies their copy number comparing distribution and amount of GlyRs from hippocampus and striatum. Imaging data correspond well to electrophysiological measurements in the manuscript.

Field of expertise: Super-Resolution Imaging and corresponding analysis

__Reviewer #4 (Evidence, reproducibility and clarity (Required)): __

In this study, Camuso et al., make use of a knock-in mouse model expressing endogenously mEos4b-tagged GlyRβ to detect endogenous glycine receptors using single-molecule localization microscopy. The main conclusion from this study is that in the hippocampus GlyRβ molecules are barely detected, while inhibitory synapses in the ventral striatum seem to express functionally relevant GlyR numbers.

I have a few points that I hope help to improve the strength of this study.

• In the hippocampus, this study finds that the numbers of detections are very low. The authors perform adequate controls to indicate that these localizations are above noise level. Nevertheless, it remains questionable that these reflect proper GlyRs. The suggestion that in hippocampal synapses the low numbers of GlyRβ molecules "are important in assembly or maintenance of inhibitory synaptic structures in the brain" is on itself interesting, but is not at all supported. It is also difficult to envision how such low numbers could support the structure of a synapse. A functional experiment showing that knockdown of GlyRs affects inhibitory synapse structure in hippocampal neurons would be a minimal test of this.

*It is not clear what the reviewer means by “it remains questionable that these reflect proper GlyRs”. The PALM experiments include a series of stringent controls (see R1, point 1) demonstrating the existence of low-copy GlyRs at inhibitory synapses in the hippocampus (Fig. 1) and in the striatum (Fig. 3), and are backed up by dSTORM experiments (Fig. 2). We have no reason to doubt that these receptors are fully functional (as demonstrated for the ventral striatum (Fig. 4). However, due to their low number, a role in inhibitory synaptic transmission is clearly limited, at least in the hippocampus and dorsal striatum. *

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We therefore propose a structural role, where the GlyRs could be required to stabilise the postsynaptic gephyrin domain in hippocampal neurons. This is based on the idea that the GlyR-gephyrin affinity is much higher than that of the GABAAR-gephyrin interaction (reviewed in Kasaragod & Schindelin 2018 Front Mol Neurosci). Accordingly, there is a close relationship between GlyRs and gephyrin numbers, sub-synaptic distribution, and dynamics in spinal cord synapses that are mostly glycinergic (Specht et al. 2013 Neuron; Maynard et al. 2021 eLife; Chapdelaine et al. 2021 Biophys J). It is reasonable to assume that low-copy GlyRs could play a similar structural role at hippocampal synapses. A knockdown experiment targeting these few receptors is technically very challenging and beyond the scope of this study. However, in response to the reviewer's question we have conducted new experiments in cultured hippocampal neurons (new__ Fig. 5__). They demonstrate that overexpression of GlyRa1/b heteropentamers increases the size of the postsynaptic domain in these neurons, supporting our interpretation of a structural role of low-copy GlyRs (p. 14).

• The endogenous tagging strategy is a very strong aspect of this study and provides confidence in the labeling of GlyRβ molecules. One caveat however, is that this labeling strategy does not discriminate whether GlyRβ molecules are on the cell membrane or in internal compartments. Can the authors provide an estimate of the ratio of surface to internal GlyRβ molecules?

Gephyrin is known to form a two-dimensional scaffold below the synaptic membrane to which inhibitory GlyRs and GABAARs attach (reviewed in Alvarez 2017 Brain Res). The majority of the synaptic receptors are therefore thought to be located in the synaptic membrane, which is supported by the close relationship between the sub-synaptic distribution of GlyRs and gephyrin in spinal cord neurons (e.g. Maynard et al. 2021 eLife). To demonstrate the surface expression of GlyRs at hippocampal synapses we labelled cultured hippocampal neurons expressing mEos4b-GlyRa1 with anti-Eos nanobody in non-permeabilised neurons (see Figure below for the reviewer only). The close correspondence between the nanobody (AF647) and the mEos4b signal confirms that the majority of the GlyRs are indeed located in the synaptic membrane.

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Figure (for the reviewer only).* Left: Lentivirus expression of mEos4b-GlyRa1 in fixed and non-permeabilised hippocampal neurons (mEos4b signal). Right: Surface labelling of the recombinant subunit with anti-Eos nanoboby (AF647). *

• 'We also estimated the absolute number of GlyRs per synapse in the hippocampus. The number of mEos4b detections was converted into copy numbers by dividing the detections at synapses by the average number of detections of individual mEos4b-GlyRβ containing receptor complexes'. In essence this is a correct method to estimate copy numbers, and the authors discuss some of the pitfalls associated with this approach (i.e., maturation of fluorophore and detection limit). Nevertheless, the authors did not subtract the number of background localizations determined in the two negative control groups. This is critical, particularly at these low-number estimations.

We fully agree that background subtraction can be useful with low detection numbers. In the revised manuscript, copy numbers are now reported as background-corrected values. Specifically, the mean number of detections measured in wildtype slices was used to calculate an equivalent receptor number, which was then subtracted from the copy number estimates across hippocampus, spinal cord and striatum. This procedure is described in the methods (p. 20) and results (p. 5, 8), and mentioned in the figure legends of Fig. 1C, 3C. The background corrected values are given in the text and Table 1.

Furthermore, the authors state that "The advantage of this estimation is that it is independent of the stoichiometry of heteropentameric GlyRs". However, if the stoichometry is unknown, the number of counted GlyRβ subunits cannot simply be reported as the number of GlyRs. This should be discussed in more detail, and more carefully reported throughout the manuscript.

*The reviewer is right to point this out. There is still some debate about the stoichiometry of heteropentameric GlyRs. Configurations with 2a:3b, 3a:2b and 4a:1b subunits have been advanced (e.g. Grudzinska et al. 2005 Neuron; Durisic et al. 2012 J Neurosci; Patrizio et al. 2017 Sci Rep; Zhu & Gouaux 2021 Nature). We have therefore chosen a quantification that is independent of the underlying stoichiometry. Since our quantification is based on very sparse clusters of mEos4b detections that likely originate from a single receptor complex (irrespective of its stoichiometry), the reported values actually reflect the number of GlyRs (and not GlyRb subunits). We have clarified this in the results (p. 5) and throughout the manuscript (Table 1). *

• The dual-color imaging provides insights in the subsynaptic distribution of GlyRβ molecules in hippocampal synapses. Why are similar studies not performed on synapses in the ventral striatum where functionally relevant numbers of GlyRβ molecules are found? Here insights in the subsynaptic receptor distribution would be of much more interest as it can be tight to the function.

This is an interesting suggestion. However, the primary aim of our study was to identify the existence of GlyRs in hippocampal regions. At low copy numbers, the concept of sub-synaptic domains (SSDs, e.g. Yang et al. 2021 EMBO Rep) becomes irrelevant (see R1 point 13). It should be pointed out that the dSTORM pointillist images (Fig. 2A) represent individual GlyR detections rather than clusters of molecules. In the striatum, our specific purpose was to solve an open question about the presence of GlyRs in different subregions (putamen, nucleus accumbens).

• It is unclear how the experiments in Figure 5 add to this study. These results are valid, but do not seem to directly test the hypothesis that "the expression of α subunits may be limiting factor controlling the number of synaptic GlyRs". These experiments simply test if overexpressed α subunits can be detected. If the α subunits are limiting, measuring the effect of α subunit overexpression on GlyRβ surface expression would be a more direct test.

Both R1 and R2 have also commented on the data in Fig. 5 and their interpretation. We have substantially revised this section as described before (see R1 point 3) including additional experiments and quantification of the data (new Fig. 5). The findings lend support to our earlier hypothesis that GlyR alpha subunits (in particular GlyRa1) are the limiting factor for the expression of heteropentameric GlyRa/b in hippocampal neurons (pp. 13-14). Since the GlyRa1 subunit itself does not bind to gephyrin (Patrizio et al. 2017 Sci Rep), the synaptic localisation of the recombinant mEos4b-GlyRa1 subunits is proof that they have formed heteropentamers with endogenous GlyRb subunits and driven their membrane trafficking, which the GlyRb subunits are incapable of doing on their own.

__Reviewer #4 (Significance (Required)): __

These results are based on carefully performed single-molecule localization experiments, and are well-presented and described. The knockin mouse with endogenously tagged GlyRβ molecules is a very strong aspect of this study and provides confidence in the labeling, the combination with single-molecule localization microscopy is very strong as it provides high sensitivity and spatial resolution.

The conceptual innovation however seems relatively modest, these results confirm previous studies but do not seem to add novel insights. This study is entirely descriptive and does not bring new mechanistic insights.

This study could be of interest to a specialized audience interested in glycine receptor biology, inhibitory synapse biology and super-resolution microscopy.

my expertise is in super-resolution microscopy, synaptic transmission and plasticity

As we have stated before, the novelty of our study lies in the use of SMLM for the identification of very small numbers of molecules, which requires careful control experiments. This is something that has not been done before and that can be of interest to a wider readership, as it opens up SMLM for ultrasensitive detection of rare molecular events. Using this approach, we solve two open scientific questions: (1) the demonstration that low-copy GlyRs are present at inhibitory synapses in the hippocampus, (2) the sub-region specific expression and functional role of GlyRs in the ventral versus dorsal striatum.

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The following review was provided later under the name “Reviewer #4”. To avoid confusion with the last reviewer from above we will refer to this review as R4-2.

__Reviewer #4-2 (Evidence, reproducibility and clarity (Required)): __

Summary:

Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate).

The authors investigate the presence of synaptic glycine receptors in the telencephalon, whose presence and function is poorly understood.

Using a transgenically labeled glycine receptor beta subunit (Glrb-mEos4b) mouse model together with super-resolution microscopy (SLMM, dSTORM), they demonstrate the presence of a low but detectable amount of synaptically localized GLRB in the hippocampus. While they do not perform a functional analysis of these receptors, they do demonstrate that these subunits are integrated into the inhibitory postsynaptic density (iPSD) as labeled by the scaffold protein gephyrin. These findings demonstrate that a low level of synaptically localized glycerine receptor subunits exist in the hippocampal formation, although whether or not they have a functional relevance remains unknown.

They then proceed to quantify synaptic glycine receptors in the striatum, demonstrating that the ventral striatum has a significantly higher amount of GLRB co-localized with gephyrin than the dorsal striatum or the hippocampus. They then recorded pharmacologically isolated glycinergic miniature inhibitory postsynaptic currents (mIPSCs) from striatal neurons. In line with their structural observations, these recordings confirmed the presence of synaptic glycinergic signaling in the ventral striatum, and an almost complete absence in the dorsal striatum. Together, these findings demonstrate that synaptic glycine receptors in the ventral striatum are present and functional, while an important contribution to dorsal striatal activity is less likely.

Lastly, the authors use existing mRNA and protein datasets to show that the expression level of GLRA1 across the brain positively correlates with the presence of synaptic GLRB.

The authors use lentiviral expression of mEos4b-tagged glycine receptor alpha1, alpha2, and beta subunits (GLRA1, GLRA1, GLRB) in cultured hippocampal neurons to investigate the ability of these subunits to cause the synaptic localization of glycine receptors. They suggest that the alpha1 subunit has a higher propensity to localize at the inhibitory postsynapse (labeled via gephyrin) than the alpha2 or beta subunits, and may therefore contribute to the distribution of functional synaptic glycine receptors across the brain.

Major comments:

• Are the key conclusions convincing?

The authors are generally precise in the formulation of their conclusions.

• They demonstrate a very low, but detectable, amount of a synaptically localized glycine receptor subunit in a transgenic (GlrB-mEos4b) mouse model. They demonstrate that the GLRB-mEos4b fusion protein is integrated into the iPSD as determined by gephyrin labelling. The authors do not perform functional tests of these receptors and do not state any such conclusions.
• The authors show that GLRB-mEos4b is clearly detectable in the striatum and integrated into gephyrin clusters at a significantly higher rate in the ventral striatum compared to the dorsal striatum, which is in line with previous studies.
• Adding to their quantification of GLRB-mEos4b in the striatum, the authors demonstrate the presence of glycinergic miniature IPSCs in the ventral striatum, and an almost complete absence of mIPSCs in the dorsal striatum. These currents support the observation that GLRB-mEos4b is more synaptically integrated in the ventral striatum compared to the dorsal striatum.

• The authors show that lentiviral expression of GLRA1-mEos4b leads to a visually higher number of GLR clusters in cultured hippocampal neurons, and a co-localization of some clusters with gephyrin. The authors claim that this supports the idea that GLRA1 may be an important driver of synaptic glycine receptor localization. However, no quantification or statistical analysis of the number of puncta or their colocalization with gephyrin is provided for any of the expressed subunits. Such a claim should be supported by quantification and statistics A thorough analysis and quantification of the data in Fig.5 has been carried out as requested by all the other reviewers (e.g. R1, point 3). The new data and results have been described in the revised manuscript (pp. 9-10, 13-14).

• Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

One unaddressed caveat is the fact that a GLRB-mEos4b fusion protein may behave differently in terms of localization and synaptic integration than wild-type GLRB. While unlikely, it is possible that mEos4b interacts either with itself or synaptic proteins in a way that changes the fused GLRB subunit’s localization. Such an effect would be unlikely to affect synaptic function in a measurable way, but might be detected at a structural level by highly sensitive methods such as SMLM and STORM in regions with very low molecule numbers (such as the hippocampus). Since reliable antibodies against GLRB in brain tissue sections are not available, this would be difficult to test. Considering that no functional measures of the hippocampal detections exist, we would suggest that this possible caveat be mentioned for this particular experiment.

*This question has also been raised before (R1, point 5). According to an earlier study the mEos4b-GlyRb knock-in does not cause any obvious phenotypes, with the possible exception of minor loss of glycine potency (Maynard et al. 2021 eLife). The fact that the synaptic levels in the spinal cord in heterozygous animals are precisely half of those of homozygous animals argues against differences in receptor expression, heteropentameric assembly, forward trafficking to the plasma membrane and integration into the synaptic membrane as confirmed using quantitative super-resolution CLEM (Maynard et al. 2021 eLife). Accordingly, we did not observe any behavioural deficits in these animals, making it a powerful experimental model. We have added this information in the revised manuscript (p. 4). *

In addition, without any quantification or statistical analysis, the author’s claims regarding the necessity of GLRA1 expression for the synaptic localization of glycine receptors in cultured hippocampal neurons should probably be described as preliminary (Fig. 5).

As mentioned before, we have substantially revised this part (R1, point 3). The quantification and analysis in the new Fig. 5 support our earlier interpretation.

• 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.

The authors show that there is colocalization of gephyrin with the mEos4b-GlyRβ subunit using the Dual-colour SMLM. This is a powerful approach that allows for a claim to be made on the synaptic location of the glycine receptors. The images presented in Figure 1, together with the distance analysis in Figure 2, display the co-localization of the fluorophores. The co-localization images in all the selected regions, hippocampus and striatum, also show detections outside of the gephyrin clusters, which the authors refer to as extrasynaptic. These punctated small clusters seem to have the same size as the ones detected and assigned as part of the synapse. It would be informative if the authors analysed the distribution, density and size of these non-synaptic clusters and presented the data in the manuscript and also compared it against the synaptic ones. Validating this extrasynaptic signal by staining for a dendritic marker, such as MAP-2 or maybe a somatic marker and assessing the co-localization with the non-synaptic clusters would also add even more credibility to them being extrasynaptic.

The existence of extrasynaptic GlyRs is well attested in spinal cord neurons (e.g. Specht et al. 2013 Neuron; this study see Fig. S2). The fact that these appear as small clusters of detections in SMLM recordings results from the fact that a single fluorophore can be detected several times in consecutive image frames and because of blinking. Therefore, small clusters of detections likely represent single GlyRs (that can be counted), and not assemblies of several receptor complexes. Due to their diffusion in the neuronal membrane, they are seen as diffuse signals throughout the somatodendritic compartment in epifluorescence images (e.g. Fig. 5A). SMLM recordings of the same cells resolves this diffuse signal into discrete nanoclusters representing individual receptors (Fig. 5B). It is not clear what information co-localisation experiments with specific markers could provide, especially in hippocampal neurons, in which the copy numbers (and density) of GlyRs is next to zero.

In addition we would encourage the authors to quantify the clustering and co-localization of virally expressed GLRA1, GLRA2, and GLRB with gephyrin in order to support the associated claims (Fig. 5). Preferably, the density of GLR and gephyrin clusters (at least on the somatic surface, the proximal dendrites, or both) as well as their co-localization probability should be quantified if a causal claim about subunit-specific requirements for synaptic localization is to be made.

Quantification of the data have been carried out (new Fig.5C,D). The results have been described before (R1, point 3) and support our earlier interpretation of the data (pp. 13-14).

Lastly, even though it may be outside of the scope of such a study analysing other parts of the hippocampal area could provide additional important information. If one looks at the Allen Institute’s ISH of the beta subunit the strongest signal comes from the stratum oriens in the CA1 for example, suggesting that interneurons residing there would more likely have a higher expression of the glycine receptors. This could also be assessed by looking more carefully at the single cell transcriptomics, to see which cell types in the hippocampus show the highest mRNA levels. If the authors think that this is too much additional work, then perhaps a mention of this in the discussion would be good.

We have added the requested information from the ISH database of the Allen Institute in the discussion as suggested by the reviewer (p. 12). However, in combination with the transcriptomic data (Fig. S1) our finding strongly suggest that the expression of synaptic GlyRs depends on the availability of alpha subunits rather than on the presence of the GlyRb transcript. This is obvious when one compares the mRNA levels in the hippocampus with those in the basal ganglia (striatum) and medulla. While the transcript concentrations of GlyRb are elevated in all three regions and essentially the same, our data show that the GlyRb copy numbers *at synapses differ over more than 2 orders of magnitude (Fig. 1B, Table 1). *

• 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.

Since the labeling and some imaging has been performed already, the requested experiment would be a matter of deploying a method of quantification. In principle, it should not require any additional wet-lab experiments, although it may require additional imaging of existing samples.

• Are the data and the methods presented in such a way that they can be reproduced?

Yes, for the most part.

• Are the experiments adequately replicated and statistical analysis adequate?

Yes

Minor comments:

• Specific experimental issues that are easily addressable.

N/A

• Are prior studies referenced appropriately?

Yes

• Are the text and figures clear and accurate?

Yes, although quantification in figure 5 is currently not present.

A quantification has been added (see R1, point 3).

• Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

This paper presents a method that could be used to localize receptors and perhaps other proteins that are in low abundance or for which a detailed quantification is necessary. I would therefore suggest that Figure S4 is included into Figure 2 as the first panel, showcasing the demixing, followed by the results.

We agree in principle with this suggestion. However, the revised Fig. S4 is more complex and we think that it would distract from the data shown in Fig. 2. Given that Fig. S4 is mostly methodological and not essential to understand the text, we have kept it in the supplement for the time being. We leave the final decision on this point to the editor.

__Reviewer #4-2 (Significance (Required)): __

[This review was supplied later]

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.

Using a novel and high resolution method, the authors have provided strong evidence for the presence of glycine receptors in the murine hippocampus and in the dorsal striatum. The number of receptors calculated is small compared to the numbers found in the ventral striatum. This is the first study to quantify receptor numbers in these region. In addition it also lays a roadmap for future studies addressing similar questions.

• Place the work in the context of the existing literature (provide references, where appropriate).

This is done well by the authors in the curation of the literature. As stated above, the authors have filled a gap in the presence of glycine receptors in different brain regions, a subject of importance in understanding the role they play in brain activity and function.

• State what audience might be interested in and influenced by the reported findings.

Neuroscientists working at the synaptic level, on inhibitory neurotransmission and on fundamental mechanisms of expression of genes at low levels and their relationship to the presence of the protein would be interested. Furthermore, researchers in neuroscience and cell biology may benefit from and be inspired by the approach used in this manuscript, to potentially apply it to address their own aims.

*We thank the reviewer for the positive assessment of the technical and biological implications of our work, as well as the interest of our findings to a wide readership of neuroscientists and cell biologists. *

• 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.

Synaptic transmission, inhibitory cells and GABAergic synapses functionally and structurally, cortex and cortical circuits. No strong expertise in super-resolution imaging methods.

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Referee #4

Evidence, reproducibility and clarity

Summary: Provide a short summary of the findings and key conclusions (including methodology and model system(s) where appropriate).

The authors investigate the presence of synaptic glycine receptors in the telencephalon, whose presence and function is poorly understood.

Using a transgenically labeled glycine receptor beta subunit (Glrb-mEos4b) mouse model together with super-resolution microscopy (SLMM, dSTORM), they demonstrate the presence of a low but detectable amount of synaptically localized GLRB in the hippocampus. While they do not perform a functional analysis of these receptors, they do demonstrate that these subunits are integrated into the inhibitory postsynaptic density (iPSD) as labeled by the scaffold protein gephyrin. These findings demonstrate that a low level of synaptically localized glycerine receptor subunits exist in the hippocampal formation, although whether or not they have a functional relevance remains unknown.

They then proceed to quantify synaptic glycine receptors in the striatum, demonstrating that the ventral striatum has a significantly higher amount of GLRB co-localized with gephyrin than the dorsal striatum or the hippocampus. They then recorded pharmacologically isolated glycinergic miniature inhibitory postsynaptic currents (mIPSCs) from striatal neurons. In line with their structural observations, these recordings confirmed the presence of synaptic glycinergic signaling in the ventral striatum, and an almost complete absence in the dorsal striatum. Together, these findings demonstrate that synaptic glycine receptors in the ventral striatum are present and functional, while an important contribution to dorsal striatal activity is less likely.

Lastly, the authors use existing mRNA and protein datasets to show that the expression level of GLRA1 across the brain positively correlates with the presence of synaptic GLRB. The authors use lentiviral expression of mEos4b-tagged glycine receptor alpha1, alpha2, and beta subunits (GLRA1, GLRA1, GLRB) in cultured hippocampal neurons to investigate the ability of these subunits to cause the synaptic localization of glycine receptors. They suggest that the alpha1 subunit has a higher propensity to localize at the inhibitory postsynapse (labeled via gephyrin) than the alpha2 or beta subunits, and may therefore contribute to the distribution of functional synaptic glycine receptors across the brain.

Major comments: - Are the key conclusions convincing?

The authors are generally precise in the formulation of their conclusions.

1) They demonstrate a very low, but detectable, amount of a synaptically localized glycine receptor subunit in a transgenic (GlrB-mEos4b) mouse model. They demonstrate that the GLRB-mEos4b fusion protein is integrated into the iPSD as determined by gephyrin labelling. The authors do not perform functional tests of these receptors and do not state any such conclusions. 2) The authors show that GLRB-mEos4b is clearly detectable in the striatum and integrated into gephyrin clusters at a significantly higher rate in the ventral striatum compared to the dorsal striatum, which is in line with previous studies. 3) Adding to their quantification of GLRB-mEos4b in the striatum, the authors demonstrate the presence of glycinergic miniature IPSCs in the ventral striatum, and an almost complete absence of mIPSCs in the dorsal striatum. These currents support the observation that GLRB-mEos4b is more synaptically integrated in the ventral striatum compared to the dorsal striatum. 4) The authors show that lentiviral expression of GLRA1-mEos4b leads to a visually higher number of GLR clusters in cultured hippocampal neurons, and a co-localization of some clusters with gephyrin. The authors claim that this supports the idea that GLRA1 may be an important driver of synaptic glycine receptor localization. However, no quantification or statistical analysis of the number of puncta or their colocalization with gephyrin is provided for any of the expressed subunits. Such a claim should be supported by quantification and statistics

• Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

One unaddressed caveat is the fact that a GLRB-mEos4b fusion protein may behave differently in terms of localization and synaptic integration than wild-type GLRB. While unlikely, it is possible that mEos4b interacts either with itself or synaptic proteins in a way that changes the fused GLRB subunit's localization. Such an effect would be unlikely to affect synaptic function in a measurable way, but might be detected at a structural level by highly sensitive methods such as SMLM and STORM in regions with very low molecule numbers (such as the hippocampus). Since reliable antibodies against GLRB in brain tissue sections are not available, this would be difficult to test. Considering that no functional measures of the hippocampal detections exist, we would suggest that this possible caveat be mentioned for this particular experiment.

In addition, without any quantification or statistical analysis, the author's claims regarding the necessity of GLRA1 expression for the synaptic localization of glycine receptors in cultured hippocampal neurons should probably be described as preliminary (Fig. 5).

• 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.

The authors show that there is colocalization of gephyrin with the mEos4b-GlyRβ subunit using the Dual-colour SMLM. This is a powerful approach that allows for a claim to be made on the synaptic location of the glycine receptors. The images presented in Figure 1, together with the distance analysis in Figure 2, display the co-localization of the fluorophores. The co-localization images in all the selected regions, hippocampus and striatum, also show detections outside of the gephyrin clusters, which the authors refer to as extrasynaptic. These punctated small clusters seem to have the same size as the ones detected and assigned as part of the synapse. It would be informative if the authors analysed the distribution, density and size of these non-synaptic clusters and presented the data in the manuscript and also compared it against the synaptic ones. Validating this extrasynaptic signal by staining for a dendritic marker, such as MAP-2 or maybe a somatic marker and assessing the co-localization with the non-synaptic clusters would also add even more credibility to them being extrasynaptic.

In addition we would encourage the authors to quantify the clustering and co-localization of virally expressed GLRA1, GLRA2, and GLRB with gephyrin in order to support the associated claims (Fig. 5). Preferably, the density of GLR and gephyrin clusters (at least on the somatic surface, the proximal dendrites, or both) as well as their co-localization probability should be quantified if a causal claim about subunit-specific requirements for synaptic localization is to be made.

Lastly, even though it may be outside of the scope of such a study analysing other parts of the hippocampal area could provide additional important information. If one looks at the Allen Institute's ISH of the beta subunit the strongest signal comes from the stratum oriens in the CA1 for example, suggesting that interneurons residing there would more likely have a higher expression of the glycine receptors. This could also be assessed by looking more carefully at the single cell transcriptomics, to see which cell types in the hippocampus show the highest mRNA levels. If the authors think that this is too much additional work, then perhaps a mention of this in the discussion would be good.

• 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.

Since the labeling and some imaging has been performed already, the requested experiment would be a matter of deploying a method of quantification. In principle, it should not require any additional wet-lab experiments, although it may require additional imaging of existing samples.

• Are the data and the methods presented in such a way that they can be reproduced?

Yes, for the most part.

• Are the experiments adequately replicated and statistical analysis adequate?

Yes

Minor comments: - Specific experimental issues that are easily addressable.

N/A

• Are prior studies referenced appropriately?

Yes

• Are the text and figures clear and accurate?

Yes, although quantification in figure 5 is currently not present.

• Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

This paper presents a method that could be used to localize receptors and perhaps other proteins that are in low abundance or for which a detailed quantification is necessary. I would therefore suggest that Figure S4 is included into Figure 2 as the first panel, showcasing the demixing, followed by the results.

Significance

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.

Using a novel and high resolution method, the authors have provided strong evidence for the presence of glycine receptors in the murine hippocampus and in the dorsal striatum. The number of receptors calculated is small compared to the numbers found in the ventral striatum. This is the first study to quantify receptor numbers in these region. In addition it also lays a roadmap for future studies addressing similar questions.

• Place the work in the context of the existing literature (provide references, where appropriate).

This is done well by the authors in the curation of the literature. As stated above, the authors have filled a gap in the presence of glycine receptors in different brain regions, a subject of importance in understanding the role they play in brain activity and function.

• State what audience might be interested in and influenced by the reported findings.

Neuroscientists working at the synaptic level, on inhibitory neurotransmission and on fundamental mechanisms of expression of genes at low levels and their relationship to the presence of the protein would be interested. Furthermore, researchers in neuroscience and cell biology may benefit from and be inspired by the approach used in this manuscript, to potentially apply it to address their own aims.

• 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.

Synaptic transmission, inhibitory cells and GABAergic synapses functionally and structurally, cortex and cortical circuits. No strong expertise in super-resolution imaging methods.

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Referee #3

Evidence, reproducibility and clarity

In this study, Camuso et al., make use of a knock-in mouse model expressing endogenously mEos4b-tagged GlyRβ to detect endogenous glycine receptors using single-molecule localization microscopy. The main conclusion from this study is that in the hippocampus GlyRβ molecules are barely detected, while inhibitory synapses in the ventral striatum seem to express functionally relevant GlyR numbers.

I have a few points that I hope help to improve the strength of this study.

• In the hippocampus, this study finds that the numbers of detections are very low. The authors perform adequate controls to indicate that these localizations are above noise level. Nevertheless, it remains questionable that these reflect proper GlyRs. The suggestion that in hippocampal synapses the low numbers of GlyRβ molecules "are important in assembly or maintenance of inhibitory synaptic structures in the brain" is on itself interesting, but is not at all supported. It is also difficult to envision how such low numbers could support the structure of a synapse. A functional experiment showing that knockdown of GlyRs affects inhibitory synapse structure in hippocampal neurons would be a minimal test of this.
• The endogenous tagging strategy is a very strong aspect of this study and provides confidence in the labeling of GlyRβ molecules. One caveat however, is that this labeling strategy does not discriminate whether GlyRβ molecules are on the cell membrane or in internal compartments. Can the authors provide an estimate of the ratio of surface to internal GlyRβ molecules?
• 'We also estimated the absolute number of GlyRs per synapse in the hippocampus. The number of mEos4b detections was converted into copy numbers by dividing the detections at synapses by the average number of detections of individual mEos4b-GlyRβ containing receptor complexes'. In essence this is a correct method to estimate copy numbers, and the authors discuss some of the pitfalls associated with this approach (i.e., maturation of fluorophore and detection limit). Nevertheless, the authors did not subtract the number of background localizations determined in the two negative control groups. This is critical, particularly at these low-number estimations. Furthermore, the authors state that "The advantage of this estimation is that it is independent of the stoichiometry of heteropentameric GlyRs". However, if the stoichometry is unknown, the number of counted GlyRβ subunits cannot simply be reported as the number of GlyRs. This should be discussed in more detail, and more carefully reported throughout the manuscript.
• The dual-color imaging provides insights in the subsynaptic distribution of GlyRβ molecules in hippocampal synapses. Why are similar studies not performed on synapses in the ventral striatum where functionally relevant numbers of GlyRβ molecules are found? Here insights in the subsynaptic receptor distribution would be of much more interest as it can be tight to the function.
• It is unclear how the experiments in Figure 5 add to this study. These results are valid, but do not seem to directly test the hypothesis that "the expression of α subunits may be limiting factor controlling the number of synaptic GlyRs". These experiments simply test if overexpressed α subunits can be detected. If the α subunits are limiting, measuring the effect of α subunit overexpression on GlyRβ surface expression would be a more direct test.

Significance

These results are based on carefully performed single-molecule localization experiments, and are well-presented and described. The knockin mouse with endogenously tagged GlyRβ molecules is a very strong aspect of this study and provides confidence in the labeling, the combination with single-molecule localization microscopy is very strong as it provides high sensitivity and spatial resolution.

The conceptual innovation however seems relatively modest, these results confirm previous studies but do not seem to add novel insights. This study is entirely descriptive and does not bring new mechanistic insights.

This study could be of interest to a specialized audience interested in glycine receptor biology, inhibitory synapse biology and super-resolution microscopy.

my expertise is in super-resolution microscopy, synaptic transmission and plasticity

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Referee #2

Evidence, reproducibility and clarity

In their manuscript "Single molecule counting detects low-copy glycine receptors in hippocampal and striatal synapses" Camuso and colleagues apply single molecule localization microscopy (SMLM) methods to visualize low copy numbers of GlyRs at inhibitory synapses in the hippocampal formation and the striatum. SMLM analysis revealed higher copy numbers in striatum compared to hippocampal inhibitory synapses. They further provide evidence that these low copy numbers are tightly linked to post-synaptic scaffolding protein gephyrin at inhibitory synapses. Their approach profits from the high sensitivity and resolution of SMLM and challenges the controversial view on the presence of GlyRs in these formations although there are reports (electrophysiology) on the presence of GlyRs in these particular brain regions. These new datasets in the current manuscript may certainly assist in understanding the complexity of fundamental building blocks of inhibitory synapses.

However I have some minor points that the authors may address for clarification:

1. In Figure 1 the authors apply PALM imaging of mEos4b-GlyRß (knockin) and here the corresponding Sylite label seems to be recorded in widefield, it is not clearly stated in the figure legend if it is widefield or super-resolved. In Fig 1 A - is the scale bar 5 µm? Some Sylite spots appear to be sized around 1 µm, especially the brighter spots, but maybe this is due to the lower resolution of widefield imaging? Regarding the statistical comparison: what method was chosen to test for normality distribution, I think this point is missing in the methods section. Moreover I would appreciate a clarification and/or citation that the knockin model results in no structural and physiological changes at inhibitory synapses, I believe this model has been applied in previous studies and corresponding clarification can be provided.
2. In the next set of experiments the authors switch to demixing dSTORM experiments - an explanation why this is performed is missing in the text - I guess better resolution to perform more detailed distance measurements? For these experiments: which region of the hippocampus did the authors select, I cannot find this information in legend or main text.
3. Regarding parameters of demixing experiments: the number of frames (10.000) seems quite low and the exposure time higher than expected for Alexa 647. Can the authors explain the reason for chosing these particular parameters (low expression profile of the target - so better separation?, less fluorophores on label and shorter collection time?) or is there a reference that can be cited? The laser power is given in the methods in percentage of maximal output power, but for better comparison and reproducibility I recommend to provide the values of a power meter (kW/cm2) as lasers may change their maximum output power during their lifetime.
4. For analysis of subsynaptic distribution: how did the authors decide to choose the parameters in the NEO software for DBSCAN clustering - was a series of parameters tested to find optimal conditions and did the analysis start with an initial test if data is indeed clustered (K-ripley) or is there a reference in literature that can be provided?
5. A conclusion/discussion of the results presented in Figure 5 is missing in the text/discussion.
6. in line 552 "suspension" is misleading, better use "solution"

Significance

Significance: The manuscript provides new insights to presence of low-copy numbers by visualizing them via SMLM. This is the first report that visualizes GlyR optically in the brain applying the knock-in model of mEOS4b tagged GlyRß and quantifies their copy number comparing distribution and amount of GlyRs from hippocampus and striatum. Imaging data correspond well to electrophysiological measurements in the manuscript.

Field of expertise: Super-Resolution Imaging and corresponding analysis

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Referee #1

Evidence, reproducibility and clarity

In this manuscript, the authors investigate the nanoscopic distribution of glycine receptor subunits in the hippocampus, dorsal striatum, and ventral striatum of the mouse brain using single-molecule localization microscopy (SMLM). They demonstrate that only a small number of glycine receptors are localized at hippocampal inhibitory synapses. Using dual-color SMLM, they further show that clusters of glycine receptors are predominantly localized within gephyrin-positive synapses. A comparison between the dorsal and ventral striatum reveals that the ventral striatum contains approximately eight times more glycine receptors and this finding is consistent with electrophysiological data on postsynaptic inhibitory currents. Finally, using cultured hippocampal neurons, they examine the differential synaptic localization of glycine receptor subunits (α1, α2, and β). This study is significant as it provides insights into the nanoscopic localization patterns of glycine receptors in brain regions where this protein is expressed at low levels. Additionally, the study demonstrates the different localization patterns of GlyR in distinct striatal regions and its physiological relevance using SMLM and electrophysiological experiments. However, several concerns should be addressed.

The following are specific comments:

1. Colocalization analysis in Figure 1A. The colocalization between Sylite and mEos-GlyRβ appears to be quite low. It is essential to assess whether the observed colocalization is not due to random overlap. The authors should consider quantifying colocalization using statistical methods, such as a pixel shift analysis, to determine whether colocalization frequencies remain similar after artificially displacing one of the channels.
2. Inconsistency between Figure 3A and 3B. While Figure 3B indicates an ~8-fold difference in the number of mEos4b-GlyRβ detections per synapse between the dorsal and ventral striatum, Figure 3A does not appear to show a pronounced difference in the localization of mEos4b-GlyRβ on Sylite puncta between these two regions. If the images presented in Figure 3A are not representative, the authors should consider replacing them with more representative examples or providing an expanded images with multiple representative examples. Alternatively, if this inconsistency can be explained by differences in spot density within clusters, the authors should explain that.
3. Quantification in Figure 5. It is recommended that the authors provide quantitative data on cluster formation and colocalization with Sylite puncta in Figure 5 to support their qualitative observations.
4. Potential for pseudo replication. It's not clear whether they're performing stats tests across biological replica, images, or even synapses. They often quote mean +/- SEM with n = 1000s, and so does that mean they're doing tests on those 1000s? Need to clarify.
5. Does mEoS effect expression levels or function of the protein? Can't see any experiments done to confirm this. Could suggest WB on homogenate, or mass spec?
6. Quantification of protein numbers is challenging with SMLM. Issues include i) some of FP not correctly folded/mature, and ii) dependence of localisation rate on instrument, excitation/illumination intensities, and also the thresholds used in analysis. Can the authors compare with another protein that has known expression levels- e.g. PSD95? This is quite an ask, but if they could show copy number of something known to compare with, it would be useful.
7. Rationale for doing nanobody dSTORM not clear at all. They don't explain the reason for doing the dSTORM experiments. Why not just rely on PALM for coincidence measurements, rather than tagging mEoS with a nanobody, and then doing dSTORM with that? Can they explain? Is it to get extra localisations- i.e. multiple per nanobody? If so, localising same FP multiple times wouldn't improve resolution. Also, no controls for nanobody dSTORM experiments- what about non-spec nb, or use on WT sections?
8. What resolutions/precisions were obtained in SMLM experiments? Should perform Fourier Ring Correlation (FRC) on SR images to state resolutions obtained (particularly useful for when they're presenting distance histograms, as this will be dependent on resolution). Likewise for precision, what was mean precision? Can they show histograms of localisation precision.
9. Why were DBSCAN parameters selected? How can they rule out multiple localisations per fluor? If low copy numbers (<10), then why bother with DBSCAN? Could just measure distance to each one.
10. For microscopy experiment methods, state power densities, not % or "nominal power".
11. In general, not much data presented. Any SI file with extra images etc.?
12. Clarification of the discussion on GlyR expression and synaptic localization: The discussion on GlyR expression, complex formation, and synaptic localization is sometimes unclear, and needs terminological distinctions between "expression level", "complex formation" and "synaptic localization". For example, the authors state:"What then is the reason for the low protein expression of GlyRβ? One possibility is that the assembly of mature heteropentameric GlyR complexes depends critically on the expression of endogenous GlyR α subunits." Does this mean that GlyRβ proteins that fail to form complexes with GlyRα subunits are unstable and subject to rapid degradation? If so, the authors should clarify this point. The statement "This raises the interesting possibility that synaptic GlyRs may depend specifically on the concomitant expression of both α1 and β transcripts." suggests a dependency on α1 and β transcripts. However, is the authors' focus on synaptic localization or overall protein expression levels? If this means synaptic localization, it would be beneficial to state this explicitly to avoid confusion. To improve clarity, the authors should carefully distinguish between these different aspects of GlyR biology throughout the discussion. Additionally, a schematic diagram illustrating these processes would be highly beneficial for readers.
13. Interpretation of GlyR localization in the context of nanodomains. The distribution of GlyR molecules on inhibitory synapses appears to be non-homogeneous, instead forming nanoclusters or nanodomains, similar to many other synaptic proteins. It is important to interpret GlyR localization in the context of nanodomain organization.

Significance

The paper presents biological and technical advances. The biological insights revolve mostly on the documentation of Glycine receptors in particular synapses in forebrain, where they are typically expressed at very low levels. The authors provide compelling data indicating that the expression is of physiological significance. The authors have done a nice job of combining genetically-tagged mice with advanced microscopy methods to tackle the question of distributions of synaptic proteins. Overall these advances are more incremental than groundbreaking.

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Reply to the reviewers

Manuscript number: RC-2025-03111

Corresponding author(s): Qingyin Qian and Ryusuke Niwa

1. General Statements [optional]

We would like to thank reviewers for their feedback on our initial submission. Changes in figures were noted in the point-to-point reply. For submission of our current revised manuscript, we provide two Word files, which are the “clean” and “Track-and-Change” files. Page and line numbers described below correspond to those of the “clean” file. The “Track-and-Change” file might be helpful for Reviewers to find what we have changed for the current revision.

In the revised manuscript, major changes in the text were tracked, while minor edits in figure numbers and legends were not tracked. In the Discussion, the section “Xrp1-mediated EE plasticity…” was moved before “Xrp1, a transcription factor …”, to follow the order of the Results, and was split into two: “EE plasticity …” and “Xrp1-mediated EE plasticity …”.

2. Description of the planned revisions

- The authors should investigate the regenerative growth of the adult midgut after irradiation. Is there an impact on ISCs proliferation or cell turn over. Is Xrp1 in EEs required in this adaptive response. It would be elegant to use the recently generated tracing method by Tobias Reiff lab to observe overall impact on tissue renewal (rapport-tracing esglexReDDM esg-lexA, 13xLexAop2-CD8::GFP, 13xLexAop2-H2B::mCherry::HA, tub-Gal80ts on the second chromosome. It can be combined with any EEs Gal4-driver (see Nat Commun 2025, https://doi.org/10.1038/s41467-024-55664-2, the stock is already existing, see table1). This reviewer thinks that it is a key experiment to support the proposed model.

2.1. Author response:

We will conduct the following experiments to answer these criticisms.

(1) We will investigate the ISC behavior, proliferation and differentiation, after 100 Gy of radiation by examining changes in the number of progenitor cells and their progenies, using esgtsF/O (esg-Gal4, UAS-GFP, tub-Gal80ts; Act>Cd2>Gal4, UAS-Flp) generated in the study (Jiang et al. Cell 2009 DOI: 10.1016/j.cell.2009.05.014) or esgReDDM (esg-Gal4, UAS-CD8::GFP; UAS-H2B::RFP, tubGal80ts) generated in the study (Antonello et al. EMBO J. 2015 DOI: 10.15252/embj.201591517). Flies will have progenitor cell lineages traced for 7 days, irradiated on day 6, and examined at different time points after radiation, following the design shown in Fig. 2A. Based on the previous findings (Sharma et al. Sci. Rep. 2020 DOI: 10.1038/s41598-020-75867-z; Pyo et al. Radiat. Res. 2014 DOI: 10.1667/RR13545.1), we anticipate that radiation compromises ISCs’ proliferation and differentiation. Should this be the case, our results can be interpreted in relation to those earlier studies.

(2) In parallel, we will examine whether Xrp1 expression in EEs affects radiation-induced ISC behaviors. As suggested, we will use “EE Rapport” (esg-lexA, 13xLexAop2-CD8::GFP, 13xLexAop2-H2B::mCherry::HA, tub-Gal80ts; Rab3-Gal4) generated in the study (Zipper et al. Nat. Commun. 2025 DOI: 10.1038/s41467-024-55664-2) and compare control flies to flies with Xrp1 knocked down in EEs to assess the impact on ISC behaviors.

- Is p53 required for Xrp1 induction in the gut after irradiation?

2.2. Author response:

To answer this point, we will perform immunostaining of anti-Xrp1 antibody to examine whether p53 is required for Xrp1 induction in irradiated flies with p53 knocked down in EEs.

- Xrp1 over expression has been shown to induce upd3 ligand and nutrient-driven dedifferentiation of enteroendocrine cells is occuring by activation of the JAK-STAT pathway (DOI: 10.1016/j.devcel.2023.08.022). Could the authors test the function of this signaling pathway during irradiation (upd3-lacZ and Stat-GFP can be used in parallel of upd3 RNAi and UAS Dome-DN.

2.3. Author response:

We will conduct the following experiments to answer these points.

(1) We will examine the cell type in which upd3 ligand induction occurs after radiation by using the upd3.1-LacZ reporter generated in the study (Jiang et al. Cell Stem Cell 2011 DOI: doi.org/10.1016/j.stem.2010.11.026).

(2) One possibility is that upd3.1-LacZ is detected in EEs. In this case, we will examine the requirement of upd3 in EEs for radiation-induced EE plasticity by knocking down upd3. Another possibility is that upd3.1-LacZ is detected in non-EE cells. If so, we will examine the requirement of the JAK-STAT pathway in EEs by overexpressing dome[△cyt] generated in the study (Brown et al. Curr. Biol. 2001 DOI: 10.1016/s0960-9822(01)00524-3) or knocking down Stat92E in EEs. Because these conditions are not mutually exclusive, both approaches may be pursued, with the latter relating our results to nutrient-driven EE dedifferentiation.

- Xrp1 is known for its role in cell competition and elimination of looser cells by induction of apoptosis. It would be interesting to check for induction of cell death and/or caspase activation in the fly gut after irradiation and verify a non apoptotic role of DRONC activation in this context using a Dronc RNAi (as proposed by Bergmann lab (https://doi.org/10.1038/s41598-021-81261-0) or Baena-Lopez lab (DOI: 10.15252/embr.201948892)). Overexpression of Xrp1 could be combined with UAS-p35.

2.4. Author response:

To address these points, we will investigate apoptosis induction following radiation with anti-cleaved Dcp-1 immunostaining. Based on the previous finding (Sharma et al. Sci. Rep. 2020 DOI: 10.1038/s41598-020-75867-z), we anticipate seeing increased cleaved Dcp-1 signals in all cell types after radiation. We intend to clarify whether radiation increases the ratio of apoptotic EEs among EEs; however, we cannot yet be certain whether it will be feasible.

Regarding Dronc activation, we previously requested the antibody used in the study (Wilson et al. Nat. Cell Biol. 2002 DOI: 10.1038/ncb799; Lindblad et al. Sci. Rep. 2021 DOI: 10.1038/s41598-021-81261-0) and tested it in our context, after radiation and by Xrp1-S O/E in EEs. We present our data below. In the anterior midgut, anti-Dronc signals were not observed under both control conditions. After radiation and by Xrp1-S O/E in EEs, anti-Dronc signals were seen in part of past EEs (#2 past) and progenitor cells (#3 prgn), implying their EB identity. However, anti-Dronc signals were never observed in current EEs (#1 current), suggesting Dronc does not act directly downstream to Xrp1.

We will address UAS-p35 in 3.3. Author response and Dronc-RNAi in 4.2. Author response.

- The authors do not justify or explain why they used 100 Gy of radiation. This is higher than doses used in comparable regeneration studies in adult Drosophila (e.g., PMID25959206, PMID: 28925355). The authors should clarify why this dose was chosen.

2.5. Author response:

Our initial rationale was based on the paper (Sharma et al. Sci. Rep. 2020 DOI: 10.1038/s41598-020-75867-z), where the authors claimed that ISC proliferation was inhibited and the ISC number was decreased by 100 Gy of radiation.

Nevertheless, we understand the reviewer’s concern and will examine 50 Gy of radiation as used in the papers the reviewer listed. We will examine radiation-induced changes in EE lineages and ISC behaviors. Depending on the results, we will evaluate whether and how they should be incorporated into the manuscript.

- Fig. 2C, the number of past EE’s increased transiently so that baseline number is restored at 18 hr after IR. The authors conclude that fate plasticity is a transient event. Can they rule out loss due to cell death?

2.6. Author response:

In our system, past EEs were detected transiently but did not persist. We agree that we cannot distinguish whether the transient appearance of past EEs reflects transient adoption of another identity that ends in cell death or reversible plasticity.

To partially address this criticism, as noted in 2.4. Author response, we will examine the apoptosis marker cleaved Dcp-1, which also tests whether cleaved Dcp-1-positive cells can be past EEs. However, regardless of detecting apoptosis markers in past EEs, we have changed “transient” into “temporary” to describe a short-lived cell state (see Page 8, Line 178; Page 15, Line 338).

- They authors interpret fate-conversion as beneficial for tissue repair but never test whether blocking this process impairs recovery or organismal survival or whether promoting it improves outcomes.

2.7. Author response:

We have removed this potentially misleading interpretation (see Page 4, removed the last part of the previous introduction, “and propose the possibility that such plasticity contributes to tissue repair”). We present below the data showing a severe reduction of the ISC number in 7-day post-radiation guts, suggesting the inability of tissue repair. We will add this to the manuscript together with results from the following experiments.

(1) We will examine if the blockage of radiation-induced EE plasticity, via knocking down Xrp1 in EEs, alters the epithelial cell number and cell junction protein localization.

(2) To complement the result of plasticity inhibition, we attempt to promote plasticity by overexpressing Xrp1 in EEs, to test whether this rescues ISC loss or restores junctions.

Should knockdown worsen ISC loss and junction integrity, or overexpression rescue them, we will describe EE plasticity as beneficial; otherwise, we will present it as a radiation-induced response without inferring benefits, while noting our limitations.

We will address organismal survival in 4.3. Author response.

- Related to the above, it would be helpful to know if fate-converted cells function as true ISCs or ECs (e.g., through proliferation or absorption assays).

2.8. Author response:

To partially answer this criticism, we will examine whether EE-derived ISCs are proliferative by examining whether they can be positive for the mitotic marker phospho-histone 3.

We will address absorption assays in 4.4. Author response.

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

- It is surprising to observe EEs dedifferentiation at a steady state during homeostasis, a condition in which Xrp1 is not detected in the gut. Can the authors comment this point in the discussion?

3.1. Author response:

We have added our thoughts in terms of Xrp1 being not detectable in homeostatic EE lineages (see Page 15, Line 350 - 356). We have also added our thoughts regarding observation of EE plasticity in homeostatic guts (see Page 14, Line 322 - 332).

- Xrp1 is existing as a short of long isoforms. The short form has been recently proposed to be required for cell competition (https://doi.org/10.1101/2025.06.15.659587) whereas Xrp1 long isoform may be responsible for reduced cell growth. Could the authors test which isoform is induced in the gut after irradiation? Is the overexpression of Xrp1 long isoform having the same effect that the short isoform used by the authors.

3.2. Author response:

We have added data on the effect of Xrp1 long isoform overexpression on EE plasticity (see Fig. 5A - 5B, Page 12, Line 276 - 278), showing that overexpression of the Xrp1 long isoform caused a similar increase in past EEs. In addition, we have changed Xrp1 O/E to Xrp1-S O/E in the contents related to Figs 4, 5, S4, and S5.

We will address radiation-induced Xrp1 isoforms in 4.1. Author response.

- Xrp1 is known for its role in cell competition and elimination of looser cells by induction of apoptosis. It would be interesting to check for induction of cell death and/or caspase activation in the fly gut after irradiation and verify a non apoptotic role of DRONC activation in this context using a Dronc RNAi (as proposed by Bergmann lab (https://doi.org/10.1038/s41598-021-81261-0) or Baena-Lopez lab (DOI: 10.15252/embr.201948892)). Overexpression of Xrp1 could be combined with UAS-p35.

3.3. Author response:

We have added data regarding p35 O/E combined with Xrp1 O/E, showing that p35 O/E did not further increase the number of past EEs, thereby suggesting that Xrp1-driven EE plasticity has a non-apoptotic nature (see Fig. 5C - 5D, Page 13, Line 293 - 297).

- Line 221: fig S3E should be S3F

- Line 230: fig S3F-G should be S3G-H

• • Line 230, Fig S3F-G should be Fig S3G-H.*

3.4. Author response:

We have fixed this error.

- The posterior gut region R4 is more proliferative than the anterior part and is usually used for testing regenerative growth. What is happening there after irradiation?

3.5. Author response:

We present below radiation-induced changes in EE lineages and ISC number in the R4bc gut region. Radiation did not alter the proportion of past EEs among EE lineages but reduced the ISC number. We acknowledge differences between anterior and posterior gut regions, but we do not plan to further analyze regional differences or underlying mechanisms.

- The authors’ explanation for cells with weak GFP in Figure 1 is not convincing. Induction of GFP is an all or nothing event as it results from Pros-driven FLPase and a recombination that removes the transcription stop signals to express GFP from a Ubi promotor. Once that happens, it should not matter how strong or weak Pros is, GFP should be the same. So, another explanation is needed. Nuclear staining of cell #2 in Fig 1B resembles a metaphase chromosome arrangement. Nuclear GFP may appear ‘weak’ in mitosis as the nuclear envelope breaks down. It is positive for the purple Pros/Dl stain, which makes it hard to tell if it is Pros+ or Pros- even though the authors state that cells with weak GFP are Pros- in line 104 (see the point above regarding confusing same-color stain for ISC and EE markers). Could cell #2 be a pre-EE that is undergoing mitosis since the lineage tracer marks both EE and pre-EE cells (line 119)? Or do the authors mean recombination on one or both homologs? This should not be possible since the cells are heterozygotes for the Ubi-GFP locus.

3.6. Author response:

For cell #5, RFP- GFPweak may result from the leakiness of the G-TRACE system. We have added our observations of the G-TRACE strains and changed our previous explanation (see Fig. S1B - S1C, Page 5, Line 94 - 97, 103 - 106).

For cell #2, we agree that RFP+ GFPweak cells may either be a cell turning on pros expression just before sample preparation or a pre-EE undergoing mitosis. Nevertheless, it is not a past EE that has lost the EE marker Pros, so it is considered a current EE. We have removed our previous interpretation of cell #2 (see Page 5, removed “which likely had not yet fully activated recombination”), and changed the image to avoid confusion (see Fig. 1C).

- Fig. 2C, if past-EE’s increased in number while current EE’s stayed the same, where are new past-EE’s coming from? There cannot be compensatory proliferations since EE’s are post-mitotic. For fate conversion, one would expect the generation of each past-EE to accompany loss of one current EE.

3.7. Author response:

We agree that the generation of one past EE should be accompanied by the loss of one current EE. We do not have a clear answer to this question. Our data showed cell numbers per ROI rather than the total cell number across the whole gut. To address this, we have changed the number to the proportion, calculated from [past EE] / ([past EE] + [current EE]), in experiments examining damage-induced EE plasticity, which provides a more informative measure for EE fate conversion (see Fig. 2C, also Fig. S2B and 3E).

- Fig. 2E. Dl+ past-EE cell number declined at 14 and 18 h after IR and because cell sized increased, the authors conclude that EE cells that de-differentiated into ISCs subsequently re-differentiated into EC’s. To reach this conclusion, the authors should count past-EEs that are positive for EC markers. Cell size alone is insufficient evidence.

3.8. Author response:

We have added data quantifying the proportion of past EEs that are positive for the EC marker Pdm1, showing that past EEs were more likely to be ECs in guts examined 14 h after radiation (see Fig. 2F - 2G, Page 9, Line 189).

- Fig. 6. Where are the % numbers for ISC, EB and EE’s coming from? And wouldn’t these change with time after IR, etc?

3.9. Author response:

The numbers came from the calculation of the percentage of the absolute values of control and 14 h post-IR conditions from Fig. 2E. These numbers changed with time after radiation. We realized that the precise numbers were misleading. We therefore have removed such illustration and instead added phrases “more current EEs → past EEs, more past EEs being ISCs → past EEs being ECs” to describe the increase in past EE cell number and the shift in the composition of past EEs (see Fig. 6).

- Improve Figure 1B: Pros and Dl are shown in the same color, creating confusion. If both are stained together, different colors or clearer labeling should be used. Clarify how cells are identified as Pros+ vs Dl+.

3.10. Author response:

Anti-Pros and anti-Dl antibodies were produced from the same host species and were detected with the same secondary antibody, so they were in the same color. We have stated that solid nuclear staining indicates Pros, whereas punctate cytoplasmic staining indicates Dl (see Page 5, Line 100, 102, and 103). Such staining has been reported in previous studies (for example, Fig. 2A - 2B, Veneti et al. Nat. Commun. 2024 DOI: 10.1038/s41467-024-46119-9).

- Why is Dl (supposed to be cytoplasmic) overlapping with nuclear GFP in cells #3 and 4 in Fig. 1B?

3.11. Author response:

Because Dl signals were located apically to DAPI/GFP signals, the overlap was likely due to Z-projection from stacked slices. We present below orthogonal slices along the z-axis, from top to bottom by row, and composite and individual color channels, from left to right by columns, for cell #3 (left) and cell #4 (right).

For cell #3, Dl signals were present in slices 1/8 and 2/8 and disappeared in slice 3/8, whereas DAPI signals appeared from slice 2/8. For cell #4, Dl signals surrounded DAPI signals when viewed separately. In addition, we realized that nuclear GFP signals slightly outgrew DAPI signals, despite our confirmation that the GFP channel was not saturated.

We have included separate color channels for DAPI signals and Pros, Dl and DAPI merged channels, showing that Dl signals were absent from the nucleus. For cell #3, in which the nuclear DAPI and cytoplasmic Dl cannot be distinguished in the stacked view, we show the images from a single orthogonal slice in the main panel, and the image from stacked slices as insets (see Fig. 1C).

- Fig. S1E and F. Very hard to see what the authors describe about Arm and Cora. One problem is that cell boundaries are not visible, just the nuclei, so it is hard to know whether cell-cell interactions the authors describe as normal are really normal. Another problem is the overlap of Arm (supposed to be cytoplasmic) with the nuclear GFP signal. What is that?

3.12. Author response:

Regarding the invisibility of cell boundaries, we have improved the image of anti-Cora staining and added anti-Mesh staining and a separate color channel for DAPI signals to reinforce junction integrity (see Fig. S1H - S1I).

Regarding the overlap of Arm signals with nuclear GFP signals, we realized similar problems as those noted in 3.11. Author response. We present below orthogonal slices along the z-axis and combined and individual color channels, for cell #2 (left) and cell #3 (right). For both cells, Arm signals did not overlap with DAPI signals. We have adjusted the maximum intensity projection to include slices 1-4 instead of 1-8 and added a separate color channel for DAPI signals to avoid the signals appearing to overlap (see Fig. S1G).

- Include a simple schematic of ISC to EE/EC lineages for readers unfamiliar with Drosophila gut biology.

3.13. Author response:

We have included a schematic (see Fig. 1A). Although not requested, we have also improved Fig. 1B to enhance clarity.

- Discuss the regional difference in Xrp1 efficacy (R2a vs R2b). Is there something known about gene expression differences in different gut regions that can explain the results?

3.14. Author response:

At present, we do not have an explanation for these results. We have refined our discussion regarding such regional differences (see Page 16 - 17, Line 381 - 390).

- Consider moving scRNAseq (Fig. S1G) into main paper: this is a central part of the conclusion.

3.15. Author response:

We have moved Fig. S1G, as well as Fig. S1H and S1I, into the main figure (see Fig. 1G - 1I).

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

- Xrp1 is existing as a short of long isoforms. The short form has been recently proposed to be required for cell competition (https://doi.org/10.1101/2025.06.15.659587) whereas Xrp1 long isoform may be responsible for reduced cell growth. Could the authors test which isoform is induced in the gut after irradiation? Is the overexpression of Xrp1 long isoform having the same effect that the short isoform used by the authors.

4.1. Author response:

We prefer not to distinguish whether the long or short Xrp1 isoform is induced in the gut after radiation. This presents technical challenges and falls outside the scope of the present study. As noted in 3.2. Author response, we instead report in the revised manuscript that both isoforms similarly promote EE plasticity.

- Xrp1 is known for its role in cell competition and elimination of looser cells by induction of apoptosis. It would be interesting to check for induction of cell death and/or caspase activation in the fly gut after irradiation and verify a non apoptotic role of DRONC activation in this context using a Dronc RNAi (as proposed by Bergmann lab (https://doi.org/10.1038/s41598-021-81261-0) or Baena-Lopez lab (DOI: 10.15252/embr.201948892)). Overexpression of Xrp1 could be combined with UAS-p35.

4.2. Author response:

We prefer not to perform Dronc-RNAi, because we did not observe Dronc activation downstream to Xrp1, as shown in 2.4. Author response.

- They authors interpret fate-conversion as beneficial for tissue repair but never test whether blocking this process impairs recovery or organismal survival or whether promoting it improves outcomes.

4.3. Author response:

We prefer not to examine organismal survival. We agree that organismal survival would be informative, but our study focuses on epithelial cell number, which will be tested as noted in 2.7. Author response. We will not mention broad claims at the organismal level.

- Related to the above, it would be helpful to know if fate-converted cells function as true ISCs or ECs (e.g., through proliferation or absorption assays).

4.4. Author response:

We prefer not to perform absorptive assays due to technical challenges. We will instead test proliferation, as noted in 2.8. Author response, and note our limitations.

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Referee #2

Evidence, reproducibility and clarity

Summary

Qian and colleagues report a study on radiation induced cell fate plasticity in the intestine of Drosophila. Using lineage tracing to mark pre-EE and EE cells, the authors how that these cells can lose EE/pre-EE marker Pros and express ISC or EC markers, indicating fate conversion. Single cell RNAseq analysis showed that even under basal conditions, ISC/EB cell population includes those with EE/pre-EE lineage tracer, confirming fate conversion. The same analysis showed that fate converted ISC/EB cells express transcription factor Ets21C, which is associated with regeneration but not normal development. Exposure to ionizing radiation (IR) increases the frequency of fate conversion and accompanies the induction of Xrp1 (which is not expressed normally in the EE's). Xrp1 knock down reduced IR-induced fate conversion, demonstrating necessity. Xrp1 is also sufficient because overexpression of it resulted in increased fate conversion without IR. scRNAseq analysis showed that overexpression of Xrp1 in pre-EE/EE cells (without IR) resulted in the induction of ISC/progenitor state genes such as esg and Sox homologs. Functional testing of the latter group of genes demonstrated their essential role in cell fate plasticity induced by Xrp1.

Major comments

• The authors do not justify or explain why they used 100 Gy of radiation. This is higher than doses used in comparable regeneration studies in adult Drosophila (e.g., PMID25959206, PMID: 28925355). The authors should clarify why this dose was chosen.
• The authors' explanation for cells with weak GFP in Figure 1 is not convincing. Induction of GFP is an all or nothing event as it results from Pros-driven FLPase and a recombination that removes the transcription stop signals to express GFP from a Ubi promotor. Once that happens, it should not matter how strong or weak Pros is, GFP should be the same. So, another explanation is needed. Nuclear staining of cell #2 in Fig 1B resembles a metaphase chromosome arrangement. Nuclear GFP may appear 'weak' in mitosis as the nuclear envelope breaks down. It is positive for the purple Pros/Dl stain, which makes it hard to tell if it is Pros+ or Pros- even though the authors state that cells with weak GFP are Pros- in line 104 (see the point above regarding confusing same-color stain for ISC and EE markers). Could cell #2 be a pre-EE that is undergoing mitosis since the lineage tracer marks both EE and pre-EE cells (line 119)? Or do the authors mean recombination on one or both homologs? This should not be possible since the cells are heterozygotes for the Ubi-GFP locus.
• Fig. 2C, if past-EE's increased in number while current EE's stayed the same, where are new past-EE's coming from? There cannot be compensatory proliferations since EE's are post-mitotic. For fate conversion, one would expect the generation of each past-EE to accompany loss of one current EE.
• Fig. 2C, the number of past EE's increased transiently so that baseline number is restored at 18 hr after IR. The authors conclude that fate plasticity is a transient event. Can they rule out loss due to cell death?
• Fig. 2E. Dl+ past-EE cell number declined at 14 and 18 h after IR and because cell sized increased, the authors conclude that EE cells that de-differentiated into ISCs subsequently re-differentiated into EC's. To reach this conclusion, the authors should count past-EEs that are positive for EC markers. Cell size alone is insufficient evidence.
• Fig. 6. Where are the % numbers for ISC, EB and EE's coming from? And wouldn't these change with time after IR, etc?
• They authors interpret fate-conversion as beneficial for tissue repair but never test whether blocking this process impairs recovery or organismal survival or whether promoting it improves outcomes.
• Related to the above, it would be helpful to know if fate-converted cells function as true ISCs or ECs (e.g., through proliferation or absorption assays).

Minor comments

• Improve Figure 1B: Pros and Dl are shown in the same color, creating confusion. If both are stained together, different colors or clearer labeling should be used. Clarify how cells are identified as Pros+ vs Dl+.
• Why is Dl (supposed to be cytoplasmic) overlapping with nuclear GFP in cells #3 and 4 in Fig. 1B?
• Fig. S1E and F. Very hard to see what the authors describe about Arm and Cora. One problem is that cell boundaries are not visible, just the nuclei, so it is hard to know whether cell-cell interactions the authors describe as normal are really normal. Another problem is the overlap of Arm (supposed to be cytoplasmic) with the nuclear GFP signal. What is that?
• Include a simple schematic of ISC to EE/EC lineages for readers unfamiliar with Drosophila gut biology.
• Discuss the regional difference in Xrp1 efficacy (R2a vs R2b). Is there something known about gene expression differences in different gut regions that can explain the results?
• Consider moving scRNAseq (Fig. S1G) into main paper: this is a central part of the conclusion.
• Line 230, Fig S3F-G should be Fig S3G-H.

Significance

Xrp1 is known to have a role in DNA Damage Responses and in cell competition and to function in the context of the p53 network, but this is the first time its role in fate conversion has been demonstrated. For the most part, the data are convincing and include strong genetic evidence from loss- and gain-of-function approaches that demonstrate a role for Xrp1 in activating progenitor gene expression and fate conversion. However, there are several experimental and presentation issues that need to be addressed first as outlined in the previous sections.

The work highlights how mature cells may revert to stem-like states in response to injury, a theme with broad relevance in regenerative medicine.

My field of expertise lies in DNA damage responses in Drosophila and human cancer models.

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Referee #1

Evidence, reproducibility and clarity

Adult tissue homeostasis refers to the process by which tissues maintain a stable and functional state over time. This usually depends on stem cell activity and the balance between cell proliferation and differentiation to ensure that tissues can repair damage, replace old or dead cells, and maintain their structure and function.

Damage-induced plasticity plays an important role in restoring tissue homeostasis. Cellular plasticity is the ability of differentiated cells to acquire alternative phenotypic identities. It is typically constrained under homeostatic conditions but can be activated in response to tissue damage to support regeneration. In this study entitled "Xrp1 drives damage-induced cellular plasticity of enteroendocrine cells in the adult Drosophila midgut", Qian Q. et al., describe damage-induced plasticity of secretory enteroendocrine cells (EEs) in the adult Drosophila midgut. They found that ionizing radiation enhances EE plasticity, enabling EEs to dedifferentiate into intestinal stem cells (ISCs), which subsequently re-differentiate into absorptive enterocytes (ECs). Mechanistically, radiation triggers the expression of Xrp1, a stress-responsive transcription factor, within EE lineages. Xrp1 upregulation is necessary for initiating EE plasticity by expressing progenitor specific genes (like escargot for example), as verified by single-cell RNA sequencing of midguts with EE-specific Xrp1 overexpression. This is suggesting that Xrp1 reprograms EEs by promoting progenitor-like transcriptional states.

The authors nicely describe the dedifferentiation of EEs using the G-TRACE system in response to irradiation and the role of Xrp1 in this process. Yet, the authors need to show the requirement of the EEs dedifferenciation during regenerative growth.

Major comments:

• The authors should investigate the regenerative growth of the adult midgut after irradiation. Is there an impact on ISCs proliferation or cell turn over. Is Xrp1 in EEs required in this adaptive response. It would be elegant to use the recently generated tracing method by Tobias Reiff lab to observe overall impact on tissue renewal (rapport-tracing esglexReDDM esg-lexA, 13xLexAop2-CD8::GFP, 13xLexAop2-H2B::mCherry::HA, tub-Gal80ts on the second chromosome. It can be combined with any EEs Gal4-driver (see Nat Commun 2025, https://doi.org/10.1038/s41467-024-55664-2, the stock is already existing, see table1). This reviewer thinks that it is a key experiment to support the proposed model.
• It is surprising to observe EEs dedifferentiation at a steady state during homeostasis, a condition in which Xrp1 is not detected in the gut. Can the authors comment this point in the discussion?

Minor comments:

• Is p53 required for Xrp1 induction in the gut after irradiation?
• Xrp1 is existing as a short of long isoforms. The short form has been recently proposed to be required for cell competition (https://doi.org/10.1101/2025.06.15.659587) whereas Xrp1 long isoform may be responsible for reduced cell growth. Could the authors test which isoform is induced in the gut after irradiation? Is the overexpression of Xrp1 long isoform having the same effect that the short isoform used by the authors.
• Xrp1 over expression has been shown to induce upd3 ligand and nutrient-driven dedifferentiation of enteroendocrine cells is occuring by activation of the JAK-STAT pathway (DOI: 10.1016/j.devcel.2023.08.022). Could the authors test the function of this signaling pathway during irradiation (upd3-lacZ and Stat-GFP can be used in parallel of upd3 RNAi and UAS Dome-DN.
• Xrp1 is known for its role in cell competition and elimination of looser cells by induction of apoptosis. It would be interesting to check for induction of cell death and/or caspase activation in the fly gut after irradiation and verify a non apoptotic role of DRONC activation in this context using a Dronc RNAi (as proposed by Bergmann lab (https://doi.org/10.1038/s41598-021-81261-0) or Baena-Lopez lab (DOI: 10.15252/embr.201948892)). Overexpression of Xrp1 could be combined with UAS-p35.
• Line 221: fig S3E should be S3F
• Line 230: fig S3F-G should be S3G-H
• The posterior gut region R4 is more proliferative than the anterior part and is usually used for testing regenerative growth. What is happening there after irradiation?

Significance

Altogether, the paper present compiling lines of evidence supporting the proposed model. The experiments are well designed and are convincing. The papers is interesting and relevant for a broad audience.

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Reply to the reviewers

Based on the below reviews, we propose the following revision plan. Briefly:

• We will re-focus the manuscript on the developmental data providing a molecular and cellular blueprint __of lining macrophage development. The __novelty and relevance of our developmental data have been highlighted by all three reviewers, and they have also praised the rigor of these experiments and their interpretation. We thus believe that this re-focus will improve the manuscript's message.
• We will include our data on CSF1 as a key signal. Whilst previously appreciated as a factor required for tissue-resident macrophages, including those in the joint, our study is the first to show the requirement of lining macrophages over a complete developmental time course, using modern readouts, and in a model that circumvents the limitations of previously used approaches (see point-by-point response for details).
• However, we will remove the functional data on TGFβ signaling and mechanical loading/mechanosensing. We agree with the reviewers that we would need to generate additional histological and molecular data from conditional knockout mice, antibody and (ant)agonist treatments and the optogenetic model to determine their exact involvement in lining macrophage maturation. These experiments require significant time and other resources. We would therefore like to uncouple this question for a follow-on manuscript, and to re-focus the current study as a developmental atlas. Removal of (some) of these data has been suggested in the reviewers' comments as well.
• To further elevate our developmental atlas, we are proposing to include additional data and new analyses delineating the developmental dynamics of synovial fibroblasts on single cell (transcriptomic) level. This change to the original manuscript had not been requested by the reviewers, but we are proposing this pro-actively because we believe this would be an impactful addition to a revised version of our study, providing data also on the maturation of the synovial (lining) macrophage niche. Again, this will re-focus the manuscript on the developmental data and provide a novel, valuable resource for those interested in joint biology.
• We will otherwise respond to all individual reviewer comments and implement the requested changes, unless technically not possible. We are convinced that this revision plan will result in a manuscript that fits very well with the remit of Genes & Development.

Please find below detailed point-by-point answers.

Reviewer #1

Evidence, reproducibility and clarity

In their manuscript entitled "The synovial lining macrophage layer develops in the first weeks of life in a CSF1- and TGFβ-dependent but monocyte-independent process," the authors explore the developmental trajectory of synovial lining macrophages. They demonstrate that the formation of this specialized macrophage layer is age-dependent and governed by a distinct developmental program that proceeds independently of circulating monocytes. Through scRNA-Seq, the authors show that synovial lining macrophages originate locally from Aqp1⁺ macrophages and are marked by the expression of Csf1r, Tgfbr, and Piezo1. Notably, genetic ablation of each of these factors impaired the development of lining macrophages to varying degrees, suggesting differential contributions of CSF1, TGFβ, and PIEZO1 signaling pathways to their maturation and maintenance.

The manuscript is well written, and the data quality and representation is of a high standard. The authors have employed a sophisticated array of state-of-the-art mouse models and cutting-edge technologies to elucidate the developmental origin of synovial lining macrophages. Notably, the supporting scRNA-Seq datasets are of excellence and provide valuable insights that will likely be of significant interest to researchers in the field of immunology and joint biology. Accordingly, the experimental approach and interpretations regarding macrophage origin are well-founded and compelling. However, in the eye of the reviewer, the section addressing the underlying molecular mechanisms is a bit less convincing. This part of the study appears slightly underdeveloped, and some of the mechanistic claims lack sufficient experimental clarity. A more rigorous experimental investigation would be essential to reinforce the manuscript's conclusions, particularly concerning the data related to Tgfbr and Piezo1, where the current evidence appears insufficiently substantiated.

We thank the reviewer for their positive and constructive evaluation of our manuscript. We agree with them (and the other reviewers) that our functional data on the involvement of TGFβ signaling and mechanical loading/mechanosensing are comparably less convincing and substantiated than our developmental data. We are very grateful for their (and the other reviewers') suggestions to provide more support for the involvement of these factors in lining macrophage development. However, we think that carrying this out to the same high standard will require substantial time and other resources. We have therefore decided to uncouple this from the developmental data and pursue this in follow-up work. We will re-focus the current manuscript on the developmental data. We have proposed to the editors to instead include additional data on synovial fibroblast development, to complement our macrophage data and also delineate the maturation of their niche, thereby providing a conclusive developmental atlas.

Major point:

1. The numbers of VSIG4⁺ macrophages appear either unaffected or only minimally altered in both Csf1rMerCreMer Tgfbr2floxed and Fcgr1Cre Piezo1floxed mouse models, respectively. This raises an important question: was the gene deletion efficiency sufficient in each model? Accordingly, the authors are encouraged to include quantitative data on gene deletion efficiency for both mouse models, as this information is critical for interpreting the observed phenotypic outcomes and validating the conclusions regarding gene function. Furthermore, to better assess the impact of Tgfbr2 and Piezo1 disruption, the authors should provide more comprehensive flow cytometry analyses and histological data for these mouse models. Given the apparent homogeneity of VSIG4⁺ macrophages (as shown by the authors themselves), bulk RNA-Seq of sorted Tgfbr2- and Piezo1-deficient VSIG4⁺ macrophages (or from TGFβ-treated animals) would offer valuable insights into both the effectiveness of gene deletion and the molecular pathways governed by TGFβ and PIEZO1 in lining macrophages.

As outlined above, we have decided to uncouple our functional data on TGFβ, Piezo1 and mechanical loading. The points raised here are all very valid, and we will implement your suggestions in our follow-up functional work focusing on signaling events regulating lining macrophage development. On the suggestion to perform bulk RNA sequencing for VSIG4+ macrophages: This is a good one in principle - although we will not be able to use this strategy where we want to assess the consequences of experimental treatments or genetic models on lining macrophage maturation, because acquisition of VSIG4 is a key maturation event that might be impaired in these conditions.

Minor points:

Consistent usage of Cx3cr1-GFP+ nomenclature (for instance: Fig. S1 legend "adult mouse synovial tissue, showing PDGFRα⁺ fibroblasts (yellow) and CX3CR1-GFP⁺ cells (cyan)." versus Fig. 1 legend "Automated spot detection highlights Cx3cr1-GFP⁺ macrophages)".

We will implement these changes.

Unclear Fig. 3 legend: "Representative immunofluorescence images of synovial tissue from Clec9aCre:Rosa26lsl-tdT mice at 3 weeks and in adulthood, showing and tdTomato (yellow) and stained for DAPI (blue), VSIG4 (cyan)" Check 'showing and tdTomato.'

We will implement these changes.

For greater clarity, it would have been helpful if the transcript names had been directly included within Figures 3C, S3A, and S3C.

We will implement these changes.

Page 24: "(Mki67CreERT2:Rosa26lsl-tdT)" Last bracket not superscript.

We will implement these changes.

Page 25: "we again leveraged our scRNAsequencing dataset" Missing punctuation.

We will implement these changes.

Page 27: Fig. 5C legend: " of synovial tissue of 1 week-old, 3 weeks-old and adult mice." Please specify and change to 'adult Csf1rΔFIRE/ΔFIRE mice'.

We will implement these changes.

Page 30: The outcome observed in the Acta1-rtTA:tetO-Cre:ChR2-V5fl mouse model appears to be inconclusive: "This approach resulted in an increased density of VSIG4+ and total (F4/80+) macrophages in the exposed leg of some 5 days-old pups, but others showed the opposite trend (Figure S5D)." This variability may reflect low efficiency of the model or other technical limitations (e.g. muscle contractions frequency or time point of analysis). Given this ambiguity, it is worth reconsidering whether the data are sufficiently robust to warrant inclusion. Should the authors choose to include these findings, further experimentation of appropriate depth and precision is required to allow a conclusive interpretation (either it increases the density of VSIG4+ macrophages or not). The same applies to the Yoda1-treated mice, for which additional data are needed to determine whether VSIG4⁺ macrophage density is truly affected.

We have decided to remove the data on the optogenetic mouse model and Yoda1 treatment and follow-on separately, implementing these suggestions, including proof of concept data for optogenetically induced muscle contractions.

Significance

General assessment: provide a summary of the strengths and limitations of the study. What are the strongest and most important aspects? What aspects of the study should be improved or could be developed? This is a well-designed study that uses cutting-edge methodologies to investigate the developmental trajectory of synovial lining macrophages under homeostatic conditions. The authors present robust experimental evidence and compelling interpretations concerning synovial macrophage origin, which are both well-substantiated and impactful. Nonetheless, from the reviewer's perspective, the section exploring the molecular mechanisms underlying macrophage differentiation is comparatively less convincing. This section appears somewhat underdeveloped, as some of the mechanistic claims lack sufficient depth and experimental rigor to fully substantiate the conclusions.

Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field: In contrast to earlier studies (PMID: 31391580, 32601335), the inclusion of fate-mapping experiments adds an important dimension, offering novel insight into the ontogeny of synovial macrophages. This expanded perspective may prove particularly valuable in advancing our understanding of joint immunology, especially regarding the local origins and lineage relationships of macrophage populations.

Furthermore, the authors present novel insights into the molecular pathways underlying the differentiation and development of synovial lining macrophages. By demonstrating previously unrecognized regulatory mechanisms, this work significantly deepens our understanding of the cellular and transcriptional programs that drive macrophage specialization within the joint microenvironment.

Place the work in the context of the existing literature (provide references, where appropriate): This study builds upon previous work characterizing the macrophage compartment in the joint (PMID: 31391580, 32601335), yet provides a substantially more comprehensive dataset that spans multiple developmental time points and data on the origin of this specialized macrophage subset.

State what audience might be interested in and influenced by the reported findings: Immunologist, clinicians

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. This study falls well within the scope of the reviewer's expertise in innate immunity.

Reviewer #2

Evidence, reproducibility and clarity

In the manuscript „The synovial lining macrophage layer develops in the first weeks of life in a CSF1- and TGFβ- dependent but monocyte-independent process", Magalhaes Pinto and colleagues carefully employ a wide range of technologies including single cell profiling, imaging and an exceptional combination of fate mapping models to characterize the ontogeny and development of lining macrophages in the joint, thus dissecting their maturation during postnatal development. Over the last decade, several landmark studies highlighted the imprinting of tissue-resident macrophages by a combination of ontogenetic and tissue-specific niche factors during development. So far, the ontogeny and the tissue niche factors governing the development and maturation of lining macrophages have not been described. Therefore, the results of this study offers insights on a small highly adapted macrophage population with relevance in many disease settings in the joint. Furthermore, the findings are nicely showcasing how macrophages are specializing to even very small tissue niches across development within one bigger anatomical compartment to serve dedicated functions within this niche.

This manuscript is beautifully written and highlights many novel, highly relevant findings on lining macrophage biology and the authors employ a wide range of different technologies to carefully dissect the postnatal development of lining macrophages.

In particular, the combination of scRNA-seq and fate mapping is providing a unique the link of transcriptional programs to ontogeny within the tissue niche. Furthermore, the integrative use of distinct fate mapping strategies, transgenic mouse lines, and treatment paradigms to elucidate key niche factors guiding the development and maturation of lining macrophages provides many interesting findings and data that are highly relevant to the field. I really enjoyed reading this manuscript.

Thank you for your complimentary and constructive assessment of our manuscript, and the detailed comments below, which are very helpful. Please find point-by-point responses below.

Major points:

The authors show dynamic regulation of VSIG4 in lining macrophages during development, therefore VSIG4 is maybe not an ideal choice for gating strategies to define lining macrophages or to show as a single markers in immunofluorescence (IF) stainings to demonstrate their abundance across development (even though it is clear that this is the reason why the F4/80 staining is shown next to it). To demonstrate the increase of lining macrophages during development in IF, it would be more helpful if the authors would show quantifications of all F4/80+ cells and additionally VSIG4+ as a proportion of F4/80+ cells (or VSIG4+ F4/80+ and all F4/80+ in a stacked bar plot). We agree with the assessment of VSIG4 not being ideal since this is a key marker of mature lining macrophages only.

We agree with the assessment of VSIG4 not being ideal since this is a key marker of mature lining macrophages only. We will provide additional data and analyses.

In Figure 1C, the authors nicely demonstrate that the lining macrophages get closer in their distance across development to build the epithelial-like macrophage structure along the adult lining. Is the close proximity between lining macrophages already fully "matured" at 3 weeks of age and comparable to adults? Please quantify the distance in adult linings.

We will provide additional data for adult joints.

Can the authors explain how the grouping was performed between the analyzed human fetal joints? It is not clear why the cut was chosen between the groups at 16/17 weeks of age. Maybe it would be also beneficial if the authors would consider not grouping these samples but rather show the specific quantifications for each samples individually and estimate via linear regression the expansion over time across human development. Furthermore, can the authors give additional information about the distancing of lining macrophages in the human fetal samples, it would be great to see if they follow the same dynamics as in mouse. Maybe comparison to human juvenile/adult joints would also add on to substantiate the findings in human samples (if possible).

We will show samples ungrouped and perform new linear regression analysis as suggested.

The scRNA-seq analysis leaves several questions open and some conclusions and workflows cannot be easily followed.

We appreciate this comment and the complexity of the data, and will implement the below recommendations, and clarify the issues raised. Detailed:

a. It is not clear how and especially why the signature genes to define macrophages vs. monocytes were chosen. Especially as the signature genes for monocytes would not include patrolling monocytes and the macrophage signature genes seem to be highly regulated during development, see also Apoe expression in NB vs. adult in Figure S2e. Why did the authors not take classical markers such as Itgam, Fcgr1a, Csf1r?

We will include new analyses using these markers.

b. Can dendritic cell signatures be excluded? Cluster 11 and 12 show indeed some DC markers, are these really macrophages?

We will include new analyses to account for DC markers.

c. The authors provide several figure panels showing TOP marker genes or key marker genes for the identified clusters, however it is not clear if these are TOP DE genes or if the genes were hand chosen. Somehow, the authors give the impression that the clusters were chosen and labeled not based on DE genes, but more on existing literature that previously reported these macrophage populations. DE gene lists for all annotated cell types and macrophage clusters need to be provided within the manuscript.

We will provide the full DEG analysis results.

d. The authors claim that Clusters 1 and 4 are "developing" macrophages. How is this defined? Why are these developing cells compared to other clusters? And why are these clusters later on not considered as progenitors of Aqp1 macrophages and Vsig4 macrophages? Why are Aqp1+ macrophages not labeled as developing when they are later on in the manuscript shown as potential intermediate progenitors of lining macrophages?

As per below comment, we will expand on this and clarify nomenclature and (potential) relationships between these and other macrophages.

e. Furthermore, it is again confusing that markers are used throughout Figure 2 which are labeled as "key marker genes" for a population and then later on they are claimed to be regulated during development within this population, see for example Figure 2D and 2H.

We will clarify this as per above answer.

f. It is appreciated that the authors distinguished cycling clusters such as 8, 9, and 10 based on their cycling gene signature. Here it would be very exciting to see a cell cycle analysis across all clusters and time points to see when exactly the cells are expanding during development; this would also substantiate the data later shown for the Mki67-CreERT2 mouse model.

We will perform the proposed cell cycle analysis, and implement this and the other reviewer's suggestions for marker selection and cluster annotation (this is also covered in below comments from other reviewers).

g. Can the authors identify certain gene modules during development of lining macrophages (and/or their progenitors) which are associated with certain functions (e.g. GO terms, GSEA enrichment)?

This will be included in the revised manuscript.

To determine the actual presence of the identified macrophage clusters from the scRNA-seq as macrophage populations in the joint, the authors should perform IF or FACS for key markers. Especially, Aqp1+ macrophages should be shown in the developing joint.

We will provide additional data on Aqp1+ macrophages in the developing joint, and related these to a study by collaborators currently in revision at Immunity, which characterizes the Aqp1+ population in detail (we are hoping to have a doi available during our revision process).

The authors used a wide range of fate mapping models, which is quite unique and highly appreciated. The obtained results and the conclusions made from the models raise a couple of questions: Whereas contribution of HSC-derived/monocyte-derived macrophages to the lining compartment seems to be minor, there is still labeling across different models. Various aspects would need to be clarified.

We will clarify these data throughout as per below suggestions.

a. For example, the authors employ Ms4a3-Cre as a tracing model for GMP-derived monocytes, however all quantifications of the labeling efficiency are not normalized to the labeling in monocytes or another highly recombined cell population. This should be shown, similar to the other fate mapping models (Figure 3 F-I).

Labelling efficacy for Ms4a3-Cre is near complete for GMP-derived monocytes (and neutrophils) with the Rosa-lsl-tdT (aka Ai14) reporter we have used (see also PMID: 31491389 and doi: 10.1101/2024.12.03.626330); but we will include normalized data as requested.

b. Please show Ms4a3 expression across clusters across time points, to exclude expression in fetal-derived clusters.

We will include this in the revised supplementary information, but there is indeed very little at birth (in line with the original report for other tissues PMID: 31491389).

c. In line with the question raised above, if the authors can exclude a development of the Egfr1+ and Clec4n+ developing macrophages into Aqp1+ macrophages and subsequently into Vsig4 lining macrophages, the obtained data from the Ms4a3-Cre model highly suggests a correlative labeling across these clusters what could implicate a relation. However, the authors do not discuss throughout the manuscript the role of these developing macrophages. It is highly encouraged to include this into the manuscript and it would be of high relevance to understand lining macrophage development.

This is an interesting point and we agree it deserves consideration in the revised manuscript. Indeed, our trajectory analyses do not predict differentiation of the Egfr1+ and Clec4n+ developing macrophages into Aqp1+ macrophages, and hence, ultimately lining macrophages. Conversely, Aqp1+ cells might also convert into Egfr1+ and Clec4n+ developing macrophages. We will elaborate on this more in the revised manuscript.

d. The authors conclude from the pseudo bulk transcriptomic profiling of the different macrophage clusters that TdT+ and TdT- macrophages do not differ in their gene expression profile and that this is due to niche imprinting rather than origin imprinting. Even though the data supports that conclusion, the authors should verify if inkling cells early during development also show this similar gene expression profile and gene expression should be compared at the different developmental time points. Tissue niche imprinting is happening within the niche during development, most likely in a stepwise progress, and therefore there should be differences in the beginning.

This is another important point that we will address in the revised manuscript by performing additional differential gene expression analyses at the different developmental time points, including the earliest stages, as suggested.

The trajectorial analysis using different pseudotime pipelines is very interesting and nicely points out the potential role of Aqp1 macrophages as intermediates of Vsig4 lining macrophages. From my point of view, all trajectories seem to suggest that Egfr1 developing macrophages and Clec4n developing macrophages might differentiate into Aqp1 macrophages, however the authors are not exploring this further and the role of both developing macrophage clusters is not further discussed (see also comments above).

We will address and discuss this in the revised manuscript.

How was the starting point of the trajectorial analyses defined and is it the same for each pipeline used?

We will clarify this in the revised manuscript.

Are there potentially two trajectories? It looks like there is one in the beginning of postnatal life and a second one appearing from the monocyte-compartment later in life. If this is true, that would rather speak for a dual ontogeny of Vsig4+ macrophages, wouldn't it?

We will discuss this in the revised manuscript.

A heatmap (transcriptional shift) of trajectories between more clusters should be shown at least for Cluster 0,1,2, and 3. It is not sufficient to demonstrate this only between two clusters.

We will add these analyses during revision.

To show the similarity between Aqp1 macrophages and proliferating macrophage clusters, the authors should remove the cycling signature and compare these clusters to show that the cycling cells might be Aqp1 macrophages or earlier developing macrophage progenitors aka Clec4n or Egfr1 macrophages.

We will address this in the revised manuscript.

The conclusions made from the Mki67-CreERT2 data are a bit difficult to understand, whereas all progenitors (monocyte progenitors and macrophage progenitors will proliferate at the neonatal time point and no conclusions can be made if the cells expand in the niche. The authors should employ Confetti mice or other models (Ubow mice) to analyze clonal expansion in the niche.

We acknowledge that interpretation of the Mki67-CreERT2 data is complicated by labeling of other cells, and notably, labeling observed in BM-derived cells. To complement the Mki67-CreERT2 data, and specifically account for proliferation of BM-derived cells, we have tried using Ms4a3-Cre:Ubow mice to quantify expansion of the few monocyte-derived macrophages in the joint (lining). However, this yielded

All predicted cell-cell interactions between macrophages and fibroblasts should be provided in a supplementary table. Are the interactions shown in Figure 5 chosen interactions or the TOP predicted ones? Whereas the authors show different numbers of interactions, it is most likely hand-picked and therefore biased.

We will provide a full list of all predicted interactions in the revised supplementary material in addition to a list of the full differential gene expression analysis.

The authors further aim to dissect the factors involved in the developmental niche imprinting of lining macrophages. Even though it is highly appreciated that the authors used so many experimental setups to show the reliance of lining macrophages on Csf1 and TGF-beta as well as mechanosensation, the wide range of models the different methods used and selected developmental time points make it very difficult to really interpret the data. The authors should carefully choose time points and methods (either FACS analysis across all models or IF across all, or both). Often deletion efficiencies for transgenic models and proof of concept that the inhibitors and agonists are working in the treatment paradigm are not provided. For example, Csf1rMer-iCre-Mer Tgfbr2fl/fl mice are used but no deletion efficiency is shown or different time points of analysis, maybe the macrophages are not properly targeted in the set up.

We have decided to uncouple our experimental data on Tgfb, Piezo1 and mechanosensing/mechanical loading, but are taking this into consideration for revision. In many cases, we have in fact performed flow cytometry and imaging analyses, and agree, we should be showing this consistently.

The authors have shown the role of Csf1 and Tgfbr2 only for lining macrophages, is this specific in the joint to this population of are subliming macrophages affected in a similar manner.

We will include data on sublining macrophages in the revised figure (for CSF1; Tgfb data will be uncoupled from this current manuscript).

Can the authors confirm their results in CSF1R-FIRE mice with anti-Csf1 injections or in Csf1op/op mice?

We will expand our discussion of the Csf1 findings, and aim to include data for anti-CSF1 antibody treatment during revision. Csf1 has previously been reported as a key factor required for maintenance of tissue-resident macrophages, including those in the joint (lining). Indeed, Csf1op/op mice are deficient in synovial lining macrophages, from 2 days of age onwards (PMID: 8050349), and lining macrophages are also absent from 2-weeks-old and adult Csf1r-/- mice (PMID: 11756160). However, a full developmental analysis has not been performed. We are thus the first to show a full developmental time course, using state-of-the-art experimental readouts, and specifically focusing on the early postnatal window of lining maturation that we have identified here in this study. Moreover, we have used a more specific model, Csf1rFIRE ko, in which Csf1 deficiency is restricted to myeloid cells. This model circumvents issues with other models, which show many developmental defects, some of which unrelated to macrophages. These include growth retardation and skeletal defects, which may influence joint macrophage development. Therefore, although Csf1 dependence of synovial lining macrophage had indeed been previously reported in principle, our data substantially expand on and solidify these findings, thereby adding novelty.

The setup in Figure S5G is very interesting to test the role of movement and mechanical load on the joint, however, there is basically no data on the model provided showing the efficiency of the induced optogenetic muscle contractions, and only one time point is shown.

Data on mechanical loading will be uncoupled from the current manuscript and substantiated in a separate follow-up.

The results regarding the role of Piezo1 and mechanosensation vary a lot. Could it be that analyses were done too early or that actually proper weight load on the joint must be applied for the maturation of the macrophages? The authors should test this to.

We will uncouple these data from the current manuscript during revision in order to investigate the contribution of these (and other) factors in sufficient detail. However, this is a possibility that we have discussed. In fact, the most appropriate experimental approach to address the involvement of mechanical loading, onset of walking and specifically, weight bearing would be a loss-of-function approach (i.e. paralysis at the newborn stage), for which we unfortunately could not obtain ethics approval from the UK Home Office.

The Rolipram experiment is shown in Figure S5G, but is not described in the result section. It only appears at some point in the discussion part. The authors should move it to results or remove it from the manuscript.

We will incorporate these data with the revised section on developing synovial macrophage populations.

Minor points:

Please reference the Figure panels in numeric order throughout the text.

We will change this where not the case already.

Figure 2a and 2b are a bit out of the storyline, it is not obvious why this is shown here and maybe it would be good to move it to the supplements. Gating strategy is also not used for scRNA-seq. Therefore, it would better fit to the later analysis of joint macrophages across different transgenic mouse models and treatment paradigms. The gating strategies are changing across different experiments throughout the figures, it would be nice to have a similar gating strategy for all experiments, see also Figure 3 where the defining markers for joint macrophages are changing between models.

We will revise Figures 2, 3 and the related supplementary figures.

A lot of figure panels have very small labeling that is basically unreadable. Axes at FACS plots for example. Sometimes, it is even impossible to distinguish cluster labels especially when they have similar colors.

We will revise this, thanks for pointing it out.

In the text on page 14, many markers are named which are specifically regulated during development in lining macrophages, but these factors are not labeled anywhere in the volcano plot. It would be good to showcase at least some of these named genes in the figure panel, e.g. Trem2.

We will do this for revision.

Figure 2F and Figure S2F are really nicely showing the percentage of cells per cluster in each analyzed biological sample. Maybe the authors could additionally consider to show a stacked bar plot with the mean percentage of cells per cluster and how the clusters are distributed across time points?

We will include this in the revised manuscript.

Figure 3A: IF for adult lining macrophages and the quantification are missing.

This will be included in the revised version.

Reviewer #3 - Major

Generally, the story could be more streamlined by introducing earlier reporter lines and lineage-origin logic. Clearly state which reporter/CreERT2 lines and acrosses are used. It was unclear in Figure 2 that cells of the cross of the Cx3cr1-GFP and Ms4a3Cre:Rosa26lsl-tdT reporter lines were used for the scRNA-seq. The principle that there are fetal-derived and bone marrow (GMP)-derived monocytes and macrophages doesn't need to be "hidden" until Figure 3. For example, also the imaging of Ms4a3Cre could be introduced before the scRNA-seq.

We will revise the structure and order of the manuscript during revision. However, we will streamline this between reviewer comments, and would also like to point out that the 2 other reviewers were very complimentary about the writing and clarity, i.e. we may not follow every specific suggestion of reviewer 3, but are very much taking on board their overall comment on structure and clarity.

Figure 1 could benefit from a cartoon visualizing the anatomy of the knee joint. The terms "sublining" and "synovium" are now a bit unclear, as it appears that sometimes the synovium is indicated as sublining and vice versa. Additionally, a schematic developmental timeline could be added to indicate the parallels between mouse and human development (fetal and postnatal development in mouse versus gestational age in human). Also, the various waves of hematopoiesis could be indicated in this timeline, which would be particularly helpful for Figure 3 for the lineage-tracing readouts. Lastly, the authors could end the manuscript (a new Figure 6) with a general cartoon summarizing all the results presented.

We will include these illustrations as suggested.

Figure 1 could be rearranged: first introduce the markers CX3CR1 and VSIG4 (Figure 1D) and then present the quantifications (Figure 1B/E). Where possible, co-visualization CX3CR1-GFP and VSIG4 on tissue sections to strengthen the claims on the relationship between these 2 markers. Tying the scRNA-seq insights (Figure 2) to the imaging would be elegant. Moreover, it would be informative to represent the CX3CR1+ and VSIG4+ macrophages as a percentage of F4/80+ macrophages (Figure 1B/E). Similarly, for the flow cytometry data in Figure 2, the relationship between the markers CX3CR1 and VSIG4 on macrophages could be more clearly displayed and discussed.

Thanks for this remark. We will endeavour to show co-localization and analysis of both markers wherever possible. However, where we did not use Cx3cr1gfp mice, co-staining was limited by antibody choice and availability.

The 3D imaging of the joint is a nice addition to the manuscript, as it provides more context to the anatomical structure; however, while the text suggests several newborn joints were imaged, Figure 1F visualizes (again) the knee joint. Could other joints also be represented by 3D imaging? If the knee joint is the only joint available for imaging, and previous confocal imaging focused specifically on the meniscus in the knee joint, could the meniscus also be highlighted in the lightsheet imaging?

Apologies if this was not clear from the original manuscript text, but we have only imaged the knee joint in 3D. We will clarify this during revision. Whilst we want to maintain the focus on knee joints throughout this manuscript, but we will include additional 3D lightsheet imaging data from micro-dissected knee joints to further substantiate the original data.

Clarification is requested regarding the imaging quantification representation. The M&M section under "Statistical analysis and reproducibility" states that individual data points are displayed, and bars represent the mean. However, some of the Figure legends (e.g., Figures 1B and S1C) specify that each dot corresponds to an individual mouse, with quantification based on 2-3 sections per mouse. While this appears to be a very reasonable representation of the data, does this mean that for each dot, the mean value from the 2-3 sections per mouse was calculated and plotted?

We will clarify this.

It is not clear how the differential expression analysis was performed on the Vsig4+ cells. Please specify if Cluster 0 was used for analysis, or all Vsig4-expressing cells? Not all cells in Cluster 0 have Vsig4+ expression. The authors described the expression dynamics of Aqp1 as intriguing, but lack a reasoning on why this is interesting.

We will revise this section.

Figure S3E: In line with the previous comment, can the authors justify that the tdTomato+/- comparisons are not biased by scRNA-seq dropout (scRNA-seq is zero-inflated, so some tdTomato- cells could be false negatives), and provide methodological details (thresholds, ambient RNA correction, etc.) to support this?

We will clarify this and include additional representations of the tdTomato transcript data.

Although the sex-related differences in macrophage composition and the absence of differential expression are interesting, they distract from the manuscript's main messages. Moreover, the Discussion does not elaborate on how these observations relate to joint (disease) biology. Consider removing this section or integrating it clearly into the relevant biological context.

We will remove this section as suggested.

CreERT2 transgenic lines are often not 100% efficient in recombination, also depending on whether tamoxifen or 4-OHT is used. Could the authors report the percentage of tdTomato+ cells in the joints and compare them to the recombination efficiencies in the monocytes/microglia under the same tamoxifen or 4-OHT conditions? This would help clarify how the interpret the macrophage labeling %'s.

We will report labelling efficacies and/or show normalized data in the revised manuscript.

Could the authors draw parallels between the observations in the mouse knee joint macrophage populations and literature on other joints in mouse and the knee joint in human (for example, as described in Alivernini et al., 2020 and in the very recent Raut et al., 2025)?

We will include a section on this in the revised manuscript.

Reviewer #3 - Minor comments:

In general, the authors should clarify in the Results what each marker used for imaging, flow cytometry, or in the mouse reporter lines delineates. For example, mention that F4/80 is a marker for tissue-resident macrophages (correct?) in immunofluorescence, that IBA1 is a marker for macrophages on human tissue sections (Figure S1), and PDPN is GP38 (Figure S2 - align usage of marker reference across main text and figures).

We will implement this request.

Figure S1B: Is CX3CR1 also restricted to the lining macrophages in human? Could a co-staining with IBA1 be performed to strengthen the species similarities?

To our knowledge, there is no antibody available that works for imaging of human CX3CR1. Moreover, CX3CR1 is only limited to the lining population in adult joints, in fetal and newborn (mouse) joints, all macrophages express this receptor, as do fetal progenitors to macrophages. However, Alivernini and colleagues have reported that TREM2high macrophages are the human counterpart of the mouse CX3CR1+ lining population (PMID: 32601335). We do not have access to postnatal human joint tissue samples, unfortunately, but we will attempt to stain for and quantify TREM2+ macrophages in human fetal joints for the revised manuscript.

Adipocyte diameter quantification: Avoid plotting individual adipocytes from 2 mice without per-mouse visualization. Instead, report the mean adipocyte diameter per mouse and plot those means.

We will implement this change.

A little typo was spotted in the "Statistical analysis and reproducibility" section: it is Dunn's, not Bunn's multiple-comparison correction.

Thanks for spotting this.

Figure 2A: The gating strategy for the CX3CR1-GFP cells is missing.

We will provide this in the revised manuscript or supplementary material.

Improve the visualization of some plots. For example, Figure 2F is hard to read because of the big dot size. The dots seem to add no information to the graph and could be removed. Additionally, for comparing the clusters across the different time points, one could project the cells from the other time points in grey in the background.

We will revise the presentation of these data.

Figure S2: The dotplot is more informative than the heatmap, consider removing the heatmap.

We will do that.

Figure 3A: If technically feasible, image and visualize both the GFP and tdTomato expression. It would be informative to see the Cx3cr1+ and Ms4a3-derived cells in the same specimen.

We will strive to show this in the revised manuscript.

Figure 3C: Highlight that tdTomato expression is visualized here.

We will do that.

Figure 3G,F: The authors should place the schematics and graphs next to each other, so the data points can be more easily compared.

We aim to do this in the revised manuscript.

Figure 4B: Which co-staining was performed for the immunofluorescence to quantify the % of tdTomato+ cells?

We co-stained for F4/80 and assessed localization in the lining or sublining. This will be clarified in the revised Figure legend.

Figure 4C: The trajectory analysis appears to have an arrow pointing from the Ccr2+ macrophages to the Ly6c+ monocytes. Please verify this directionality, as its seems against the known biology.

This will be addressed during revision.

Figure 5 mentions that the Csfr1 levels were reduced in a tissue-specific manner, but it is unclear how this tissue specificity was achieved.

We apologize for this misunderstanding. Csfr1FIRE mice are not tissue-specific knockouts, but they are more specific than global knockout mice, since only a (myeloid-specific) enhancer is affected. We will clarify this in the relevant section.

For the TGFb perturbations (Tgfbr2 KO and systemic TGFb depletion): did the authors validate reduced TGFb pathway activity in the macrophages, for example, reduced pSMAD2/3 levels? This would validate the effectiveness of the perturbations.

This is an important point, and assessing signaling events downstream of TGFb is a very good suggestion. As per above comment, we have decided to uncouple the functional data with exception of CSF1 from the revised version of the current manuscript, but we will be taking this into account for substantiating our functional data in follow-up work.

Figure 5F could benefit from a timeline of the treatment.

As for 15., we will be taking this into account for follow-up work on the uncoupled functional data.

The Methods mention that Gene Ontology analysis was performed on the single-cell data, but the results are not plotted in a figure. It would be informative to include this GO/pathway analysis in the appropriate figure(s).

We will include this in the revised (supplementary) information.

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Referee #3

Evidence, reproducibility and clarity

Summary:

Magalhaes Pinto, Malengier-Devlies, and co-authors investigated the developmental origins and maturation of synovial (lining and sublining) macrophages across embryonic, newborn, and postnatal stages in mouse. The authors used multiple transgenic reporter lines, lineage tracing, scRNA-seq, 2D confocal and 3D lightsheet imaging, and perturbations to delineate the macrophage states and ontogeny. They propose a model in which the majority of the joint lining macrophages has a fetal (EMP-derived) origin and a small proportion has a definitive HSC-derived monocyte origin, which both seed and mature within the synovial space in the postnatal period in the first 3 weeks of life. Using cell-cell communication analysis on their scRNA-seq data, they identified Fgf2, Csf1, and Tgfb as candidate signaling pathways that support (lining) macrophage development and maturation. Functional experiments indicate that the process is CSF1 and TGFb-dependent and also partly dependent on mechanosensing through Piezo1. The key conclusions on the composition of the synovial macrophages are convincing based on the presented results, and are carefully phrased. The study is very comprehensive, yet the description and organization of the results of the different mouse models could be altered to improve the storyline. Several refinements in data presentation, formulation, and minor validation experiments would further improve the clarity of the story, as well as summary recaps of the major findings throughout the text.

Major comments:

1. Generally, the story could be more streamlined by introducing earlier reporter lines and lineage-origin logic. Clearly state which reporter/CreERT2 lines and acrosses are used. It was unclear in Figure 2 that cells of the cross of the Cx3cr1-GFP and Ms4a3Cre:Rosa26lsl-tdT reporter lines were used for the scRNA-seq. The principle that there are fetal-derived and bone marrow (GMP)-derived monocytes and macrophages doesn't need to be "hidden" until Figure 3. For example, also the imaging of Ms4a3Cre could be introduced before the scRNA-seq.
2. Figure 1 could benefit from a cartoon visualizing the anatomy of the knee joint. The terms "sublining" and "synovium" are now a bit unclear, as it appears that sometimes the synovium is indicated as sublining and vice versa. Additionally, a schematic developmental timeline could be added to indicate the parallels between mouse and human development (fetal and postnatal development in mouse versus gestational age in human). Also, the various waves of hematopoiesis could be indicated in this timeline, which would be particularly helpful for Figure 3 for the lineage-tracing readouts. Lastly, the authors could end the manuscript (a new Figure 6) with a general cartoon summarizing all the results presented.
3. Figure 1 could be rearranged: first introduce the markers CX3CR1 and VSIG4 (Figure 1D) and then present the quantifications (Figure 1B/E). Where possible, co-visualization CX3CR1-GFP and VSIG4 on tissue sections to strengthen the claims on the relationship between these 2 markers. Tying the scRNA-seq insights (Figure 2) to the imaging would be elegant. Moreover, it would be informative to represent the CX3CR1+ and VSIG4+ macrophages as a percentage of F4/80+ macrophages (Figure 1B/E). Similarly, for the flow cytometry data in Figure 2, the relationship between the markers CX3CR1 and VSIG4 on macrophages could be more clearly displayed and discussed.
4. The 3D imaging of the joint is a nice addition to the manuscript, as it provides more context to the anatomical structure; however, while the text suggests several newborn joints were imaged, Figure 1F visualizes (again) the knee joint. Could other joints also be represented by 3D imaging? If the knee joint is the only joint available for imaging, and previous confocal imaging focused specifically on the meniscus in the knee joint, could the meniscus also be highlighted in the lightsheet imaging?
5. Clarification is requested regarding the imaging quantification representation. The M&M section under "Statistical analysis and reproducibility" states that individual data points are displayed, and bars represent the mean. However, some of the Figure legends (e.g., Figures 1B and S1C) specify that each dot corresponds to an individual mouse, with quantification based on 2-3 sections per mouse. While this appears to be a very reasonable representation of the data, does this mean that for each dot, the mean value from the 2-3 sections per mouse was calculated and plotted?
6. It is not clear how the differential expression analysis was performed on the Vsig4+ cells. Please specify if Cluster 0 was used for analysis, or all Vsig4-expressing cells? Not all cells in Cluster 0 have Vsig4+ expression. The authors described the expression dynamics of Aqp1 as intriguing, but lack a reasoning on why this is interesting.
7. Figure S3E: In line with the previous comment, can the authors justify that the tdTomato+/- comparisons are not biased by scRNA-seq dropout (scRNA-seq is zero-inflated, so some tdTomato- cells could be false negatives), and provide methodological details (thresholds, ambient RNA correction, etc.) to support this?
8. Although the sex-related differences in macrophage composition and the absence of differential expression are interesting, they distract from the manuscript's main messages. Moreover, the Discussion does not elaborate on how these observations relate to joint (disease) biology. Consider removing this section or integrating it clearly into the relevant biological context.
9. CreERT2 transgenic lines are often not 100% efficient in recombination, also depending on whether tamoxifen or 4-OHT is used. Could the authors report the percentage of tdTomato+ cells in the joints and compare them to the recombination efficiencies in the monocytes/microglia under the same tamoxifen or 4-OHT conditions? This would help clarify how the interpret the macrophage labeling %'s.
10. Could the authors draw parallels between the observations in the mouse knee joint macrophage populations and literature on other joints in mouse and the knee joint in human (for example, as described in Alivernini et al., 2020 and in the very recent Raut et al., 2025)?

Minor comments:

1. In general, the authors should clarify in the Results what each marker used for imaging, flow cytometry, or in the mouse reporter lines delineates. For example, mention that F4/80 is a marker for tissue-resident macrophages (correct?) in immunofluorescence, that IBA1 is a marker for macrophages on human tissue sections (Figure S1), and PDPN is GP38 (Figure S2 - align usage of marker reference across main text and figures).
2. For clarity in the microscopy representation, the single channels should be represented in a grey scale.
3. Figure S1B: Is CX3CR1 also restricted to the lining macrophages in human? Could a co-staining with IBA1 be performed to strengthen the species similarities?
4. Adipocyte diameter quantification: Avoid plotting individual adipocytes from 2 mice without per-mouse visualization. Instead, report the mean adipocyte diameter per mouse and plot those means.
5. A little typo was spotted in the "Statistical analysis and reproducibility" section: it is Dunn's, not Bunn's multiple-comparison correction.
6. Figure 2A: The gating strategy for the CX3CR1-GFP cells is missing.
7. Improve the visualization of some plots. For example, Figure 2F is hard to read because of the big dot size. The dots seem to add no information to the graph and could be removed. Additionally, for comparing the clusters across the different time points, one could project the cells from the other time points in grey in the background.
8. Figure S2: The dotplot is more informative than the heatmap, consider removing the heatmap.
9. Figure 3A: If technically feasible, image and visualize both the GFP and tdTomato expression. It would be informative to see the Cx3cr1+ and Ms4a3-derived cells in the same specimen.
10. Figure 3C: Highlight that tdTomato expression is visualized here.
11. Figure 3G,F: The authors should place the schematics and graphs next to each other, so the data points can be more easily compared.
12. Figure 4B: Which co-staining was performed for the immunofluorescence to quantify the % of tdTomato+ cells?
13. Figure 4C: The trajectory analysis appears to have an arrow pointing from the Ccr2+ macrophages to the Ly6c+ monocytes. Please verify this directionality, as its seems against the known biology.
14. Figure 5 mentions that the Csfr1 levels were reduced in a tissue-specific manner, but it is unclear how this tissue specificity was achieved.
15. For the TGFb perturbations (Tgfbr2 KO and systemic TGFb depletion): did the authors validate reduced TGFb pathway activity in the macrophages, for example, reduced pSMAD2/3 levels? This would validate the effectiveness of the perturbations.
16. Figure 5F could benefit from a timeline of the treatment.
17. The Methods mention that Gene Ontology analysis was performed on the single-cell data, but the results are not plotted in a figure. It would be informative to include this GO/pathway analysis in the appropriate figure(s).

Significance

This work provides a high temporal-resolution and "spatial" resolution reference map of the ontogeny and maturation of the synovial lining macrophages in the knee joint. It complements existing literature that demonstrated the presence of tissue-resident macrophages in the synovial space and lining (Culemann, et al., 2019 and others) by charting the embryonic-to-postnatal emergence of lining and sublining subsets. In particular, this mouse work identified some key signaling pathways in shaping this tissue compartment. This dataset serves as a robust, steady-state reference for joint pathology and can be implemented with human studies on disease biology of the knee joint (e.g., Alivernini et al., 2020; Raut et al., 2025). Insights into the exact developmental origins, mechanisms contributing to diverse or seemingly similar cell types, and distinct maturation processes are crucial to understanding disease biology, in which developmental processes can be hijacked/reactivated.

These findings will interest researchers in joint disease biology (osteoarthritis and immune-mediated arthritides such as RA and psoriasis), macrophage development (tissue-resident vs monocyte-derived lineages), the bone/joint microenvironment, and joint mechanobiology.

The reviewer's expertise is in developmental biology, mesoderm, bone biology, hematopoiesis, and monocyte/macrophage biology in disease

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Referee #2

Evidence, reproducibility and clarity

In the manuscript „The synovial lining macrophage layer develops in the first weeks of life in a CSF1- and TGFβ- dependent but monocyte-independent process", Magalhaes Pinto and colleagues carefully employ a wide range of technologies including single cell profiling, imaging and an exceptional combination of fate mapping models to characterize the ontogeny and development of lining macrophages in the joint, thus dissecting their maturation during postnatal development. Over the last decade, several landmark studies highlighted the imprinting of tissue-resident macrophages by a combination of ontogenetic and tissue-specific niche factors during development. So far, the ontogeny and the tissue niche factors governing the development and maturation of lining macrophages have not been described. Therefore, the results of this study offers insights on a small highly adapted macrophage population with relevance in many disease settings in the joint. Furthermore, the findings are nicely showcasing how macrophages are specializing to even very small tissue niches across development within one bigger anatomical compartment to serve dedicated functions within this niche.

This manuscript is beautifully written and highlights many novel, highly relevant findings on lining macrophage biology and the authors employ a wide range of different technologies to carefully dissect the postnatal development of lining macrophages.

In particular, the combination of scRNA-seq and fate mapping is providing a unique the link of transcriptional programs to ontogeny within the tissue niche. Furthermore, the integrative use of distinct fate mapping strategies, transgenic mouse lines, and treatment paradigms to elucidate key niche factors guiding the development and maturation of lining macrophages provides many interesting findings and data that are highly relevant to the field. I really enjoyed reading this manuscript.

Major points:

1) The authors show dynamic regulation of VSIG4 in lining macrophages during development, therefore VSIG4 is maybe not an ideal choice for gating strategies to define lining macrophages or to show as a single markers in immunofluorescence (IF) stainings to demonstrate their abundance across development (even though it is clear that this is the reason why the F4/80 staining is shown next to it). To demonstrate the increase of lining macrophages during development in IF, it would be more helpful if the authors would show quantifications of all F4/80+ cells and additionally VSIG4+ as a proportion of F4/80+ cells (or VSIG4+ F4/80+ and all F4/80+ in a stacked bar plot).

2) In Figure 1C, the authors nicely demonstrate that the lining macrophages get closer in their distance across development to build the epithelial-like macrophage structure along the adult lining. Is the close proximity between lining macrophages already fully "matured" at 3 weeks of age and comparable to adults? Please quantify the distance in adult linings.

3) Can the authors explain how the grouping was performed between the analyzed human fetal joints? It is not clear why the cut was chosen between the groups at 16/17 weeks of age. Maybe it would be also beneficial if the authors would consider not grouping these samples but rather show the specific quantifications for each samples individually and estimate via linear regression the expansion over time across human development. Furthermore, can the authors give additional information about the distancing of lining macrophages in the human fetal samples, it would be great to see if they follow the same dynamics as in mouse. Maybe comparison to human juvenile/adult joints would also add on to substantiate the findings in human samples (if possible).

4) The scRNA-seq analysis leaves several questions open and some conclusions and workflows cannot be easily followed.

a. It is not clear how and especially why the signature genes to define macrophages vs. monocytes were chosen. Especially as the signature genes for monocytes would not include patrolling monocytes and the macrophage signature genes seem to be highly regulated during development, see also Apoe expression in NB vs. adult in Figure S2e. Why did the authors not take classical markers such as Itgam, Fcgr1a, Csf1r?

b. Can dendritic cell signatures be excluded? Cluster 11 and 12 show indeed some DC markers, are these really macrophages?

c. The authors provide several figure panels showing TOP marker genes or key marker genes for the identified clusters, however it is not clear if these are TOP DE genes or if the genes were hand chosen. Somehow, the authors give the impression that the clusters were chosen and labeled not based on DE genes, but more on existing literature that previously reported these macrophage populations. DE gene lists for all annotated cell types and macrophage clusters need to be provided within the manuscript.

d. The authors claim that Clusters 1 and 4 are "developing" macrophages. How is this defined? Why are these developing cells compared to other clusters? And why are these clusters later on not considered as progenitors of Aqp1 macrophages and Vsig4 macrophages? Why are Aqp1+ macrophages not labeled as developing when they are later on in the manuscript shown as potential intermediate progenitors of lining macrophages?

e. Furthermore, it is again confusing that markers are used throughout Figure 2 which are labeled as "key marker genes" for a population and then later on they are claimed to be regulated during development within this population, see for example Figure 2D and 2H.

f. It is appreciated that the authors distinguished cycling clusters such as 8, 9, and 10 based on their cycling gene signature. Here it would be very exciting to see a cell cycle analysis across all clusters and time points to see when exactly the cells are expanding during development; this would also substantiate the data later shown for the Mki67-CreERT2 mouse model.

g. Can the authors identify certain gene modules during development of lining macrophages (and/or their progenitors) which are associated with certain functions (e.g. GO terms, GSEA enrichment)?

5) To determine the actual presence of the identified macrophage clusters from the scRNA-seq as macrophage populations in the joint, the authors should perform IF or FACS for key markers. Especially, Aqp1+ macrophages should be shown in the developing joint.

6) The authors used a wide range of fate mapping models, which is quite unique and highly appreciated. The obtained results and the conclusions made from the models raise a couple of questions: Whereas contribution of HSC-derived/monocyte-derived macrophages to the lining compartment seems to be minor, there is still labeling across different models. Various aspects would need to be clarified.

a. For example, the authors employ Ms4a3-Cre as a tracing model for GMP-derived monocytes, however all quantifications of the labeling efficiency are not normalized to the labeling in monocytes or another highly recombined cell population. This should be shown, similar to the other fate mapping models (Figure 3 F-I).

b. Please show Ms4a3 expression across clusters across time points, to exclude expression in fetal-derived clusters.

c. In line with the question raised above, if the authors can exclude a development of the Egfr1+ and Clec4n+ developing macrophages into Aqp1+ macrophages and subsequently into Vsig4 lining macrophages, the obtained data from the Ms4a3-Cre model highly suggests a correlative labeling across these clusters what could implicate a relation. However, the authors do not discuss throughout the manuscript the role of these developing macrophages. It is highly encouraged to include this into the manuscript and it would be of high relevance to understand lining macrophage development.

d. The authors conclude from the pseudo bulk transcriptomic profiling of the different macrophage clusters that TdT+ and TdT- macrophages do not differ in their gene expression profile and that this is due to niche imprinting rather than origin imprinting. Even though the data supports that conclusion, the authors should verify if inkling cells early during development also show this similar gene expression profile and gene expression should be compared at the different developmental time points. Tissue niche imprinting is happening within the niche during development, most likely in a stepwise progress, and therefore there should be differences in the beginning.

7) The trajectorial analysis using different pseudotime pipelines is very interesting and nicely points out the potential role of Aqp1 macrophages as intermediates of Vsig4 lining macrophages. From my point of view, all trajectories seem to suggest that Egfr1 developing macrophages and Clec4n developing macrophages might differentiate into Aqp1 macrophages, however the authors are not exploring this further and the role of both developing macrophage clusters is not further discussed (see also comments above).

8) How was the starting point of the trajectorial analyses defined and is it the same for each pipeline used?

9) Are there potentially two trajectories? It looks like there is one in the beginning of postnatal life and a second one appearing from the monocyte-compartment later in life. If this is true, that would rather speak for a dual ontogeny of Vsig4+ macrophages, wouldn't it?

10) A heatmap (transcriptional shift) of trajectories between more clusters should be shown at least for Cluster 0,1,2, and 3. It is not sufficient to demonstrate this only between two clusters.

11) To show the similarity between Aqp1 macrophages and proliferating macrophage clusters, the authors should remove the cycling signature and compare these clusters to show that the cycling cells might be Aqp1 macrophages or earlier developing macrophage progenitors aka Clec4n or Egfr1 macrophages.

12) The conclusions made from the Mki67-CreERT2 data are a bit difficult to understand, whereas all progenitors (monocyte progenitors and macrophage progenitors will proliferate at the neonatal time point and no conclusions can be made if the cells expand in the niche. The authors should employ Confetti mice or other models (Ubow mice) to analyze clonal expansion in the niche.

13) All predicted cell-cell interactions between macrophages and fibroblasts should be provided in a supplementary table. Are the interactions shown in Figure 5 chosen interactions or the TOP predicted ones? Whereas the authors show different numbers of interactions, it is most likely hand-picked and therefore biased.

14) The authors further aim to dissect the factors involved in the developmental niche imprinting of lining macrophages. Even though it is highly appreciated that the authors used so many experimental setups to show the reliance of lining macrophages on Csf1 and TGF-beta as well as mechanosensation, the wide range of models the different methods used and selected developmental time points make it very difficult to really interpret the data. The authors should carefully choose time points and methods (either FACS analysis across all models or IF across all, or both). Often deletion efficiencies for transgenic models and proof of concept that the inhibitors and agonists are working in the treatment paradigm are not provided. For example, Csf1rMer-iCre-Mer Tgfbr2fl/fl mice are used but no deletion efficiency is shown or different time points of analysis, maybe the macrophages are not properly targeted in the set up.

15) The authors have shown the role of Csf1 and Tgfbr2 only for lining macrophages, is this specific in the joint to this population of are subliming macrophages affected in a similar manner.

16) Can the authors confirm their results in CSF1R-FIRE mice with anti-Csf1 injections or in Csf1op/op mice?

17) The setup in Figure S5G is very interesting to test the role of movement and mechanical load on the joint, however, there is basically no data on the model provided showing the efficiency of the induced optogenetic muscle contractions, and only one time point is shown.

18) The results regarding the role of Piezo1 and mechanosensation vary a lot. Could it be that analyses were done too early or that actually proper weight load on the joint must be applied for the maturation of the macrophages? The authors should test this to

19) The Rolipram experiment is shown in Figure S5G, but is not described in the result section. It only appears at some point in the discussion part. The authors should move it to results or remove it from the manuscript.

Minor points:

1) Please reference the Figure panels in numeric order throughout the text.

2) Figure 2a and 2b are a bit out of the storyline, it is not obvious why this is shown here and maybe it would be good to move it to the supplements. Gating strategy is also not used for scRNA-seq. Therefore, it would better fit to the later analysis of joint macrophages across different transgenic mouse models and treatment paradigms. The gating strategies are changing across different experiments throughout the figures, it would be nice to have a similar gating strategy for all experiments, see also Figure 3 where the defining markers for joint macrophages are changing between models.

3) A lot of figure panels have very small labeling that is basically unreadable. Axes at FACS plots for example. Sometimes, it is even impossible to distinguish cluster labels especially when they have similar colors.

4) In the text on page 14, many markers are named which are specifically regulated during development in lining macrophages, but these factors are not labeled anywhere in the volcano plot. It would be good to showcase at least some of these named genes in the figure panel, e.g. Trem2.

5) Figure 2F and Figure S2F are really nicely showing the percentage of cells per cluster in each analyzed biological sample. Maybe the authors could additionally consider to show a stacked bar plot with the mean percentage of cells per cluster and how the clusters are distributed across time points?

6) Figure 3A: IF for adult lining macrophages and the quantification are missing

Significance

This manuscript highlights novel, highly relevant findings on lining macrophage biology and the authors employ a wide range of different technologies to carefully dissect the postnatal development of lining macrophages. Furthermore, this study showcases in a very elegant and detailed way the adaptation of macrophage progenitors to a highly specific anatomical tissue niche.

The manuscript is of high interest to basic scientists focussing on macrophage biology and immune cell development and clinicians and clinician scientists focussing on joint diseases such as RA

Therefore the manuscript is of interest to a wide community working in immunology.

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Referee #1

Evidence, reproducibility and clarity

In their manuscript entitled "The synovial lining macrophage layer develops in the first weeks of life in a CSF1- and TGFβ-dependent but monocyte-independent process," the authors explore the developmental trajectory of synovial lining macrophages. They demonstrate that the formation of this specialized macrophage layer is age-dependent and governed by a distinct developmental program that proceeds independently of circulating monocytes. Through scRNA-Seq, the authors show that synovial lining macrophages originate locally from Aqp1⁺ macrophages and are marked by the expression of Csf1r, Tgfbr, and Piezo1. Notably, genetic ablation of each of these factors impaired the development of lining macrophages to varying degrees, suggesting differential contributions of CSF1, TGFβ, and PIEZO1 signaling pathways to their maturation and maintenance.

The manuscript is well written, and the data quality and representation is of a high standard. The authors have employed a sophisticated array of state-of-the-art mouse models and cutting-edge technologies to elucidate the developmental origin of synovial lining macrophages. Notably, the supporting scRNA-Seq datasets are of excellence and provide valuable insights that will likely be of significant interest to researchers in the field of immunology and joint biology. Accordingly, the experimental approach and interpretations regarding macrophage origin are well-founded and compelling. However, in the eye of the reviewer, the section addressing the underlying molecular mechanisms is a bit less convincing. This part of the study appears slightly underdeveloped, and some of the mechanistic claims lack sufficient experimental clarity. A more rigorous experimental investigation would be essential to reinforce the manuscript's conclusions, particularly concerning the data related to Tgfbr and Piezo1, where the current evidence appears insufficiently substantiated.

Major point:

• The numbers of VSIG4⁺ macrophages appear either unaffected or only minimally altered in both Csf1rMerCreMer Tgfbr2floxed and Fcgr1Cre Piezo1floxed mouse models, respectively. This raises an important question: was the gene deletion efficiency sufficient in each model? Accordingly, the authors are encouraged to include quantitative data on gene deletion efficiency for both mouse models, as this information is critical for interpreting the observed phenotypic outcomes and validating the conclusions regarding gene function. Furthermore, to better assess the impact of Tgfbr2 and Piezo1 disruption, the authors should provide more comprehensive flow cytometry analyses and histological data for these mouse models. Given the apparent homogeneity of VSIG4⁺ macrophages (as shown by the authors themselves), bulk RNA-Seq of sorted Tgfbr2- and Piezo1-deficient VSIG4⁺ macrophages (or from TGFβ-treated animals) would offer valuable insights into both the effectiveness of gene deletion and the molecular pathways governed by TGFβ and PIEZO1 in lining macrophages.

Minor points:

• Consistent usage of Cx3cr1-GFP+ nomenclature (for instance: Fig. S1 legend "adult mouse synovial tissue, showing PDGFRα⁺ fibroblasts (yellow) and CX3CR1-GFP⁺ cells (cyan)." versus Fig. 1 legend "Automated spot detection highlights Cx3cr1-GFP⁺ macrophages)"
• Unclear Fig. 3 legend: "Representative immunofluorescence images of synovial tissue from Clec9aCre:Rosa26lsl-tdT mice at 3 weeks and in adulthood, showing and tdTomato (yellow) and stained for DAPI (blue), VSIG4 (cyan)" Check 'showing and tdTomato.'
• For greater clarity, it would have been helpful if the transcript names had been directly included within Figures 3C, S3A, and S3C.
• Page 24: "(Mki67CreERT2:Rosa26lsl-tdT)" Last bracket not superscript.
• Page 25: "we again leveraged our scRNAsequencing dataset" Missing punctuation.
• Page 27: Fig. 5C legend: " of synovial tissue of 1 week-old, 3 weeks-old and adult mice." Please specify and change to 'adult Csf1rΔFIRE/ΔFIRE mice'.
• Page 30: The outcome observed in the Acta1-rtTA:tetO-Cre:ChR2-V5fl mouse model appears to be inconclusive: "This approach resulted in an increased density of VSIG4+ and total (F4/80+) macrophages in the exposed leg of some 5 days-old pups, but others showed the opposite trend (Figure S5D)." This variability may reflect low efficiency of the model or other technical limitations (e.g. muscle contractions frequency or time point of analysis). Given this ambiguity, it is worth reconsidering whether the data are sufficiently robust to warrant inclusion. Should the authors choose to include these findings, further experimentation of appropriate depth and precision is required to allow a conclusive interpretation (either it increases the density of VSIG4+ macrophages or not). The same applies to the Yoda1-treated mice, for which additional data are needed to determine whether VSIG4⁺ macrophage density is truly affected.

Significance

• General assessment: provide a summary of the strengths and limitations of the study. What are the strongest and most important aspects? What aspects of the study should be improved or could be developed?

This is a well-designed study that uses cutting-edge methodologies to investigate the developmental trajectory of synovial lining macrophages under homeostatic conditions. The authors present robust experimental evidence and compelling interpretations concerning synovial macrophage origin, which are both well-substantiated and impactful. Nonetheless, from the reviewer's perspective, the section exploring the molecular mechanisms underlying macrophage differentiation is comparatively less convincing. This section appears somewhat underdeveloped, as some of the mechanistic claims lack sufficient depth and experimental rigor to fully substantiate the conclusions. - Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field:

In contrast to earlier studies (PMID: 31391580, 32601335), the inclusion of fate-mapping experiments adds an important dimension, offering novel insight into the ontogeny of synovial macrophages. This expanded perspective may prove particularly valuable in advancing our understanding of joint immunology, especially regarding the local origins and lineage relationships of macrophage populations. Furthermore, the authors present novel insights into the molecular pathways underlying the differentiation and development of synovial lining macrophages. By demonstrating previously unrecognized regulatory mechanisms, this work significantly deepens our understanding of the cellular and transcriptional programs that drive macrophage specialization within the joint microenvironment. -Place the work in the context of the existing literature (provide references, where appropriate):

This study builds upon previous work characterizing the macrophage compartment in the joint (PMID: 31391580, 32601335), yet provides a substantially more comprehensive dataset that spans multiple developmental time points and data on the origin of this specialized macrophage subset. - State what audience might be interested in and influenced by the reported findings:

Immunologist, clinicians - 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.

This study falls well within the scope of the reviewer's expertise in innate immunity.

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Reply to the reviewers

Manuscript number: RC-2025-02879 Corresponding author(s): Matteo Allegretti; Alia dos Santos

1. General Statements

In this study, we investigated the effects of paclitaxel on both healthy and cancerous cells, focusing on alterations in nuclear architecture. Our novel findings show that:

• Paclitaxel-induced microtubule reorganisation during interphase alters the perinuclear distribution of actin and vimentin. The formation of extensive microtubule bundles, in paclitaxel or following GFP-Tau overexpression, coincides with nuclear shape deformation, loss of regulation of nuclear envelope spacing, and alteration of the nuclear lamina.

• Paclitaxel treatment reduces Lamin A/C protein levels via a SUN2-dependent mechanism. SUN2, which links the lamina to the cytoskeleton, undergoes ubiquitination and consequent degradation following paclitaxel exposure.

• Lamin A/C expression, frequently dysregulated in cancer cells, is a key determinant of cellular sensitivity to, and recovery from, paclitaxel treatment.

Collectively, our data support a model in which paclitaxel disrupts nuclear architecture through two mechanisms: (i) aberrant nuclear-cytoskeletal coupling during interphase, and (ii) multimicronucleation following defective mitotic exit. This represents an additional mode of action for paclitaxel beyond its well-established mechanism of mitotic arrest.

We thank the reviewers for their time and constructive feedback. We have carefully considered all comments and have carried out a full revision. The updated manuscript now includes additional data showing:

• Overexpression of microtubule-associated protein Tau causes similar nuclear aberration phenotypes to paclitaxel. This supports our hypothesis that increased microtubule bundling directly leads to nuclear disruption in paclitaxel during interphase.

• Paclitaxel's effects on nuclear shape and Lamin A/C and SUN2 expression levels occur independently of cell division.

• Reduced levels of Lamin A/C and SUN2 upon paclitaxel treatment occur at the protein level via ubiquitination of SUN2.

• The effects of paclitaxel on the nucleus are conserved in breast cancer cells.

Full Revision

We have also edited our text and added further detail to clarify points raised by the reviewers. We believe that our revised manuscript is overall more complete, solid and compelling thanks to the reviewers' comments.

1. Point-by-point description of the revisions

Reviewer #1 Evidence, reproducibility and clarity

This description of the down-regulation of the expression of lamin A/C upon treatment with paclitaxel and its sensitivity to SUN2 is quite interesting but still somehow preliminary. It is unclear whether this effect involves the regulation of gene expression, or of the stability of the proteins. How SUN2 mediates this effect is still unknown.

We thank the reviewer for this valuable comment. To elucidate the mechanism behind the decrease in Lamin A/C and SUN2 levels, we have now performed several additional experiments. First, we performed RT-qPCR to quantify mRNA levels of these genes, relative to the housekeeping gene GAPDH (Supplementary Figure 3B and O). The levels of SUN2 and LMNA mRNA remained the same between control and paclitaxel-treated cells, indicating that this effect instead occurs at the protein level. We have also tested post-translational modifications as a potential regulatory mechanism for Lamin A/C and SUN2. In addition to the phosphorylation of Ser404 which we had already tested (Supplementary Figure 3C), we have now included additional Phos-tag gel and Western blotting data showing that the overall phosphorylation status of Lamin A/C is not affected by paclitaxel (Supplementary Figure 3E and F). We also pulled-down Lamin A/C from cell lysates and then Western blotted for polyubiquitin and acetyl-lysine, which showed that the ubiquitination and acetylation states of Lamin A/C are also not affected by paclitaxel (Supplementary Figure 3G-I). However, Western blots for polyubiquitin of SUN2 pulled down from cell lysates showed that paclitaxel treatment results in significant SUN2 ubiquitination (Figure 3M and N). Therefore, we propose that the downregulation of SUN2 following paclitaxel treatment occurs by ubiquitin-mediated proteolysis.

The roles of free tubulins and polymerized microtubules, and thus the potential role of paclitaxel, need to be uncovered.

We addressed this important point by using an alternative method to stabilise/bundle microtubules in interphase, namely by overexpressing GFP-Tau, as suggested by reviewer 2. Following GFP- Tau overexpression, large microtubule bundles were observed throughout the cytoplasm (Figure 4A), and this resulted in a significant decrease in nuclear solidity (Figure 4B). Furthermore, in cells where microtubule bundles extensively contacted the nucleus, the nuclear lamina became unevenly distributed and appeared patchy (Figure 4C). This supports our hypothesis that the aberrations to nuclear shape and Lamin A/C localisation in paclitaxel-treated cells are due to the presence of microtubules bundles surrounding the nucleus.

The doses of paclitaxel at which occur the effects described in the paper are not fully consistent with all the conclusions. Most experiments have been done at 5 nM. However, at this dose the effect of lamin A/C over or down expression on the growth (differences in the slopes of the curves in Figure 4A) are not fully convincing and not fully consistent with the clear effect on viability as well (in addition, duration of treatments before assessing vialbility are not specified). At 1 nM, cell growth is reduced and the rescuing effect of lamin over-expression is much more clear (Fig 4A), and the nucleus deformation clear (Fig 2A) but this dose has no effect on lamin A/C expression (Fig 3C), which questions how lamins impact nucleus shape and cell survival. Cytoskeleton reorganisation in these conditions is not described although it could clarify the respective role of force production (suggested in figure 1) and nuclei resistance (shown in figure 2) in paclitaxel sensitivity.

We thank the reviewer for raising this important point. We have addressed this by conducting additional repeats for the cell confluency measurements to increase the statistical power of our experiments (Figure 5A). Our data now show that GFP-lamin A/C had a statistically significant effect on rescuing cell growth at both 1 nM and 5 nM paclitaxel, while Lamin A/C knockdown exacerbated the inhibition of cell growth at 5 nM paclitaxel but not 1 nM paclitaxel (Figure 5A). In addition, we note that the duration of paclitaxel treatment before assessing viability was specified in the figure legend: "Bar graph comparing cell viability between wild-type (red), GFP-Lamin A/C overexpression (green), and Lamin A/C knockdown (blue) cells following 20 h incubation in 0, 1, 5, or 10 nM paclitaxel." We also repeated cell viability analysis after 48 h incubation in paclitaxel instead of 20 h to allow for a longer time for differences to take effect (Figure 5B).

We also added figures showing the cytoskeletal reorganisation at both 1 and 10 nM in addition to 0 and 5 nM (Supplementary Figure 1A) showing that microtubule bundling and condensation of actin into puncta correlated with increased paclitaxel concentration. Vimentin colocalised well with microtubules at all concentrations.

We have also included in our results section further clarification for the use of 5nM paclitaxel in this study. The new section reads as follows: "Experiments were performed at 5 nM paclitaxel (with additional experiments to determine dose relationships at 1 and 10 nM) because this aligns with previous studies7,14,24. Furthermore, previous analysis of patient plasma reveals that typical concentrations are within the low nanomolar range8, and concentrations of 5-10 nM are required in cell culture to reach the same intracellular concentrations observed in vivo in patient tumours9. This aligns with in vitro cytotoxic studies of paclitaxel in eight human tumour cell lines which show that paclitaxel's IC50 ranges between 2.5 and 7.5 nM41."

Finally, although the absence of role of mitotic arrest is clear from the data, the defective reorganisation of the nucleus after mitosis still suggest that the effect of paclitaxel is not independent of mitosis.

We thank the reviewer for pointing out the need for clarification in the wording of our manuscript. We have reworded the title and relevant sections of our abstract, introduction, and discussion to make it clearer that the effects of paclitaxel on the nucleus are due to a combination of aberrant nuclear cytoskeletal coupling during interphase and multimicronucleation following mitotic slippage. We have also added additional data in support of the effect of paclitaxel on nuclear architecture during interphase. For this, we used serum-starved cells (which divide only very slowly such that the majority of cells do not pass through mitosis during the 16 h incubation in paclitaxel [Supplementary Figure 2D]). Our new data confirmed that paclitaxel's effects on nuclear solidity, and Lamin A/C and SUN2 proteins levels can occur independently of cell division (Figure 2C; Figure 3H-J). Finally, when we overexpressed GFP-Tau (as discussed above) we observed similar aberrations to nuclear solidity and Lamin A/C localisation. This indicates that these effects occur due to microtubule bundling in interphase, especially as in our study GFP-Tau did not lead to multimicronucleation or appear to affect mitosis (Figure 4).

Below are the main changes to the text regarding the interphase effect of paclitaxel:

• Title: "Paclitaxel compromises nuclear integrity in interphase through SUN2-mediated cytoskeletal coupling"

• Abstract: "Overall, our data supports nuclear architecture disruption, caused by both aberrant nuclear-cytoskeletal coupling during interphase and exit from defective mitosis, as an additional mechanism for paclitaxel beyond mitotic arrest."

• Introduction: "Here we propose that cancer cells have increased vulnerability to paclitaxel both during interphase and following aberrant mitosis due to pre-existing defects in their NE and nuclear lamina."

• Discussion: "Overall, our work builds on previous studies investigating loss of nuclear integrity as an anti-cancer mechanism of paclitaxel separate from mitotic arrest14,20,21. We propose that cancer cells show increased sensitivity to nuclear deformation induced by aberrant nuclear-cytoskeletal coupling and multimicronucleation following mitotic slippage. Therefore, we conclude that paclitaxel functions in interphase as well as mitosis, elucidating how slowly growing tumours are targeted."

minor: a more thorough introduction of known data about dose response of cells in culture and in vivo would help understanding the range of concentrations used in this study.

As mentioned above, we have now included additional information in our Results section to clarify our paclitaxel dose range: "Experiments were performed at 5 nM paclitaxel (with additional experiments to determine dose relationships at 1 and 10 nM) because this aligns with previous studies7,14,24. Furthermore, previous analysis of patient plasma reveals that typical concentrations are within the low nanomolar range8, and concentrations of 5-10 nM are required in cell culture to reach the same intracellular concentrations observed in vivo in patient tumours9. This aligns with in vitro cytotoxic studies of paclitaxel in eight human tumour cell lines which show that paclitaxel's IC50 ranges between 2.5 and 7.5 nM41."

Significance

In this manuscript, Hale and colleagues describe the effect of paclitaxel on nucleus deformation and cell survival. They showed that 5nM of paclitaxel induces nucleus fragmentation, cytoskeleton reorganisation, reduced expression of LaminA/C and SUN2, and reduced cell growth and viability. They also showed that these effects could be at least partly compensated by the over-expression of lamin A/C. As fairly acknowledged by the authors, the induction of nuclear deformation in paclitaxel-treated cells, and the increased sensitivity to paclitaxel of cells expressing low level of lamin A/C are not novel (reference #14). Here the authors provided more details on the cytoskeleton changes and nuclear membrane deformation upon paclitaxel treatment. The effect of lamin A/C over and down expression on cell growth and survival are not fully convincing, as further discussed below. The most novel part is the observation that paclitaxel can induce the down-regulation of the expression of lamin A/C and that this effect is mediated by SUN2.

We appreciate the reviewer's summary and thank them for their time. We believe our comprehensive revisions have addressed all comments, strengthening the manuscript and making it more robust and compelling.

Reviewer #2 Evidence, reproducibility and clarity This study investigates the effects of the chemotherapeutic drug paclitaxel on nuclear-cytoskeletal coupling during interphase, claiming a novel mechanism for its anti-cancer activity. The study uses hTERT-immortalized human fibroblasts. After paclitaxel exposure, a suite of state- of-the-art imaging modalities visualizes changes in the cytoskeleton and nuclear architecture. These include STORM imaging and a large number of FIB-SEM tomograms.

We thank the reviewer for the summary and for highlighting our efforts in using the latest imaging technical advances.

Major comments:

The authors make a major claim that in addition to the somewhat well-described mechanism of paclitaxel on mitosis, they have discovered 'an alternative, poorly characterised mechanism in interphase'.

However, none of the data proves that the effects shown are independent of mitosis. To the contrary, measurements are presented 48 hours after paclitaxel treatment starts, after which it can be assumed that 100% of cells have completed at least one mitotic event. The appearance of micronuclei evidences this, as discussed by the authors shortly. It looks like most of the results shown are based on botched mitosis or, more specifically, errors on nuclear assembly upon exit from mitosis rather than a specific effect of paclitaxel on interphase. The readouts the authors show just happen to be measurements while the cells are in interphase.

Alternative hypotheses are missing throughout the manuscript, and so are critical controls and interpretations.

We thank the reviewer for highlighting the lack of clarity in our wording. We have revised the title, abstract and relevant sections of the introduction and discussion to clarify our message that the effects of paclitaxel on the nucleus arise from a combination of aberrant nuclear-cytoskeletal coupling during interphase and multimicronucleation following exit from defective mitosis. We have also included additional data where we used slow-dividing, serum-starved cells (under these conditions, the majority of cells do not undergo mitosis during the 16 h incubation in paclitaxel [Supplementary Figure 2D]). Our new data show that even in these cells there is a clear effect of paclitaxel on nuclear solidity, and Lamin A/C and SUN2 protein levels, further supporting our hypothesis that these phenotypes can occur independently of cell division (Figure 2C; Figure 3H-J). Furthermore, we performed additional experiments where we used overexpression of GFP-Tau as an alternative method of stabilising microtubules in interphase and observed similar aberrations to nuclear solidity and Lamin A/C localisation. As GFP-Tau overexpression did not lead to micronucleation or appear to affect mitosis, these data support the hypothesis that nuclear aberrations occur due to microtubule bundling in interphase (Figure 4). We discuss these experiments in more detail below. Finally, we have reworded the introduction to better introduce alternative hypotheses and mechanisms for paclitaxel's activity.

The authors claim that 'Previously, the anti-cancer activity of paclitaxel was thought to rely mostly on the activation of the mitotic checkpoint through disruption of microtubule dynamics, ultimately resulting in apoptosis.' The authors may have overlooked much of the existing literature on the topic, including many recent manuscripts from Xiang-Xi Xu's and another lab.

We would like to note that the paper from Xiang-Xi Xu's lab (Smith et al, 2021) was cited in our original manuscript (reference 14 in both the original and revised manuscripts). We have now also included additional review articles from the Xiang-Xi Xu lab (PMID:36368286 20 and PMID: 35048083 21). Furthermore, we have clarified the wording in both the introduction and discussion to better reflect the current understanding of paclitaxel's mechanism and alternative hypotheses.

The data, e.g. in Figure 1, does not hold up to the first alternative hypothesis, e.g. that paclitaxel stabilizes microtubules and that excessive mechanical bundling of microtubules induces major changes to cell shape and mechanical stress on the nucleus. Even the simplest controls for this effect (the application of an alternative MT stabilizing drug or the overexpression of an MT stabilizer, e.g., tau).

We thank the reviewer for suggesting this control experiment using the microtubule stabiliser Tau. We have now included these experiments in the revised version of the manuscript (Figure 4). The overexpression of GFP-Tau supports our hypothesis that cytoskeletal reorganisation in paclitaxel exerts mechanical stress on the nucleus during interphase, resulting in nuclear deformation and aberrations to the nuclear lamina. In particular, GFP-Tau overexpression resulted in large microtubule bundles throughout the cytoplasm (Figure 4A). Notably, in cells where these bundles extensively contacted the nucleus, we observed a significant decrease in nuclear solidity (Figure 4B) accompanied by changes in nuclear lamina organisation, including a patchy lamina phenotype, similar to that induced by paclitaxel (Figure 4C).

The focus on nuclear lamina seems somewhat arbitrary and adjacent to previously published work by other groups. What would happen if the authors stained for focal adhesion markers? There would probably be a major change in number and distribution. Would the authors conclude that paclitaxel exerts a specific effect on focal adhesions? Or would the conclusion be that microtubule stabilization and the following mechanical disruption induce pleiotropic effects in cells? Which effects are significant for paclitaxel function on cancer cells?

We thank the reviewer for raising important points regarding the specificity of paclitaxel's effects. We agree that microtubule stabilisation can induce myriad cellular changes, including alterations to focal adhesions and other cytoskeletal components. Our focus on Lamin A/C and nuclear morphology is grounded both in the established clinical relevance of nuclear mechanics in cancer and builds on mechanistic work from other groups.

Lamin A/C expression is commonly altered in cancer, and nuclear morphology is frequently used in cancer diagnosis35. Lamin A/C also plays a crucial role in regulating nuclear mechanics32 and, importantly, determines cell sensitivity to paclitaxel14. However, the mechanism by which Lamin A/C determines sensitivity of cancer cells to paclitaxel is unclear.

Our data are consistent with Lamin A/C being a determinant of paclitaxel survival sensitivity. We also provide evidence that paclitaxel itself reduces Lamin A/C protein levels and disrupts its organisation at the nuclear envelope. We directly link these effects to microtubule bundling around the nucleus and degradation of force-sensing LINC component SUN2, highlighting the importance of nuclear architecture and mechanics to overall cellular function. Furthermore, we show that recovery from paclitaxel treatment depends on Lamin A/C expression levels. This has clinical relevance, as unlike cancer cells, healthy tissue with non-aberrant lamina would be able to selectively recover from paclitaxel treatment.

Minor comments:

While I understand the difficulty of the experiments and the effort the authors have put into producing FIB-SEM tomograms, I am not sure they are helping their study or adding anything beyond the light microscopy images. Some of the images may even be in the way, such as supplementary Figure 6, which lacks in quality, controls, and interpretation. Do I see a lot of mitochondria in that slice?

We agree with the reviewer that Supplementary Figure 6 does not add significant value to the manuscript and thank the reviewer for pointing this out. We have removed it from the manuscript accordingly.

I may have overlooked it, but has the number of cells from which lamellae have been produced been stated?

We thank the reviewer for pointing out the missing information. For our cryo-ET experiments, we collected data from 9 lamellae from paclitaxel-treated cells and 6 lamellae from control cells, with each lamella derived from a single cell. This information has now been added to the figure legend (Figure 2F).

Significance

The significance of studying the effect of paclitaxel, the most successful chemotherapy drug, should be broad and of interest to basic researchers and clinicians.

As outlined above, I believe that major concerns about the design and interpretation of the study hamper its significance and advancements.

We appreciate the reviewer's concerns and have performed major revisions to strengthen the significance of our study. Specifically, we conducted two key sets of experiments to validate our original conclusions: serum starvation to control for the effects of cell division, and overexpression of the microtubule stabiliser Tau to demonstrate that paclitaxel can affect the nucleus via its microtubule bundling activity in interphase.

By elucidating the mechanistic link between microtubule stabilisation and nuclear-cytoskeletal coupling, our findings contribute to our understanding of paclitaxel's multifaceted actions in cancer cells.

My areas of expertise could be broadly defined as Cell Biology, Cytoskeleton, Microtubules, and Structural Biology.

Reviewer #3 Evidence, reproducibility and clarity The manuscript presents interesting new ideas for the mechanism of an old drug, taxol, which has been studied for the last 40 years.

We thank the reviewer for the positive feedback.

Although similar ideas are published, which may be suitable to be cited? • Paclitaxel resistance related to nuclear envelope structural sturdiness. Smith ER, Wang JQ, Yang DH, Xu XX. Drug Resist Updat. 2022 Dec;65:100881. doi: 10.1016/j.drup.2022.100881. Epub 2022 Oct 15. PMID: 36368286 Review. • Breaking malignant nuclei as a non-mitotic mechanism of taxol/paclitaxel. Smith ER, Xu XX. J Cancer Biol. 2021;2(4):86-93. doi: 10.46439/cancerbiology.2.031. PMID: 35048083 Free PMC article.

We thank the reviewer for bringing to our attention these important review articles. In our initial manuscript, we only cited the original paper (14, also reference 14 in the original manuscript). We have now included citations to the suggested publications (20,21).

We would also like to emphasise how our manuscript distinguishes itself from the work of Smith et al.14,20,21:

• Cell-type focus: In their study 14, Smith et al. examined the effect of paclitaxel on malignant ovarian cancer cells and proposed that paclitaxel's effects on the nucleus are limited to cancer cells. However, our data extends these findings by demonstrating paclitaxel's effects in both cancerous and non-cancerous backgrounds.

• Cytoskeletal reorganisation: Smith et al. show reorganisation of microtubules in paclitaxel-treated cells14. Our data show re-organisation of other cytoskeletal components, including F-actin and vimentin.

• Multimicronucleation: Smith et al. propose that paclitaxel-induced multimicronucleation occurs independently of cell division14. Although we observe progressive nuclear abnormalities during interphase over the course of paclitaxel treatment, our data do not support this conclusion; we find that multimicronucleation occurs only following mitosis.

• Direct link between microtubule bundling and nuclear aberrations: We show that nuclear aberrations caused by paclitaxel during interphase (distinct from multimicronucleation) are directly linked to microtubule bundling around the nucleus, suggesting they result from mechanical disruption and altered force propagation.

• Lamin A/C regulation: Consistent with Smith et al.14, we show that Lamin A/C depletion leads to increased sensitivity to paclitaxel treatment. However, we further demonstrate that paclitaxel itself leads to reduced levels of Lamin A/C and that this effect occurs independently of mitosis and is mediated via force-sensing LINC component SUN2. Upon SUN2 knockdown, Lamin A/C levels are no longer affected by paclitaxel treatment.

• Recovery: Finally, our work reveals that cells expressing low levels of Lamin A/C recover less efficiently after paclitaxel removal. This might help explain how cancer cells could be more susceptible to paclitaxel.

Only one cell line was used in all the experiments? "Human telomerase reverse transcriptase (hTERT) immortalised human fibroblasts" ? The cells used are not very relevant to cancer cells (carcinomas) that are treated with paclitaxel. It is not clear if the observations and conclusions will be able to be generalized to cancer cells.

We thank the reviewer for this comment. Our initial study aimed to understand the effects of paclitaxel on nuclear architecture in non-aberrant backgrounds. To show that the observed effects of paclitaxel are also applicable to cancer cells, we have now repeated our main experiments using MDA-MB-231 human breast cancer cells (Supplementary Figure 1B; Supplementary Figure 3P-T). Similar to our findings in human fibroblasts, paclitaxel treatment of MDA-MB-231 led to cytoskeletal reorganisation (Supplementary Figure 1B), a decrease in nuclear solidity (Supplementary Figure 3P), aberrant (patchy) localisation of Lamin A/C (Supplementary Figure 3Q), and a reduction in Lamin A/C and SUN2 levels (Supplementary Figure 3R-T).

"Fig. 1. (B) STORM imaging of α-tubulin immunofluorescence in cells fixed after 16 h incubation in control media or 5 nM paclitaxel. Lower panels show α-tubulin clusters generated with HDBSCAN analysis. Scale bars = 10 μm." It needs explanation of what is meaning of the different color lines in the lower panels, just different filaments?

We have added further detail to the figure legend for clarification: "Lower panels show α-tubulin clusters generated with HDBSCAN analysis. Different colours distinguish individual α-tubulin clusters, representing individual microtubule filaments or filament bundles."

Generally, the figures need additional description to be clear.

We have added further clarification and detail to our figure legends.

"Figure 3 - Paclitaxel results in aberrations to the nuclear lamina." The sentence seems not to be well constructed. "Paclitaxel treatment causes ..."?

We changed this sentence to: "Figure 3 - Paclitaxel treatment results in aberrant organisation of the nuclear lamina and decreased Lamin A/C levels via SUN2."

Lamin A and C levels are different in different images (Fig. 3B, H): some Lamin A is higher, and sometime Lamin C is higher? This may possibly due to culture condition or subtle difference in sample handling?.

We thank the reviewer for pointing this out and we agree that the ratio of Lamin A to Lamin C can vary with culture conditions. To confirm that paclitaxel treatment reduces total Lamin A/C levels regardless of this ratio, we repeated the Western blot analysis in three additional biological replicates using cells in which Lamin C levels exceeded Lamin A levels. These experiments confirmed a comparable decrease in total Lamin A/C levels. Figure 3B and 3C have been updated accordingly.

Also, the effect on Lamin A/C and SUN2 levels are not significant of robust.

Decreased Lamin A/C and SUN2 levels following paclitaxel treatment were consistently seen across three or more biological repeats (Figure 3B-C), and this could be replicated in a different cell type (MDA-MB-231) (Supplementary Figure 3R-T). Furthermore, Western blotting results are consistent with the patchy Lamin A/C distribution observed using confocal and STORM following paclitaxel treatment (Figure 3A; Supplementary Figure 3A), where Lamin A/C appears to be absent from discrete areas of the lamina.

Any mechanisms are speculated for the reason for the reduction?

We have now included additional data which aims to shed light on the mechanism behind the decrease in Lamin A/C and SUN2 levels following paclitaxel treatment. We found that SUN2 is selectively degraded during paclitaxel treatment. Immunoprecipitation of SUN2 followed by Western blotting against Polyubiquitin C showed increased SUN2 ubiquitination in paclitaxel (Figure 3M and N). Furthermore, in our original manuscript, we showed that Lamina A/C levels remained unaltered during paclitaxel treatment in cells where SUN2 had been knocked down. We propose that changes in microtubule organisation affect force propagation to Lamin A/C specifically via SUN2 and that this leads to Lamina A/C removal and depletion. Future work will be needed to fully understand this mechanism.

In addition to the findings described above, we report no significant changes in mRNA levels for LMNA or SUN2 in paclitaxel (Supplementary Figure 3B and O). Phos-tag gels followed by Western blotting analysis for Lamin A/C also did not detect changes to the overall phosphorylation status of Lamin A/C due to paclitaxel treatment. This is in agreement with our initial data showing no changes to Lamin A/C Ser 404 phosphorylation levels (Supplementary Figure 3E and F). Finally, Lamin A/C immunoprecipitation experiments followed by Western blotting for Polyubiquitin C and acetyl-lysine showed no significant changes in the ubiquitination and acetylation state of Lamin A/C in paclitaxel-treated cells (Supplementary Figure 3G-I).

Also, the about 50% reduction in protein level is difficult to be convincing as an explanation of nuclear disruption.

The nuclear lamina and LINC complex proteins play a critical role in regulating nuclear integrity, stiffness and mechanical responsiveness to external forces28,31-33,54,75, as well as in maintaining the nuclear intermembrane distance69,74. In particular, SUN-domain proteins physically bridge the nuclear lamina to the cytoskeleton through interactions with Nesprins, thereby preserving the perinuclear space distance30,69,74. Mutations in Lamins have been shown to disrupt chromatin organization, alter gene expression, and compromise nuclear structural integrity, and experiments with LMNA knockout cells reveal that nuclear mechanical fragility is closely coupled to nuclear deformation47. Furthermore, nuclear-cytoskeletal coupling is essential during processes such as cell migration, where cells undergo stretching and compression of the nucleus; weakening or loss of the lamina in such cases compromises cell movement47,73. In our work, we show that alterations to nuclear Lamin A/C and SUN2 by paclitaxel treatment coincide with nuclear deformations (Figure 2A-D, F, G; Figure 3A-D, F, G; Supplementary Figure 3A, P-T) and that these deformations are reversible following paclitaxel removal (Supplementary Figure 4B-D). Our experiments also demonstrate that Lamin A/C expression levels significantly influence cell growth, cell viability, and cell recovery in paclitaxel (Figure 5). Therefore, drawing on current literature and our results, we propose that, during interphase, paclitaxel induces severe nuclear aberrations through the combined effects of: i) increased cytoskeletal forces on the NE caused by microtubule bundling; ii) loss of ~50% Lamin A/C and SUN2; iii) reorganisation of nucleo-cytoskeletal components.

Significance

The manuscript presents interesting new ideas for the mechanism of an old drug, taxol, which has been studied for the last 40 years.

The data may be improved to provide stronger support.

Additional cell lines (of cancer or epithelial origin) may be repeated to confirm the generality of the observation and conclusions.?

We thank the reviewer for the feedback and valuable suggestions. In response, we have included experiments using human breast cancer cell line MDA-MB-231 to further corroborate our findings and interpretations. We believe these additions have improved the clarity, robustness and impact of our manuscript, and we are grateful for the reviewer's contributions to its improvement.

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

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Referee #3

Evidence, reproducibility and clarity

The manuscript presents interesting new ideas for the mechanism of an old drug, taxol, which has been studied for the last 40 years. Although similar ideas are published, which may be suitable to be cited?

• Paclitaxel resistance related to nuclear envelope structural sturdiness. Smith ER, Wang JQ, Yang DH, Xu XX. Drug Resist Updat. 2022 Dec;65:100881. doi: 10.1016/j.drup.2022.100881. Epub 2022 Oct 15. PMID: 36368286 Review.
• Breaking malignant nuclei as a non-mitotic mechanism of taxol/paclitaxel. Smith ER, Xu XX. J Cancer Biol. 2021;2(4):86-93. doi: 10.46439/cancerbiology.2.031. PMID: 35048083 Free PMC article.

Only one cell line was used in all the experiments? "Human telomerase reverse transcriptase (hTERT) immortalised human fibroblasts" ? The cells used are not very relevant to cancer cells (carcinomas) that are treated with paclitaxel. It is not clear if the observations and conclusions will be able to be generalized to cancer cells.

"Fig. 1. (B) STORM imaging of α-tubulin immunofluorescence in cells fixed after 16 h incubation in control media or 5 nM paclitaxel. Lower panels show α-tubulin clusters generated with HDBSCAN analysis. Scale bars = 10 μm." It needs explanation of what is meaning of the different color lines in the lower panels, just different filaments?

Generally, the figures need additional description to be clear.

"Figure 3 - Paclitaxel results in aberrations to the nuclear lamina." The sentence seems not to be well constructed. "Paclitaxel treatment causes ..."?

Lamin A and C levels are different in different images (Fig. 3B, H): some Lamin A is higher, and sometime Lamin C is higher? This may possibly due to culture condition or subtle difference in sample handling?. Also, the effect on Lamin A/C and SUN2 levels are not significant of robust. Any mechanisms are speculated for the reason for the reduction? Also, the about 50% reduction in protein level is difficult to be convincing as an explanation of nuclear disruption.

Significance

The manuscript presents interesting new ideas for the mechanism of an old drug, taxol, which has been studied for the last 40 years.

The data may be improved to provide stronger support.

Additional cell lines (of cancer or epithelial origin) may be repeated to confirm the generality of the observation and conclusions.?

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

This study investigates the effects of the chemotherapeutic drug paclitaxel on nuclear-cytoskeletal coupling during interphase, claiming a novel mechanism for its anti-cancer activity. The study uses hTERT-immortalized human fibroblasts. After paclitaxel exposure, a suite of state-of-the-art imaging modalities visualizes changes in the cytoskeleton and nuclear architecture. These include STORM imaging and a large number of FIB-SEM tomograms.

Major comments:

The authors make a major claim that in addition to the somewhat well-described mechanism of paclitaxel on mitosis, they have discovered 'an alternative, poorly characterised mechanism in interphase'.

However, none of the data proves that the effects shown are independent of mitosis. To the contrary, measurements are presented 48 hours after paclitaxel treatment starts, after which it can be assumed that 100% of cells have completed at least one mitotic event. The appearance of micronuclei evidences this, as discussed by the authors shortly. It looks like most of the results shown are based on botched mitosis or, more specifically, errors on nuclear assembly upon exit from mitosis rather than a specific effect of paclitaxel on interphase. The readouts the authors show just happen to be measurements while the cells are in interphase.

Alternative hypotheses are missing throughout the manuscript, and so are critical controls and interpretations.

The authors claim that 'Previously, the anti-cancer activity of paclitaxel was thought to rely mostly on the activation of the mitotic checkpoint through disruption of microtubule dynamics, ultimately resulting in apoptosis.' The authors may have overlooked much of the existing literature on the topic, including many recent manuscripts from Xiang-Xi Xu's and another lab.

The data, e.g. in Figure 1, does not hold up to the first alternative hypothesis, e.g. that paclitaxel stabilizes microtubules and that excessive mechanical bundling of microtubules induces major changes to cell shape and mechanical stress on the nucleus. Even the simplest controls for this effect (the application of an alternative MT stabilizing drug or the overexpression of an MT stabilizer, e.g., tau).

The focus on nuclear lamina seems somewhat arbitrary and adjacent to previously published work by other groups. What would happen if the authors stained for focal adhesion markers? There would probably be a major change in number and distribution. Would the authors conclude that paclitaxel exerts a specific effect on focal adhesions? Or would the conclusion be that microtubule stabilization and the following mechanical disruption induce pleiotropic effects in cells? Which effects are significant for paclitaxel function on cancer cells?

Minor comments:

While I understand the difficulty of the experiments and the effort the authors have put into producing FIB-SEM tomograms, I am not sure they are helping their study or adding anything beyond the light microscopy images. Some of the images may even be in the way, such as supplementary Figure 6, which lacks in quality, controls, and interpretation. Do I see a lot of mitochondria in that slice?

I may have overlooked it, but has the number of cells from which lamellae have been produced been stated?

Significance

The significance of studying the effect of paclitaxel, the most successful chemotherapy drug, should be broad and of interest to basic researchers and clinicians.

As outlined above, I believe that major concerns about the design and interpretation of the study hamper its significance and advancements.

My areas of expertise could be broadly defined as Cell Biology, Cytoskeleton, Microtubules, and Structural Biology.

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Referee #1

Evidence, reproducibility and clarity

This description of the down-regulation of the expression of lamin A/C upon treatment with paclitaxel and its sensitivity to SUN2 is quite interesting but still somehow preliminary. It is unclear whether this effect involves the regulation of gene expression, or of the stability of the proteins. How SUN2 mediates this effect is still unknown. The roles of free tubulins and polymerized microtubules, and thus the potential role of paclitaxel, need to be uncovered.

The doses of paclitaxel at which occur the effects described in the paper are not fully consistent with all the conclusions. Most experiments have been done at 5 nM. However, at this dose the effect of lamin A/C over or down expression on the growth (differences in the slopes of the curves in Figure 4A) are not fully convincing and not fully consistent with the clear effect on viability as well (in addition, duration of treatments before assessing vialbility are not specified). At 1 nM, cell growth is reduced and the rescuing effect of lamin over-expression is much more clear (Fig 4A), and the nucleus deformation clear (Fig 2A) but this dose has no effect on lamin A/C expression (Fig 3C), which questions how lamins impact nucleus shape and cell survival. Cytoskeleton reorganisation in these conditions is not described although it could clarify the respective role of force production (suggested in figure 1) and nuclei resistance (shown in figure 2) in paclitaxel sensitivity.

Finally, although the absence of role of mitotic arrest is clear from the data, the defective reorganisation of the nucleus after mitosis still suggest that the effect of paclitaxel is not independent of mitosis.

minor: a more thorough introduction of known data about dose response of cells in culture and in vivo would help understanding the range of concentrations used in this study.

Significance

In this manuscript, Hale and colleagues describe the effect of paclitaxel on nucleus deformation and cell survival. They showed that 5nM of paclitaxel induces nucleus fragmentation, cytoskeleton reorganisation, reduced expression of LaminA/C and SUN2, and reduced cell growth and viability. They also showed that these effects could be at least partly compensated by the over-expression of lamin A/C. As fairly acknowledged by the authors, the induction of nuclear deformation in paclitaxel-treated cells, and the increased sensitivity to paclitaxel of cells expressing low level of lamin A/C are not novel (reference #14). Here the authors provided more details on the cytoskeleton changes and nuclear membrane deformation upon paclitaxel treatment. The effect of lamin A/C over and down expression on cell growth and survival are not fully convincing, as further discussed below. The most novel part is the observation that paclitaxel can induce the down-regulation of the expression of lamin A/C and that this effect is mediated by SUN2.

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Reply to the reviewers

I have already provided a document with a point-by-point response. I do not wish to re-format all of the text again in this HTML box. The document I provided can be published as it is.

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Referee #2

Evidence, reproducibility and clarity

Summary:

This study demonstrates an improved integral gene drive (IGD) for use in Anopheles gambiae. Inserting the coding sequence for Cas9 in-frame with a germline-specific gene (nanos) improved the performance of this IGD relative to previously reported systems while reducing fitness costs. Integration of the gRNA cassette within a synthetic intron is an elegant solution to constraining the minimal elements of the IGD within a single insertion. The results of this study found that while the IGD can be used to propagate anti-malarial effectors (MM-CP) within a population, fitness costs and resistance alleles were higher than anticipated, potentially limiting the application of this particular IGD design without further optimisation.

The results comprehensively demonstrate the effective transmission and stability of the IGD over several generations, while also characterising the limitations of the system. Although I don't think the authors make any claims which are not supported by their results. It might be good to provide more of an explanation for how the performance of this IGD compares to the zpg IGD reported in Ellis et al 2022 for readers less familiar with the IGD literature.

The manuscript is overall very well written with clear results and methods. However, I found the descriptions referring to the effects of the maternal, paternal, and even grandmaternal inheritance hard to follow. The statistical analysis and replications are adequate as well.

Referee cross-commenting

I agree with the other reviewer's comments regarding the need to clarify a few points made in the overall well written manuscript.

Significance

Gene drives are the most promising genetic biocontrol method for controlling the spread of malaria. However, there are many technical challenges that have made the development of gene drives quite difficult. This study works to address one such challenge - constraining the expression of Cas9 to the germline by integrating it within an endogenous loci rather than using semi-synthetic promoters. While IGD have been demonstrated before, this study further improves on their performance while reducing off-target effects.

The manuscript is written for a highly specialized audience that is very familiar with the genetic biocontrol, and especially the gene-drive field of research.

My fields of research include genetic biocontrol and insect synthetic biology.

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Referee #1

Evidence, reproducibility and clarity

In this study, the authors develop a complete integral drive system in Anopheles gambiae malaria mosquitoes. This type of gene drive is interesting, with special advantages and disadvantages compared to more common designs. Here, the authors develop the Cas9 element and combine it with a previously developed antimalaria effector element. The new element performs very well in terms of drive efficiency, but it has unintended fitness costs, and a higher than desirable rate of functional resistance allele formation. Nevertheless, this study represents a very good step forward toward developing effective gene drives and is thus of high impact.

The format of the manuscript is a bit suboptimal for review. Please add line numbers next time for easy reference. It would also help to have spaces between paragraphs and to have figures (with legends) added to the text where they first appear.

It might be useful to add subsections to the results, just like in the methods section. It could even be expanded a bit with some specific parts from the discussion, through this is optional.

Abstract: The text says: "As a minimal genetic modification, nanosd does not induce widespread transcriptomic perturbations." However, it does seem to change things based on Figure 3c.

Page 2: "drive technologies for public health and pest control applications" needs a period afterward.

Page 2: "The fitness costs, homing efficiency, and resistance rate of the gene drive is" should be "The fitness costs, homing efficiency, and resistance rate of the gene drive are".

Page 2: "When they target important mosquito genes, gene drives are designed to ensure that the nuclease activity window (germline) does not overlap with that of the target gene (somatic)." is note quite correct. This is, of course, sensible for suppression drives, but it's not a necessary requirement for modification drives with rescue elements in many situations.

Page 2: "recessive somatic fitness cost phenotypes" is unclear. I think that you are trying to avoid the recessive fitness cost of null alleles becoming a dominant fitness cost from a gene drive allele (in drive-wild-type heterozygotes).

Page 2: "This optimization approach has had only limited success, and suboptimal performance is commonly attributed to not capturing all the regulatory elements specific to the germline gene's expression9,12". I don't think this is correct. There are several examples where a new promoter helped a lot. The zpg promoter in Anopheles gambiae allowed success at the dsx site in suppression cage studies (Kyrou et al 2018), and nanos gave big improvement to modification drives at the cardinal locus (Carballer et al 2020). In flies, several promoters were tested, and one allowed success in cage experiments (Du et al 2024). In Aedes, the shu promoter allowed for high drive performance (Anderson et al 2023), though this last one hasn't been tested in more difficult situations. I think you could certainly argue in the general case that not all promoters will work the way their transcriptome says, but there are many examples where they seem to be pretty good.

Page 2: "make it more likely that mutations that disrupt the drive components are selected against though loss of function of the host gene." I think that this needs a bit more explanation. You are referring to mutations in regulatory elements or frameshift mutations. This will make it more resistant to mutation. Also, these mutations would tend to have a minor effect expect perhaps in the cargo gene of a modification drive. By using a cargo gene in an integral drive, you could still keep it somewhat safer, but whether this is 1.2x or 10x safer is unclear.

Page 3: "they can incur severe unintended fitness costs". This is central to integral drives and this manuscript. It's worth elaborating on.

Page 3: "Regulatory elements from germline genes that have worked sub-optimally in traditional gene drive designs for the reasons outlined above may work well in an IDG design20." This is setting up the integral drive with nanos, but nanos DOES work well in traditional Anopheles gambiae gene drive designs. It is possible that you might end up with less somatic expression than Hammond et al 2020 (though the comparison is unclear due to batch effects in that study), but there is no direct comparison in this manuscript to that.

Page 3: "This suggests an impact of maternal deposition on drive efficiency only in female drive carriers." This is quite strange. Usually, I would expect to see an equal reduction in efficiency between male and female progeny. Could this be due to limited sample size? Random idea: It's also possible that almost all maternal deposition was mosaic and wouldn't be enough to direct affect drive conversion. However, it could cause enough of a fitness cost TOGETHER with new drive expression in females that perhaps only tissues with randomly low expression rates properly developed and led to progeny, reducing drive inheritance? Another possibility: Could the drive/resistance males have impaired fertility, so these ones are underrepresented in the batch cross? If nanos is needed in males and a single drive copy is not quite enough for good fertility or mating competitiveness, they may be underrepresented in your crosses. They might have worse fertility than drive homozygous males, which at least have two partially working copies of nanos rather than just one (in many cells, at least). Maybe check the testis for abnormal phenotypes?

Overall, it would be favorable if the drive allele was somewhere more fit than a nonfunctional resistance allele. This could already be achieved in this drive, but it doesn't get much mention.

Page 3: There should be a comma after, "Interestingly, while many of the observed mutations were predicted to abolish nanos expression" and "This could indicate that in these experiments".

Page 3 last sentence: Please improve the clarity.

Removing the EGFP is supposed to restore the fitness, and this was helpful in some previous integral drive constructs. This could get a bit more mention (it is possible that I missed this somewhere in the manuscript).

Page 4: The MM-CP line and it's association with the integral drive strategy could get a little more introduction. Maybe even a supplemental figure showing the general idea.

Page 5: "cassette is predicted to disrupt the CP function entirely (Fig. 5d)" also lacks a period.

Page 5: "The subsequent stabilization of the nanosd frequency and the lack of rapid loss suggests that any associated fitness cost is primarily recessive." This is not quite correct because by this point, drive/wild-type heterozygotes are rare, and this is where you'd find a potential dominant fitness cost. It should be correct in the end stages where it is a mix of drive and functional/nonfunctional resistance alleles (though the nonfunctional resistance alleles may cause greater fitness costs when together with a drive - see above).

Page 6: "Maternal deposition of Cas9, or Cas9;gRNA, into the zygote can lead to cutting at stages when homing is not favoured, and has been commonly observed for canonical Anopheles nanos drives9,10,35." Reference 35 (which is more suitable for referencing an example of nanos in other Anopheles) found some resistance alleles by deep sequencing, but the timing that they formed was unclear (it's not certain if it was maternal deposition). This study may be a more suitable reference: Carballar-Lejarazú R, Tushar T, Pham TB, James AA. Cas9-mediated maternal-effect and derived resistance alleles in a gene-drive strain of the African malaria vector mosquito, Anopheles gambiae. Genetics, 2022.

Page 8: "could further reduce the likelihood of resistance allele formation by increasing the frequency of HDR events." Multiple gRNAs would mostly help by reducing functional resistance allele formation, especially since drive conversion is already very high in Anopheles.

Page 8, last paragraph: This conclusion is perhaps a little optimistic considering the functional resistance alleles, which should get a little more attention in the summary or elsewhere in the discussion section.

Figure 1d: The vertical text saying "Non-WT" is confusing. The circles themselves show + and -. Also, "-" isn't necessarily a knockout allele, so I'm not sure if - is the best symbol for resistance.

Figure 2e: The vertical scale is not the most intuitive. Consider rearranging it to "Transition from larvae to pupae" starting at zero and going to 1 when all the larvae become pupae.

Figure 2e-f: For both of these, there are clear differences between males and females. Thus, when comparing drive homozygotes to wild-type, it would probably be better to have separate statistical comparisons for males and females.

Figure 3: Can any of these transcription results in individual genes potentially explain the observed fitness cost?

Figure 3b: The scale here also doesn't quite make sense. It's the fraction of underdeveloped ovaries, but the graph is also perhaps trying to show whether just 1-2 ovaries are present, or maybe how many ovaries are undeveloped, but then it would say "zero"? This should be clarified. Number of ovaries and how well-developed they are is separate (it can be put on the same graph, but needs to be more clear).

Figure 4f: The vertical axis should say "ONNV."

Figure 5c-d: These should be labeled as the most common resistance allele. Also, I'm not sure how relevant it is, but we also found an alternate start codon here: Hou S, Chen J, Feng R, Xu X, Liang N, Champer J. A homing rescue gene drive with multiplexed gRNAs reaches high frequency in cage populations but generates functional resistance. J Genet Genomics, 2024. Maybe this is a more common problem than one would expect?

Figure 5cd,S4,S5: They have a bit of a weird plot. Why not make four line graphs for each? Also, some alleles use the  symbol. + is wild-type, which is well understood, but - as resistance is not always clear, and seeing them together may confuse readers. Additionally, the fact that you have the most common resistance allele in Figure 5cd might mean that you know more about the genotype? If so, it would be best to separate wild-type and resistance alleles in whatever the final figure looks like.

Some supplemental raw data files would be useful if they were available, but the figures are through enough that this isn't essential.

Review by:

Jackson Champer, with major assistance from Ruobing Feng (essentially section B) and Jie Du

Referee cross-commenting

We don't have any cross-comments, other than supporting the idea of slightly more comparisons to the authors' previous construct.

Significance

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.

A key innovation of the nanosd gene drive is its integral gene drive (IGD) design, which inserts the drive cassette directly into the A. gambiae nanos gene, incorporating only the minimal components necessary for drive function. The drive achieves high transmission rates, without causing widespread disruption of gene expression or increasing susceptibility to malaria parasites, and imposes an acceptable fitness cost-primarily a reduction in female fecundity when homozygous. The strong performance of nanosd can be attributed to its design: Cas9 is expressed in the correct cells and timing to induce efficient homing, effectively hijacking the nanos gene's natural expression profile. However, despite the careful design aimed at preserving nanos function, the rescue was incomplete: homozygous female drive carriers exhibited a clear reduction in ovarian function.

In caged population trials, both the drive and a co-introduced anti-malaria effector gene reached high frequencies, even in the presence of emerging resistance alleles. Because the drive is inserted into an essential gene, nonfunctional resistance alleles are selected against and tend to be purged over time. Nonetheless, functional resistance remains a concern. The use of a single, though precisely positioned gRNA targeting the native nanos gene ATG site increases the likelihood of generating functional resistance alleles. Over the long term, if the drive imposes fitness costs, it may be outcompeted by such functional resistance alleles, potentially undermining the goal of sustained population modification.

Overall, this study represent a notable advance in Anopheles mosquito gene drive development and can be considered as high impact. - Place the work in the context of the existing literature (provide references, where appropriate).

Previous IGD efforts in Drosophila, mice and mosquitoes have demonstrated nearly super‐Mendelian inheritance but often at the expense of host fitness. For example, Nash et al. built an intronic‐gRNA Cas9 drive at the D. melanogaster rcd-1r locus that propagated efficiently through cage populations (Nash et al., 2022), and Gonzalez et al. reported that a Cas9 drive inserted at the germline zpg locus in Anopheles stephensi biased inheritance by ~99.8% (Gonzalez et al., 2025). However, these strong drives disrupted essential genes: in A. gambiae, inserting Cas9 into zpg produced efficient homing but rendered females largely sterile (Ellis et al., 2022). A similar germline Cas9 knock-in in Mus musculus enabled gene conversion in both sexes, albeit with only modest efficiency and potential fitness trade-offs (Weitzel et al., 2021). The current nanosd IGD is explicitly designed to overcome this limitation by selecting a more permissive gene target and using a minimal drive cassette, so as to preserve mosquito viability while maintaining robust drive efficiency, although still with reduced female drive homozygotes fertility.

This nanosd gene drive like previous homing drives in Anopheles, is capable of achieving a high level of inheritance bias. Although it uses the endogenous nanos regulatory elements, which have less leaky somatic expression compared to using vasa (Gantz et al., 2015; Hammond et al., 2016; Hammond et al., 2017) or zpg promoters(Hammond et al., 2021; Kyrou et al., 2018), to drive Cas9 expression and thereby reduces somatic expression-induced female sterility, the incomplete rescue of nanos function still leads to reduced female fertility in drive homozygotes. - State what audience might be interested in and influenced by the reported findings.

It's worth noting the broad audience that will find this work relevant. Gene drive developers and molecular geneticists will be impressed by the good drive performance and directly influenced by the design principles showcased here. The study's integral gene drive architecture that leverages the endogenous nanos regulatory elements, in-frame E2A peptide linkage for co-expression, and intronic insertion of gRNA and selectable markers addresses long-standing challenges in promoter leakage, somatic fitness costs, and resistance allele evolution. What's more, vector biologists and malaria researchers will be interested in the successful deployment of a gene drive in A. gambiae that actually carries a disease-blocking trait. - 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.

We have worked on CRISPR gene drive development in both fruit flies and Anopheles mosquitoes and have experience with modeling their spread.

References

Ellis, D.A., Avraam, G., Hoermann, A., Wyer, C.A.S., Ong, Y.X., Christophides, G.K., and Windbichler, N. (2022). Testing non-autonomous antimalarial gene drive effectors using self-eliminating drivers in the African mosquito vector Anopheles gambiae. PLOS Genetics 18, e1010244-e1010244.

Gantz, V.M., Jasinskiene, N., Tatarenkova, O., Fazekas, A., Macias, V.M., Bier, E., and James, A.A. (2015). Highly efficient Cas9-mediated gene drive for population modification of the malaria vector mosquito Anopheles stephensi. Proc Natl Acad Sci U S A 112, E6736-E6743.

Gonzalez, E., Anderson, M.A.E., Ang, J.X.D., Nevard, K., Shackleford, L., Larrosa-Godall, M., Leftwich, P.T., and Alphey, L. (2025). Optimization of SgRNA expression with RNA pol III regulatory elements in Anopheles stephensi. Scientific Reports 15, 13408.

Hammond, A., Galizi, R., Kyrou, K., Simoni, A., Siniscalchi, C., Katsanos, D., Gribble, M., Baker, D., Marois, E., Russell, S., et al. (2016). A CRISPR-Cas9 gene drive system targeting female reproduction in the malaria mosquito vector Anopheles gambiae. Nat Biotechnol 34, 78-83.

Hammond, A., Karlsson, X., Morianou, I., Kyrou, K., Beaghton, A., Gribble, M., Kranjc, N., Galizi, R., Burt, A., Crisanti, A., et al. (2021). Regulating the expression of gene drives is key to increasing their invasive potential and the mitigation of resistance. PLOS Genetics 17, e1009321-e1009321.

Hammond, A.M., Kyrou, K., Bruttini, M., North, A., Galizi, R., Karlsson, X., Kranjc, N., Carpi, F.M., D'Aurizio, R., Crisanti, A., et al. (2017). The creation and selection of mutations resistant to a gene drive over multiple generations in the malaria mosquito. PLOS Genetics 13, e1007039-e1007039.

Kyrou, K., Hammond, A.M., Galizi, R., Kranjc, N., Burt, A., Beaghton, A.K., Nolan, T., and Crisanti, A. (2018). A CRISPR-Cas9 gene drive targeting doublesex causes complete population suppression in caged Anopheles gambiae mosquitoes. Nature Biotechnology 36, 1062-1066.

Nash, A., Capriotti, P., Hoermann, A., Papathanos, P.A., and Windbichler, N. (2022). Intronic gRNAs for the construction of minimal gene drive systems. Frontiers in Bioengineering and Biotechnology 0, 570-570. Weitzel, A.J., Grunwald, H.A., Ceri, W., Levina, R., Gantz, V.M., Hedrick, S.M., Bier, E., and Cooper, K.L. (2021). Meiotic Cas9 expression mediates gene conversion in the male and female mouse germline. Plos Biol 19, e3001478-e3001478.

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Reply to the reviewers

Manuscript number: RC-2025-03064

Corresponding author(s): Massimo, Hilliard; Sean, Coakley

1. General Statements

We are grateful to the reviewers for taking time to review our manuscript and for providing such clear, insightful and actionable suggestions. The consensus between 4 independent reviewers that this story is of general interest to cell biologists, neurobiologists and clinical researchers is remarkable. In addition to our mechanistic insights into the regulation of GTPase activity, we think that the experimental systems we have developed will be of great value to study how GTPases their associated GAPs and GEFs function to maintain the nervous system, especially due to the demonstrated conservation of these molecules. We believe that our data provides a powerful and tractable model to study such molecules in a physiological context.

We agree with the reviewers' concerns and propose the following plan below to address them.

2. Description of the planned revisions

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

__Summary Stability of the PLM axon in C. elegans is maintained through interactions with the epidermis. Previous studies by this group found that loss of the tbc-10 Rab GTPase Activating Protein strongly enhanced the PLM axon break phenotype of unc-70/beta-spectrin mutants. TBC-10 is a GAP for RAB-35 and thus loss of rab-35 suppresses the tbc-10 phenotype. Of the two RAB-35 GEFs, loss of RME-4 partially suppressed the tbc-10 phenotype and FLCN-1 was not involved suggesting that there may be an additional GEF involved. Here Bonacossa-Pereira et al identify a point mutation in agef-1a (vd92) as a suppressor of tbc-10 PLM axon break phenotype (all experiments also have a dominant allele of unc-70) and confirm that point mutation is causative by replicating the mutation via genome editing (vd123). Rescue experiments demonstrate that AGEF-1a is required in the epidermis and not PLM as previous demonstrated with tbc-10 and unc-70. Rescue is dependent on a functional SEC7/GEF activity. AGEF-1a is a functional ortholog to human BIG2/ArfGEF2 as its expression fully rescues tbc-10. AGEF-1a functions upstream of RAB-35 as expression of activated RAB-35 can suppress loss of agef-1. AGEF-1a functions in parallel to RME-4 as the double has stronger suppression of tbc-10. AGEF-1a is an ARF GEF, however it functions independently of ARF-1.2 as loss of arf-1.2 does not suppress tbc-10. They demonstrate that AGEF-1a interacts with RAB-35 through colocalization experiments suggesting that AGEF-1a could directly activate RAB-35. Finally, they demonstrate that AGEF-1a regulates the localization of the LET-805 epidermal attached complex component as it restores localization in a tbc-10 mutant.

Major comments

The manuscript is well written and easy to understand.

The experiments are well done and controlled.

I enjoyed reading this paper. However...

Some of the claims are not supported by the data.__

__1) The claim that AGEF-1a directly interacts with RAB-35 was not demonstrated. The evidence provided to support a direct interaction are colocalization experiments in Figure 3. AGEF-1a does partially colocalize with RAB-35 in the epidermis. However, colocalization does not indicate a physical interaction direct or indirect. A simple fix would be to change the claim to that they partially colocalize. Optional, a physical interaction could be done with the split-GFP since they already have the AGEF-1 strain or they could perform co-IP experiments, though neither of those are proof of direct interactions.

__

We agree that the biochemical co-IP experiment could provide some answers, however, using a full length AGEF-1a would not only represent a significant technical challenge but will also not prove a direct interaction in a physiological context. To overcome this limitation, and to directly test their interaction in vivo, we propose to use a split-GFP approach as suggested by the reviewer. In this experiment, we will generate an endogenously tagged GFP1-10::rab-35 allele and combine it with the previously generated and available tagged agef-1a::GFP11x7. If AGEF-1 and RAB-35 closely interact, we should observe the reconstitution of full length GFP. It is possible that the endogenously tagged versions only provide a very weak GFP signal that will be difficult to detect. As an alternative approach, we will generate the same tagged molecules as overexpressed transgenes under epidermal-specific promoters (such as Pdpy-7). If the results are still negative, we agree to temper our claim that these molecules physically interact and rephrase the manuscript to reflect the new data.

• *

2) The claim that AGEF-1a facilitates RAB-35 activation is not supported. While it is likely that AGEF-1a facilitates RAB-35 activation based on the epistasis experiments as well as studies in mammalian cells there were no experiments to demonstrate that modulating AGEF-1a activity resulted in a change in RAB-35 activity. I would suggest tempering this claim to something along the line that the data are consistent with AGEF-1a regulating RAB-35 activity as shown in mammalian cells. An optional experiment would be to look at the colocalization of RAB-35 with a known effector in wild type and agef-1(vd92) with the expectation that there would be a higher level of colocalization in agef-1 mutants. Effector pull-down experiments or perhaps a cell based GEF assay could be used (PMID: 35196081).

We welcome this suggestion and acknowledge the limitations of these experiments. While we might be able to determine if AGEF-1 and RAB-35 physically interact in vivo with the experiments proposed above, screening for the relevant rab-35 effector in this context and/or doing effector pull-down/cell based GEF assays would be a significant technical challenge. We propose to temper our claim as suggested.

3) The claim that AGEF-1a functions independently of ARF-1.2 is not well supported. The fact that the ARF-1.2 mutant does not suppress tbc-10 suggests that ARF-1.2 may not be involved but does not eliminate the possibility that ARF-1.2 functions redundantly with ARF-5 or WARF-1/ARF-1.1. This can be resolved by toning down the claim. Alternatively, this can be tested by RNAi of arf-5 and warf-1 in tbc-10 and arf-1.2; tbc-10 mutants.

We agree that warf-1 and arf-5 could be functioning redundantly with arf-1.2. We have attempted to generate an AID::arf-5 allele to test the effect of cell-specific degradation, but homozygous AID::arf-5 animals were lethal. We have not yet examined warf-1. We believe the best way to test these two molecules is through RNAi knockdown, and we propose to do this experiment and adjust our interpretation and discussion according to the new data.

Minor comments

Figure 1C the CRISPR generated allele (vd123) is referred to as [S784L] and then in 1E vd92 is referred to as [S784L]. Perhaps it would be clearer if the allele name was used instead of the amino acid change.

We will reformat the manuscript to include the allele names instead of amino acid change.

Page 6 "We reasoned that if the S784L mutation we isolated causes a similar loss of the GTPase activation function, then SKIN::AGEF-1a[E608K] would not have the capacity to restore the rate of PLM axon breaks to background levels in agef-1[S784L]; tbc-10; vdSi2 animals." It was unclear to me whether you were testing if the S784L mutation could be disrupting a GEF independent function or might disrupt the nucleotide exchange activity as might be tested in a biochemical assay. There are many reasons this change could cause a loss of function phenotype (ie. Improper folding, mislocalization, etc.). The most clear explanation would be that you were testing if GEF function was required for rescue rather than testing if the S784L mutation disrupted GEF activity.

Indeed, this experiment reveals that reducing the activation of the AGEF-1 target phenocopies the effect of S784L and does not further enhance the effect of S784L. However, it does not answer if, specifically, the GEF function is affected by S784L. We propose to rewrite the quoted sentence as follows: "We asked whether the GEF function is required for axonal damage. If that is the case, then SKIN::AGEF-1a[E608K] overexpression should phenocopy the effect of AGEF-1a[S784L]."

• *

Page 13. It was unclear how testing if AGEF-1, RME-4, ARF-5 and RAB-35 form complexes in vivo (I assume you are suggesting colocalize based on figure 3 interpretation) would resolve how AGEF-1 was regulating RAB-35.

We apologize that our phrasing was not clear. We will rewrite this section to better reflect the following idea. Given literature data showing an allosteric interaction between RME-4/DENND1 and ARF-5/Arf5, and our own data showing that AGEF-1 regulates RAB-35, we believe these molecules could form a complex. Considering that we do not have data to support this notion, mostly due to the inability to test the effect of ARF-5, we will present this possibility in the discussion section.

__**Cross-commenting**

I agree with the comments made by the other reviewers and I stand by my own as well. I will echo that it is important to know the nature of their agef-1 allele.

Reviewer #1 (Significance (Required)):

Bonacossa-Pereira et al identify AGEF-1 as a regulator of axon integrity that functions in a pathway with RAB-35 in the epidermis is an exciting finding. As pointed out in the discussion, mutations in the human ortholog cause neurodevelopmental defects which leads to obvious characterization of BIG2/ArfGEF2 in neurons while this study indicates that this protein can have cell non-autonomous roles in regulating neurons. These findings could have important implications for understanding the etiology of these defects that would be of interest to neurobiologists and clinical researchers.

The finding of this paper would also be of interest to cell biologists and particularly those studying the roles of Rab and Arf GTPases in membrane trafficking, such as myself. The idea that AGEF-1 might function as a Rab35 GEF is provocative and would generate a lot of interest and skepticism from the field. However, there is no data to support that AGEF-1 would be a direct regulator of Rab35 over the previously demonstrated cross regulation of Rab35 by Arf GTPases. Therefore, it would be fine to speculate in the discussion a direct interaction, but I would refrain from suggesting this as a model and elsewhere in the manuscript.

__

Although we agree that current evidence is not sufficient to support the model where AGEF-1 is a direct regulator of RAB-35, our data points to the direction where there is an important genetic relationship between these molecules in a physiological context in a living animal, with a defined phenotype relevant to the nervous system maintenance. We think that the proposed revision experiments will provide a better understanding of how AGEF-1 functions with RAB-35 and we agree with the suggestion to rephrase our manuscript to reflect the limitations of our results.

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

This interesting manuscript reports the outcome of a fruitful C. elegans genetic screen with a complex but clever design. Through it, the authors identify AGEF-1 as a GEF that likely regulates the active state of the GTPase RAB-35 in the skin to protect touch receptor axons from mechanical breakage.

Major points: 1. Based on localization experiments, the authors claim "AGEF-1a interacts with RAB-35 in the epidermis" (Results heading) and state "these data demonstrate that AGEF-1a interacts with a subset of RAB-35 molecules in the epidermis." In general, localization studies cannot be used to conclude physical interaction (with some exceptions such as single-molecule kinetics). In this case, the data in my view do not even make a compelling argument for co-localization. There is a lot of AGEF-1 and RAB-35 signal everywhere and it may not be meaningful that the signals sometimes overlap. A more quantitative approach with controls would be needed to conclude meaningful co-localization. Importantly, this would still not demonstrate interaction.__

We thank the reviewer for the comment. Indeed, co-localization does prove a physical interaction, and we appreciate the concern about our imaging data not making a compelling argument. To address this notion, we plan to perform an experiment using a more robust, quantitative and physiologically relevant strategy. We will generate an endogenously tagged mScarlet3::rab-35 allele for precise endogenous localization. In addition, as a positive control, we will generate an endogenous rme-4::GFP11x7 allele to cell-specifically demonstrate the level of colocalization of RME-4 with mScarlet3::RAB-35 within the epidermis. To address the possible interaction between AGEF-1a and RAB-35 we will leverage a split-GFP approach to assess their interaction in vivo, in the context relevant to the phenotypes we observed (see reply to reviewer #1 point 1).

__2. The effect of the AGEF-1(S784L) mutation is not clear to me. Naively, as the S784L mutation lies in the auto-inhibitory domain, I would have expected AGEF-1 to become constitutively active, not inactive as the authors seem to suggest. Is the idea that it is constitutively auto-inhibited? The main evidence for a loss of function effect seems to be that a putative dominant negative mutation AGEF-1(E608K) does not further supress axon breakage when co-expressed in trans to AGEF(S784L), but in my view this only shows that, once the defect is suppressed, it cannot be suppressed any further. Defining the nature of the S784L allele is important. Some suggestions, although the authors may come up with different approaches: use of an inducible or cell-specific depletion system like AID/TIR1, Cre/lox, or FLP/FRT to circumvent the lethality of agef-1(0) and reveal what a true loss-of-function looks like; testing if deletion of the auto-inhibitory domain phenocopies S784L to test if this mutation impairs autoinhibition.

__

This is an very insightful comment. To address this point, we will follow the reviewer's suggestion and deplete AGEF-1 cell-specifically in the epidermis using the auxin-inducible degron system. Specifically, we will generate an agef-1::AID allele to degrade this molecule in a spatially and temporally controlled fashion, which will allow to circumvent the lethality of agef-1(0) and determine whether the S784L allele mimics the depletion of AGEF-1.

Although it would be interesting to further dissect the effect of this mutation on AGEF-1 activity, we believe that this falls outside of the scope of this manuscript. As an alternative, we propose to elaborate more in the discussion the implications of the possible roles for the S784L mutation to clarify our model of its function. Our data supports a model in which this mutation reduces AGEF-1 function leading to a reduction in the activity of its downstream target GTPases. It is possible that this is due to AGEF-1 becoming constitutively autoinhibited, or that this mutation affects the structure of the molecule in a way that it reduces its affinity towards its downstream effectors.

Minor points: 1. I am not able to see the "vesicle-like structures with a clear luminal space" or RAB-35 being "notably enriched at the membrane near the epidermal furrow" in Fig. 3. The "3D surface rendering" in Fig. 3e is grossly oversampled and should not be included.

We will rectify this section and include new super-resolved images using Airyscan confocal microscopy. We hope these will yield a better-quality representation of these concepts. __ 2. As the agef-1a isoform is specifically referenced throughout, please describe the different agef-1 isoforms somewhere to save readers from having to look this up.__

Yes, we will include a description of the isoforms. In C. elegans there are two: AGEF-1a which has been confirmed by cDNA and AGEF-1b which is predicted and partially confirmed by cDNA. The mutation we isolated exclusively affects AGEF-1a.

3. The authors include an interesting speculation in the Discussion: "Future investigations of BIG2-associated neurological disorders should consider... hyper-activity of BIG2 as a driver of neuropathology." If the authors have the tools to test the effect of hyperactive BIG2 in this system, it could be an exciting addition.

This is an exciting idea that we would like to keep in the Discussion. The biology of BIG2 activity regulation is a nascent field of research and we believe that to accurately generate and characterise a hyperactive BIG2 would be beyond the scope of this manuscript.

__ On a personal note, since GEFs act oppositely to GTPase Activating Proteins (GAPs), I had to stop and re-read carefully whenever the authors referred to a GEF "activating" a GTPase. I understand their meaning (i.e., putting the GTPase in its active GTP-bound state, not activating its GTPase function) but I wanted to point out this potential confusion in case there is a way to better define terms in the Introduction or change word choice. I realize this may be a standard jargon in the field.__

Indeed, this is confusing nomenclature and a difficult concept to deliver in an accurate and succinct manner. We propose to include a clearer, more didactic explanation of their function. In a simple explanation, GTPases perform cellular functions when bound to GTP. GAPs terminate GTPase activity by catalysing GTP hydrolysis, generating GDP. GEFs initiate GTPase activity by catalysing the release of GDP and allowing GTP binding.

__ Please check the correct nomenclature for CRISPR/Cas9.__

We will rectify where appropriate.

__6. p.7 "these molecules act in synergy", consider replacing with "redundantly".

__

We will rectify where appropriate.

__Reviewer #2 (Significance (Required)):

The significance of this story is to show that GEF-GTPases pairing can be highly context-dependent. Previous studies have identified GEFs that pair with RAB-35 and GTPases that pair with AGEF-1, but the authors find that these factors have at best a modest role in the context of skin-axon interactions. Instead, the authors suggest a novel GTPase-GEF pairing of RAB-35 with AGEF-1 and provide evidence that this relationship is conserved in the human homolog of AGEF-1. These results suggest that GTPase-GEF pairings depend not only on chemical affinity but also cellular context.

The main strength of the study is its clever genetics. For the screen, the authors looked for suppressors of a synthetic defect in axon integrity caused in part by elevated activity of RAB-35 due to loss of its GAP TBC-10. It is satisfying that this screen isolated a mutation in a GEF that in principle could counterbalance the loss of a GAP.

The main weakness of the study is the lack of direct evidence for an AGEF-1/RAB-35 interaction. While not necessary for publication, the inclusion of biochemical data to support the role of AGEF-1 as a GEF for RAB-35 and the effect of the S784L mutation on this activity would strongly elevate the study. The genetic data for this interaction are consistent with the model but not conclusive, and in my view the colocalization data are not compelling. Nevertheless this is a solid genetic story with a clever screen.__

__ __We appreciate the feedback and are grateful for the positive comments on the significance of our study. As explained in the significance section related to Reviewer 1, if we find evidence of a direct interaction between AGEF-1 and RAB-35 in the proposed new experiments, we will include it in the manuscript; alternatively, we will present it as a possibility in the discussion section, as suggested. We agree that a more nuanced understanding of the effect of the S784L is interesting and that our colocalization data can be improved, and we have proposed experiments to address these concerns.

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

This paper investigates the mechanism by which molecular pathways in the skin protect the processes of nerves that innervate them from damage. The authors previously showed that spectrin and the small GTPase RAB-35 act in the epidermis of C. elegans to protect mechanosensory axons from breaking. In this paper they used a suppression screen to identify another gene involved in this process, an ARF-GEF called AGEF-1. Partial loss-of-function mutations in agef-1 suppress the axon-breakage phenotype of spectrin mutations, and genetic experiments by the authors are consistent with the possibility that AGEF-1 could act directly as an exchange factor for RAB-35. Consistent with this model, they show that AGEF-1 and RAB-35 colocalise in the skin.

Major comments: The experiments in this paper are well-designed and well-controlled, and the interpretations of the results are all reasonable. On the other hand, I don't think the authors' hypothesis that AGEF-1 acts directly as an exchange factor for RAB-35, or that these two proteins directly interact, is definitively proven. This is not an issue of the authors overinterpreting their data--the paper is very carefully and thoughtfully written. However, the most interesting and counterintuitive finding--that an ARF-GEF could also be a RAB-GEF--might be strengthened with more experiments (for example, could they more directly show protein-protein interaction through co-IP or mass spec?).__

We thank the reviewer for the suggestion. We propose to further investigate the notion that AGEF-1a might be a direct interactor of RAB-35 using a split-GFP approach to assess whether these molecules closely interact, in vivo, in the physiological context that is relevant for the maintenance of the touch sensing neurons (please see reply to reviewer #1 major point 1 and reviewer #2 major point 1 for more details).

Minor comments: There are also two places where the fact that null mutations are lethal (for agef-1 and arf-5) prevented the authors from addressing the effect of agef-1 loss of function in the skin, and addressing whether ARF-5 could be an AGEF-1 target, respectively. In principle, they could have tried to make a CRISPR line in which these genes could be cell-specifically deleted in the skin (using a dpy-7-driven recombinase). I don't think either of these experiments are essential, but if it is feasible to make these lines it would tie up a couple of loose ends.

We agree to explore the roles of agef-1 and arf-5 loss-of-function. We propose to tissue-specifically degrade agef-1 using an auxin-inducible degradation strategy (please see reviewer #2 major point 2 reply for more details). For arf-5, we propose knocking-down its function using RNAi to overcome lethality (please see reviewer #1 major point 3 reply for more details).

__Reviewer #3 (Significance (Required)):

Overall I think this is an interesting paper on a topic of general interest. The most interesting finding is that an exchange factor for an ARF (a small GRPase involved in vesicle coating/uncoating) could also be an exchange factor for a RAB (a small GTPase involved in vesicle tethering). The evidence presented is suggestive and intriguing, though as noted above not completely definitive. In summary, I think it is an interesting paper in its current form, and anything it could do to more firmly establish a direct interaction between AGEF-1 and RAB-35 would increase its impact and importance.

__

We thank the reviewer for the positive evaluation of the significance of our study.

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

Summary: In this study Bonacossa-Pereira et al. identify AGEF-1a, an Arf-GEF, as a factor that functions in the epidermis through RAB-35 to regulate axonal integrity of the PLM mechanosensory neurons in C. elegans. Specifically, epidermal attachment sites are regulated by these genes form the epidermis and compromising these attachment sites results in axonal degeneration. The study provides some evidence that that RAB-35 and AGEF-1 at least partially colocalize in the skin. Finally, the authors provide evidence that the human orthologue BIG2 is capable of functionally replacing AGEF-1a in C. elegans. Overall, the experiments are well designed and the paper is clear and succinct. The conclusions are supported by the findings and provide an important extension of the author's findings a few back, when they identified the role of rab-35 in mediating the epidermal-neuronal attachment sites.

Major comments: 1. AGEF-1/BIG2 are known to regulate other GTPases such as ARF-5 or ARF-2. The authors exclude a non-redundant function for ARF-2, but are unable to establish a role for ARF-5 because of the lethality associated with the mutation. Alternative approaches, such as cell specific knock out or knock down experiment. In addition, studies to test potentially physical interaction such as pull-down assays, co-IP experiments and FRET could be used to test whether AGEF-can bind RAB-35 or ARF-5.__

We thank the reviewer for this suggestion. We propose addressing these concerns using a tissue-specific degradation for AGEF-1a (please see reviewer #1 major point 2 for details). To establish a role for ARF-5 we propose to do an RNAi mediated knock-down to overcome lethality (please see reviewer #1 major point 3 for details). Finally, we plan to use a split-GFP approach to test the physical interaction between agef-1a and rab-35 in vivo (please see reviewer #1 major point 1 for details)

__ Phenotypic readout has been limited to only axon breaks. It may be interesting to also test other aspects such as axonal deformities including swellings and vesiculation in other parts of the nervous system. Moreover, behavioral or functional experiments such as response to gentle touch or synaptic integrity could be informative.__

We have not observed any obvious touch receptor neurons axonal phenotypes other than axonal breaks in these mutants, and we will include a statement that reflects this concept. In relation to the behavior, we have not tested it as the results will be difficult to interpret for two reasons: first, the breaks are not always bilateral and one neuron is sufficient to provide mechanical response; second, the mixed identity of the PLM neurite allows it to retain some function despite being severed. However, if deemed essential, we will perform these experiments.

__ Overexpression constructs such as SKIN::RAB-35[Q69L], SKIN::BIG2, SKIN::AGEF-1a[E608K] in extrachromosomal transgenes could lead to non-physiological localization or effects. Single copy expression using MosSCI or CRISPR insertions are generally considered better approaches (other than endogenous reporters) to provide accurate insights at the physiological level. While the authors tacitly acknowledge this by conducting the experiments in a rab-35 mutant background and very low transgene concentration, at the very least this caveat regarding the localization should be discussed.__

This is an important remark, and we appreciate the comment. We acknowledge that experiments using extrachromosomal arrays have inherent caveats, especially for localization studies. To address the RAB-35 localization concern we plan to repeat the localization studies using an endogenously tagged RAB-35 using CRISPR to overcome the possible artifacts caused by extrachromosomal array driven expression (please see reviewer #1 point 1 for more details). For the cell-specific rescues or dominant-negative constructs expression, we believe that using extrachromosomal arrays is sufficient, since this allows us to compare genetically identical transgenic vs non-transgenic siblings of independent lines. Moreover, given these constructs are already driven by a tissue-specific promoter that is inherently stronger than their respective endogenous promoters, even a single-copy insertion would have the same caveats.

__4. The study does not address clearly whether AGEF-1a acts in parallel to spectrin or upstream/ downstream to it. Epistasis experiments could help to figure out the signaling pathway involved.

__

Indeed, this is a concept that we need to communicate more clearly. We have data showing that a mutation in agef-1 does not cause axonal damage on its own, and that it has no effect on the axonal damage caused by unc-70 dominant negative mutation alone. We only detect an effect of agef-1 when tbc-10 is mutated together with unc-70 (Fig. 1a of manuscript). Together, these data indicate that agef-1 functions upstream of rab-35, thus acting in parallel to unc-70 (see schematic below) to ensure the mechanical stability of neuron epidermal attachment. We plan to include this data and the following schematic as a supplement to better convey the idea and discuss the results appropriately.

__ The finding that BIG2 rescues the mutant defect is an important finding and rightfully finds its place in the abstract. I wonder whether a reference to the human diseases caused by loss of BIG2 in the abstract and introduction would not increase interest/impact for the study, rather than burying this potentially interesting connection in the discussion.

__

We appreciate the reviewer's comment, and welcome the suggestion. We propose to include relevant background about BIG2-related human diseases in the abstract and introduction as suggested and expand the discussion regarding BIG2 mutations.

__Minor comments:

1. Some explanation about how mutating the autoinhibitory domain could impact the catalytic activity of a GEF might be helpful.__

2. *

We acknowledge that this notion was not well communicated. We propose to elaborate more about why we think a mutation in the autoinhibitory domain might be affecting the GEF activity and we plan to do further experiments to dissect how this might be happening. Please see reviewer #2 major point 2 for a more detailed explanation.

__ The paper refers to rme-4(b1001) as a null allele while wormbase refers to the same as a missense allele. It would be more accurate to refer rme-4(b1001) as a strong loss of function or putative null.__

We agree and will refer to b1001 as a strong loss-of-function.

__ The paper does not clearly discuss limitations of the hypomorphic agef-1[S784L] and that the observed phenotypes in this hypomorph might underestimate the complete role of AGEF-1a.__

• *

We thank the reviewer for this suggestion. We propose to elaborate more on these limitations, especially considering the possible new results from the experiments suggested in reply to reviewer #2 major comment point 2.

__ In figure 1, where there really only one extrachromosomal transgenic line for some of the construct tested? __

• *

For the Pdpy-7::AGEF-1a lines we have scored 3 transgenic lines (data not included) and only one yielded a full rescue. For all extrachromosomal lines presented, we tested 3 independent transgenic lines. For brevity, we only included the result for the positive rescues (1 for BIG2 and 1 for AGEF-1a), except for the Pmec-4 lines, of which none rescued the phenotype (data included in Table S2). We will update Table S2 to include all the lines tested.

__ The concentrations of transgenes vary in different transgenes. Is there a rationale behind this? __

Yes, we have attempted multiple concentrations of injections for each transgene and there was some variability for each construct injected, thus we only included the ones where we observed an effect. As mentioned in point 4 above, we will update Table S2 to include details of all lines tested.

__ In Fig.1e: I may be useful to also show the "WT" phenotype, i.e. the strong defects to get a visual comparison for the degree of rescue. __

• *

We think this suggestion will help the readers. We will include this as a representative dashed line showing the WT phenotype.

__Reviewer #4 (Significance (Required)):

The study has identified AGEF-1a as a regulator of axonal maintenance, functioning to protect neurons against mechanical stress by acting through RAB-35. Additionally, this epidermal GEF, AGEF-1a is functionally conserved as its human orthologue BIG2 can replace AGEF-1a in C. elegans for axonal protection. Important points here are that the findings extend prior work by the authors of non-autonomous mechanism that regulates epidermal-neuronal attachment. In my humble opinion, the human disease connection, in particular with regard to the unexplained neuronal phenotypes in patients could be better developed in the manuscript. It may also increase impact/interest of a wonderful story that right now reads a bit 'wormy'.__

This is an important remark and we are grateful for the positive comments. The fact that human BIG2 is also conserved in C. elegans points to a fundamental role of this molecule in multicellular life, and it provides a tractable model to investigate the function of this molecule in a physiological context. We welcome the suggestion to elaborate more the connection with the unexplained neuronal phenotypes in patients and use a more accessible language to convey our findings to a wider audience.

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

N/A

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

__Reviewer #1 __

"...studies to test potentially physical interaction such as pull-down assays, co-IP experiments and FRET could be used to test whether AGEF-can bind RAB-35 or ARF-5."

While pull-down assays, co-IP and FRET would reveal whether AGEF-1a can form a complex with RAB-35, we believe that using a full length AGEF-1a would not only represent a significant technical challenge but will also not prove a direct interaction in a physiological context.

"...An optional experiment would be to look at the colocalization of RAB-35 with a known effector in wild type and agef-1(vd92) with the expectation that there would be a higher level of colocalization in agef-1 mutants. Effector pull-down experiments or perhaps a cell based GEF assay could be used (PMID: 35196081)."

We think that screening for the relevant rab-35 effector in this context and/or doing effector pull-down/cell based GEF assays would be a significant technical challenge. We propose to address this concern by tempering our claim as suggested by the reviewer.

"...It may be interesting to also test other aspects such as axonal deformities including swellings and vesiculation in other parts of the nervous system. Moreover, behavioral or functional experiments such as response to gentle touch or synaptic integrity could be informative."

As indicated above in major point 2 of reviewer 4, these are interesting ideas that might answer how the function of these neurons might be affected. However, in addition to the challenges indicated above, they will not provide further insights into how their integrity is maintained. We believe these will fall outside the scope of the manuscript, but if deemed essential we will perform behavioral analysis.

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Referee #4

Evidence, reproducibility and clarity

Summary:

In this study Bonacossa-Pereira et al. identify AGEF-1a, an Arf-GEF, as a factor that functions in the epidermis through RAB-35 to regulate axonal integrity of the PLM mechanosensory neurons in C. elegans. Specifically, epidermal attachment sites are regulated by these genes form the epidermis and compromising these attachment sites results in axonal degeneration. The study provides some evidence that that RAB-35 and AGEF-1 at least partially colocalize in the skin. Finally, the authors provide evidence that the human orthologue BIG2 is capable of functionally replacing AGEF-1a in C. elegans. Overall, the experiments are well designed and the paper is clear and succinct. The conclusions are supported by the findings and provide an important extension of the author's findings a few back, when they identified the role of rab-35 in mediating the epidermal-neuronal attachment sites.

Major comments:

1. AGEF-1/BIG2 are known to regulate other GTPases such as ARF-5 or ARF-2. The authors exclude a non-redundant function for ARF-2, but are unable to establish a role for ARF-5 because of the lethality associated with the mutation. Alternative approaches, such as cell specific knock out or knock down experiment. In addition, studies to test potentially physical interaction such as pull-down assays, co-IP experiments and FRET could be used to test whether AGEF-can bind RAB-35 or ARF-5.
2. Phenotypic readout has been limited to only axon breaks. It may be interesting to also test other aspects such as axonal deformities including swellings and vesiculation in other parts of the nervous system. Moreover, behavioral or functional experiments such as response to gentle touch orsynaptic integrity could be informative.
3. Overexpression constructs such as SKIN::RAB-35[Q69L], SKIN::BIG2, SKIN::AGEF-1a[E608K] in extrachromosomal transgenes could lead to non-physiological localization or effects. Single copy expression using MosSCI or CRISPR insertions are generally considered better approaches (other than endogenous reporters) to provide accurate insights at the physiological level. While the authors tacitly acknowledge this by conducting the experiments in a rab-35 mutant background and very low transgene concentration, at the very least this caveat regarding the localization should be discussed.
4. The study does not address clearly whether AGEF-1a acts in parallel to spectrin or upstream/ downstream to it. Epistasis experiments could help to figure out the signaling pathway involved.
5. The finding that BIG2 rescues the mutant defect is an important finding and rightfully finds its place in the abstract. I wonder whether a reference to the human diseases caused by loss of BIG2 in the abstract and introduction would not increase interest/impact for the study, rather than burying this potentially interesting connection in the discussion.

Minor comments:

1. Some explanation about how mutating the autoinhibitory domain could impact the catalytic activity of a GEF might be helpful.
2. The paper refers to rme-4(b1001) as a null allele while wormbase refers to the same as a missense allele. It would be more accurate to refer rme-4(b1001) as a strong loss of function or putative null.
3. The paper does not clearly discuss limitations of the hypomorphic agef-1[S784L] and that the observed phenotypes in this hypomorph might underestimate the complete role of AGEF-1a.
4. In figure 1, where there really only one extrachromosomal transgenic line for some of the construct tested?
5. The concentrations of transgenes vary in different transgenes. Is there a rationale behind this?
6. In Fig.1e: I may be useful to also show the "WT" phenotype, i.e. the strong defects to get a visual comparison for the degree of rescue.

Significance

The study has identified AGEF-1a as a regulator of axonal maintenance, functioning to protect neurons against mechanical stress by acting through RAB-35. Additionally, this epidermal GEF, AGEF-1a is functionally conserved as its human orthologue BIG2 can replace AGEF-1a in C. elegans for axonal protection. Important points here are that the findings extend prior work by the authors of non-autonomous mechanism that regulates epidermal-neuronal attachment. In my humble opinion, the human disease connection, in particular with regard to the unexplained neuronal phenotypes in patients could be better developed in the manuscript. It may also increase impact/interest of a wonderful story that right now reads a bit 'wormy'.

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Referee #3

Evidence, reproducibility and clarity

This paper investigates the mechanism by which molecular pathways in the skin protect the processes of nerves that innervate them from damage. The authors previously showed that spectrin and the small GTPase RAB-35 act in the epidermis of C. elegans to protect mechanosensory axons from breaking. In this paper they used a suppression screen to identify another gene involved in this process, an ARF-GEF called AGEF-1. Partial loss-of-function mutations in agef-1 suppress the axon-breakage phenotype of spectrin mutations, and genetic experiments by the authors are consistent with the possibility that AGEF-1 could act directly as an exchange factor for RAB-35. Consistent with this model, they show that AGEF-1 and RAB-35 colocalise in the skin.

Major comments: The experiments in this paper are well-designed and well-controlled, and the interpretations of the results are all reasonable. On the other hand, I don't think the authors' hypothesis that AGEF-1 acts directly as an exchange factor for RAB-35, or that these two proteins directly interact, is definitively proven. This is not an issue of the authors overinterpreting their data--the paper is very carefully and thoughtfully written. However, the most interesting and counterintuitive finding--that an ARF-GEF could also be a RAB-GEF--might be strengthened with more experiments (for example, could they more directly show protein-protein interaction through co-IP or mass spec?).

Minor comments: There are also two places where the fact that null mutations are lethal (for agef-1 and arf-5) prevented the authors from addressing the effect of agef-1 loss of function in the skin, and addressing whether ARF-5 could be an AGEF-1 target, respectively. In principle, they could have tried to make a CRISPR line in which these genes could be cell-specifically deleted in the skin (using a dpy-7-driven recombinase). I don't think either of these experiments are essential, but if it is feasible to make these lines it would tie up a couple of loose ends.

Significance

Overall I think this is an interesting paper on a topic of general interest. The most interesting finding is that an exchange factor for an ARF (a small GRPase involved in vesicle coating/uncoating) could also be an exchange factor for a RAB (a small GTPase involved in vesicle tethering). The evidence presented is suggestive and intriguing, though as noted above not completely definitive. In summary, I think it is an interesting paper in its current form, and anything it could do to more firmly establish a direct interaction between AGEF-1 and RAB-35 would increase its impact and importance.

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

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Referee #2

Evidence, reproducibility and clarity

This interesting manuscript reports the outcome of a fruitful C. elegans genetic screen with a complex but clever design. Through it, the authors identify AGEF-1 as a GEF that likely regulates the active state of the GTPase RAB-35 in the skin to protect touch receptor axons from mechanical breakage.

Major points:

1. Based on localization experiments, the authors claim "AGEF-1a interacts with RAB-35 in the epidermis" (Results heading) and state "these data demonstrate that AGEF-1a interacts with a subset of RAB-35 molecules in the epidermis." In general, localization studies cannot be used to conclude physical interaction (with some exceptions such as single-molecule kinetics). In this case, the data in my view do not even make a compelling argument for co-localization. There is a lot of AGEF-1 and RAB-35 signal everywhere and it may not be meaningful that the signals sometimes overlap. A more quantitative approach with controls would be needed to conclude meaningful co-localization. Importantly, this would still not demonstrate interaction.
2. The effect of the AGEF-1(S784L) mutation is not clear to me. Naively, as the S784L mutation lies in the auto-inhibitory domain, I would have expected AGEF-1 to become constitutively active, not inactive as the authors seem to suggest. Is the idea that it is constitutively auto-inhibited? The main evidence for a loss of function effect seems to be that a putative dominant negative mutation AGEF-1(E608K) does not further supress axon breakage when co-expressed in trans to AGEF(S784L), but in my view this only shows that, once the defect is suppressed, it cannot be suppressed any further. Defining the nature of the S784L allele is important. Some suggestions, although the authors may come up with different approaches: use of an inducible or cell-specific depletion system like AID/TIR1, Cre/lox, or FLP/FRT to circumvent the lethality of agef-1(0) and reveal what a true loss-of-function looks like; testing if deletion of the auto-inhibitory domain phenocopies S784L to test if this mutation impairs autoinhibition.

Minor points:

1. I am not able to see the "vesicle-like structures with a clear luminal space" or RAB-35 being "notably enriched at the membrane near the epidermal furrow" in Fig. 3. The "3D surface rendering" in Fig. 3e is grossly oversampled and should not be included.
2. As the agef-1a isoform is specifically referenced throughout, please describe the different agef-1 isoforms somewhere to save readers from having to look this up.
3. The authors include an interesting speculation in the Discussion: "Future investigations of BIG2-associated neurological disorders should consider... hyper-activity of BIG2 as a driver of neuropathology." If the authors have the tools to test the effect of hyperactive BIG2 in this system, it could be an exciting addition.
4. On a personal note, since GEFs act oppositely to GTPase Activating Proteins (GAPs), I had to stop and re-read carefully whenever the authors referred to a GEF "activating" a GTPase. I understand their meaning (i.e., putting the GTPase in its active GTP-bound state, not activating its GTPase function) but I wanted to point out this potential confusion in case there is a way to better define terms in the Introduction or change word choice. I realize this may be a standard jargon in the field.
5. Please check the correct nomenclature for CRISPR/Cas9.
6. p.7 "these molecules act in synergy", consider replacing with "redundantly".

Significance

The significance of this story is to show that GEF-GTPases pairing can be highly context-dependent. Previous studies have identified GEFs that pair with RAB-35 and GTPases that pair with AGEF-1, but the authors find that these factors have at best a modest role in the context of skin-axon interactions. Instead, the authors suggest a novel GTPase-GEF pairing of RAB-35 with AGEF-1 and provide evidence that this relationship is conserved in the human homolog of AGEF-1. These results suggest that GTPase-GEF pairings depend not only on chemical affinity but also cellular context.

The main strength of the study is its clever genetics. For the screen, the authors looked for suppressors of a synthetic defect in axon integrity caused in part by elevated activity of RAB-35 due to loss of its GAP TBC-10. It is satisfying that this screen isolated a mutation in a GEF that in principle could counterbalance the loss of a GAP.

The main weakness of the study is the lack of direct evidence for an AGEF-1/RAB-35 interaction. While not necessary for publication, the inclusion of biochemical data to support the role of AGEF-1 as a GEF for RAB-35 and the effect of the S784L mutation on this activity would strongly elevate the study. The genetic data for this interaction are consistent with the model but not conclusive, and in my view the colocalization data are not compelling. Nevertheless this is a solid genetic story with a clever screen.

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Referee #1

Evidence, reproducibility and clarity

Summary

Stability of the PLM axon in C. elegans is maintained through interactions with the epidermis. Previous studies by this group found that loss of the tbc-10 Rab GTPase Activating Protein strongly enhanced the PLM axon break phenotype of unc-70/beta-spectrin mutants. TBC-10 is a GAP for RAB-35 and thus loss of rab-35 suppresses the tbc-10 phenotype. Of the two RAB-35 GEFs, loss of RME-4 partially suppressed the tbc-10 phenotype and FLCN-1 was not involved suggesting that there may be an additional GEF involved. Here Bonacossa-Pereira et al identify a point mutation in agef-1a (vd92) as a suppressor of tbc-10 PLM axon break phenotype (all experiments also have a dominant allele of unc-70) and confirm that point mutation is causative by replicating the mutation via genome editing (vd123). Rescue experiments demonstrate that AGEF-1a is required in the epidermis and not PLM as previous demonstrated with tbc-10 and unc-70. Rescue is dependent on a functional SEC7/GEF activity. AGEF-1a is a functional ortholog to human BIG2/ArfGEF2 as its expression fully rescues tbc-10. AGEF-1a functions upstream of RAB-35 as expression of activated RAB-35 can suppress loss of agef-1. AGEF-1a functions in parallel to RME-4 as the double has stronger suppression of tbc-10. AGEF-1a is an ARF GEF, however it functions independently of ARF-1.2 as loss of arf-1.2 does not suppress tbc-10. They demonstrate that AGEF-1a interacts with RAB-35 through colocalization experiments suggesting that AGEF-1a could directly activate RAB-35. Finally, they demonstrate that AGEF-1a regulates the localization of the LET-805 epidermal attached complex component as it restores localization in a tbc-10 mutant.

Major comments

The manuscript is well written and easy to understand.

The experiments are well done and controlled.

I enjoyed reading this paper. However...

Some of the claims are not supported by the data.

1. The claim that AGEF-1a directly interacts with RAB-35 was not demonstrated. The evidence provided to support a direct interaction are colocalization experiments in Figure 3. AGEF-1a does partially colocalize with RAB-35 in the epidermis. However, colocalization does not indicate a physical interaction direct or indirect. A simple fix would be to change the claim to that they partially colocalize. Optional, a physical interaction could be done with the split-GFP since they already have the AGEF-1 strain or they could perform co-IP experiments, though neither of those are proof of direct interactions.
2. The claim that AGEF-1a facilitates RAB-35 activation is not supported. While it is likely that AGEF-1a facilitates RAB-35 activation based on the epistasis experiments as well as studies in mammalian cells there were no experiments to demonstrate that modulating AGEF-1a activity resulted in a change in RAB-35 activity. I would suggest tempering this claim to something along the line that the data are consistent with AGEF-1a regulating RAB-35 activity as shown in mammalian cells. An optional experiment would be to look at the colocalization of RAB-35 with a known effector in wild type and agef-1(vd92) with the expectation that there would be a higher level of colocalization in agef-1 mutants. Effector pull-down experiments or perhaps a cell based GEF assay could be used (PMID: 35196081).
3. The claim that AGEF-1a functions independently of ARF-1.2 is not well supported. The fact that the ARF-1.2 mutant does not suppress tbc-10 suggests that ARF-1.2 may not be involved but does not eliminate the possibility that ARF-1.2 functions redundantly with ARF-5 or WARF-1/ARF-1.1. This can be resolved by toning down the claim. Alternatively, this can be tested by RNAi of arf-5 and warf-1 in tbc-10 and arf-1.2; tbc-10 mutants.

Minor comments

Figure 1C the CRISPR generated allele (vd123) is referred to as [S784L] and then in 1E vd92 is referred to as [S784L]. Perhaps it would be clearer if the allele name was used instead of the amino acid change.

Page 6 "We reasoned that if the S784L mutation we isolated causes a similar loss of the GTPase activation function, then SKIN::AGEF-1a[E608K] would not have the capacity to restore the rate of PLM axon breaks to background levels in agef-1[S784L]; tbc-10; vdSi2 animals." It was unclear to me whether you were testing if the S784L mutation could be disrupting a GEF independent function or might disrupt the nucleotide exchange activity as might be tested in a biochemical assay. There are many reasons this change could cause a loss of function phenotype (ie. Improper folding, mislocalization, etc.). The most clear explanation would be that you were testing if GEF function was required for rescue rather than testing if the S784L mutation disrupted GEF activity.

Page 13. It was unclear how testing if AGEF-1, RME-4, ARF-5 and RAB-35 form complexes in vivo (I assume you are suggesting colocalize based on figure 3 interpretation) would resolve how AGEF-1 was regulating RAB-35.

Cross-commenting

I agree with the comments made by the other reviewers and I stand by my own as well. I will echo that it is important to know the nature of their agef-1 allele.

Significance

Bonacossa-Pereira et al identify AGEF-1 as a regulator of axon integrity that functions in a pathway with RAB-35 in the epidermis is an exciting finding. As pointed out in the discussion, mutations in the human ortholog cause neurodevelopmental defects which leads to obvious characterization of BIG2/ArfGEF2 in neurons while this study indicates that this protein can have cell non-autonomous roles in regulating neurons. These findings could have important implications for understanding the etiology of these defects that would be of interest to neurobiologists and clinical researchers.

The finding of this paper would also be of interest to cell biologists and particularly those studying the roles of Rab and Arf GTPases in membrane trafficking, such as myself. The idea that AGEF-1 might function as a Rab35 GEF is provocative and would generate a lot of interest and skepticism from the field. However, there is no data to support that AGEF-1 would be a direct regulator of Rab35 over the previously demonstrated cross regulation of Rab35 by Arf GTPases. Therefore, it would be fine to speculate in the discussion a direct interaction, but I would refrain from suggesting this as a model and elsewhere in the manuscript.

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Reply to the reviewers

We thank the reviewers for their careful assessment and enthusiastic appreciation of our work.

__Reviewer #1 (Evidence, reproducibility and clarity (Required)): __In this article, Thomas et al. use a super-resolution approach in living cells to track proteins involved in the fusion event of sexual reproduction. They study the spatial organization and dynamics of the actin fusion focus, a key structure in cell-cell fusion in Schizosaccharomyces pombe. The researchers have adapted a high-precision centroid mapping method using three-color live-cell epifluorescence imaging to map the dynamic architecture of the fusion focus during yeast mating. The approach relies on tracking the centroid of fluorescence signals for proteins of interest, spatially referenced to Myo52-mScarlet-I (as a robust marker) and temporally referenced using a weakly fluorescent cytosolic protein (mRaspberry), which redistributes strongly upon fusion. The trajectories of five key proteins, including markers of polarity, cytoskeleton, exocytosis and membrane fusion, were compared to Myo52 over a 75-minute window spanning fusion. Their observations indicate that secretory vesicles maintain a constant distance from the plasma membrane whereas the actin network compacts. Most importantly, they discovered a positive feedback mechanism in which myosin V (Myo52) transports Fus1 formin along pre-existing actin filaments, thereby enhancing aster compaction.

This article is well written, the arguments are convincing and the assertions are balanced. The centroid tracking method has been clearly and solidly controlled. Overall, this is a solid addition to our understanding of cytoskeletal organization in cell fusion.

Major comments: No major comment.

Minor comments: _ Page 8 authors wrote "Upon depletion of Myo52, Ypt3 did not accumulate at the fusion focus (Figure 3C). A thin, wide localization at the fusion site was occasionally observed (Figure 3C, Movies S3)" : Is there a quantification of this accumulation in the mutant?

We will provide the requested quantification. The localization is very faint, so we are not sure that quantification will capture this faithfully, but we will try.

_ The framerate of movies could be improved for reader comfort: For example, movie S6 lasts 0.5 sec.

We agree that movies S3 and S6 frame rates could be improved. We will provide them with slower frame rate.

Reviewer #1 (Significance (Required)):

This study represents a conceptual and technical breakthrough in our understanding of cytoskeletal organization during cell-cell fusion. The authors introduce a high-precision, three-color live-cell centroid mapping method capable of resolving the spatio-temporal dynamics of protein complexes at the nanometer scale in living yeast cells. This methodological innovation enables systematic and quantitative mapping of the dynamic architecture of proteins at the cell fusion site, making it a powerful live-cell imaging approach. However, it is important to keep in mind that the increased precision achieved through averaging comes at the expense of overlooking atypical or outlier behaviors. The authors discovered a myosin V-dependent mechanism for the recruitment of formin that leads to actin aster compaction. The identification of Myo52 (myosin V) as a transporter of Fus1 (formin) to the fusion focus adds a new layer to our understanding of how polarized actin structures are generated and maintained during developmentally regulated processes such as mating.

Previous studies have shown the importance of formins and myosins during fusion, but this paper provides a quantitative and dynamic mapping that demonstrates how Myo52 modulates Fus1 positioning in living cells. This provides a better understanding of actin organization, beyond what has been demonstrated by fixed-cell imaging or genetic perturbation.

Audience: Cell biologists working on actin dynamics, cell-cell fusion and intracellular transport. Scientists involved in live-cell imaging, single particle tracking and cytoskeleton modeling.

I have expertise in live-cell microscopy, image analysis, fungal growth machinery and actin organization.

We thank the reviewer for their appreciation of our work.

__Reviewer #2 (Evidence, reproducibility and clarity (Required)): __ A three-color imaging approach to use centroid tracking is employed to determine the high resolution position over time of tagged actin fusion focus proteins during mating in fission yeast. In particular, the position of different protein components (tagged in a 3rd color) were determined in relation to the position (and axis) of the molecular motor Myo52, which is tagged with two different colors in the mating cells. Furthermore, time is normalized by the rapid diffusion of a weak fluorescent protein probe (mRaspberry) from one cell to the other upon fusion pore opening. From this approach multiple important mechanistic insights were determined for the compaction of fusion focus proteins during mating, including the general compaction of different components as fusion proceeds with different proteins having specific stereotypical behaviors that indicate underlying molecular insights. For example, secretory vesicles remain a constant distance from the plasma membrane, whereas the formin Fus1 rapidly accumulates at the fusion focus in a Myo52-dependent manner.

I have minor suggestions/points: (1) Figure 1, for clarity it would be helpful if the cells shown in B were in the same orientation as the cartoon cells shown in A. Similarly, it would be helpful to have the orientation shown in D the same as the data that is subsequently presented in the rest of the manuscript (such as Figure 2) where time is on the X axis and distance (position) is on the Y axis.

We have turned each image in panel B by 180° to match the cartoon in A. For panel D, we are not sure what the reviewer would like. This panel shows the coordinates of each Myo52 position, whereas Figure 2 shows oriented distance (on the Y axis) over time (on the X axis). Perhaps the reviewer suggests that we should display panel D with a rotation onto the Y axis rather than the X axis. We feel that this would not bring more clarity and prefer to keep it as is.

(2) Figure 2, for clarity useful to introduce how the position of Myo52 changes over time with respect to the fusion site (plasma membrane) earlier, and then come back to the positions of different proteins with respect to Myo52 shown in 2E. Currently the authors discuss this point after introducing Figure 2E, but better for the reader to have this in mind beforehand.

We have added a sentence at the start of the section describing Figure 2, pointing out that the static appearance of Myo52 is due to it being used as reference, but that in reality, it moves relative to the plasma membrane: “Because Myo52 is the reference, its trace is flat, even though in reality Myo52 also moves relative to other proteins and the plasma membrane (see Figure 2E)”. This change is already in the text.

(3) First sentence of page 8 "..., peaked at fusion time and sharply dropped post-fusion (Figure S3)." Figure S3 should be cited so that the reader knows where this data is presented.

Thanks, we have added the missing figure reference to the text.

(4) Figure 3D-H, why is Exo70 used as a marker for vesicles instead of Ypt3 for these experiments? Exo70 seems to have a more confusing localization than Ypt3 (3C vs 3D), which seems to complicate interpretations.

There are two main reasons for this choice. First, the GFP-Ypt3 fluorescence intensity is lower than that of Exo70-GFP, which makes analysis more difficult and less reliable. Second, in contrast to Exo70-GFP where the endogenous gene is tagged at the native genomic locus, GFP-Ypt3 is expressed as additional copy in addition to endogenous untagged Ypt3. Although GFP-Ypt3 was reported to be fully functional as it can complement the lethality of a ypt3 temperature sensitive mutant (Cheng et al, MBoC 2002), its expression levels are non-native and we do not have a strain in which ypt3 is tagged at the 5’ end at the native genomic locus. For these reasons, we preferred to examine in detail the localization of Exo70. We do not think it complicates interpretations. Exo70 faithfully decorates vesicles and exhibits the same localization as Ypt3 in WT cells (see Figure 2D) and in myo52-AID (see Figure 3C-D). We realize that our text was a bit confusing as we opposed the localization of Exo70 and Ypt3, when all we wanted to state was that the Exo70-GFP signal is stronger. We have corrected this in the text.

(5) Page 10, end of first paragraph, "We conclude...and promotes separation of Myo52 from the vesicles." This is an interesting hypothesis/interpretation that is consistent with the spatial-temporal organization of vesicles and the compacting fusion focus, but the underlying molecular mechanism has not be concluded.

This is an interpretation that is in line with our data. Firm conclusion that the organization of the actin fusion focus imposes a steric barrier to bulk vesicle entry will require in vitro reconstitution of an actin aster driven by formin-myosin V feedback and addition of myosin V vesicle-like cargo, which can be a target for future studies. To make clear that it is an interpretation and not a definitive statement, we have added “likely” to the sentence, as in: “We conclude that the distal position of vesicles in WT cells is a likely steric consequence of the architecture of the fusion focus, which restricts space at the center of the actin aster and promotes separation of Myo52 from the vesicles”.

(6) Figure 5F and 5G, the results are confusing and should be discussed further. Depletion of Myo52 decreases Fus1 long-range movements, indicating that Fus1 is being transported by Myo52 (5F). Similarly, the Fus1 actin assembly mutant greatly decreases Fus1 long-range movements and prevents Myo52 binding (5G), perhaps indicating that Fus1-mediated actin assembly is important. It seems the author's interpretations are oversimplified.

We show that Myo52 is critical for Fus1 long-range movements, as stated by the reviewer. We also show that Fus1-mediated actin assembly is important. The question is in what way.

One possibility is that FH2-mediated actin assembly powers the movement, which in this case represents the displacement of the formin due to actin monomer addition on the polymerizing filament. A second possibility is that actin filaments assembled by Fus1 somehow help Myo52 move Fus1. This could be for instance because Fus1-assembled actin filaments are preferred tracks for Myo52-mediated movements, or because they allow Myo52 to accumulate in the vicinity of Fus1, enhancing their chance encounter and thus the number of long-range movements (on any actin track). Based on the analysis of the K1112A point mutant in Fus1 FH2 domain, our data cannot discriminate between these three different options, which is why we concluded that the mutant allele does not allow us to make a firm conclusion. However, the Myo52-dependence clearly shows that a large fraction of the movements requires the myosin V. We have clarified the end of the paragraph in the following way: “Therefore, analysis of the K1112A mutant phenotype does not allow us to clearly distinguish between Fus1-powered from Myo52-powered movements. Future work will be required to test whether, in addition to myosin V-dependent transport, Fus1-mediated actin polymerization also directly contributes to Fus1 long-range movements.”

(7) Figure 6, why not measure the fluorescence intensity of Fus1 as a proxy for the number of Fus1 molecules (rather than the width of the Fus1 signal), which seems to be the more straight-forward analysis?

The aim of the measurement was to test whether Myo52 and Fus1 activity help focalize the formin at the fusion site, not whether these are required for localization in this region. This is why we are measuring the lateral spread of the signal (its width) rather than the fluorescence intensity of the signal. We know from previous work that Fus1 localizes to the shmoo tip independently of myosin V (Dudin et al, JCB 2015), and we also show this in Figure 6. However, the precise distribution of Fus1 is wider in absence of the myosins.

We can and will measure intensities to test whether there is also a quantitative difference in the number of molecules at the shmoo tip.

(8) Figure 7, the authors should note (and perhaps discuss) any evidence as to whether activation of Fus1 to facilitate actin assembly depends upon Fus1 dissociating from Myo52 or whether Fus1 can be activated while still associated with Myo52, as both circumstances are included in the figure.

This is an interesting point. We have no experimental evidence for or against Fus1 dissociating from Myo52 to assemble actin. However, it is known that formins rotate along the actin filament double helix as they assemble it, a movement that seems poorly compatible with processive transport by myosin V. In Figure 7, we do not particularly want to imply that Myo52 associates with Fus1 linked or not with an actin filament. The figure serves to illustrate the focusing mechanism of myosin V transporting a formin, which is more evident when we draw the formin attached to a filament end. We have now added a sentence in the figure legend to clarify this point: “Note that it is unknown whether Myo52 transports Fus1 associated or not with an actin filament.”

(9) Figure 7, the color of secretory vesicles should be the same in A and B.

This is now corrected.

Reviewer #2 (Significance (Required)):

This is an impactful and high quality manuscript that describes an elegant experimental strategy with important insights determined. The experimental imaging strategy (and analysis), as well as the insight into the pombe mating fusion focus and its comparison to other cytoskeletal compaction events will be of broad scientific interest.

We thank the reviewer for their appreciation of our work.

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

Summary:

Fission yeast cell-cell fusion during mating is mediated by an actin-based structure called the 'fusion focus', which orchestrates actin polymerization by the mating-specific formin, Fus1, to direct polarized secretion towards the mating site. In the current study, Thomas and colleagues quantitatively map the spatial distribution of proteins mediating cell-cell fusion using a three-color fluorescence imaging methodology in the fission yeast Schizosaccharomyces pombe. Using Myo52 (Type V myosin) as a fluorescence reference point, the authors discover that proteins known to localize to the fusion focus have distinct spatial distributions and accumulation profiles at the mating site. Myo52 and Fus1 form a complex in vivo detected by co-immunoprecipitation and each contribute to directing secretory vesicles to the fusion focus. Previous work from this group has shown that the intrinsically disordered region (IDR) of Fus1 plays a critical role in forming the fusion focus. Here, the authors swap out the IDR of fission yeast Fus1 for the IDR of an unrelated mammalian protein, coincidentally called 'fused in sarcoma' (FUS). They express the Fus1∆IDR-FUSLC-27R chimera in mitotically dividing fission yeast cells, where Fus1 is not normally expressed, and discover that the Fus1∆IDR-FUSLC-27R chimera can travel with Myo52 on actively polymerizing actin cables. Additionally, they show that acute loss of Myo52 or Fus1 function, using Auxin-Inducible Degradation (AID) tags and point mutations, impair the normal compaction of the fusion focus, suggesting that direct interaction and coordination of Fus1 and Myo52 helps shape this structure.

Major Comments:

(1) In the Results section for Figure 2, the authors claim that actin filaments become shorter and more cross-linked they move away from the fusion site during mating, and suggest that this may be due to the presence of Myo51. However, the evidence to support this claim is not made clear. Is it supported by high-resolution electron microscopy of the actin filaments, or some other results? This needs to be clarified.

Sorry if our text was unclear. The basis for the claim that actin filaments become shorter comes from our observation that the average position of tropomyosin and Myo51, both of which decorate actin filaments, is progressively closer to both Fus1 and the plasma membrane. Thus, the actin structure protrudes less into the cytosol as fusion progresses. The basis for claiming that Myo51 promotes actin filament crosslinking comes mainly from previously published papers, which had shown that 1) Myo51 forms complexes with the Rng8 and Rng9 proteins (Wang et al, JCB 2014), and 2) the Myo51-Rng8/9 not only binds actin through Myo51 head domain but also binds tropomyosin-decorated actin through the Rng8/9 moiety (Tang et al, JCB 2016; reference 27 in our manuscript). We had also previously shown that these proteins are necessary for compaction of the fusion focus (Dudin et al, PLoS Genetics 2017; reference 28 in our manuscript). Except for measuring the width of Fus1 distribution in myo51∆ mutants, which confirms previous findings, we did not re-investigate here the function of Myo51.

We have now re-written this paragraph to present the previous data more clearly: “The distal localization of Myo51 was mirrored by that of tropomyosin Cdc8, which decorates linear actin filaments (Figure 2B) (Hatano et al, 2022). The distal position of the bulk of Myo51-decorated actin filaments was confirmed using Airyscan super-resolution microscopy (Figure 2B, right). Thus, the average position of actin filaments and decreasing distance to Myo52 indicates they initially extend a few hundred nanometers into the cytosol and become progressively shorter as fusion proceeds. Previous work had shown that Myo51 cross-links and slides Cdc8-decorated actin filaments relative to each other (Tang et al, 2016) and that both proteins contribute to compaction of the fusion focus in the lateral dimension along the cell-cell contact area (perpendicular to the fusion axis) (Dudin et al, 2017). We confirmed this function by measuring the lateral distribution of Fus1 along the cell-cell contact area (perpendicular to the fusion axis), which was indeed wider in myo51∆ than WT cells (see below Figure 6A-B).”

(2) In Figure 4, the authors comment that disrupting Fus1 results in more disperse Myo52 spatial distribution at the fusion focus, raising the possibility that Myo52 normally becomes focused by moving on the actin filaments assembled by Fus1. This can be tested by asking whether latrunculin treatment phenocopies the 'more dispersed' Myo52 localization seen in fus1∆ cells? If Myo52 is focused instead by its direct interaction with Fus1, the latrunculin treatment should not cause the same phenotype.

This is in principle a good idea, though it is technically challenging because pharmacological treatment of cell pairs in fusion is difficult to do without disturbing pheromone gradients which are critical throughout the fusion process (see Dudin et al, Genes and Dev 2016). We will try the experiment but are unsure about the likelihood of technical success.

We note however that a similar experiment was done previously on Fus1 overexpressed in mitotic cells (Billault-Chaumartin et al, Curr Biol 2022; Fig 1D). Here, Fus1 also forms a focus and latrunculin A treatment leads to Myo52 dispersion while keeping the Fus1 focus, which is in line with our proposal that Myo52 becomes focused by moving on Fus1-assembled actin filaments. Similarly, we showed in Figure 5B that Latrunculin A treatment of mitotic cells expressing Fus1∆IDR-FUSLC-27R also results in Myo52, but not Fus1 dispersion.

(3) The Fus1∆IDR-FUSLC-27R chimera used in Figure 5 is an interesting construct to examine actin-based transport of formins in cells. I was curious if the authors could provide the rates of movement for Myo52 and for Fus1∆IDR-FUSLC-27R, both before and after acute depletion of Myo52. It would be interesting to see if loss of Myo52 alters the rate of movement, or instead the movement stems from formin-mediated actin polymerization.

We will measure these rates.

(4) Also, Myo52 is known to interact with the mitotic formin For3. Does For3 colocalize with Myo52 and Fus1∆IDR-FUSLC-27R along actin cables?

This is an interesting question for which we do not have an answer. For technical reasons, we do not have the tools to co-image For3 with Fus1∆IDR-FUSLC-27R because both are tagged with GFP. We feel that this question goes beyond the scope of this paper.

(5) If Fus1∆IDR-FUSLC-27R is active, does having ectopic formin activity in mitotic cells affect actin cable architecture? This could be assessed by comparing phalloidin staining for wildtype and Fus1∆IDR-FUSLC-27R cells.

We are not sure what the purpose of this experiment is, or how informative it would be. If it is to evaluate whether Fus1∆IDR-FUSLC-27R is active, our current data already demonstrates this. Indeed, Fus1∆IDR-FUSLC-27R recruits Myo52 in a F-actin and FH2 domain-dependent manner (shown in Figure 5B and 5G), which demonstrates that Fus1∆IDR-FUSLC-27R FH2 domain is active. Even though Fus1∆IDR-FUSLC-27R assembles actin, we predict that its effect on general actin organization will be weak. Indeed, it is expressed under endogenous fus1 promoter, leading to very low expression levels during mitotic growth, such that only a subset of cells exhibit a Fus1 focus. Furthermore, most of these Fus1 foci are at or close to cell poles, where linear actin cables are assembled by For3, such that they may not have a strong disturbing effect. Because analysis of actin cable organization by phalloidin staining is difficult (due to the more strongly staining actin patches), cells with clear change in organization predicted to be rare in the population, and the gain in knowledge not transformative, we are not keen to do this experiment.

Minor Comments:

Prior studies are referenced appropriately. Text and figures are clear and accurate. My only suggestion would be Figure 1E-H could be moved to the supplemental material, due to their extremely technical nature. I believe this would help the broad audience focus on the experimental design mapped out in Figure 1A-D.

We are relatively neutral about this. If this suggestion is supported by the Editor, we can move these panels to supplement.

Reviewer #3 (Significance (Required)):

Significance: This study provides an improved imaging method for detecting the spatial distributions of proteins below 100 nm, providing new insights about how a relatively small cellular structure is organized. The use of three-color cell imaging to accurately measure accumulation rates of molecular components of the fusion focus provides new insight into the development of this structure and its roles in mating. This method could be applied to other multi-protein structures found in different cell types. This work uses rigorously genetic tools such as knockout, knockdown and point mutants to dissect the roles of the formin Fus1 and Type V myosin Myo52 in creating a proper fusion focus. The study could be improved by biochemical assays to test whether Myo52 and Fus1 directly interact, since the interaction is only shown by co-immunoprecipitation from extracts, which may reflect an indirect interaction.

Indeed, future studies should dissect the Fus1-Myo52 interaction, to determine whether it is direct and identify mutants that impair it.

I believe this work advances the cell-mating field by providing others with a spatial and temporal map of conserved factors arriving to the mating site. Additionally, they identified a way to study a mating specific protein in mitotically dividing cells, offering future questions to address.

This study should appeal to a range of basic scientists interested in cell biology, the cytoskeleton, and model organisms. The three-colored quantitative imaging could be applied to defining the architecture of many other cellular structures in different systems. Myosin and actin scientists will be interested in how this work expands the interplay of these two fields.

I am a cell biologist with expertise in live cell imaging, genetics and biochemistry.

We thank the reviewer for their appreciation of our work.

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Referee #3

Evidence, reproducibility and clarity

Summary:

Fission yeast cell-cell fusion during mating is mediated by an actin-based structure called the 'fusion focus', which orchestrates actin polymerization by the mating-specific formin, Fus1, to direct polarized secretion towards the mating site. In the current study, Thomas and colleagues quantitatively map the spatial distribution of proteins mediating cell-cell fusion using a three-color fluorescence imaging methodology in the fission yeast Schizosaccharomyces pombe. Using Myo52 (Type V myosin) as a fluorescence reference point, the authors discover that proteins known to localize to the fusion focus have distinct spatial distributions and accumulation profiles at the mating site. Myo52 and Fus1 form a complex in vivo detected by co-immunoprecipitation and each contribute to directing secretory vesicles to the fusion focus. Previous work from this group has shown that the intrinsically disordered region (IDR) of Fus1 plays a critical role in forming the fusion focus. Here, the authors swap out the IDR of fission yeast Fus1 for the IDR of an unrelated mammalian protein, coincidentally called 'fused in sarcoma' (FUS). They express the Fus1∆IDR-FUSLC-27R chimera in mitotically dividing fission yeast cells, where Fus1 is not normally expressed, and discover that the Fus1∆IDR-FUSLC-27R chimera can travel with Myo52 on actively polymerizing actin cables. Additionally, they show that acute loss of Myo52 or Fus1 function, using Auxin-Inducible Degradation (AID) tags and point mutations, impair the normal compaction of the fusion focus, suggesting that direct interaction and coordination of Fus1 and Myo52 helps shape this structure.

Major Comments:

• In the Results section for Figure 2, the authors claim that actin filaments become shorter and more cross-linked they move away from the fusion site during mating, and suggest that this may be due to the presence of Myo51. However, the evidence to support this claim is not made clear. Is it supported by high-resolution electron microscopy of the actin filaments, or some other results? This needs to be clarified.

• In Figure 4, the authors comment that disrupting Fus1 results in more disperse Myo52 spatial distribution at the fusion focus, raising the possibility that Myo52 normally becomes focused by moving on the actin filaments assembled by Fus1. This can be tested by asking whether latrunculin treatment phenocopies the 'more dispersed' Myo52 localization seen in fus1∆ cells? If Myo52 is focused instead by its direct interaction with Fus1, the latrunculin treatment should not cause the same phenotype.

• The Fus1∆IDR-FUSLC-27R chimera used in Figure 5 is an interesting construct to examine actin-based transport of formins in cells. I was curious if the authors could provide the rates of movement for Myo52 and for Fus1∆IDR-FUSLC-27R, both before and after acute depletion of Myo52. It would be interesting to see if loss of Myo52 alters the rate of movement, or instead the movement stems from formin-mediated actin polymerization.

• Also, Myo52 is known to interact with the mitotic formin For3. Does For3 colocalize with Myo52 and Fus1∆IDR-FUSLC-27R along actin cables?

• If Fus1∆IDR-FUSLC-27R is active, does having ectopic formin activity in mitotic cells affect actin cable architecture? This could be assessed by comparing phalloidin staining for wildtype and Fus1∆IDR-FUSLC-27R cells.

Minor Comments:

• Prior studies are referenced appropriately.

• Text and figures are clear and accurate. My only suggestion would be Figure 1E-H could be moved to the supplemental material, due to their extremely technical nature. I believe this would help the broad audience focus on the experimental design mapped out in Figure 1A-D.

Significance

Significance: This study provides an improved imaging method for detecting the spatial distributions of proteins below 100 nm, providing new insights about how a relatively small cellular structure is organized. The use of three-color cell imaging to accurately measure accumulation rates of molecular components of the fusion focus provides new insight into the development of this structure and its roles in mating. This method could be applied to other multi-protein structures found in different cell types. This work uses rigorously genetic tools such as knockout, knockdown and point mutants to dissect the roles of the formin Fus1 and Type V myosin Myo52 in creating a proper fusion focus. The study could be improved by biochemical assays to test whether Myo52 and Fus1 directly interact, since the interaction is only shown by co-immunoprecipitation from extracts, which may reflect an indirect interaction.

I believe this work advances the cell-mating field by providing others with a spatial and temporal map of conserved factors arriving to the mating site. Additionally, they identified a way to study a mating specific protein in mitotically dividing cells, offering future questions to address.

This study should appeal to a range of basic scientists interested in cell biology, the cytoskeleton, and model organisms. The three-colored quantitative imaging could be applied to defining the architecture of many other cellular structures in different systems. Myosin and actin scientists will be interested in how this work expands the interplay of these two fields.

I am a cell biologist with expertise in live cell imaging, genetics and biochemistry.

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Referee #2

Evidence, reproducibility and clarity

A three-color imaging approach to use centroid tracking is employed to determine the high resolution position over time of tagged actin fusion focus proteins during mating in fission yeast. In particular, the position of different protein components (tagged in a 3rd color) were determined in relation to the position (and axis) of the molecular motor Myo52, which is tagged with two different colors in the mating cells. Furthermore, time is normalized by the rapid diffusion of a weak fluorescent protein probe (mRaspberry) from one cell to the other upon fusion pore opening. From this approach multiple important mechanistic insights were determined for the compaction of fusion focus proteins during mating, including the general compaction of different components as fusion proceeds with different proteins having specific stereotypical behaviors that indicate underlying molecular insights. For example, secretory vesicles remain a constant distance from the plasma membrane, whereas the formin Fus1 rapidly accumulates at the fusion focus in a Myo52-dependent manner.

I have minor suggestions/points:

(1) Figure 1, for clarity it would be helpful if the cells shown in B were in the same orientation as the cartoon cells shown in A. Similarly, it would be helpful to have the orientation shown in D the same as the data that is subsequently presented in the rest of the manuscript (such as Figure 2) where time is on the X axis and distance (position) is on the Y axis.

(2) Figure 2, for clarity useful to introduce how the position of Myo52 changes over time with respect to the fusion site (plasma membrane) earlier, and then come back to the positions of different proteins with respect to Myo52 shown in 2E. Currently the authors discuss this point after introducing Figure 2E, but better for the reader to have this in mind beforehand.

(3) First sentence of page 8 "..., peaked at fusion time and sharply dropped post-fusion (Figure S3)." Figure S3 should be cited so that the reader knows where this data is presented.

(4) Figure 3D-H, why is Exo70 used as a marker for vesicles instead of Ypt3 for these experiments? Exo70 seems to have a more confusing localization than Ypt3 (3C vs 3D), which seems to complicate interpretations.

(5) Page 10, end of first paragraph, "We conclude...and promotes separation of Myo52 from the vesicles." This is an interesting hypothesis/interpretation that is consistent with the spatial-temporal organization of vesicles and the compacting fusion focus, but the underlying molecular mechanism has not be concluded.

(6) Figure 5F and 5G, the results are confusing and should be discussed further. Depletion of Myo52 decreases Fus1 long-range movements, indicating that Fus1 is being transported by Myo52 (5F). Similarly, the Fus1 actin assembly mutant greatly decreases Fus1 long-range movements and prevents Myo52 binding (5G), perhaps indicating that Fus1-mediated actin assembly is important. It seems the author's interpretations are oversimplified.

(7) Figure 6, why not measure the fluorescence intensity of Fus1 as a proxy for the number of Fus1 molecules (rather than the width of the Fus1 signal), which seems to be the more straight-forward analysis?

(8) Figure 7, the authors should note (and perhaps discuss) any evidence as to whether activation of Fus1 to facilitate actin assembly depends upon Fus1 dissociating from Myo52 or whether Fus1 can be activated while still associated with Myo52, as both circumstances are included in the figure.

(9) Figure 7, the color of secretory vesicles should be the same in A and B.

Significance

This is an impactful and high quality manuscript that describes an elegant experimental strategy with important insights determined. The experimental imaging strategy (and analysis), as well as the insight into the pombe mating fusion focus and its comparison to other cytoskeletal compaction events will be of broad scientific nterest.

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Referee #1

Evidence, reproducibility and clarity

Summary:

• In this article, Thomas et al. use a super-resolution approach in living cells to track proteins involved in the fusion event of sexual reproduction. They study the spatial organization and dynamics of the actin fusion focus, a key structure in cell-cell fusion in Schizosaccharomyces pombe. The researchers have adapted a high-precision centroid mapping method using three-color live-cell epifluorescence imaging to map the dynamic architecture of the fusion focus during yeast mating. The approach relies on tracking the centroid of fluorescence signals for proteins of interest, spatially referenced to Myo52-mScarlet-I (as a robust marker) and temporally referenced using a weakly fluorescent cytosolic protein (mRaspberry), which redistributes strongly upon fusion. The trajectories of five key proteins, including markers of polarity, cytoskeleton, exocytosis and membrane fusion, were compared to Myo52 over a 75-minute window spanning fusion. Their observations indicate that secretory vesicles maintain a constant distance from the plasma membrane whereas the actin network compacts. Most importantly, they discovered a positive feedback mechanism in which myosin V (Myo52) transports Fus1 formin along pre-existing actin filaments, thereby enhancing aster compaction.

• This article is well written, the arguments are convincing and the assertions are balanced. The centroid tracking method has been clearly and solidly controlled. Overall, this is a solid addition to our understanding of cytoskeletal organization in cell fusion. Major comments: No major comment.

Minor comments:

• Page 8 authors wrote "Upon depletion of Myo52, Ypt3 did not accumulate at the fusion focus (Figure 3C). A thin, wide localization at the fusion site was occasionally observed (Figure 3C, Movies S3)" : Is there a quantification of this accumulation in the mutant?

• The framerate of movies could be improved for reader comfort: For example, movie S6 lasts 0.5 sec.

Significance

This study represents a conceptual and technical breakthrough in our understanding of cytoskeletal organization during cell-cell fusion. The authors introduce a high-precision, three-color live-cell centroid mapping method capable of resolving the spatio-temporal dynamics of protein complexes at the nanometer scale in living yeast cells. This methodological innovation enables systematic and quantitative mapping of the dynamic architecture of proteins at the cell fusion site, making it a powerful live-cell imaging approach. However, it is important to keep in mind that the increased precision achieved through averaging comes at the expense of overlooking atypical or outlier behaviors. The authors discovered a myosin V-dependent mechanism for the recruitment of formin that leads to actin aster compaction. The identification of Myo52 (myosin V) as a transporter of Fus1 (formin) to the fusion focus adds a new layer to our understanding of how polarized actin structures are generated and maintained during developmentally regulated processes such as mating.

Previous studies have shown the importance of formins and myosins during fusion, but this paper provides a quantitative and dynamic mapping that demonstrates how Myo52 modulates Fus1 positioning in living cells. This provides a better understanding of actin organization, beyond what has been demonstrated by fixed-cell imaging or genetic perturbation.

Audience: Cell biologists working on actin dynamics, cell-cell fusion and intracellular transport. Scientists involved in live-cell imaging, single particle tracking and cytoskeleton modeling.

I have expertise in live-cell microscopy, image analysis, fungal growth machinery and actin organization.

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Reply to the reviewers

Note to all Reviewers:

We would like to thank all the reviewers for their time and insightful feedback. In response to the comments and points raised, we have performed major revisions to our manuscript. We have expanded our analysis on the role of TP53 loss of function in BM activation (Figure 3), investigating human LUAD datasets as well as murine LUAD models. We show that TP53 pathway is significantly negatively correlated with BM, and that loss of TP53 leads to the acquisition of the basal-like phenotype regardless of the type of driver oncogene present (KRAS/EGFR). Furthermore, we added a new figure (Figure 7), where we demonstrate that type I interferon can promote BM activation in LUAD harboring TP53 mutations but not in those with wild type TP53. With this, we propose a mechanism of action of how a subset of LUAD tumors (TP53-mut) upregulate BM, become more aggressive and resistant to therapies.

Finally, we have made the manuscript clearer and transparent by improving the presentation of plots, as well as including source data files and Rmarkdown files for reproducibility.

Reviewer 1:

Major comments

R1-Comment 1: The authors did not submit with the manuscript all the results that they have obtained from their analysis, on which they based their claims. I suggest that the authors submit a SourceData file in Excel format. This file should contain the values and the relevant information for each of the plots presented in the main and supplementary figures. For example, in case of box plots, the five-number summary should be provided. Further, the p-values and the test used for their calculations should be also mentioned. The file could be organized in a way that the data and relevant information for each figure panel are presented in separated data sheets in order that the reader can easily navigate through the file and find the information for each figure panel fast. Similarly, the authors should provide access to the scripts that they have developed or adapted from published scripts to perform the analysis of the datasets and obtain the results presented in the manuscript. The access to the scripts used in the manuscript is important to reproduce analysis. The scripts can be deposited at github, for example.

Reply: We thank the reviewer for their advice in making the presentation of our results and methods more transparent and reproducible. We have now provided the source data file (supplementary file 2), which contains relevant data for each figure. We have also uploaded Rmarkdown files to github and R Markdown HTML reports are compiled in Supplementary File 3, this shows how the analyses were performed and how each figure generated. All datasets required to reproduce the analyses and figures have also been added to Zenodo (10.5281/zenodo.16964654) and will be published when the article is in press.

R1-Comment 2: The results and their interpretations are mainly done based on in silico analysis from publicly available transcriptomic datasets. The confirmation of the results obtained by the in silico analysis is limited to the last figure, in which the authors show results obtained by multiplexed immunohistochemistry and histo-cytometry of tissue microarrays from a curated cohort of FFPE samples. The relevance of the results obtained by the in silico analysis may increase if the authors could present results either in a conditional (lung-specific) Kras mutant mouse model, or patient-derived xenograft (PDX) mouse model of lung cancer. The PDX mouse model will be more suitable in case that access to genetically modified mouse models is not given and/or the time for the experiments is limited. In both cases, the hyperactivation of the small GTPase KRAS should expand the BM gene expression signature in the mouse lung in a Sox9-dependent manner, thereby leading to lung tumors. Further, Sox9 loss-of-function experiments should reduce the BM gene expression signature and favor the ALV gene expression signature. These results would strongly support the interpretation of the in silico results by the authors in the present manuscript, and would significantly increase the impact of the manuscript in the scientific field of lung cancer.

Reply: We thank the reviewer for their insightful feedback on how to improve the impact of our study through further functional validation of in silico findings. To address this comment, we have performed additional analyses, including data and experiments from both murine and human LUAD model systems to elucidate a novel mechanism of BM activation in LUAD. We appreciate the reviewer’s suggestion to pursue analysis of Sox9 involvement in regulating BM activation and agree that both KRAS and SOX9 activation are likely to be involved in at least some elements of the process of disease progression we described in this manuscript. Indeed, previous studies have completed the experiments suggested, demonstrating Sox9 knock-out reduced Kras driven tumour progression and morphological grade in vivo (PMID: 37258742 and 34021911); and was associated with loss of AT2 lineage identity (PMID: 37468622).

Our analysis of human LUAD using scRNA-seq data has demonstrated that this differentiation spectrum in fact extends beyond loss of lineage fidelity and in a subset of cells leads to transdifferentiation to a basal-like cell state. In our revised manuscript, we have more clearly elucidated the role of KRAS and TP53 in these two events during LUAD progression, demonstrating that while oncogenic KRAS (and likely downstream SOX9 activation) can lead to the loss of lineage commitment in LUAD cells, mutations in TP53 are required for acquisition of the basal-like phenotype. We have also expanded on this mechanism identifying a novel role for type-1 interferon signaling in the presence of TP53 loss-of-function as a mechanism that can lead to BM activation and acquisition of a basal-like cell state in LUAD. The data related to these analyses are now presented in figures 3 and 7.

In accordance with the 3Rs principles for ethical use of animals in research we have taken advantage of publicly available data from previous experiments analyzing conditional (lung-specific) Kras mutant mouse model to validate our in-silico findings. This confirmed our in silico analysis of human LUAD, demonstrating an important role for TP53 loss of function in regulating BM activation (presented in Figure 3E&F and Figure S3F&G)

We also showed that the type I interferon signaling is capable of driving BM activation in LUAD but only in the context of TP53 loss-of-function. These experiments were performed using 3D organotypic cultures of H441 cells (human adenocarcinoma cell line with mutant TP53) and A549 cells (human adenocarcinoma cell line with wild-type TP53). These 3D cultures were treated with IFN-alpha, both BM and basal-like marker upregulation (MKI67, CDC20, TOP2A, S100A9, S100A2, SOX9 and KRT17) was observed only in LUAD cells carrying a mutation in TP53. These data are now presented in Figure S7D.

R1-Comment 3: In general, the description of the results in the corresponding section of the manuscript can be improved to facilitate the understanding of the results presented.

As an example, the figure 1B is described on page 13 as follows: "...we first used a publicly available microarray dataset [9] to identify genes differentially expressed between epithelial cells engaged in BM (embryonic day 14 [E14]) or ALV (embryonic day 19 [E19]) (Figure 1B and TABLE S1)." By looking at the plot in figure 1B, this description is not sufficient to understand what the authors present in this figure panel, not even after reading the corresponding figure legend.

Reply: We thank the reviewer for their advice on making our manuscript clearer. Throughout the manuscript we have now edited the result descriptions, we have also provided further detail to the methods sections, figure legends and axes labels to enhance clarity and facilitate understanding of the analyses performed.

In the example cited we have edited the sections referenced above as follows:

“To test this hypothesis, we identified genes that were differentially expressed in epithelial cells engaged in active BM (corresponding to embryonic day 14) vs active ALV (corresponding to embryonic day 19), using a publicly available microarray dataset.”

We have also changed the Y axis label of Figure 1B to: “log2(FC E19 [ALV] – E14[BM])”.

The description in the figure legend has also been modified to provide more context: “Dot plot showing the identification of genes differentially expressed by epithelial cells during murine developmental-BM (embryonic day 14) and ALV (embryonic day 19) [1]. Genes with the highest Fold Change of expression between day 14 (BM) and 19 (ALV) of murine lung development are coloured green or red, respectively. These genes were used to generate ALV/BM signatures [9]”

R1-Comment 5: Another example is the description of the figure 3B on page 16: "This showed low levels of BM activation in tumour cells from residual disease (RD) that was significantly increased in samples with recurrent progressive disease (PD) (Figure 3B)." By looking figure 3B and the corresponding figure legend, one cannot find the group "residual disease (RD)".

__Reply: __We thank the reviewer for their diligent reading and have now corrected the figures to provide clearer labelling of axes and maintain consistency throughout. In the example cited, we have corrected the axis label to Residual disease (RD) and partial response (PR).

R1-Comment 6: Another example is the description of the figure 3C and 3D on page 16: "Single-cell analysis showed that both ALV-BM- and ALV-BM+ LUAD cells were increased in samples from recurrent progressive disease (Figure 3C,D)." By looking at figure 3D and the corresponding legend, I do not find the explanation of "TRUE" and "FALSE". The same is for figures 3J and 3M.

Reply: For this example (Figure 3 in the original manuscript is now figure 4), TRUE/FALSE labels have been replaced by PR (partial response) and PD (progressive disease) in panel D; replaced by “Responder (R)” or “Non-responder (NR)” in panels J&M.

R1-Comment 7: Other figure panels were also poorly described in the results section and in the corresponding legends. Further, the presentation of the results in the main and supplementary figures has to be improved. For example, labeling of the Y-axis in the figures 1H to 1J, 2C, 2D, 2G, 2H, 3B, 3C, 3J, 3L, etc. has to be improved. As a point of reference, I would suggest checking how other authors present similar results in life science journals. These deficiencies in the presentation and description of the results make it difficult for the readers to understand the manuscript.

Reply: These axes labels have been changed throughout to provide more information. “BM” changed to “BM (ssGSEA score)” or “BM (module score)” and “ALV” changed to “ALV (ssGSEA score)” or “ALV (module score)” for figures 1H, 1I, 1J, S1H-L, 2C, 2D, 3B, 3F, S3E, S3F, S3G, 4B, 4C, 4J, 4L, S4C, S4D, S5A, 6A, S6A, S6B, ssGSEA score was applied to bulk RNAseq samples, and modules scores were calculated for single cells.

Additionally:

S2A, S2B – OS label changed to Survival probability/OS probability.

S4H – y axis label changed to PDL1 (RPPA).

S3B – y axis label changed to “Tumour mutational burden (mut/mB).

S3C – y axis label changed to “Tobacco smoking (SBS mutational signature)”.

4F – y axis label changed to “DFS (proportion)”.

4H – y axis label changed to “PFS (proportion)”.

R1-R1-Comment 8: The authors write on page 18 "Despite AT2 cells being well described as the cell of origin for LUAD, this population was significantly less abundant in LUAD samples compared to control, demonstrating a high degree of transcriptomic plasticity within LUAD epithelium (Figure 4D)." How can the authors show that these results are not produced by the process of integration of the four scRNA-seq NSCLC datasets, the implementation of a specific machine learning classifier for the cell type-classification, or the manually filtration to exclude doublets? For example, will the authors achieve the same (or similar) results using a different machine learning classifier? If yes, please include the results in the manuscript.

Reply: The integration was performed using the method described by Stuart et al. (PMID: 31178118), implemented in the Seurat package. The term “machine learning classifier” has now been replaced by “label transfer” to clarify the method used and avoid confusion. Label transfer was only used to identify major cell types in the datasets used, i.e. the whole epithelial population. Doublet removal was performed as follows (and described in the methods section): epithelial cells were clustered using the shared nearest neighbor (SNN) modularity optimization algorithm implemented by the FindClusters function in the Seurat R package, based on 30 principal components and setting the resolution parameter to 0.1. This clustering solution identified multiple small clusters with divergent expression profiles to the majority of cells that were initially classified as epithelial (in the label transfer analysis). Manual examination of the marker genes for these small clusters showed they were characterized by expression of epithelial genes alongside canonical markers for either B cells (CD79A), macrophages (CD68, SPP1, APOE, CD14, MARCO) or Tcells/NK cells (CD3D, NKG7, CXCR4). These cells were therefore classed as heterotypic doublets and excluded from further analysis. All other cell types from the integrated datasets were analyzed in the same way, and no further epithelial clusters (that were not small clusters of doublets) were identified.

Further clustering to identify epithelial subpopulations was performed on the integrated dataset and the results presented from this analysis represent the clustering solution that ensures all subpopulations were identified across datasets to mitigate any potential batch-effects not resolved by the integration process. Furthermore, our results showing that LUAD cells exhibit a high degree of transcriptomic plasticity were also confirmed by the lineage fidelity analysis (Figure 5G&I), which demonstrates this observation is not dependent on a single clustering, integration or machine learning algorithm. This observation is also supported by other studies that have described loss of lineage commitment during LUAD tumorigenesis, where tumour cells become transcriptionally and phenotypically distinct from healthy AT2 cells.

Reviewer 1:

Minor comments:

__R1-Comment 9: __Please introduce the abbreviation for alveogenesis the first time that is used in the abstract, as it was done for branching morphogenesis.

__Reply: __Abbreviation for alveogenesis has now been added to the abstract.

R1-Comment 10: On page 18 the author write: "Consistent with the analyses presented above, pseudo bulk expression profiles for each sample showed that ALV and BM scores were significantly negatively correlated (r = -0.68, p = 4.1e-09)." Where are these results shown? I was not able to find these results. If they are not in the current version of the manuscript, please include the results

Reply: Scatter plot showing the negative correlation has now been added as Figure S5A.

__R1-Comment 11: __The authors should submit a supplementary table containing a list of the different data sets that were used for this manuscript. The table should include accession numbers and links to the different depositories, in which the data sets can be found. This will improve the overview of the datasets used in the study, as well as facilitate the finding of the datasets by the readers.

Reply: The list of all datasets used in this study, together with accession numbers and links are now in Supplementary file1.

R1-Comment 12: In figure 1G, change the color for FALSE in the legend.

Reply: Color for FALSE changed in Figure 1G and Figure S1E.

R1-Comment 13: Provide the complete list of mutated genes for Figure S2C.

Reply: Figure S2C has been replaced by figures 3C (top mutated genes in LUAD-BM) and S3A (top mutated genes in LUAD-ALV).

Reviewer 1 (Significance (required)):

__R1-Comment 14: __Conceptually, Bienkowska KJ et al. propose that LUAD tumors undergo reversion from an alveogenic to branching morphogenic phenotype during disease progression, generating inflamed or basal-like cell states that are variably persistent following TKI or ICB treatments. This concept is in line with reports using murine models of Kras-driven LUAD. In addition, there are parallels with findings in idiopathic pulmonary fibrosis (IPF, another hyperproliferative lung disease), in which KRT5-/KRT17+ basaloid cells were transiently found, like the basal-like phenotype that Bienkowska KJ identified in human LUAD. In other words, the concept proposed by the authors is novel and in line with previous publication in LC and IPF.

Response: We are glad the reviewer found our results novel and appreciated how they provide a linkage of previously defined mechanisms seen in murine developmental models to human cancer progression, and how they may be relevant for other diseases such as IPF.

__R1-Comment 15: __The in silico analysis of publicly available transcriptomic datasets presented by Bienkowska KJ et al. is original and comprehensive. It is an interesting contribution to the cancer research field. However, the impact of their findings to this scientific field will significantly increase if the authors could confirm the interpretation of their results using other experimental systems in addition to the one used in the las figure. For example, the experiments that I suggested in point 2., using either conditional Kras transgenic mice or a PDX mouse model for lung cancer will not only confirm the concpet proposed by the authors, but it will also provide further mechanistic insides related to this model at cellular and molecular level.

Response: We thank the reviewer for describing our analysis as original and comprehensive and their suggestion to develop the manuscript further with additional mechanistic analyses. We have comprehensively examined the mechanisms responsible for regulating BM activation using a combination of in vivo models and 3D organotypic cultures, elucidating a novel role for type-1 interferon signaling in the presence of TP53 loss-of-function as a mechanism that can lead to BM activation and acquisition of a basal-like cell state in LUAD. For further information regarding these additions to the revised manuscript, we direct the reviewer to the response provided to R1-comment 2 (above).

__R1-Comment 16: __Overall, the manuscript by Bienkowska KJ et al. addresses topics that are relevant to the field of lung cancer, the leading cause of cancer-related deaths worldwide. The bioinformatic methods implemented are cutting-edge. However, the text of the manuscript and the presentation of the results in the figures have to be improved to better exploit the potential of their findings. In addition, further experiments should be performed to confirm (and perhaps complement) the interpretation of their findings. I hope that my comments support the authors to improve the manuscript to reach the standard of manuscripts recently published at renowned journals in Review COMMONS. I recommend a major revision of the manuscript before publication.

__Reply: __We are pleased to read that the reviewer found the methods implemented by us to be cutting-edge, and that they recognized the relevance of this topic to the lung cancer field.

We thank the reviewer for their comments, which have helped us to significantly improve our manuscript.

We have made changes to how we present our data (as described in responses above) and performed further analyses to support our original findings. We have also now performed further in silico and functional analyses to expand and complement our original findings.

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

R2-Comment 1: __The study is novel and interesting, but the mechanisms how the dysregulation of developmental program was driven by specific oncogene and how to link these signatures to therapy were also not clear. __

__Reply: __We are pleased that the reviewer finds our study to be novel and interesting. We appreciate the reviewer pointing out the need to clarify the role of specific oncogenes to BM activation and response to therapies.

We have now added further analyses and edited the text to examine and explain how the ALV and BM signatures are driven by different oncogenes (Figure 3 and results section “TP53 loss of function is required for BM activation”), which showed that common oncogenic drives (e.g. KRAS and EGFR) can drive reduced ALV signature expression but TP53 mutations (or deletion in murine models) was critical for driving BM activation. Implications for therapy response are shown in (Figure 4). We have shown that BM activation is a key determinant of tyrosine kinase inhibitor (TKI) resistance in LUAD, representing a frequently activated off-target mechanism of resistance that supersedes the presence of an actionable oncogenic driver in terms of response rates; and that the BM signature also identified patients that, although positive for immune checkpoint blockade (ICB) response biomarkers, will likely fail to respond to this treatment. In the manuscript we have now thoroughly revised these sections of the results to clarify the details associated with these conclusions (results sections: “BM activation is associated with targeted-therapy resistance in lung adenocarcinomas” and “BM activation predicts poor response to immune-checkpoint blockade”).

We have also added further data to the manuscript elucidating the molecular mechanisms regulating BM activation (Figure 7), which has identified an important role for aberrant type-I interferon signaling in the context of mutant TP53.

Reviewer #2 (Significance (Required)):

__R2-Comment 2: __The authors in this manuscript aimed to examine the role of developmental programmes, alveogenesis and branching morphogenesis (BM), in regulating phenotypic diversity in NSCLC. They demonstrated that developmental programmes (ALV and BM) frequently become

dysregulated in NSCLC, with BM activation identifying aggressive LUAD that were resistant

to multiple therapies, including TKIs and ICB. They found that BM activation in LUAD was associated with TP53 pathway mutations and required AT2 cells to lose their alveolar identity, acquiring a basallike state. The study is very intriguing, and the findings may pave a link to the disease progression and therapy resistance in LUAD.

__Response: __We are pleased the reviewer found the study intriguing and with the potential to better understand LUAD progression and resistance to therapies.

__R2-Comment 3: __The current results presented, although comprehensively presented, is still many an association study, the mechanisms how these dysregulations of developmental programmes driven by the driver oncogenes or carcinogens are still unknown.

Response: We thank the reviewer for challenging us to further examine the molecular mechanisms underpinning our initial observations. As described above (see response to Reviewer #1 comment 2), we have performed additional in silico and mechanistic experimental analyses, which identified a novel role for type-I IFN signaling and TP53 loss-of-function in the activation of the BM program in LUAD. We hope these additions have enhanced the significance of the manuscript presented.

__R2-Comment 4: __The NSCLC is a heterogeneous disease, LUAD and LUSC are two different diseases in terms of oncogenesis, driver mutations and response to treatment. The manuscript may either just focused on LUAD or describe results carefully to include both LUAD and LUSC. For example, in the result of abstract, only LUAD was described, there was no mention of LUSC.

__Response: __We agree with the reviewer that NSCLC is a heterogeneous and complex disease. Indeed, this was in part what motivated us to investigate the role played by developmental processes in these distinct oncogenic processes. Our analyses showed that LUSC tumors were generally high for the BM signature (Figure 1I), which likely contributed to why this signature did not stratify survival rates for LUSC (Figure S2B). As a result, we opted to focus on LUAD as we found that BM activation was predictive of disease progression and survival in this NSCLC subtype. However, we did not completely remove LUSC from our manuscript to examine the degree to which LUAD tumors upregulating BM become “LUSC-like” and evaluate whether histological transformations occurred in LUAD cases with BM activation (as described in Figure 5 and the “BM activation in LUAD is associated with a basal-like phenotype” results section).

We have also now added a description of results from both LUAD and LUSC analyses to the abstract to clarify these points.

__R2-Comment 5: __The most common driver mutation of LUAD was EGFR, the authors also try to link the BM activation link to TKI resistance. I assumed that the TKIs most of the patients used were EGFR TKI, but the study did not examine the role of EGFR in the dysregulation of developmental programmes.

__Response: __We would like to thank the reviewer for highlighting an important aspect of how our work fits with current clinical practice in LUAD management. Our analyses were carried out over multiple cohorts that include different patient demographics, which have varied prevalence for specific oncogenic driver mutations (with EGFR mutations typically being more prevalent in Asian cohorts and KRAS mutations generally being the most common oncogenic driver in Western cohorts). To examine these two common oncogenic drivers impact on BM activation, we now include a direct analysis of BM level in cases harboring these mutations (Figure S3D-E). This showed that that irrespective of oncogenic driver mutations TP53 loss of function was associated with increased BM. Our new analysis of KRAS driven mouse models has also showed that KRAS activation is sufficient to induce reduced expression of the ALV signature but failed to elicit increased BM activation. Given our analysis of human tumours showed that EGFR mutant LUAD cases with wild-type TP53 had low levels of BM activation (Figure S3D), we have no reason to suspect that EGFR mutations alone would be sufficient to elicit BM activation.

__R2-Comment 6: __The TKI resistance was very complicated, not just EGFR T790M, the results and discussion regarding the activation of BM and TKI resistance seems not adequate. The mouse model used by Dr. Chang was mainly KRAS driven mouse lung cancer model (mice carrying RosatdT, Sox2EGFP, ShhCre, Sox9CKO, Fgfr2CKO, RosamTmG, Sox9CreER, Nkx2.1CreER, and KrasLSL-G12D alleles). It is not clear whether the EGFR driven (the most common driver of LUAD) mouse model also has same genetic signature. At least, the authors should describe or discuss these discrepancies.

__Response: __We thank the reviewer for their comments and advice on making our manuscript clearer. We have now revised the description of BM activation and TKI resistance in the results section (titled “BM activation is associated with targeted-therapy resistance in lung adenocarcinomas”).

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Referee #2

Evidence, reproducibility and clarity

The study is novel and interesting, but the mechanisms how the dysregulation of developmental program was driven by specific oncogene and how to link these signatures to therapy were also not clear.

Significance

The authors in this manuscript aimed to examine the role of developmental programmes, alveogenesis and branching morphogenesis (BM), in regulating phenotypic diversity in NSCLC. They demonstrated that developmental programmes (ALV and BM) frequently become dysregulated in NSCLC, with BM activation identifying aggressive LUAD that were resistant to multiple therapies, including TKIs and ICB. They found that BM activation in LUAD was associated with TP53 pathway mutations and required AT2 cells to lose their alveolar identity, acquiring a basallike state.

The study is very intriguing and the findings may pave a link to the disease progression and therapy resistance in LUAD. The current results presented, although comprehensively presented, is still many an association study, the mechanisms how these dysregulations of developmental programmes driven by the driver oncogenes or carcinogens are still unknown. The NSCLC is a heterogeneous disease, LUAD and LUSC are two different diseases in terms of oncogenesis, driver mutations and response to treatment. The manuscript may either just focused on LUAD or describe results carefully to include both LUAD and LUSC. For example, in the result of abstract, only LUAD was described, there was no mention of LUSC. The most common driver mutation of LUAD was EGFR, the authors also try to link the BM activation link to TKI resistance. I assumed that the TKIs most of the patients used were EGFR TKI, but the study did not examine the role of EGFR in the dysregulation of developmental programmes. The TKI resistance was very complicated, not just EGFR T790M, the results and discussion regarding the activation of BM and TKI resistance seems not adequate. The mouse model used by Dr. Chang was mainly KRAS driven mouse lung cancer model (mice carrying RosatdT, Sox2EGFP, ShhCre, Sox9CKO, Fgfr2CKO, RosamTmG, Sox9CreER, Nkx2.1CreER, and KrasLSL-G12D alleles). It is not clear whether the EGFR driven (the most common driver of LUAD) mouse model also has same genetic signature. At least, the authors should describe or discuss these discrepancies.

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Referee #1

Evidence, reproducibility and clarity

Summary:

Bienkowska KJ et al show in this manuscript a compilation of bioinformatic analysis of publicly available microarray datasets, bulk RNA sequencing (RNA-seq) datasets and single cell RNA sequencing (scRNA-seq) datasets. One transcriptomic data set from mouse (Chang DR et al., Proc Natl Acad Sci USA, 2013) was analyzed in this manuscript to determine the gene expression signatures specific for the developmental processes alveogenesis (ALV) and branching morphogenesis (BM). The rest of the transcriptomic data sets that were analyzed for this manuscript were selected based on different parameters including the involvement of non-small cell lung cancer (NSCLC), lug adenocarcinoma (LUAD), lung squamous cell carcinoma (LUSC) and various cohorts with different characteristics related to lung cancer (LC), such as mutations related to LC (in EGFR, ALK, BRAF, ROS1 and KRAS), and/or treatments/resistance of LC patients with/to tyrosine kinase inhibitors (TKI), anti-PD1 strategies, immune checkpoint blockade, (ICB) among others. In the last figure, the authors present results obtained by multiplexed immunohistochemistry and histo-cytometry of tissue microarrays from a curated cohort of archival formalin-fixed paraffin-embedded (FFPE) samples to confirm their interpretation of the results obtained by the transcriptomic analysis.

The findings and/or claims of the authors could be summarized in the following bullet points:

• After defining the ALV and BM gene expression signatures, the authors determined the expression of these signatures in bulk RNA-seq data sets from The Cancer Genome Atlas (TCGA). The ALV signature was significantly downregulated in LUAD and LUSC tumour subtypes compared to control samples, whereas BM was upregulated. These findings were validated using a Laser Capture Micro-Dissected (LCMD) microarray dataset (Lin J et al., AM J Pathol, 2014) comparing the epithelial compartment from non-tumour alveoli, non-tumour bronchi, LUAD and LUSC. Interestingly, ALV was suppressed and BM was activated in all LUSC tumours analyzed; whereas in LUAD tumours were heterogeneous for BM activation with some cases exhibiting ALV expression comparable to control tissue. In summary, the mutually antagonistic regulation of ALV and BM was found to account for a significant proportion of transcriptomic variance in human NSCLC bulk tissue datasets.
• BM activation was associated with poor overall survival rates in five independent LUAD cohorts (p=2.04e-13); and was significantly prognostic for resistance to TKIs (p=0.003) and ICBs (p=0.014), in pre-treatment biopsies.
• ScRNA-seq analysis revealed that malignant LUAD cells with loss of alveolar lineage fidelity predominantly acquired inflamed or basal-like cellular states, which were variably persistent in samples from TKI and ICB recurrence.
• The authors conclude from their analysis that LUAD tumours undergo reversion from an alveogenic to branching morphogenic phenotype during disease progression, generating inflamed or basal-like cell states that are variably persistent following TKI or ICB treatments.

Major comments:

1. The authors did not submit with the manuscript all the results that they have obtained from their analysis, on which they based their claims. I suggest that the authors submit a SourceData file in Excel format. This file should contain the values and the relevant information for each of the plots presented in the main and supplementary figures. For example, in case of box plots, the five-number summary should be provided. Further, the p-values and the test used for their calculations should be also mentioned.

The file could be organized in a way that the data and relevant information for each figure panel are presented in separated data sheets in order that the reader can easily navigate through the file and find the information for each figure panel fast.

Similarly, the authors should provide access to the scripts that they have developed or adapted from published scripts to perform the analysis of the datasets and obtain the results presented in the manuscript. The access to the scripts used in the manuscript is important to reproduce analysis. The scripts can be deposited at github, for example. 2. The results and their interpretations are mainly done based on in silico analysis from publicly available transcriptomic datasets. The confirmation of the results obtained by the in silico analysis is limited to the last figure, in which the authors show results obtained by multiplexed immunohistochemistry and histo-cytometry of tissue microarrays from a curated cohort of FFPE samples.

The relevance of the results obtained by the in silico analysis may increase if the authors could present results either in a conditional (lung-specific) Kras mutant mouse model, or patient-derived xenograft (PDX) mouse model of lung cancer. The PDX mouse model will be more suitable in case that access to genetically modified mouse models is not given and/or the time for the experiments is limited. In both cases, the hyperactivation of the small GTPase KRAS should expand the BM gene expression signature in the mouse lung in a Sox9-dependent manner, thereby leading to lung tumors. Further, Sox9 loss-of-function experiments should reduce the BM gene expression signature and favor the ALV gene expression signature. These results would strongly support the interpretation of the in silico results by the authors in the present manuscript, and would significantly increase the impact of the manuscript in the scientific field of lung cancer. 3. In general, the description of the results in the corresponding section of the manuscript can be improved to facilitate the understanding of the results presented. As an example, the figure 1B is described on page 13 as follows:

"...we first used a publicly available microarray dataset [9] to identify genes differentially expressed between epithelial cells engaged in BM (embryonic day 14 [E14]) or ALV (embryonic day 19 [E19]) (Figure 1B and TABLE S1)."

By looking at the plot in figure 1B, this description is not sufficient to understand what the authors present in this figure panel, not even after reading the corresponding figure legend.

Another example is the description of the figure 3B on page 16:

"This showed low levels of BM activation in tumour cells from residual disease (RD) that was significantly increased in samples with recurrent progressive disease (PD) (Figure 3B)."

By looking figure 3B and the corresponding figure legend, one cannot find the group "residual disease (RD)".

Another example is the description of the figure 3C and 3D on page 16:

"Single-cell analysis showed that both ALV-BM- and ALV-BM+ LUAD cells were increased in samples from recurrent progressive disease (Figure 3C,D)."

By looking at figure 3D and the corresponding legend, I do not find the explanation of "TRUE" and "FALSE". The same is for figures 3J and 3M.

Other figure panels were also poorly described in the results section and in the corresponding legends.

Further, the presentation of the results in the main and supplementary figures has to be improved. For example, labeling of the Y-axis in the figures 1H to 1J, 2C, 2D, 2G, 2H, 3B, 3C, 3J, 3L, etc. has to be improved. As a point of reference, I would suggest checking how other authors present similar results in life science journals.

These deficiencies in the presentation and description of the results make it difficult for the readers to understand the manuscript. 4. The authors write on page 18

"Despite AT2 cells being well described as the cell of origin for LUAD, this population was significantly less abundant in LUAD samples compared to control, demonstrating a high degree of transcriptomic plasticity within LUAD epithelium (Figure 4D)."

How can the authors show that these results are not produced by the process of integration of the four scRNA-seq NSCLC datasets, the implementation of a specific machine learning classifier for the cell type-classification, or the manually filtration to exclude doublets? For example, will the authors achieve the same (or similar) results using a different machine learning classifier? If yes, please include the results in the manuscript.

Minor comments:

1. Please introduce the abbreviation for alveogenesis the first time that is used in the abstract, as it was done for branching morphogenesis.
2. On page 18 the author write:

"Consistent with the analyses presented above, pseudo bulk expression profiles for each sample showed that ALV and BM scores were significantly negatively correlated (r = -0.68, p = 4.1e-09)."

Where are these results shown? I was not able to find these results. If they are not in the current version of the manuscript, please include the results 7. The authors should submit a supplementary table containing a list of the different data sets that were used for this manuscript. The table should include accession numbers and links to the different depositories, in which the data sets can be found. Thiy will improve the overview of the datasets used in the study, as well as facilitate the finding of the datasets by the readers. 8. In figure 1G, change the color for FALSE in the legend. 9. Provide the complete list of mutated genes for Figure S2C

Significance

Conceptually, Bienkowska KJ et al. propose that LUAD tumors undergo reversion from an alveogenic to branching morphogenic phenotype during disease progression, generating inflamed or basal-like cell states that are variably persistent following TKI or ICB treatments. This concept is in line with reports using murine models of Kras-driven LUAD. In addition, there are parallels with findings in idiopathic pulmonary fibrosis (IPF, another hyperproliferative lung disease), in which KRT5-/KRT17+ basaloid cells were transiently found, like the basal-like phenotype that Bienkowska KJ identified in human LUAD. In other words, the concept proposed by the authors is novel and in line with previous publication in LC and IPF.

The in silico analysis of publicly available transcriptomic datasets presented by Bienkowska KJ et al. is original and comprehensive. It is an interesting contribution to the cancer research field. However, the impact of their findings to this scientific field will significantly increase if the authors could confirm the interpretation of their results using other experimental systems in addition to the one used in the las figure. For example, the experiments that I suggested in point 2., using either conditional Kras transgenic mice or a PDX mouse model for lung cancer will not only confirm the concpet proposed by the authors, but it will also provide further mechanistic insides related to this model at cellular and molecular level.

Overall, the manuscript by Bienkowska KJ et al. addresses topics that are relevant to the field of lung cancer, the leading cause of cancer-related deaths worldwide. The bioinformatic methods implemented are cutting-edge. However, the text of the manuscript and the presentation of the results in the figures have to be improved to better exploit the potential of their findings. In addition, further experiments should be performed to confirm (and perhaps complement) the interpretation of their findings. I hope that my comments support the authors to improve the manuscript to reach the standard of manuscripts recently published at renowned journals in Review COMMONS. I recommend a major revision of the manuscript before publication.

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Reply to the reviewers

GENERAL COMMENTS

We thank the three reviewers for their comments on the paper.

We are pleased to see that they consider it be a comprehensive and well-executed study, which clearly establishes a previously overlooked connection between MRTF-SRF signalling and proliferation, and that its conclusions require no further experimentation.

As review 3 points out, this work has implications for cancer biology, and suggests new research routes to understand the relation between cell adhesion, proliferation, and transformation.

However, two referees raise significant concerns about its impact

Review 1 suggests that the paper lacks impact without exploration the wider biological significance of our observations, although it considers it to be a good basic cell biology study. It suggests further work extending the findings to tissue- or tumor-based systems. While we consider such studies worthwhile – indeed we are currently pursuing these directions – we consider them beyond the scope of the present paper.

Review 2 questions the novelty of our findings. We strongly disagree. This is is the first study to show that MRTF-SRF signalling is required for the proliferation of both primary and immortalised fibroblasts, and epithelial cells. We show that MRTF inactivation leads cells to enter a quiescence-like state under conditions that would permit efficient cell cycle progression in wildtype cells. The study will alter the field's perspective on the role of MRTF-SRF signalling, previously viewed as concerned with cell adhesion, morphology, and motility.

Responses to individual reviews (italic) follow in regular text.

RESPONSE TO INDIVIDUAL REVIEWS (comments in italic, response in regular, changes made)

__Reviewer #1 __

*(Evidence, reproducibility and clarity (Required)): *

*The manuscript by Neilsen et al. presents a thorough and well-structured study showing that Myocardin-related transcription factors (MRTF-A/B), via MRTF-SRF, are essential for the proliferation of both primary and immortalized fibroblasts and epithelial cells. Using a combination of knockouts/rescue experiments, cytoskeletal analysis, and transcriptomics, the authors demonstrate that MRTF-SRF signalling controls actin dynamics and contractility-key drivers of cell cycle progression. Notably, they show that the proliferative arrest caused by MRTF loss is reversible, distinguishing it from classical senescence. **

Major points*

• The link between MRTF-SRF activity, cytoskeletal organisation, and cell proliferation is clearly established. The fact that disrupting contractility phenocopies MRTF loss strengthens the case that the pathway acts through mechanical control.*
• The authors support their conclusions using multiple cell types (MEFs, primary fibroblasts, epithelial cells), a range of complementary assays (RNA-seq, traction force microscopy, adhesion/spreading), and genetic tools (CRISPR, inducible rescue).*
• The ability to restore proliferation by re-expressing MRTF-A argues against true senescence and instead suggests a quiescence-like state driven by cytoskeletal disruption.*
• This work particularly highlights how mechanical inputs feed into transcriptional programs to regulate proliferation, with implications for understanding anchorage-dependent growth.**

Suggestions While the authors argue convincingly against classical senescence, elevated SA-βGal and SASP expression suggest a more nuanced arrest state. It not really clear what this state is or is not, therefore a deeper discussion of possible hybrid or intermediate states would be helpful - maybe potential additional experiments to include or exclude potential explanations - e.g. how does it differ from G0 exit?* Our findings show that MRTF inactivation inhibits cell proliferation under conditions that would permit efficient cell cycle progression in wildtype cells, inducing a state with some features associated with classical senescence, and others conventionally associated with reversible cell cycle arrest/quiescence. The reviewer correctly points out that this raises problems with accurately defining the nature of the MRTF-null proliferation defect.

To our knowledge there are no rigorously defined unambiguous markers for senescence, quiescence, or G0. Indeed, recent studies have shown that senescence and quiescence / G0 states are not as distinct as previously assumed (Anwar et al, 2018; Ashraf et al 2023) as we reviewed in detail in Discussion p27, §2; p28 §3. We therefore do not consider it a productive endeavour to define markers for the MRTF-null state as opposed to defining its mechanistic basis. However, we agree that we should have been clearer about how the phenotypes we observe relate to classical cell arrest states.

We have therefore revised the presentation of the Results to make it clear which features of the non-proliferative state associated with MRTF inactivation are seen in classical senescence, and which are found in reversible cell cycle exit or quiescence.

Things done:

• __Results pp16-17 and Fig 1. Figure panels and presentation are reordered to present “senescence” features together before marker expression (panel G is now panel I). Text now explicitly points out that the spectrum of cell cycle markers, specifically p27 upregulation, is not that associated with classical senescence (p16, p21,etc) but previously linked to reversible arrest or quiescence. Lines 371-380 have been moved up from the succeeding paragraph; statement added re p27 and reversible cell cycle exit on lines 387-389; summary sentence added in lines 398-401). __
• Statement added that reversibility distinguishes the MRTF defect from classical senescence p20§1 line 454-455.

• Note that p27 is associated with reversible arrest included on p20§2 line 460. We also explicitly summarised the features of the phenotype at the start of the Discussion.

• Sentences added p27§1 lines 626-631.

• Emphasis that p27 protein upregulation is associated with reversible cell cycle inhibition and quiescence is added on p28 line 668-669.

• The transcriptomic data are strong, but the paper would benefit from zooming in on specific MRTF-SRF targets (e.g., actin isoforms, adhesion molecules) that directly link cytoskeletal regulation to cell cycle control.*

We have now clarified presentation of the RNAseq data in Figure 5 and the data summary tables. Figure 5B now identifies which of those genes showing deficits in MRTF-null MEFs were previously identified as direct genomic targets for MRTF-SRF, and that the majority are cytoskeletal.

• __Additional columns added in Table 1 to indicate whether genes are candidate genomic MRTF-SRF targets; Table 2 now show gene symbol lists as well as ENSMBL IDs for GO categories and NCBI Entrez IDs for GSEA categories, respectively. __
• __Figure 5B revised to point out cytoskeletal genes that are genomic MRTF-SRF targets in bold, legend clarified p40 lines 920-922. __
• Now noted____ p23 lines 527-529 that cytoskeletal genes affected include many direct MRTF-SRF targets. Our data confirms that in MEFs, MRTF inactivation affects fibroblast cell morphology, adhesion, spreading, motility and contractility (Figures 5, 6), as seen in many other settings.

A critical question remains as to whether these effects a reflect limitation in one MRTF target gene or several, and how this defect relates to proliferation.

Concerning specific MRTF-SRF gene targets:

Cells lacking cytoplasmic actins are reported to exhibit defective proliferation, (__now noted in Results p23 lines 529-532). __We are currently evaluating whether this defect has similarities with the MRTF-null proliferation phenotype (see Discussion p31, §2).

Previous findings suggest that defective cytoplasmic actin expression may underlie most MRTF knockout phenotypes (Salvany et al, 2014; Maurice et al., 2024) previously noted in the Discussion (see p31, §2).

The myoferlin gene promotes growth of liver cancer cells by inhibiting ERK activation and oncogene induced senescence. We showed that myoferlin expression does not promote proliferation of MRTF-null MEFs in the original submission (see Figure S5E). Additionally, we now point out that the RNAseq data show that myoferlin expression is not significantly affected in MRTF-null MEFs __(new text p23, lines 532-534). __

• It depends on where what target journal would be, but this is is a very well executes mechanistic study that doesn't really have an impact. Extending the discussion to human systems-or tissues where contractility is critical-could broaden the impact and applicability of the findings.*

We interpret this comment as indicating that our paper does not address the wider biological implications of our findings by extension to studies in tissue or tumour systems.

As outlined in our response to review 3, our study provides strong evidence that MRTF-SRF will be required for cell proliferation in settings where physical progression through cell cycle transitions requires high contractility, either owing to intrinsic factors or external physical constraints such as tissue stiffness, fibrosis, or tumour microenvironment.

Discussion now explicitly addresses potential roles for tissue stiffness (pp30§2 lines 717-718, and p32§1 725-727). However, we feel that resolution of this question is beyond the scope of the present paper.

• As above, the paper briefly mentions transformation, but it would be valuable to elaborate on whether MRTF-SRF acts as a barrier or enabler in tumorigenesis under different conditions. This I feel is the main weakness remaining - e.g. it would be fine with enabling different effects driven by other transcription events in emerging tumour cells (oncogenic in context of RAS, suppressive in context of p53) but I think the manuscript fails to be definitive on this points. Addressing this would make a much stronger and impactful study. I believe they have an impact peice of science that outlines how mechanical events impact cell fate decisions, but this is unlikely to be the driver - ie it facilitates cell fate decisions in context of tissue stiffness.*

We find it difficult to understand the precise points being made here.

However, transformation has long been known to bypass physical constraints on proliferation such as the requirement for adhesion. Moreover, MRTF-SRF activity is not necessarily required for proliferation of all transformed cells (Hampl et al, 2013; Medjkane et al, 2009; our unpublished data). The relation of our findings to transformation is thus an open question, which we are actively pursuing. Now noted in revised Discussion p32, lines 752-755.

MRTF-independent proliferation of tumor cells could reflect oncogenic signals substituting for MRTF-dependent ones (eg from focal adhesions), or from relief of cytoskeletal contraints on proliferation (adhesion independent proliferation). In contrast, in proliferation of DLC1-deleted cancer cells is dependent on suppression of oncogene-induced senescence by MRTF-SRF signalling (Hampl et al, 2013). These points were already made in Discussion p28, pp30-31.

Although our current work is focussed on cell transformation, we would respectfully suggest the in-depth resolution of this complex question is beyond the scope of the present paper.

See also response to (3) above.

*Reviewer #1 (Significance (Required)): *

*Overall *

This is a well-executed and insightful study that deepens our understanding of how cytoskeletal signals drive proliferation through MRTF-SRF. It broadens the role of this pathway beyond motility and offers new perspectives on mechanotransduction and cellular plasticity. If is weak in its demonstration of biological significance, but if the aim to to present a pure basic cell biology story it is good.

The vast majority of work with the SRF system has led to the common perception that its role is exclusively with cell motility and adhesive processes, not proliferation. The results presented in the paper, even if limited to cell culture models, are therefore novel.

Reviewer #2

(Evidence, reproducibility and clarity (Required)):

*In this manuscript, Nielsen and colleagues examine the impact of MRTF-A/B and SRF gene inactivation on cell proliferation. They performed an extensive body of work (using multiple cell types and multiple clones) to show that MRTF inactivation causes cell cycle arrest and senescence (mimicking the phenotype of SRF knockout cells) although the changes in the expression of various CDK inhibitors were cell-type specific. *

*Very interestingly, simultaneous inactivation of all three major CDK inhibitors failed to rescue MRTF knockout cells from their proliferation defect. Expectedly, MRTF knockout cells exhibited defects in actin cytoskeleton, adhesion, and contractility. Interestingly, hyperactivating Rho also failed to rescue MRTF knockout cells from proliferation defect. The main conclusion of the paper was derived from experiments which showed that inhibition of either ROCK or myosin caused wild-type cells to behave like MRTF knockout cells rather than demonstration of any molecular perturbation that could reverse the proliferation defect of MRTF knockout cells. *

While the experimental studies are thorough and rigorous, a vast majority of the core findings related to the loss-of-function of MRTF that are reported herein (i.e. defects in cell proliferation, elevation of CDK inhibitors, migration, actin cytoskeleton, contractility) are not conceptually new and have been previously reported in other cell systems by several investigators including this research group.

This is the first study showing that MRTF-SRF signalling is required for the proliferation of both primary and immortalised fibroblasts, and epithelial cells. We show that the MRTF-SRF non-proliferative state combines features of both classical senescence and reversible cell cycle exit / quiescence.

The vast majority of previous work with the SRF system has led to the common perception that its role is exclusively related to cell motility and adhesive processes and not proliferation (see Olson and Nordheim 2010). Where proliferation has been examined directly, both others and our own previous studies of the MRTFs in immune cells and cancer cells lines have revealed no direct role in proliferation (Schratt et al, 2001;Medjkane et al 2009; Maurice et al, 2024).

The results presented here are therefore novel.

In the reviewer's opinion, since the authors have not been able to identify a molecular strategy to reverse the proliferation phenotype of MRTF knockout cells, the underlying mechanisms of MRTF-dependent regulation of cell proliferation remain largely unanswered.

Indeed, our attempts to rescue the phenotype (knockouts of the CKIs, and overexpression of different downregulated factors) did not restore proliferation. We therefore now aim to attack the problem (i) through overexpression screens, and (ii) by identifying differences between MRTF-SRF dependent and -independent (eg transformed) cells. However, these are new projects that are beyond the scope of a revised paper.

• *

Other comments: Majority of the immunoblot data have not been quantified.

P16 data in Fig 1G vs Fig S1A are not similar (although the authors mention that the findings are similar)

We have addressed these issues by reorganisation and quantification the immunoblotting data as follows:

• Figure S1A has been moved to new Figure 1I, replacing the limited analysis shown in old Figure 1G. This more comprehensive, and displays data from all three WT and Mrtfab-/-
• Figure 1I data is quantified. Marker expression in each Mrtfab-/- pool is evaluated relative its mean expression in the three WT pools treated in parallel.
• A new Figure S1A shows mean marker expression across the three Mrtfab-/- pools, drawn from 5 independent analyses (not all markers included in each analysis). Different analyses of marker expression may exhibit variation, resulting from differences in handling, culture medium, plating density, relative confluence, etc. However, Mrtfab-/- cells exhibit markedly increased p27 and TLR2 expression, while expression of the other markers tested, including p16, consistently decreases.
• Spearman comparisons among the WT and Mrtfab-/- pools show that relative marker expression is indeed well correlated between the pools of each genotype. Note on quantitation added in Methods p10 lines 209-213.

Figure 1I moved from former Figure S1A, to replace former Figure 1G. New legend now includes quantitation, and reference to Spearman correlations, p44 lines 834-841.

New Figure S1A displays data from multiple independent experiments with all 3 Mrtfab-/- pools. New legend, p44 lines 997-1002.

Figure S1B legend notes correlation between relative marker expression in untreated WT and Mrtfab-/- cells, p44, lines 1005-1008.

Results text rewritten p17 lines 383-391; no reference to “similar”.

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

*This study aims to investigate a fundamental biological question of how an actin-regulated transcription machinery regulates cell proliferation and is therefore of broad significance. Strengths and limitations of this study are described above. *

Reviewer #3

*(Evidence, reproducibility and clarity (Required)): *

Summary

*The manuscript by Nielsen et al. (Treisman lab) entitled "MRTF-dependent cytoskeletal dynamics drive efficient cell cycle progression" investigates the effects on cell proliferation elicited upon cellular depletion of the transcription factors MRTF-A and MRTF-B. The MRTFs are actin-dependent co-factors of SRF, which direct the transcription of SRF target genes. The MRTF-SRF regulatory circuit defines both the functioning and the control of actin-driven cytoskeletal dynamics. *

*The work presented identifies essential molecular links that interconnect cytoskeleton-dependent cellular activities (cell-cell adhesion, cell-substrate contact, cell spreading) and cell proliferation. *

*General assessment on used methodology. *

*The presented comprehensive body of work is performed competently; it includes all relevant and necessary state-of-the-art technologies. *

• *

Reviewer #3 (Significance (Required)):

Advance

Previously published evidence by others (including the Treisman group) had indicated that SRF does not seem essential for the proliferation of some cell types (i. e., embryonic (stem) cells, activation-dependent immune cells, etc.). In regard to this, the authors discuss in the current manuscript: "Although further work is needed to elucidate the basis for these context-dependent dfferences, our data show that MRTF-SRF signalling is likely to play a more general role in proliferation than previously thought." The current manuscript already delineates this "general role": MRTF-SRF signalling impinges on cell proliferation whenever proliferative activities are dependent upon cytoskeletal dynamics.

We of course support the view that it is MRTF-SRF's role in cytoskeletal dynamics, especially contractility, that is a limiting factor for cell cycle progression in our cells; however, this may not be the cases or other cell types or settings, such adhesion-independent or transformed cells, and/or stiff tissue environments.

We have stated this view more strongly, modifying the abstract and discussion, and rewording the sentence quoted above.

The major point is that MRTF-SRF-dependent proliferation may be more common than previously thought, the field having focussed on its role in cytoskeletal dynamics rather than proliferation.

Abstract lines 48-49; Discussion p28, line 668-669; pp30-31, lines 713-714, 725-727. See also last para pp31/32, __added lines 752-755. __

*The work has implications for cancer biology. It offers new directions to investigate the regulation of proliferative activities of anchorage-independent tumor cells. **

Audience *

*The insights generated serve the wide interests of a large and diverse group of cell and tumor biologists. *

*Reviewers field of expertise (keywords). *

Cytoskeletal dynamics, transcriptional con*

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Referee #3

Evidence, reproducibility and clarity

Summary

The manuscript by Nielsen et al. (Treisman lab) entitled "MRTF-dependent cytoskeletal dynamics drive efficient cell cycle progression" investigates the effects on cell proliferation elicited upon cellular depletion of the transcription factors MRTF-A and MRTF-B. The MRTFs are actin-dependent co-factors of SRF, which direct the transcription of SRF target genes. The MRTF-SRF regulatory circuit defines both the functioning and the control of actin-driven cytoskeletal dynamics. The work presented identifies essential molecular links that interconnect cytoskeleton-dependent cellular activities (cell-cell adhesion, cell-substrate contact, cell spreading) and cell proliferation.

General assessment on used methodology.

The presented comprehensive body of work is performed competently; it includes all relevant and necessary state-of-the-art technologies.

Significance

Advance

Previously published evidence by others (including the Treisman group) had indicated that SRF does not seem essential for the proliferation of some cell types (i. e., embryonic (stem) cells, activation-dependent immune cells, etc.). In regard to this, the authors discuss in the current manuscript: "Although further work is needed to elucidate the basis for these context-dependent dfferences, our data show that MRTFSRF signalling is likely to play a more general role in proliferation than previously thought." The current manuscript already delineates this "general role": MRTF-SRF signalling impinges on cell proliferation whenever proliferative activities are dependent upon cytoskeletal dynamics.

The work has implications for cancer biology. It offers new directions to investigate the regulation of proliferative activities of anchorage-independent tumor cells.

Audience

The insights generated serve the wide interests of a large and diverse group of cell and tumor biologists.

Reviewers field of expertise (keywords).

Cytoskeletal dynamics, transcriptional control.

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Referee #2

Evidence, reproducibility and clarity

In this manuscript, Nielsen and colleagues examine the impact of MRTF-A/B and SRF gene inactivation on cell proliferation. They performed an extensive body of work (using multiple cell types and multiple clones) to show that MRTF inactivation causes cell cycle arrest and senescence (mimicking the phenotype of SRF knockout cells) although the changes in the expression of various CDK inhibitors were cell-type specific. Very interestingly, simultaneous inactivation of all three major CDK inhibitors failed to rescue MRTF knockout cells from their proliferation defect. Expectedly, MRTF knockout cells exhibited defects in actin cytoskeleton, adhesion, and contractility. Interestingly, hyperactivating Rho also failed to rescue MRTF knockout cells from proliferation defect. The main conclusion of the paper was derived from experiments which showed that inhibition of either ROCK or myosin caused wild-type cells to behave like MRTF knockout cells rather than demonstration of any molecular perturbation that could reverse the proliferation defect of MRTF knockout cells. While the experimental studies are thorough and rigorous, a vast majority of the core findings related to the loss-of-function of MRTF that are reported herein (i.e. defects in cell proliferation, elevation of CDK inhibitors, migration, actin cytoskeleton, contractility) are not conceptually new and have been previously reported in other cell systems by several investigators including this research group. In the reviewer's opinion, since the authors have not been able to identify a molecular strategy to reverse the proliferation phenotype of MRTF knockout cells, the underlying mechanisms of MRTF-dependent regulation of cell proliferation remain largely unanswered.

Other comments: Majority of the immunoblot data have not been quantified. P16 data in Fig 1G vs Fig S1A are not similar (although the authors mention that the findings are similar)

Significance

This study aims to investigate a fundamental biological question of how an actin-regulated transcription machinery regulates cell proliferation and is therefore of broad significance. Strengths and limitations of this study are described above.

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Referee #1

Evidence, reproducibility and clarity

The manuscript by Neilsen et al. presents a thorough and well-structured study showing that Myocardin-related transcription factors (MRTF-A/B), via MRTF-SRF, are essential for the proliferation of both primary and immortalized fibroblasts and epithelial cells. Using a combination of knockouts/rescue experiments, cytoskeletal analysis, and transcriptomics, the authors demonstrate that MRTF-SRF signalling controls actin dynamics and contractility-key drivers of cell cycle progression. Notably, they show that the proliferative arrest caused by MRTF loss is reversible, distinguishing it from classical senescence.

Major points

1. The link between MRTF-SRF activity, cytoskeletal organisation, and cell proliferation is clearly established. The fact that disrupting contractility phenocopies MRTF loss strengthens the case that the pathway acts through mechanical control.
2. The authors support their conclusions using multiple cell types (MEFs, primary fibroblasts, epithelial cells), a range of complementary assays (RNA-seq, traction force microscopy, adhesion/spreading), and genetic tools (CRISPR, inducible rescue).
3. The ability to restore proliferation by re-expressing MRTF-A argues against true senescence and instead suggests a quiescence-like state driven by cytoskeletal disruption.
4. This work particularly highlights how mechanical inputs feed into transcriptional programs to regulate proliferation, with implications for understanding anchorage-dependent growth.

Suggestions

1. While the authors argue convincingly against classical senescence, elevated SA-βGal and SASP expression suggest a more nuanced arrest state. It not really clear what this state is or is not, therefore a deeper discussion of possible hybrid or intermediate states would be helpful - maybe potential additional experiments to include or exclude potential explanations - e.g. how does it differ from G0 exit?
2. The transcriptomic data are strong, but the paper would benefit from zooming in on specific MRTF-SRF targets (e.g., actin isoforms, adhesion molecules) that directly link cytoskeletal regulation to cell cycle control.
3. It depends on where what target journal would be, but this is is a very well executes mechanistic study that doesn't really have an impact. Extending the discussion to human systems-or tissues where contractility is critical-could broaden the impact and applicability of the findings.
4. As above, the paper briefly mentions transformation, but it would be valuable to elaborate on whether MRTF-SRF acts as a barrier or enabler in tumorigenesis under different conditions. This I feel is the main weakness remaining - e.g. it would be fine with enabling different effects driven by other transcription events in emerging tumour cells (oncogenic in context of RAS, suppressive in context of p53) but I think the manuscript fails to be definitive on this points. Addressing this would make a much stronger and impactful study. I believe they have an impact peice of science that outlines how mechanical events impact cell fate decisions, but this is unlikely to be the driver - ie it facilitates cell fate decisions in context of tissue stiffness.

Significance

Overall

This is a well-executed and insightful study that deepens our understanding of how cytoskeletal signals drive proliferation through MRTF-SRF. It broadens the role of this pathway beyond motility and offers new perspectives on mechanotransduction and cellular plasticity. If is weak in its demonstration of biological significance, but if the aim to to present a pure basic cell biology story it is good.

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Reply to the reviewers

Proposed revision plan

Based on the below reviews, we propose the following revision plan. Briefly:

• We will remove the functional data on TGFβ signaling and mechanical loading/mechanosensing. We agree with the reviewers that we would need to generate additional histological and molecular data from conditional knockout mice, antibody and (ant)agonist treatments and the optogenetic model to determine their exact involvement in lining macrophage maturation. These experiments require significant time and other resources.
• We would therefore like to uncouple this question for a follow-on manuscript.We will re-focus the manuscript on the developmental data providing a molecular and cellular blueprint of lining macrophage development. This will include our data on CSF1 as a key signal. The novelty and relevance of our developmental data have been highlighted by all three reviewers, and they have also praised the rigor of these experiments and their interpretation. We thus believe that this re-focus will improve the manuscript message.
• To further enhance this, we are proposing to include additional data delineating the developmental dynamics of synovial fibroblasts. We have generated an in-depth single cell RNAsequencing dataset but did not include fibroblast-specific analyses in the original manuscript. This is not a change proposed by the reviewers, but we are proposing this because we believe this would be an impactful addition to a revised version of our study, providing data also on the maturation of the synovial (lining) macrophage niche.
• We will otherwise respond to all individual reviewer comments and implement the requested changes, unless technically not possible. Please find below detailed point-by-point answers.

Reviewer #1

Evidence, reproducibility and clarity

In their manuscript entitled "The synovial lining macrophage layer develops in the first weeks of life in a CSF1- and TGFβ-dependent but monocyte-independent process," the authors explore the developmental trajectory of synovial lining macrophages. They demonstrate that the formation of this specialized macrophage layer is age-dependent and governed by a distinct developmental program that proceeds independently of circulating monocytes. Through scRNA-Seq, the authors show that synovial lining macrophages originate locally from Aqp1⁺ macrophages and are marked by the expression of Csf1r, Tgfbr, and Piezo1. Notably, genetic ablation of each of these factors impaired the development of lining macrophages to varying degrees, suggesting differential contributions of CSF1, TGFβ, and PIEZO1 signaling pathways to their maturation and maintenance.

The manuscript is well written, and the data quality and representation is of a high standard. The authors have employed a sophisticated array of state-of-the-art mouse models and cutting-edge technologies to elucidate the developmental origin of synovial lining macrophages. Notably, the supporting scRNA-Seq datasets are of excellence and provide valuable insights that will likely be of significant interest to researchers in the field of immunology and joint biology. Accordingly, the experimental approach and interpretations regarding macrophage origin are well-founded and compelling. However, in the eye of the reviewer, the section addressing the underlying molecular mechanisms is a bit less convincing. This part of the study appears slightly underdeveloped, and some of the mechanistic claims lack sufficient experimental clarity. A more rigorous experimental investigation would be essential to reinforce the manuscript's conclusions, particularly concerning the data related to Tgfbr and Piezo1, where the current evidence appears insufficiently substantiated.

We thank the reviewer for their positive and constructive evaluation of our manuscript. We agree with them (and the other reviewers) that our functional data on the involvement of TGFβ signaling and mechanical loading/mechanosensing are comparably less convincing and substantiated than our developmental data. We are very grateful for their (and the other reviewers’) suggestions to provide more support for the involvement of these factors in lining macrophage development. However, we think that carrying this out to the same high standard will require substantial time and other resources. We have therefore decided to uncouple this from the developmental data and pursue this in follow-up work. We will re-focus the current manuscript on the developmental data. We have proposed to the editors to instead include additional data on synovial fibroblast development, to complement our macrophage data and also delineate the maturation of their niche, thereby providing a conclusive developmental atlas.

Major point:

1. The numbers of VSIG4⁺ macrophages appear either unaffected or only minimally altered in both Csf1rMerCreMer Tgfbr2floxed and Fcgr1Cre Piezo1floxed mouse models, respectively. This raises an important question: was the gene deletion efficiency sufficient in each model? Accordingly, the authors are encouraged to include quantitative data on gene deletion efficiency for both mouse models, as this information is critical for interpreting the observed phenotypic outcomes and validating the conclusions regarding gene function. Furthermore, to better assess the impact of Tgfbr2 and Piezo1 disruption, the authors should provide more comprehensive flow cytometry analyses and histological data for these mouse models. Given the apparent homogeneity of VSIG4⁺ macrophages (as shown by the authors themselves), bulk RNA-Seq of sorted Tgfbr2- and Piezo1-deficient VSIG4⁺ macrophages (or from TGFβ-treated animals) would offer valuable insights into both the effectiveness of gene deletion and the molecular pathways governed by TGFβ and PIEZO1 in lining macrophages.

As outlined above, we have decided to uncouple our functional data on TGFβ, Piezo1 and mechanical loading. The points raised here are all very valid, and we will implement your suggestions in our follow-up functional work focusing on signaling events regulating lining macrophage development. On the suggestion to perform bulk RNA sequencing for VSIG4+ macrophages: This is a good one in principle – although we will not be able to use this strategy where we want to assess the consequences of experimental treatments or genetic models on lining macrophage maturation, because acquisition of VSIG4 is a key maturation event that might be impaired in these conditions.

Minor points:

Consistent usage of Cx3cr1-GFP+ nomenclature (for instance: Fig. S1 legend "adult mouse synovial tissue, showing PDGFRα⁺ fibroblasts (yellow) and CX3CR1-GFP⁺ cells (cyan)." versus Fig. 1 legend "Automated spot detection highlights Cx3cr1-GFP⁺ macrophages)".

We will implement these changes.

Unclear Fig. 3 legend: "Representative immunofluorescence images of synovial tissue from Clec9aCre:Rosa26lsl-tdT mice at 3 weeks and in adulthood, showing and tdTomato (yellow) and stained for DAPI (blue), VSIG4 (cyan)" Check 'showing and tdTomato.'

We will implement these changes.

For greater clarity, it would have been helpful if the transcript names had been directly included within Figures 3C, S3A, and S3C.

We will implement these changes.

Page 24: "(Mki67CreERT2:Rosa26lsl-tdT)" Last bracket not superscript.

We will implement these changes.

Page 25: "we again leveraged our scRNAsequencing dataset" Missing punctuation.

We will implement these changes.

Page 27: Fig. 5C legend: " of synovial tissue of 1 week-old, 3 weeks-old and adult mice." Please specify and change to 'adult Csf1rΔFIRE/ΔFIRE mice'.

We will implement these changes.

Page 30: The outcome observed in the Acta1-rtTA:tetO-Cre:ChR2-V5fl mouse model appears to be inconclusive: "This approach resulted in an increased density of VSIG4+ and total (F4/80+) macrophages in the exposed leg of some 5 days-old pups, but others showed the opposite trend (Figure S5D)." This variability may reflect low efficiency of the model or other technical limitations (e.g. muscle contractions frequency or time point of analysis). Given this ambiguity, it is worth reconsidering whether the data are sufficiently robust to warrant inclusion. Should the authors choose to include these findings, further experimentation of appropriate depth and precision is required to allow a conclusive interpretation (either it increases the density of VSIG4+ macrophages or not). The same applies to the Yoda1-treated mice, for which additional data are needed to determine whether VSIG4⁺ macrophage density is truly affected.

We have decided to remove the data on the optogenetic mouse model and Yoda1 treatment and follow-on separately, implementing these suggestions, including proof of concept data for optogenetically induced muscle contractions.

Significance

General assessment: provide a summary of the strengths and limitations of the study. What are the strongest and most important aspects? What aspects of the study should be improved or could be developed? This is a well-designed study that uses cutting-edge methodologies to investigate the developmental trajectory of synovial lining macrophages under homeostatic conditions. The authors present robust experimental evidence and compelling interpretations concerning synovial macrophage origin, which are both well-substantiated and impactful. Nonetheless, from the reviewer's perspective, the section exploring the molecular mechanisms underlying macrophage differentiation is comparatively less convincing. This section appears somewhat underdeveloped, as some of the mechanistic claims lack sufficient depth and experimental rigor to fully substantiate the conclusions.

Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field: In contrast to earlier studies (PMID: 31391580, 32601335), the inclusion of fate-mapping experiments adds an important dimension, offering novel insight into the ontogeny of synovial macrophages. This expanded perspective may prove particularly valuable in advancing our understanding of joint immunology, especially regarding the local origins and lineage relationships of macrophage populations.

Furthermore, the authors present novel insights into the molecular pathways underlying the differentiation and development of synovial lining macrophages. By demonstrating previously unrecognized regulatory mechanisms, this work significantly deepens our understanding of the cellular and transcriptional programs that drive macrophage specialization within the joint microenvironment.

Place the work in the context of the existing literature (provide references, where appropriate): This study builds upon previous work characterizing the macrophage compartment in the joint (PMID: 31391580, 32601335), yet provides a substantially more comprehensive dataset that spans multiple developmental time points and data on the origin of this specialized macrophage subset.

State what audience might be interested in and influenced by the reported findings: Immunologist, clinicians

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. This study falls well within the scope of the reviewer's expertise in innate immunity.

Reviewer #2

Evidence, reproducibility and clarity

In the manuscript „The synovial lining macrophage layer develops in the first weeks of life in a CSF1- and TGFβ- dependent but monocyte-independent process", Magalhaes Pinto and colleagues carefully employ a wide range of technologies including single cell profiling, imaging and an exceptional combination of fate mapping models to characterize the ontogeny and development of lining macrophages in the joint, thus dissecting their maturation during postnatal development. Over the last decade, several landmark studies highlighted the imprinting of tissue-resident macrophages by a combination of ontogenetic and tissue-specific niche factors during development. So far, the ontogeny and the tissue niche factors governing the development and maturation of lining macrophages have not been described. Therefore, the results of this study offers insights on a small highly adapted macrophage population with relevance in many disease settings in the joint. Furthermore, the findings are nicely showcasing how macrophages are specializing to even very small tissue niches across development within one bigger anatomical compartment to serve dedicated functions within this niche.

This manuscript is beautifully written and highlights many novel, highly relevant findings on lining macrophage biology and the authors employ a wide range of different technologies to carefully dissect the postnatal development of lining macrophages.

In particular, the combination of scRNA-seq and fate mapping is providing a unique the link of transcriptional programs to ontogeny within the tissue niche. Furthermore, the integrative use of distinct fate mapping strategies, transgenic mouse lines, and treatment paradigms to elucidate key niche factors guiding the development and maturation of lining macrophages provides many interesting findings and data that are highly relevant to the field. I really enjoyed reading this manuscript.

Thank you for your complimentary and constructive assessment of our manuscript, and the detailed comments below, which are very helpful. Please find point-by-point responses below.

Major points:

The authors show dynamic regulation of VSIG4 in lining macrophages during development, therefore VSIG4 is maybe not an ideal choice for gating strategies to define lining macrophages or to show as a single markers in immunofluorescence (IF) stainings to demonstrate their abundance across development (even though it is clear that this is the reason why the F4/80 staining is shown next to it). To demonstrate the increase of lining macrophages during development in IF, it would be more helpful if the authors would show quantifications of all F4/80+ cells and additionally VSIG4+ as a proportion of F4/80+ cells (or VSIG4+ F4/80+ and all F4/80+ in a stacked bar plot). We agree with the assessment of VSIG4 not being ideal since this is a key marker of mature lining macrophages only.

We will provide these additional analyses.

In Figure 1C, the authors nicely demonstrate that the lining macrophages get closer in their distance across development to build the epithelial-like macrophage structure along the adult lining. Is the close proximity between lining macrophages already fully "matured" at 3 weeks of age and comparable to adults? Please quantify the distance in adult linings.

We will provide data for adult joints.

Can the authors explain how the grouping was performed between the analyzed human fetal joints? It is not clear why the cut was chosen between the groups at 16/17 weeks of age. Maybe it would be also beneficial if the authors would consider not grouping these samples but rather show the specific quantifications for each samples individually and estimate via linear regression the expansion over time across human development. Furthermore, can the authors give additional information about the distancing of lining macrophages in the human fetal samples, it would be great to see if they follow the same dynamics as in mouse. Maybe comparison to human juvenile/adult joints would also add on to substantiate the findings in human samples (if possible).

We will show samples ungrouped and perform linear regression analysis as suggested.

The scRNA-seq analysis leaves several questions open and some conclusions and workflows cannot be easily followed.

We appreciate this comment and the complexity of the data, and will implement the below recommendations, and clarify the issues raised.

It is not clear how and especially why the signature genes to define macrophages vs. monocytes were chosen. Especially as the signature genes for monocytes would not include patrolling monocytes and the macrophage signature genes seem to be highly regulated during development, see also Apoe expression in NB vs. adult in Figure S2e. Why did the authors not take classical markers such as Itgam, Fcgr1a, Csf1r?

Can dendritic cell signatures be excluded? Cluster 11 and 12 show indeed some DC markers, are these really macrophages?

The authors provide several figure panels showing TOP marker genes or key marker genes for the identified clusters, however it is not clear if these are TOP DE genes or if the genes were hand chosen. Somehow, the authors give the impression that the clusters were chosen and labeled not based on DE genes, but more on existing literature that previously reported these macrophage populations. DE gene lists for all annotated cell types and macrophage clusters need to be provided within the manuscript.

The authors claim that Clusters 1 and 4 are "developing" macrophages. How is this defined? Why are these developing cells compared to other clusters? And why are these clusters later on not considered as progenitors of Aqp1 macrophages and Vsig4 macrophages? Why are Aqp1+ macrophages not labeled as developing when they are later on in the manuscript shown as potential intermediate progenitors of lining macrophages?

Furthermore, it is again confusing that markers are used throughout Figure 2 which are labeled as "key marker genes" for a population and then later on they are claimed to be regulated during development within this population, see for example Figure 2D and 2H.

It is appreciated that the authors distinguished cycling clusters such as 8, 9, and 10 based on their cycling gene signature. Here it would be very exciting to see a cell cycle analysis across all clusters and time points to see when exactly the cells are expanding during development; this would also substantiate the data later shown for the Mki67-CreERT2 mouse model.

Can the authors identify certain gene modules during development of lining macrophages (and/or their progenitors) which are associated with certain functions (e.g. GO terms, GSEA enrichment)?

To determine the actual presence of the identified macrophage clusters from the scRNA-seq as macrophage populations in the joint, the authors should perform IF or FACS for key markers. Especially, Aqp1+ macrophages should be shown in the developing joint.

We will provide additional data, but would also like to reference a study by collaborators currently in revision at Immunity, which characterizes the Aqp1+ population in detail. We are hoping to have a doi available during our revision process.

The authors used a wide range of fate mapping models, which is quite unique and highly appreciated. The obtained results and the conclusions made from the models raise a couple of questions: Whereas contribution of HSC-derived/monocyte-derived macrophages to the lining compartment seems to be minor, there is still labeling across different models. Various aspects would need to be clarified.

We will clarify these data throughout as per below suggestions.

For example, the authors employ Ms4a3-Cre as a tracing model for GMP-derived monocytes, however all quantifications of the labeling efficiency are not normalized to the labeling in monocytes or another highly recombined cell population. This should be shown, similar to the other fate mapping models (Figure 3 F-I).

Labelling efficacy for Ms4a3-Cre is near complete for GMP-derived monocytes (and neutrophils) with the Rosa-lsl-tdT (aka Ai14) reporter we have used (see also PMID: 31491389 and doi: 10.1101/2024.12.03.626330); but we will include normalized data as requested.

Please show Ms4a3 expression across clusters across time points, to exclude expression in fetal-derived clusters.

We will include this in the revised supplementary information, but there is indeed very little at birth (in line with the original report for other tissues PMID: 31491389).

In line with the question raised above, if the authors can exclude a development of the Egfr1+ and Clec4n+ developing macrophages into Aqp1+ macrophages and subsequently into Vsig4 lining macrophages, the obtained data from the Ms4a3-Cre model highly suggests a correlative labeling across these clusters what could implicate a relation. However, the authors do not discuss throughout the manuscript the role of these developing macrophages. It is highly encouraged to include this into the manuscript and it would be of high relevance to understand lining macrophage development.

This is an interesting point and we agree it deserves consideration in the revised manuscript. Indeed, our trajectory analyses do not predict differentiation of the Egfr1+ and Clec4n+ developing macrophages into Aqp1+ macrophages, and hence, ultimately lining macrophages. Conversely, Aqp1+ cells might also convert into Egfr1+ and Clec4n+ developing macrophages. We will elaborate on this more in the revised manuscript.

The authors conclude from the pseudo bulk transcriptomic profiling of the different macrophage clusters that TdT+ and TdT- macrophages do not differ in their gene expression profile and that this is due to niche imprinting rather than origin imprinting. Even though the data supports that conclusion, the authors should verify if inkling cells early during development also show this similar gene expression profile and gene expression should be compared at the different developmental time points. Tissue niche imprinting is happening within the niche during development, most likely in a stepwise progress, and therefore there should be differences in the beginning.

This is another important point that we will address in the revised manuscript by performing additional differential gene expression analyses at the different developmental time points, including the earliest stages, as suggested.

The trajectorial analysis using different pseudotime pipelines is very interesting and nicely points out the potential role of Aqp1 macrophages as intermediates of Vsig4 lining macrophages. From my point of view, all trajectories seem to suggest that Egfr1 developing macrophages and Clec4n developing macrophages might differentiate into Aqp1 macrophages, however the authors are not exploring this further and the role of both developing macrophage clusters is not further discussed (see also comments above).

We will address and discuss this in the revised manuscript.

How was the starting point of the trajectorial analyses defined and is it the same for each pipeline used?

We will clarify this in the revised manuscript.

Are there potentially two trajectories? It looks like there is one in the beginning of postnatal life and a second one appearing from the monocyte-compartment later in life. If this is true, that would rather speak for a dual ontogeny of Vsig4+ macrophages, wouldn't it?

We will discuss this in the revised manuscript.

A heatmap (transcriptional shift) of trajectories between more clusters should be shown at least for Cluster 0,1,2, and 3. It is not sufficient to demonstrate this only between two clusters.

We will add these analyses during revision.

To show the similarity between Aqp1 macrophages and proliferating macrophage clusters, the authors should remove the cycling signature and compare these clusters to show that the cycling cells might be Aqp1 macrophages or earlier developing macrophage progenitors aka Clec4n or Egfr1 macrophages.

We will address this in the revised manuscript.

The conclusions made from the Mki67-CreERT2 data are a bit difficult to understand, whereas all progenitors (monocyte progenitors and macrophage progenitors will proliferate at the neonatal time point and no conclusions can be made if the cells expand in the niche. The authors should employ Confetti mice or other models (Ubow mice) to analyze clonal expansion in the niche.

We agree that interpretation of the Mki67-CreERT2 data is complicated by labeling of other cells, and notably, labeling observed in BM-derived cells. We will highlight this better in the revised manuscript. We have tried using Ubow mice to address this issue, but the recombination efficacy we yielded was too low to draw conclusions. We will address this during revision.

All predicted cell-cell interactions between macrophages and fibroblasts should be provided in a supplementary table. Are the interactions shown in Figure 5 chosen interactions or the TOP predicted ones? Whereas the authors show different numbers of interactions, it is most likely hand-picked and therefore biased.

We will provide a full list of all predicted interactions in the revised supplementary material in addition to a list of the full differential gene expression analysis.

The authors further aim to dissect the factors involved in the developmental niche imprinting of lining macrophages. Even though it is highly appreciated that the authors used so many experimental setups to show the reliance of lining macrophages on Csf1 and TGF-beta as well as mechanosensation, the wide range of models the different methods used and selected developmental time points make it very difficult to really interpret the data. The authors should carefully choose time points and methods (either FACS analysis across all models or IF across all, or both). Often deletion efficiencies for transgenic models and proof of concept that the inhibitors and agonists are working in the treatment paradigm are not provided. For example, Csf1rMer-iCre-Mer Tgfbr2fl/fl mice are used but no deletion efficiency is shown or different time points of analysis, maybe the macrophages are not properly targeted in the set up.

We have decided to uncouple our experimental data on Tgfb, Piezo1 and mechanosensing/mechanical loading, but are taking this into consideration for revision. In many cases, we have in fact performed flow cytometry and imaging analyses, and agree, we should be showing this consistently.

The authors have shown the role of Csf1 and Tgfbr2 only for lining macrophages, is this specific in the joint to this population of are subliming macrophages affected in a similar manner.

We will include data on sublining macrophages in the revised figure (for CSF1; Tgfb data will be uncoupled from this current manuscript).

Can the authors confirm their results in CSF1R-FIRE mice with anti-Csf1 injections or in Csf1op/op mice?

We will expand our discussion of the Csf1 findings, and will consider including anti-CSF1 data during revision. Phenotypes on other Csf1(r) deficient mice are published, if not with the same developmental resolution as our time course in Csf1rFIRE knockout mice and with simpler readouts. Csf1op/op mice are indeed deficient in synovial lining macrophages, from 2 days of age onwards (PMID: 8050349), and lining macrophages are also absent from 2-weeks-old and adult Csf1r-/- mice (PMID: 11756160).

The setup in Figure S5G is very interesting to test the role of movement and mechanical load on the joint, however, there is basically no data on the model provided showing the efficiency of the induced optogenetic muscle contractions, and only one time point is shown.

Data on mechanical loading will be uncoupled from the current manuscript and substantiated in a separate follow-up.

The results regarding the role of Piezo1 and mechanosensation vary a lot. Could it be that analyses were done too early or that actually proper weight load on the joint must be applied for the maturation of the macrophages? The authors should test this to.

We will uncouple these data from the current manuscript during revision. However, this is a possibility that we have discussed. In fact, the most appropriate experimental approach to address the involvement of mechanical loading, onset of walking and specifically, weight bearing would be a loss-of-function approach (i.e. paralysis at the newborn stage), for which we unfortunately could not obtain ethics approval from the UK Home Office.

The Rolipram experiment is shown in Figure S5G, but is not described in the result section. It only appears at some point in the discussion part. The authors should move it to results or remove it from the manuscript.

We will incorporate these data with the revised section on developing synovial macrophage populations.

Minor points:

Please reference the Figure panels in numeric order throughout the text.

We will change this where not the case.

Figure 2a and 2b are a bit out of the storyline, it is not obvious why this is shown here and maybe it would be good to move it to the supplements. Gating strategy is also not used for scRNA-seq. Therefore, it would better fit to the later analysis of joint macrophages across different transgenic mouse models and treatment paradigms. The gating strategies are changing across different experiments throughout the figures, it would be nice to have a similar gating strategy for all experiments, see also Figure 3 where the defining markers for joint macrophages are changing between models.

We will revise Figures 2, 3 and the related supplementary figures.

A lot of figure panels have very small labeling that is basically unreadable. Axes at FACS plots for example. Sometimes, it is even impossible to distinguish cluster labels especially when they have similar colors.

We will revise this, thanks for pointing it out.

In the text on page 14, many markers are named which are specifically regulated during development in lining macrophages, but these factors are not labeled anywhere in the volcano plot. It would be good to showcase at least some of these named genes in the figure panel, e.g. Trem2.

We will do this for revision.

Figure 2F and Figure S2F are really nicely showing the percentage of cells per cluster in each analyzed biological sample. Maybe the authors could additionally consider to show a stacked bar plot with the mean percentage of cells per cluster and how the clusters are distributed across time points?

We will include this in the revised manuscript.

Figure 3A: IF for adult lining macrophages and the quantification are missing.

This will be included in the revised version.

Significance

This manuscript highlights novel, highly relevant findings on lining macrophage biology and the authors employ a wide range of different technologies to carefully dissect the postnatal development of lining macrophages. Furthermore, this study showcases in a very elegant and detailed way the adaptation of macrophage progenitors to a highly specific anatomical tissue niche.

The manuscript is of high interest to basic scientists focussing on macrophage biology and immune cell development and clinicians and clinician scientists focussing on joint diseases such as RA.

Therefore the manuscript is of interest to a wide community working in immunology.

Reviewer #3

Summary:

Magalhaes Pinto, Malengier-Devlies, and co-authors investigated the developmental origins and maturation of synovial (lining and sublining) macrophages across embryonic, newborn, and postnatal stages in mouse. The authors used multiple transgenic reporter lines, lineage tracing, scRNA-seq, 2D confocal and 3D lightsheet imaging, and perturbations to delineate the macrophage states and ontogeny. They propose a model in which the majority of the joint lining macrophages has a fetal (EMP-derived) origin and a small proportion has a definitive HSC-derived monocyte origin, which both seed and mature within the synovial space in the postnatal period in the first 3 weeks of life. Using cell-cell communication analysis on their scRNA-seq data, they identified Fgf2, Csf1, and Tgfb as candidate signaling pathways that support (lining) macrophage development and maturation. Functional experiments indicate that the process is CSF1 and TGFb-dependent and also partly dependent on mechanosensing through Piezo1.

The key conclusions on the composition of the synovial macrophages are convincing based on the presented results, and are carefully phrased. The study is very comprehensive, yet the description and organization of the results of the different mouse models could be altered to improve the storyline. Several refinements in data presentation, formulation, and minor validation experiments would further improve the clarity of the story, as well as summary recaps of the major findings throughout the text.

We thank this reviewer for their detailed review. We will be implementing the requested changes wherever technically feasible.

Major comments:

Generally, the story could be more streamlined by introducing earlier reporter lines and lineage-origin logic. Clearly state which reporter/CreERT2 lines and acrosses are used. It was unclear in Figure 2 that cells of the cross of the Cx3cr1-GFP and Ms4a3Cre:Rosa26lsl-tdT reporter lines were used for the scRNA-seq. The principle that there are fetal-derived and bone marrow (GMP)-derived monocytes and macrophages doesn't need to be "hidden" until Figure 3. For example, also the imaging of Ms4a3Cre could be introduced before the scRNA-seq.

We will revise the structure and order of the manuscript during revision.

Figure 1 could benefit from a cartoon visualizing the anatomy of the knee joint. The terms "sublining" and "synovium" are now a bit unclear, as it appears that sometimes the synovium is indicated as sublining and vice versa. Additionally, a schematic developmental timeline could be added to indicate the parallels between mouse and human development (fetal and postnatal development in mouse versus gestational age in human). Also, the various waves of hematopoiesis could be indicated in this timeline, which would be particularly helpful for Figure 3 for the lineage-tracing readouts. Lastly, the authors could end the manuscript (a new Figure 6) with a general cartoon summarizing all the results presented.

We will include illustrations as suggested.

Figure 1 could be rearranged: first introduce the markers CX3CR1 and VSIG4 (Figure 1D) and then present the quantifications (Figure 1B/E). Where possible, co-visualization CX3CR1-GFP and VSIG4 on tissue sections to strengthen the claims on the relationship between these 2 markers. Tying the scRNA-seq insights (Figure 2) to the imaging would be elegant. Moreover, it would be informative to represent the CX3CR1+ and VSIG4+ macrophages as a percentage of F4/80+ macrophages (Figure 1B/E). Similarly, for the flow cytometry data in Figure 2, the relationship between the markers CX3CR1 and VSIG4 on macrophages could be more clearly displayed and discussed.

Thanks for this remark. We will endeavor to show co-localization and analysis of both markers wherever possible. However, where we did not use Cx3cr1gfp mice, co-staining was limited by antibody choice.

The 3D imaging of the joint is a nice addition to the manuscript, as it provides more context to the anatomical structure; however, while the text suggests several newborn joints were imaged, Figure 1F visualizes (again) the knee joint. Could other joints also be represented by 3D imaging? If the knee joint is the only joint available for imaging, and previous confocal imaging focused specifically on the meniscus in the knee joint, could the meniscus also be highlighted in the lightsheet imaging?

Apologies if this was not clear from the original manuscript text, but we have only imaged the knee joint in 3D. We will clarify this during revision and consider inclusion of additional imaging data.

Clarification is requested regarding the imaging quantification representation. The M&M section under "Statistical analysis and reproducibility" states that individual data points are displayed, and bars represent the mean. However, some of the Figure legends (e.g., Figures 1B and S1C) specify that each dot corresponds to an individual mouse, with quantification based on 2-3 sections per mouse. While this appears to be a very reasonable representation of the data, does this mean that for each dot, the mean value from the 2-3 sections per mouse was calculated and plotted?

We will clarify this.

It is not clear how the differential expression analysis was performed on the Vsig4+ cells. Please specify if Cluster 0 was used for analysis, or all Vsig4-expressing cells? Not all cells in Cluster 0 have Vsig4+ expression. The authors described the expression dynamics of Aqp1 as intriguing, but lack a reasoning on why this is interesting.

We will revise this section.

Figure S3E: In line with the previous comment, can the authors justify that the tdTomato+/- comparisons are not biased by scRNA-seq dropout (scRNA-seq is zero-inflated, so some tdTomato- cells could be false negatives), and provide methodological details (thresholds, ambient RNA correction, etc.) to support this?

We will clarify this and include additional representations of the tdTomato transcript data.

Although the sex-related differences in macrophage composition and the absence of differential expression are interesting, they distract from the manuscript's main messages. Moreover, the Discussion does not elaborate on how these observations relate to joint (disease) biology. Consider removing this section or integrating it clearly into the relevant biological context.

We will remove this section as suggested.

CreERT2 transgenic lines are often not 100% efficient in recombination, also depending on whether tamoxifen or 4-OHT is used. Could the authors report the percentage of tdTomato+ cells in the joints and compare them to the recombination efficiencies in the monocytes/microglia under the same tamoxifen or 4-OHT conditions? This would help clarify how the interpret the macrophage labeling %'s.

We will report labelling efficacies and/or show normalized data in the revised manuscript.

Could the authors draw parallels between the observations in the mouse knee joint macrophage populations and literature on other joints in mouse and the knee joint in human (for example, as described in Alivernini et al., 2020 and in the very recent Raut et al., 2025)?

We will include a section on this in the revised manuscript.

Minor comments:

In general, the authors should clarify in the Results what each marker used for imaging, flow cytometry, or in the mouse reporter lines delineates. For example, mention that F4/80 is a marker for tissue-resident macrophages (correct?) in immunofluorescence, that IBA1 is a marker for macrophages on human tissue sections (Figure S1), and PDPN is GP38 (Figure S2 - align usage of marker reference across main text and figures).

We will implement this request.

For clarity in the microscopy representation, the single channels should be represented in a grey scale.

We will revise image presentation.

Figure S1B: Is CX3CR1 also restricted to the lining macrophages in human? Could a co-staining with IBA1 be performed to strengthen the species similarities?

To our knowledge, there is no antibody available that works for imaging of human CX3CR1. Moreover, CX3CR1 is only limited to the lining population in adult joints, in fetal and newborn (mouse) joints, all macrophages express this receptor, as do fetal progenitors to macrophages. However, Alivernini and colleagues have reported that TREM2high macrophages are the human counterpart of the mouse CX3CR1+ lining population (PMID: 32601335).

Adipocyte diameter quantification: Avoid plotting individual adipocytes from 2 mice without per-mouse visualization. Instead, report the mean adipocyte diameter per mouse and plot those means.

We will implement this change.

A little typo was spotted in the "Statistical analysis and reproducibility" section: it is Dunn's, not Bunn's multiple-comparison correction.

Thanks for spotting this.

Figure 2A: The gating strategy for the CX3CR1-GFP cells is missing.

We will provide this in the revised manuscript or supplementary material.

Improve the visualization of some plots. For example, Figure 2F is hard to read because of the big dot size. The dots seem to add no information to the graph and could be removed. Additionally, for comparing the clusters across the different time points, one could project the cells from the other time points in grey in the background.

We will revise the presentation of these data.

Figure S2: The dotplot is more informative than the heatmap, consider removing the heatmap.

We will do that.

Figure 3A: If technically feasible, image and visualize both the GFP and tdTomato expression. It would be informative to see the Cx3cr1+ and Ms4a3-derived cells in the same specimen.

We will thrive to show this in the revised manuscript.

Figure 3C: Highlight that tdTomato expression is visualized here.

We will do that.

Figure 3G,F: The authors should place the schematics and graphs next to each other, so the data points can be more easily compared.

We aim to do this in the revised manuscript.

Figure 4B: Which co-staining was performed for the immunofluorescence to quantify the % of tdTomato+ cells?

We co-stained for F4/80 and assessed localization in the lining or sublining. This will be clarified in the revised Figure legend.

Figure 4C: The trajectory analysis appears to have an arrow pointing from the Ccr2+ macrophages to the Ly6c+ monocytes. Please verify this directionality, as its seems against the known biology.

This will be addressed during revision.

Figure 5 mentions that the Csfr1 levels were reduced in a tissue-specific manner, but it is unclear how this tissue specificity was achieved.

We apologize for this misunderstanding. Csfr1FIRE mice are not tissue-specific knockouts, but they are more specific than global knockout mice, since only a (myeloid-specific) enhancer is affected. We will clarify this in the relevant section.

For the TGFb perturbations (Tgfbr2 KO and systemic TGFb depletion): did the authors validate reduced TGFb pathway activity in the macrophages, for example, reduced pSMAD2/3 levels? This would validate the effectiveness of the perturbations. This is an important point, and assessing signaling events downstream of TGFb is a very good suggestion.

As per above comment, we have decided to uncouple the functional data with exception of CSF1 from the revised version of the current manuscript, but we will be taking this into account for substantiating our functional data in follow-up work.

Figure 5F could benefit from a timeline of the treatment.

As for the previous point raised, we will be taking this into account for follow-up work on the uncoupled functional data.

The Methods mention that Gene Ontology analysis was performed on the single-cell data, but the results are not plotted in a figure. It would be informative to include this GO/pathway analysis in the appropriate figure(s).

We will include this in the revised (supplementary) information.

Significance:

This work provides a high temporal-resolution and "spatial" resolution reference map of the ontogeny and maturation of the synovial lining macrophages in the knee joint. It complements existing literature that demonstrated the presence of tissue-resident macrophages in the synovial space and lining (Culemann, et al., 2019 and others) by charting the embryonic-to-postnatal emergence of lining and sublining subsets. In particular, this mouse work identified some key signaling pathways in shaping this tissue compartment. This dataset serves as a robust, steady-state reference for joint pathology and can be implemented with human studies on disease biology of the knee joint (e.g., Alivernini et al., 2020; Raut et al., 2025). Insights into the exact developmental origins, mechanisms contributing to diverse or seemingly similar cell types, and distinct maturation processes are crucial to understanding disease biology, in which developmental processes can be hijacked/reactivated.

These findings will interest researchers in joint disease biology (osteoarthritis and immune-mediated arthritides such as RA and psoriasis), macrophage development (tissue-resident vs monocyte-derived lineages), the bone/joint microenvironment, and joint mechanobiology.

The reviewer's expertise is in developmental biology, mesoderm, bone biology, hematopoiesis, and monocyte/macrophage biology in disease

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Referee #3

Evidence, reproducibility and clarity

Summary:

Magalhaes Pinto, Malengier-Devlies, and co-authors investigated the developmental origins and maturation of synovial (lining and sublining) macrophages across embryonic, newborn, and postnatal stages in mouse. The authors used multiple transgenic reporter lines, lineage tracing, scRNA-seq, 2D confocal and 3D lightsheet imaging, and perturbations to delineate the macrophage states and ontogeny. They propose a model in which the majority of the joint lining macrophages has a fetal (EMP-derived) origin and a small proportion has a definitive HSC-derived monocyte origin, which both seed and mature within the synovial space in the postnatal period in the first 3 weeks of life. Using cell-cell communication analysis on their scRNA-seq data, they identified Fgf2, Csf1, and Tgfb as candidate signaling pathways that support (lining) macrophage development and maturation. Functional experiments indicate that the process is CSF1 and TGFb-dependent and also partly dependent on mechanosensing through Piezo1. The key conclusions on the composition of the synovial macrophages are convincing based on the presented results, and are carefully phrased. The study is very comprehensive, yet the description and organization of the results of the different mouse models could be altered to improve the storyline. Several refinements in data presentation, formulation, and minor validation experiments would further improve the clarity of the story, as well as summary recaps of the major findings throughout the text.

Major comments:

1. Generally, the story could be more streamlined by introducing earlier reporter lines and lineage-origin logic. Clearly state which reporter/CreERT2 lines and acrosses are used. It was unclear in Figure 2 that cells of the cross of the Cx3cr1-GFP and Ms4a3Cre:Rosa26lsl-tdT reporter lines were used for the scRNA-seq. The principle that there are fetal-derived and bone marrow (GMP)-derived monocytes and macrophages doesn't need to be "hidden" until Figure 3. For example, also the imaging of Ms4a3Cre could be introduced before the scRNA-seq.
2. Figure 1 could benefit from a cartoon visualizing the anatomy of the knee joint. The terms "sublining" and "synovium" are now a bit unclear, as it appears that sometimes the synovium is indicated as sublining and vice versa. Additionally, a schematic developmental timeline could be added to indicate the parallels between mouse and human development (fetal and postnatal development in mouse versus gestational age in human). Also, the various waves of hematopoiesis could be indicated in this timeline, which would be particularly helpful for Figure 3 for the lineage-tracing readouts. Lastly, the authors could end the manuscript (a new Figure 6) with a general cartoon summarizing all the results presented.
3. Figure 1 could be rearranged: first introduce the markers CX3CR1 and VSIG4 (Figure 1D) and then present the quantifications (Figure 1B/E). Where possible, co-visualization CX3CR1-GFP and VSIG4 on tissue sections to strengthen the claims on the relationship between these 2 markers. Tying the scRNA-seq insights (Figure 2) to the imaging would be elegant. Moreover, it would be informative to represent the CX3CR1+ and VSIG4+ macrophages as a percentage of F4/80+ macrophages (Figure 1B/E). Similarly, for the flow cytometry data in Figure 2, the relationship between the markers CX3CR1 and VSIG4 on macrophages could be more clearly displayed and discussed.
4. The 3D imaging of the joint is a nice addition to the manuscript, as it provides more context to the anatomical structure; however, while the text suggests several newborn joints were imaged, Figure 1F visualizes (again) the knee joint. Could other joints also be represented by 3D imaging? If the knee joint is the only joint available for imaging, and previous confocal imaging focused specifically on the meniscus in the knee joint, could the meniscus also be highlighted in the lightsheet imaging?
5. Clarification is requested regarding the imaging quantification representation. The M&M section under "Statistical analysis and reproducibility" states that individual data points are displayed, and bars represent the mean. However, some of the Figure legends (e.g., Figures 1B and S1C) specify that each dot corresponds to an individual mouse, with quantification based on 2-3 sections per mouse. While this appears to be a very reasonable representation of the data, does this mean that for each dot, the mean value from the 2-3 sections per mouse was calculated and plotted?
6. It is not clear how the differential expression analysis was performed on the Vsig4+ cells. Please specify if Cluster 0 was used for analysis, or all Vsig4-expressing cells? Not all cells in Cluster 0 have Vsig4+ expression. The authors described the expression dynamics of Aqp1 as intriguing, but lack a reasoning on why this is interesting.
7. Figure S3E: In line with the previous comment, can the authors justify that the tdTomato+/- comparisons are not biased by scRNA-seq dropout (scRNA-seq is zero-inflated, so some tdTomato- cells could be false negatives), and provide methodological details (thresholds, ambient RNA correction, etc.) to support this?
8. Although the sex-related differences in macrophage composition and the absence of differential expression are interesting, they distract from the manuscript's main messages. Moreover, the Discussion does not elaborate on how these observations relate to joint (disease) biology. Consider removing this section or integrating it clearly into the relevant biological context.
9. CreERT2 transgenic lines are often not 100% efficient in recombination, also depending on whether tamoxifen or 4-OHT is used. Could the authors report the percentage of tdTomato+ cells in the joints and compare them to the recombination efficiencies in the monocytes/microglia under the same tamoxifen or 4-OHT conditions? This would help clarify how the interpret the macrophage labeling %'s.
10. Could the authors draw parallels between the observations in the mouse knee joint macrophage populations and literature on other joints in mouse and the knee joint in human (for example, as described in Alivernini et al., 2020 and in the very recent Raut et al., 2025)?

Minor comments:

1. In general, the authors should clarify in the Results what each marker used for imaging, flow cytometry, or in the mouse reporter lines delineates. For example, mention that F4/80 is a marker for tissue-resident macrophages (correct?) in immunofluorescence, that IBA1 is a marker for macrophages on human tissue sections (Figure S1), and PDPN is GP38 (Figure S2 - align usage of marker reference across main text and figures).
2. For clarity in the microscopy representation, the single channels should be represented in a grey scale.
3. Figure S1B: Is CX3CR1 also restricted to the lining macrophages in human? Could a co-staining with IBA1 be performed to strengthen the species similarities?
4. Adipocyte diameter quantification: Avoid plotting individual adipocytes from 2 mice without per-mouse visualization. Instead, report the mean adipocyte diameter per mouse and plot those means.
5. A little typo was spotted in the "Statistical analysis and reproducibility" section: it is Dunn's, not Bunn's multiple-comparison correction.
6. Figure 2A: The gating strategy for the CX3CR1-GFP cells is missing.
7. Improve the visualization of some plots. For example, Figure 2F is hard to read because of the big dot size. The dots seem to add no information to the graph and could be removed. Additionally, for comparing the clusters across the different time points, one could project the cells from the other time points in grey in the background.
8. Figure S2: The dotplot is more informative than the heatmap, consider removing the heatmap.
9. Figure 3A: If technically feasible, image and visualize both the GFP and tdTomato expression. It would be informative to see the Cx3cr1+ and Ms4a3-derived cells in the same specimen.
10. Figure 3C: Highlight that tdTomato expression is visualized here.
11. Figure 3G,F: The authors should place the schematics and graphs next to each other, so the data points can be more easily compared.
12. Figure 4B: Which co-staining was performed for the immunofluorescence to quantify the % of tdTomato+ cells?
13. Figure 4C: The trajectory analysis appears to have an arrow pointing from the Ccr2+ macrophages to the Ly6c+ monocytes. Please verify this directionality, as its seems against the known biology.
14. Figure 5 mentions that the Csfr1 levels were reduced in a tissue-specific manner, but it is unclear how this tissue specificity was achieved.
15. For the TGFb perturbations (Tgfbr2 KO and systemic TGFb depletion): did the authors validate reduced TGFb pathway activity in the macrophages, for example, reduced pSMAD2/3 levels? This would validate the effectiveness of the perturbations.
16. Figure 5F could benefit from a timeline of the treatment.
17. The Methods mention that Gene Ontology analysis was performed on the single-cell data, but the results are not plotted in a figure. It would be informative to include this GO/pathway analysis in the appropriate figure(s).

Significance

This work provides a high temporal-resolution and "spatial" resolution reference map of the ontogeny and maturation of the synovial lining macrophages in the knee joint. It complements existing literature that demonstrated the presence of tissue-resident macrophages in the synovial space and lining (Culemann, et al., 2019 and others) by charting the embryonic-to-postnatal emergence of lining and sublining subsets. In particular, this mouse work identified some key signaling pathways in shaping this tissue compartment. This dataset serves as a robust, steady-state reference for joint pathology and can be implemented with human studies on disease biology of the knee joint (e.g., Alivernini et al., 2020; Raut et al., 2025). Insights into the exact developmental origins, mechanisms contributing to diverse or seemingly similar cell types, and distinct maturation processes are crucial to understanding disease biology, in which developmental processes can be hijacked/reactivated.

These findings will interest researchers in joint disease biology (osteoarthritis and immune-mediated arthritides such as RA and psoriasis), macrophage development (tissue-resident vs monocyte-derived lineages), the bone/joint microenvironment, and joint mechanobiology.

The reviewer's expertise is in developmental biology, mesoderm, bone biology, hematopoiesis, and monocyte/macrophage biology in disease

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

In the manuscript „The synovial lining macrophage layer develops in the first weeks of life in a CSF1- and TGFβ- dependent but monocyte-independent process", Magalhaes Pinto and colleagues carefully employ a wide range of technologies including single cell profiling, imaging and an exceptional combination of fate mapping models to characterize the ontogeny and development of lining macrophages in the joint, thus dissecting their maturation during postnatal development. Over the last decade, several landmark studies highlighted the imprinting of tissue-resident macrophages by a combination of ontogenetic and tissue-specific niche factors during development. So far, the ontogeny and the tissue niche factors governing the development and maturation of lining macrophages have not been described. Therefore, the results of this study offers insights on a small highly adapted macrophage population with relevance in many disease settings in the joint. Furthermore, the findings are nicely showcasing how macrophages are specializing to even very small tissue niches across development within one bigger anatomical compartment to serve dedicated functions within this niche.

This manuscript is beautifully written and highlights many novel, highly relevant findings on lining macrophage biology and the authors employ a wide range of different technologies to carefully dissect the postnatal development of lining macrophages.

In particular, the combination of scRNA-seq and fate mapping is providing a unique the link of transcriptional programs to ontogeny within the tissue niche. Furthermore, the integrative use of distinct fate mapping strategies, transgenic mouse lines, and treatment paradigms to elucidate key niche factors guiding the development and maturation of lining macrophages provides many interesting findings and data that are highly relevant to the field. I really enjoyed reading this manuscript.

Major points:

1) The authors show dynamic regulation of VSIG4 in lining macrophages during development, therefore VSIG4 is maybe not an ideal choice for gating strategies to define lining macrophages or to show as a single markers in immunofluorescence (IF) stainings to demonstrate their abundance across development (even though it is clear that this is the reason why the F4/80 staining is shown next to it). To demonstrate the increase of lining macrophages during development in IF, it would be more helpful if the authors would show quantifications of all F4/80+ cells and additionally VSIG4+ as a proportion of F4/80+ cells (or VSIG4+ F4/80+ and all F4/80+ in a stacked bar plot).

2) In Figure 1C, the authors nicely demonstrate that the lining macrophages get closer in their distance across development to build the epithelial-like macrophage structure along the adult lining. Is the close proximity between lining macrophages already fully "matured" at 3 weeks of age and comparable to adults? Please quantify the distance in adult linings.

3) Can the authors explain how the grouping was performed between the analyzed human fetal joints? It is not clear why the cut was chosen between the groups at 16/17 weeks of age. Maybe it would be also beneficial if the authors would consider not grouping these samples but rather show the specific quantifications for each samples individually and estimate via linear regression the expansion over time across human development. Furthermore, can the authors give additional information about the distancing of lining macrophages in the human fetal samples, it would be great to see if they follow the same dynamics as in mouse. Maybe comparison to human juvenile/adult joints would also add on to substantiate the findings in human samples (if possible).

4) The scRNA-seq analysis leaves several questions open and some conclusions and workflows cannot be easily followed.

a. It is not clear how and especially why the signature genes to define macrophages vs. monocytes were chosen. Especially as the signature genes for monocytes would not include patrolling monocytes and the macrophage signature genes seem to be highly regulated during development, see also Apoe expression in NB vs. adult in Figure S2e. Why did the authors not take classical markers such as Itgam, Fcgr1a, Csf1r?

b. Can dendritic cell signatures be excluded? Cluster 11 and 12 show indeed some DC markers, are these really macrophages?

c. The authors provide several figure panels showing TOP marker genes or key marker genes for the identified clusters, however it is not clear if these are TOP DE genes or if the genes were hand chosen. Somehow, the authors give the impression that the clusters were chosen and labeled not based on DE genes, but more on existing literature that previously reported these macrophage populations. DE gene lists for all annotated cell types and macrophage clusters need to be provided within the manuscript.

d. The authors claim that Clusters 1 and 4 are "developing" macrophages. How is this defined? Why are these developing cells compared to other clusters? And why are these clusters later on not considered as progenitors of Aqp1 macrophages and Vsig4 macrophages? Why are Aqp1+ macrophages not labeled as developing when they are later on in the manuscript shown as potential intermediate progenitors of lining macrophages?

e. Furthermore, it is again confusing that markers are used throughout Figure 2 which are labeled as "key marker genes" for a population and then later on they are claimed to be regulated during development within this population, see for example Figure 2D and 2H.

f. It is appreciated that the authors distinguished cycling clusters such as 8, 9, and 10 based on their cycling gene signature. Here it would be very exciting to see a cell cycle analysis across all clusters and time points to see when exactly the cells are expanding during development; this would also substantiate the data later shown for the Mki67-CreERT2 mouse model.

g. Can the authors identify certain gene modules during development of lining macrophages (and/or their progenitors) which are associated with certain functions (e.g. GO terms, GSEA enrichment)?

5) To determine the actual presence of the identified macrophage clusters from the scRNA-seq as macrophage populations in the joint, the authors should perform IF or FACS for key markers. Especially, Aqp1+ macrophages should be shown in the developing joint.

6) The authors used a wide range of fate mapping models, which is quite unique and highly appreciated. The obtained results and the conclusions made from the models raise a couple of questions: Whereas contribution of HSC-derived/monocyte-derived macrophages to the lining compartment seems to be minor, there is still labeling across different models. Various aspects would need to be clarified.

a. For example, the authors employ Ms4a3-Cre as a tracing model for GMP-derived monocytes, however all quantifications of the labeling efficiency are not normalized to the labeling in monocytes or another highly recombined cell population. This should be shown, similar to the other fate mapping models (Figure 3 F-I).

b. Please show Ms4a3 expression across clusters across time points, to exclude expression in fetal-derived clusters.

c. In line with the question raised above, if the authors can exclude a development of the Egfr1+ and Clec4n+ developing macrophages into Aqp1+ macrophages and subsequently into Vsig4 lining macrophages, the obtained data from the Ms4a3-Cre model highly suggests a correlative labeling across these clusters what could implicate a relation. However, the authors do not discuss throughout the manuscript the role of these developing macrophages. It is highly encouraged to include this into the manuscript and it would be of high relevance to understand lining macrophage development.

d. The authors conclude from the pseudo bulk transcriptomic profiling of the different macrophage clusters that TdT+ and TdT- macrophages do not differ in their gene expression profile and that this is due to niche imprinting rather than origin imprinting. Even though the data supports that conclusion, the authors should verify if inkling cells early during development also show this similar gene expression profile and gene expression should be compared at the different developmental time points. Tissue niche imprinting is happening within the niche during development, most likely in a stepwise progress, and therefore there should be differences in the beginning.

7) The trajectorial analysis using different pseudotime pipelines is very interesting and nicely points out the potential role of Aqp1 macrophages as intermediates of Vsig4 lining macrophages. From my point of view, all trajectories seem to suggest that Egfr1 developing macrophages and Clec4n developing macrophages might differentiate into Aqp1 macrophages, however the authors are not exploring this further and the role of both developing macrophage clusters is not further discussed (see also comments above).

8) How was the starting point of the trajectorial analyses defined and is it the same for each pipeline used?

9) Are there potentially two trajectories? It looks like there is one in the beginning of postnatal life and a second one appearing from the monocyte-compartment later in life. If this is true, that would rather speak for a dual ontogeny of Vsig4+ macrophages, wouldn't it?

10) A heatmap (transcriptional shift) of trajectories between more clusters should be shown at least for Cluster 0,1,2, and 3. It is not sufficient to demonstrate this only between two clusters.

11) To show the similarity between Aqp1 macrophages and proliferating macrophage clusters, the authors should remove the cycling signature and compare these clusters to show that the cycling cells might be Aqp1 macrophages or earlier developing macrophage progenitors aka Clec4n or Egfr1 macrophages.

12) The conclusions made from the Mki67-CreERT2 data are a bit difficult to understand, whereas all progenitors (monocyte progenitors and macrophage progenitors will proliferate at the neonatal time point and no conclusions can be made if the cells expand in the niche. The authors should employ Confetti mice or other models (Ubow mice) to analyze clonal expansion in the niche.

13) All predicted cell-cell interactions between macrophages and fibroblasts should be provided in a supplementary table. Are the interactions shown in Figure 5 chosen interactions or the TOP predicted ones? Whereas the authors show different numbers of interactions, it is most likely hand-picked and therefore biased.

14) The authors further aim to dissect the factors involved in the developmental niche imprinting of lining macrophages. Even though it is highly appreciated that the authors used so many experimental setups to show the reliance of lining macrophages on Csf1 and TGF-beta as well as mechanosensation, the wide range of models the different methods used and selected developmental time points make it very difficult to really interpret the data. The authors should carefully choose time points and methods (either FACS analysis across all models or IF across all, or both). Often deletion efficiencies for transgenic models and proof of concept that the inhibitors and agonists are working in the treatment paradigm are not provided. For example, Csf1rMer-iCre-Mer Tgfbr2fl/fl mice are used but no deletion efficiency is shown or different time points of analysis, maybe the macrophages are not properly targeted in the set up.

15) The authors have shown the role of Csf1 and Tgfbr2 only for lining macrophages, is this specific in the joint to this population of are subliming macrophages affected in a similar manner.

16) Can the authors confirm their results in CSF1R-FIRE mice with anti-Csf1 injections or in Csf1op/op mice?

17) The setup in Figure S5G is very interesting to test the role of movement and mechanical load on the joint, however, there is basically no data on the model provided showing the efficiency of the induced optogenetic muscle contractions, and only one time point is shown.

18) The results regarding the role of Piezo1 and mechanosensation vary a lot. Could it be that analyses were done too early or that actually proper weight load on the joint must be applied for the maturation of the macrophages? The authors should test this to

19) The Rolipram experiment is shown in Figure S5G, but is not described in the result section. It only appears at some point in the discussion part. The authors should move it to results or remove it from the manuscript.

Minor points:

1) Please reference the Figure panels in numeric order throughout the text.

2) Figure 2a and 2b are a bit out of the storyline, it is not obvious why this is shown here and maybe it would be good to move it to the supplements. Gating strategy is also not used for scRNA-seq. Therefore, it would better fit to the later analysis of joint macrophages across different transgenic mouse models and treatment paradigms. The gating strategies are changing across different experiments throughout the figures, it would be nice to have a similar gating strategy for all experiments, see also Figure 3 where the defining markers for joint macrophages are changing between models.

3) A lot of figure panels have very small labeling that is basically unreadable. Axes at FACS plots for example. Sometimes, it is even impossible to distinguish cluster labels especially when they have similar colors.

4) In the text on page 14, many markers are named which are specifically regulated during development in lining macrophages, but these factors are not labeled anywhere in the volcano plot. It would be good to showcase at least some of these named genes in the figure panel, e.g. Trem2.

5) Figure 2F and Figure S2F are really nicely showing the percentage of cells per cluster in each analyzed biological sample. Maybe the authors could additionally consider to show a stacked bar plot with the mean percentage of cells per cluster and how the clusters are distributed across time points?

6) Figure 3A: IF for adult lining macrophages and the quantification are missing

Significance

This manuscript highlights novel, highly relevant findings on lining macrophage biology and the authors employ a wide range of different technologies to carefully dissect the postnatal development of lining macrophages. Furthermore, this study showcases in a very elegant and detailed way the adaptation of macrophage progenitors to a highly specific anatomical tissue niche.

The manuscript is of high interest to basic scientists focussing on macrophage biology and immune cell development and clinicians and clinician scientists focussing on joint diseases such as RA

Therefore the manuscript is of interest to a wide community working in immunology.

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Referee #1

Evidence, reproducibility and clarity

In their manuscript entitled "The synovial lining macrophage layer develops in the first weeks of life in a CSF1- and TGFβ-dependent but monocyte-independent process," the authors explore the developmental trajectory of synovial lining macrophages. They demonstrate that the formation of this specialized macrophage layer is age-dependent and governed by a distinct developmental program that proceeds independently of circulating monocytes. Through scRNA-Seq, the authors show that synovial lining macrophages originate locally from Aqp1⁺ macrophages and are marked by the expression of Csf1r, Tgfbr, and Piezo1. Notably, genetic ablation of each of these factors impaired the development of lining macrophages to varying degrees, suggesting differential contributions of CSF1, TGFβ, and PIEZO1 signaling pathways to their maturation and maintenance.

The manuscript is well written, and the data quality and representation is of a high standard. The authors have employed a sophisticated array of state-of-the-art mouse models and cutting-edge technologies to elucidate the developmental origin of synovial lining macrophages. Notably, the supporting scRNA-Seq datasets are of excellence and provide valuable insights that will likely be of significant interest to researchers in the field of immunology and joint biology. Accordingly, the experimental approach and interpretations regarding macrophage origin are well-founded and compelling. However, in the eye of the reviewer, the section addressing the underlying molecular mechanisms is a bit less convincing. This part of the study appears slightly underdeveloped, and some of the mechanistic claims lack sufficient experimental clarity. A more rigorous experimental investigation would be essential to reinforce the manuscript's conclusions, particularly concerning the data related to Tgfbr and Piezo1, where the current evidence appears insufficiently substantiated.

Major point:

• The numbers of VSIG4⁺ macrophages appear either unaffected or only minimally altered in both Csf1rMerCreMer Tgfbr2floxed and Fcgr1Cre Piezo1floxed mouse models, respectively. This raises an important question: was the gene deletion efficiency sufficient in each model? Accordingly, the authors are encouraged to include quantitative data on gene deletion efficiency for both mouse models, as this information is critical for interpreting the observed phenotypic outcomes and validating the conclusions regarding gene function. Furthermore, to better assess the impact of Tgfbr2 and Piezo1 disruption, the authors should provide more comprehensive flow cytometry analyses and histological data for these mouse models. Given the apparent homogeneity of VSIG4⁺ macrophages (as shown by the authors themselves), bulk RNA-Seq of sorted Tgfbr2- and Piezo1-deficient VSIG4⁺ macrophages (or from TGFβ-treated animals) would offer valuable insights into both the effectiveness of gene deletion and the molecular pathways governed by TGFβ and PIEZO1 in lining macrophages.

Minor points:

• Consistent usage of Cx3cr1-GFP+ nomenclature (for instance: Fig. S1 legend "adult mouse synovial tissue, showing PDGFRα⁺ fibroblasts (yellow) and CX3CR1-GFP⁺ cells (cyan)." versus Fig. 1 legend "Automated spot detection highlights Cx3cr1-GFP⁺ macrophages)"
• Unclear Fig. 3 legend: "Representative immunofluorescence images of synovial tissue from Clec9aCre:Rosa26lsl-tdT mice at 3 weeks and in adulthood, showing and tdTomato (yellow) and stained for DAPI (blue), VSIG4 (cyan)" Check 'showing and tdTomato.'
• For greater clarity, it would have been helpful if the transcript names had been directly included within Figures 3C, S3A, and S3C.
• Page 24: "(Mki67CreERT2:Rosa26lsl-tdT)" Last bracket not superscript.
• Page 25: "we again leveraged our scRNAsequencing dataset" Missing punctuation.
• Page 27: Fig. 5C legend: " of synovial tissue of 1 week-old, 3 weeks-old and adult mice." Please specify and change to 'adult Csf1rΔFIRE/ΔFIRE mice'.
• Page 30: The outcome observed in the Acta1-rtTA:tetO-Cre:ChR2-V5fl mouse model appears to be inconclusive: "This approach resulted in an increased density of VSIG4+ and total (F4/80+) macrophages in the exposed leg of some 5 days-old pups, but others showed the opposite trend (Figure S5D)." This variability may reflect low efficiency of the model or other technical limitations (e.g. muscle contractions frequency or time point of analysis). Given this ambiguity, it is worth reconsidering whether the data are sufficiently robust to warrant inclusion. Should the authors choose to include these findings, further experimentation of appropriate depth and precision is required to allow a conclusive interpretation (either it increases the density of VSIG4+ macrophages or not). The same applies to the Yoda1-treated mice, for which additional data are needed to determine whether VSIG4⁺ macrophage density is truly affected.

Significance

• General assessment: provide a summary of the strengths and limitations of the study. What are the strongest and most important aspects? What aspects of the study should be improved or could be developed?

This is a well-designed study that uses cutting-edge methodologies to investigate the developmental trajectory of synovial lining macrophages under homeostatic conditions. The authors present robust experimental evidence and compelling interpretations concerning synovial macrophage origin, which are both well-substantiated and impactful. Nonetheless, from the reviewer's perspective, the section exploring the molecular mechanisms underlying macrophage differentiation is comparatively less convincing. This section appears somewhat underdeveloped, as some of the mechanistic claims lack sufficient depth and experimental rigor to fully substantiate the conclusions. - Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field:

In contrast to earlier studies (PMID: 31391580, 32601335), the inclusion of fate-mapping experiments adds an important dimension, offering novel insight into the ontogeny of synovial macrophages. This expanded perspective may prove particularly valuable in advancing our understanding of joint immunology, especially regarding the local origins and lineage relationships of macrophage populations. Furthermore, the authors present novel insights into the molecular pathways underlying the differentiation and development of synovial lining macrophages. By demonstrating previously unrecognized regulatory mechanisms, this work significantly deepens our understanding of the cellular and transcriptional programs that drive macrophage specialization within the joint microenvironment. -Place the work in the context of the existing literature (provide references, where appropriate):

This study builds upon previous work characterizing the macrophage compartment in the joint (PMID: 31391580, 32601335), yet provides a substantially more comprehensive dataset that spans multiple developmental time points and data on the origin of this specialized macrophage subset. - State what audience might be interested in and influenced by the reported findings:

Immunologist, clinicians - 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.

This study falls well within the scope of the reviewer's expertise in innate immunity.

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Reply to the reviewers

Reply to the reviewers

We would like to thank the reviewers for their overall positive evaluations of our manuscript and for their invaluable suggestions that will allow us to reinforce our conclusions. We acknowledge that there is some work to be done and are ready to address most of the reviewers' comments as detailed in our replies below.

Reviewer #1

1. The findings that mmDicer is proviral in bat cells relies exclusively on the observation that the depletion of Dicer in M. myotis cells leads to a reduced accumulation of SFV and SINV at the RNA and protein levels (figure 2). Heterologous expression of mmDicer in HEK 293T NoDice doesn't lead to an increase permissivity to viral infections (figure 1) and the accumulation of Dicer foci is only observed in M. myotis cells but not when mmDicer is expressed in HEK 293 NoDice cells (figure 6). Given that the key finding of this manuscript relies on these knockdown experiments, the authors should ensure that the impact on viral infections is due to the specific silencing of mmDicer and not caused by off-target effects of their siRNA-mediated approach. The authors designed a siRNA pool to efficiently knock-down mmDicer. They should validate their findings by using individual Dicer siRNA and verify whether the decrease SFV/SINV accumulation is observed with at least two individual siRNAs targeting Dicer. It would also strengthen their findings if they could show a complementation experiment in which a mmDicer (designed to not be affected by the siRNA-mediated silencing) is introduced exogenously in Dicer-depleted cells and show that it rescues the observed decrease in viral accumulation to demonstrate that the proviral role is strictly dependent on mmDicer. Alternatively, the authors could consider a CRISPR/Cas9 genome editing approach to knockout Dicer in bat cells to test whether this proviral effect is confirmed.

Reply: We agree with this reviewer that it is important to provide evidence for the specificity of the knock-down and to rule out any off-target effect of the siRNAs. This is the reason for using the siTool technology, which relies on the use of a pool of 30 siRNAs that are transfected at a final concentration of 3 nM. This means that each individual siRNA in the pool is at a concentration of 0.1 nM, so the possibility of off-target effect is largely avoided and the efficiency of silencing is boosted by the cooperative activity of many siRNAs (see https://www.sitoolsbiotech.com/documents/sipools/siPOOLBrochure2019_Web.pdf for more details). This being said, we agree that it would be better to confirm that the observed effect can be recapitulated using a single siRNA and that a complementation experiment would definitely strengthen our findings. For this reason, we will test two individual siRNAs targeting the 3' UTR of mmDicer, which will allow us to complement the knock-down by transfecting a cDNA construct. Regarding the CRISPR/Cas9 genome editing approach, we will give it a try, but Dicer is notoriously difficult to knock-out, so we cannot be sure that this will be successful.

Figure 2: the authors knock-downed Dicer in M. myotis nasal epithelial cells and carried out infections with SINV-GFP and SFV. The authors conclude that Dicer is proviral as its depletion causes a decrease in SINV-GFP and SFV accumulation. While this conclusion is supported by the decrease levels of viral RNA and protein levels upon Dicer depletion (figure 2D, 2E, 2G), the effect on the viral titers is non-significant for both viruses (Figure 2C and 2F) based on the statistical analysis. This reviewer appreciates that the titers are lower upon Dicer knockdown, which support the authors' findings at the viral RNA and protein levels. However, as these results are central to the core message of the manuscript, the authors should provide evidence that this proviral effect observed is statistically significant on viral titers by perhaps providing additional repeats and/or comment on this observation.

Reply: Indeed, we agree that even if the effect of Dicer knockdown results in a lowering of the viral titer, it would be better to have a statistically significant effect. We will repeat the experiment to increase the number of replicates and the power of the statistical test.

a) *In figure 4 and 5, the authors nicely show that mmDicer accumulate to cytoplasmic foci in M. myotis cells upon infection with SFV and SINV and these foci co-localise with double-stranded RNA. The authors used a commercial polyclonal antibody against Dicer (A301-937A, Bethyl according to the Material and Methods section) which is specific to human Dicer to carry out their immunostaining in bat cells. The authors should provide evidence that this antibody indeed recognises/crossreacts with mmDicer as well and that the staining shown is indeed specific to mmDicer localisation especially because the heterologous expression of HA-tagged version of mmDicer in HEK 293T NoDice cells did not show this accumulation of cytoplasmic foci. The authors should verify the specificity of their mmDicer immunostaining by performing the same labelling in bat cells in which Dicer is knock-downed (or knock out) by individual and validated siRNA against mmDicer. The decrease signal of bat Dicer staining using the anti-human Dicer antibody would indicate specificity. *

Reply: the reviewer is correct in its assertion and it is important to provide evidence that the protein that is detected by the anti-human Dicer antibody in bat cells is indeed Dicer. We will perform the suggested experiment and do an immunostaining using the Dicer antibody in bat cells upon Dicer knockdown.

b) Another complementary approach would be to test their Dicer staining between HEK NoDice cells (no Dicer present) versus NoDice complemented with either mmDicer or human Dicer constructs, which would then indicate how much the anti-human Dicer antibody recognises bat Dicer.

Reply: this complementary approach should yield even cleaner result than the previous one as there will be no expression of Dicer at all in the HEK NoDice cells. Therefore, we should be able to measure the increase of signal in the IF upon expression of either human or bat Dicer. We will perform this experiment together with the other one suggested above. In addition, since the constructs are tagged, we might be able to do a double-staining and verify the colocalization of the two signals.

c) In addition, the authors should overexpress HA-tagged mmDicer in M. myotis nasal epithelial cells and test whether HA-mmDicer accumulate into foci upon infection using an anti-HA immunostaining. This would confirm that these accumulation into foci indeed is specific to mmDicer but also would reinforce the authors' findings that host factors within bat cells are important for this formation into foci since mmDicer expression in HEK 293T No Dice cells didn't show this phenotype upon infection (figure 6). OPTIONAL: it would be interesting to overexpress HA-tagged human Dicer into M. myotis nasal epithelial cells as well to then test using anti-HA staining whether human Dicer in presence of host factors from the bat can accumulate into cytoplasmic foci or not upon viral infection.

Reply: we could perform the suggested experiment, but we might face the issue that transfected cells might mount an immune response, which makes them resistant to the infection. We have observed indeed that we needed to use a higher MOI to infect cells after they have been transfected. Since we will have controls in place, this might not be too much of a problem, but we will have to keep it in mind. Alternatively, we will perform a lentiviral transduction of the cells.

This reviewer appreciates that this might be judged as beyond the scope of this study since it is focused on the role of Dicer in M. myotis. However, the observation that mmDicer accumulates into foci containing as well viral dsRNA is very interesting and it would significantly improve the manuscript if the authors would provide further indications that this phenotype is related to the lack of antiviral activity of mmDicer compared to what has been previously shown in other bat species (P.alecto and T. brasiliensis). In other words, is this accumulation of mmDicer into foci responsible for its different impact on virus infection? It would therefore be insightful to compare Dicer localisation upon infection in M. myotis versus P.alecto and/or T. brasiliensis bat cells in which Dicer was shown to be antiviral and test whether this accumulation in foci is only observed in bat cells in which Dicer is proviral (M. myotis) but not in the other bat cells in which Dicer is antiviral (P.alecto and/or T. brasiliensis).

Reply: this is something that we have been wondering about and we have therefore started to look for the cell lines that have been described in the two published studies. While it proved difficult to find the PaKi cells from P. alecto bats, which is not commercially available, we have obtained the Tblu cells from T. brasiliensis and will look at Dicer localization in this model. However, we have to pay attention to the fact that the published data reported a contribution of RNAi in this cell line upon SARS-CoV-2 infection and that we will be using SINV. In addition, we do not know yet whether the anti-Dicer antibody will cross react with the T. brasiliensis Dicer protein.

OPTIONAL: Given the difference between the provial role of mmDicer compared to the antiviral activity of Dicer in cells from P.alecto and T. brasiliensis bat cells, it would strengthen the authors' findings. if additional experiments would be conducted in parallel using M. myotis, P.alecto and/or T. brasiliensis cells. Notably knocking down Dicer in both M. myotis, P.alecto and/or T. brasiliensis cells, compare the impact on viral infections with SINV, SFV, VSV and correlate any observed difference in phenotype with putative variations in the formation of foci.

Reply: it would indeed be really nice to be able to do the Dicer knockdown experiment in several bat cell lines and to correlate the phenotype with the formation of foci. This experiment might take a long time and we are not sure to be able to realize it in a reasonable amount of time. It could however be the subject of another manuscript further down the line.

*Minor comments *

• • Figure 2I: The authors performed a knockdown of Dicer in M. myotis nasal epithelial cells and monitor the impact on VSV-GFP infection. They found that knocking down Dicer leads to an increase in GFP protein and RNA levels suggesting an antiviral role of Dicer while, in contrast, no effect is observed on the production of infectious particles (figure 2H). On the western blot there is only a slight/weak increase of GFP protein level observed upon Dicer knockdown. Yet, the quantification of the band intensity shows a 4-fold increase relative to tubulin and compared to cells treated with siRNA control. This 4-fold increase seems exaggerated given the low increase in the intensity shown on the blot. This discrepancy is most likely due to the lower intensity of tubulin in the western blot analysis of siDicer-treated cells compared to siNeg-treated cells. The authors should reload their western blot with equal amount of protein extract loaded to ensure that the results shown on the western blot are in line with the quantification.*

Reply: the signal quantification for this experiment was done across several replicates, but we agree that the observed effect seems exaggerated when compared to the signal seen on the blot. We observed important variations between replicates, but we will make sure that this was not due to a problem in the analysis and reload the western blot if needed.

• • Figure 3D: the authors mention that in both HEK293T cells and M. myotis nasal epithelial cells infected with SINV-GFP, there was an enrichment of 22-nucleotides (nt) paired positive and negative sense reads that overlapped with a 2-nt overhang, typical of Dicer cleavage. In Figure 3D, the data shows indeed that the duplexes are enriched for reads of 22-nt but it is unclear how this analysis reveals a 3' 2nt overhang within these duplexes. Can the authors clarify this point and if the data provided in that particular analysis indeed doesn't allow to detect these overhangs, please rephrase accordingly or provide additional analysis to support that point. *

Reply: In Figure 3D, the graphs show the probability of pairing of all 22 nucleotides sequence mapping either to the plus or the minus strand of the viral RNA. Thus, for each sequence mapping to the plus strand, the number of sequences mapping to the minus strand with a full or partial overall is counted. A corresponding probability of pairing and Z score is calculated for each number of overlapping nucleotides (for more information on the calculation see Antoniewski (2014) Computing siRNA and piRNA Overlap Signatures. In Animal Endo-SiRNAs: Methods and Protocols, Werner A (ed) pp 135-146. New York, NY: Springer). The Z score peaks for an overlap of 20 nt in both HEK293T and M. myotis nasal epithelial cells infected with SINV. This means that there is a higher probability of two 22 nt sequence to pair along 20 nt, and thus that there are two unpaired nucleotides at the extremities of the duplexes. This higher Z score at 20 nt is not seen in VSV-infected cells. We will rephrase the text in the manuscript to make this point clearer.

• • Typo: page 5, line 152: the authors mention that Dicer knock down had an antiviral effect against VSV-GFP infection at the RNA and protein levels. However, the data in Figure 2I and 2J show an increase in both GFP RNA and proteins levels upon knockdown of Dicer. Although this data suggests that Dicer is antiviral against VSV, the knockdown of Dicer itself is not antiviral but rather proviral/increase virus accumulation. Please rephrase this sentence to avoid confusions. *

Reply: thank you for spotting this typo. We have corrected it accordingly.

Reviewer #2.

1. Figure 1 relies on transduction of cells and antibiotic selection to obtain mmDicer-expressing cells. Although we would expect that every cell expresses the construct of interest, this is not always the case, depending on the cell type and toxicity of the construct. As the constructs are tagged, I suggest that the authors use flow cytometry to measure expression levels in a single cell manner. While doing so, they can infect with SINV-GFP and correlate GFP signal with construct expression in each cell, providing a more accurate measurement of mmDicer effect on viral infection. Alternatively, the authors could use live microscopy, as done in Fig 2, to obtain similar data.

Reply: the reviewer is correct that we did not go for monoclonal selection of our mmDicer-expressing cells and therefore that there could be some cell-to-cell variation in expression. However, we have done immunostaining of Dicer in these cells and did not see drastic differences in expression, so we do not think this should impact SINV-GFP expression in a major way. We will provide these images and a quantification of the Dicer signal as a supplementary figure.

For Fig 1C and 1F, it would be great to have growth curves with two different MOIs, instead of a single time point, to ensure that a putative antiviral effect is not missed. Same goes for Fig 2C, especially when the authors document quite a big defect on GFP expression (a proxy for SINV infection) when Dicer is knocked down (Fig 2B). There may be a bigger difference in titers at earlier time points. This matter runs throughout the manuscript. I do not suggest that the authors should provide growth curves every time viral titers are measured, but it is still worth doing it for the 2-3 key experiments of the paper.

Reply: we will perform growth curves of virus infection for the key experiments in the manuscript as suggested. We already have done kinetic measurements of GFP accumulation at different MOIs, which we can provide as supplementary data, but we agree with the reviewer that GFP signal should not been used as the only proxy for the infection and that measuring viral titers by plaque assay is important as well.

Figure 4, could the authors provide a proof that the Dicer antibody is specific in the bat context? This can be done by staining Dicer in bat cells knocked down for Dicer and infected with SINV. The apparition of foci upon anti-Dicer antibody staining should be abbrogated or severely impaired by the knock-down.

Reply: see our reply to point 3 of Reviewer 1.

Fig 5C, please provide a quantification of the images.

Reply: these microscopy images have not been quantified because they have been obtained with an epifluorescence microscope. Indeed, the Pearson correlation coefficient can only be obtained using a confocal microscope. In fact, we have tried to use a confocal microscope to take pictures of these FISH images, but the SINV gRNA signal was too weak or the dots too small to be properly visualized. Furthermore, there is a very large difference in signal intensity between HEK293T and M. myotis cells, making it difficult to define a signal threshold compatible for both cell lines.

l.263, when comparing this work with the recent publications on bat antiviral RNAi, the authors could also provide the percentage identity between Dicers from different species.

Reply: this is a valid point, we have looked at the percentage identity between Dicer proteins from different bat species but we did not include this in our manuscript. We will provide this analysis in the revised version together with a comparison of Dicer from other mammals as a reference point.

Reviewer 3.

1. • Without direct comparison to the other bat species Dicers (especially where RNAi activity has been suggested as antiviral in previous publications) there is little in this paper that can be concluded about global aspects of bat dicer/RNAi.*

Reply: see our reply to point 4 of Reviewer 1. We are planning to look at least in Tblu cells whether there is also a relocalization of Dicer upon SINV infection. So far, we could not obtain PaKi cells, but we are still looking and should we get those, we will test them as well.

*Minor *

What rules out that the mmDicer re-localization observed in the immortalized mm nasal epithelial is due simply to greater expression levels over the NoDice cells heterologously expressing mmDicer?

Reply: we will provide an immunoblot to show the level of Dicer expression between HEK NoDice + mmDicer and M. myotis nasal epithelial cells as suggested below to address this point.

• Although partially addressed in the text stating the generally long half-life of miRNAs, it seems the simplest explanation for this observation is due to some activity of a shorter-lived miRNA is required for optimal alphavirus replication is the mm nasal epithelial cells. *

Reply: this is an interesting hypothesis that would prove difficult to test in a reasonable amount of time. We thank the reviewer and will mention this possibility in the discussion of the revised manuscript.

*Suggestions that could enhance the magnitude of conclusions that can be drawn from this work. *

*Major *

• • Making NoDice cells expressing other bat species Dicers, including those with claims that RNAi is antiviral, would address how universal these current observations are to bats/cell lines.*

Reply: this could be an alternative to the use of P. alecto or T. brasiliensis cell lines that we have mentioned above. We will try to clone Dicer from the Tblu cells that we have in the laboratory. Since we do not have PaKi cells at the moment, it will be more complicated for the Pteropus Dicer, but one possibility could be to synthesize it. However, Dicer is a big gene so it could prove tricky.

• • Including an immunoblot showing that mm cells express mmDicer no more abundantly than the heterologous NoDice cells would allow ruling out the trivial explanation that foci occur at a certain critical mass of Dicer*

Reply: yes, we will provide this piece of data as stated in reply to point 2.

*Minor *

• • I believe line 151 " In contrast, Dicer * *knock down had an ANTIVIRAL effect against VSV-GFP infection at the RNA and protein *

*levels, but no difference in titers was found (Fig. 2H-J)." should be " In contrast, Dicer *

*knock down had an PROVIRAL effect against VSV-GFP infection at the RNA and protein *

*levels, but no difference in titers was found (Fig. 2H-J)." *

Reply: thank you for spotting this error, which was also mentioned by Reviewer 1, we have corrected this in the text.

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Referee #3

Evidence, reproducibility and clarity

In this manuscript by Gaucherand and colleagues, the authors demonstrate that heterologous expression of Myotis myotis Dicer into 293 derivative Dicer KO cells did not produce antiviral effects. The authors further demonstrate that knockdown of Dicer in SV40 immortalized M myotis nasal epithelial cells results in reduced alphavirus infection. Finally, they show a correlation where mmDicer changes subcellular localization co-localizing with likely alphavirus replication foci. The manuscript is clearly written, and the conclusions drawn as stated are accurate.

Strengths

• This is an overall topical area of research: how bat antiviral responses differ from other mammals - - with enormous general interest in host-pathogen interfaces, and particular relevance to the role of RNAi.
• The manuscript is clearly written and does not overstate the conclusions.
• The team are well-qualified experts in this area with an excellent track record of findings from the Pfeffer lab in the years preceding this work

Critiques

Major

1. Without direct comparison to the other bat species Dicers (especially where RNAi activity has been suggested as antiviral in previous publications) there is little in this paper that can be concluded about global aspects of bat dicer/RNAi. Minor
2. What rules out that the mmDicer re-localization observed in the immortalized mm nasal epithelial is due simply to greater expression levels over the NoDice cells heterologously expressing mmDicer?
3. Although partially addressed in the text stating the generally long half-life of miRNAs, it seems the simplest explanation for this observation is due to some activity of a shorter-lived miRNA is required for optimal alphavirus replication is the mm nasal epithelial cells.

Suggestions that could enhance the magnitude of conclusions that can be drawn from this work.

Major

• Making NoDice cells expressing other bat species Dicers, including those with claims that RNAi is antiviral, would address how universal these current observations are to bats/cell lines.
• Including an immunoblot showing that mm cells express mmDicer no more abundantly than the heterologous NoDice cells would allow ruling out the trivial explanation that foci occur at a certain critical mass of Dicer Minor
• I believe line 151 " In contrast, Dicer knock down had an ANTIVIRAL effect against VSV-GFP infection at the RNA and protein levels, but no difference in titers was found (Fig. 2H-J)." should be " In contrast, Dicer knock down had an PROVIRAL effect against VSV-GFP infection at the RNA and protein levels, but no difference in titers was found (Fig. 2H-J)."

Significance

As written, this work would be significant to aficionados of bat RNAi. With a little extra work, this could have broader significance regarding more global aspect of Dicer in the the bat antiviral response.

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Referee #2

Evidence, reproducibility and clarity

This study by the Pfeffer lab interrogates the role of Dicer during RNA virus infection in bats. This is an interesting and important topic, as bats are well-documented to be a reservoir of viruses that can target humans. The field of bat immunology is gaining momentum, but there is still a lot to be done. This study is thus particularly timely. It also explores more of a niche pathway when it comes to immunity: antiviral RNAi and its entry point, Dicer. This work comes after two recent studies, cited by the authors (Dai 2024, Owolabi 2025), that also explore this concept. Here though, the Pfeffer lab comes to an opposite conclusion, as their results advocate against the existence of antiviral RNAi in bats. As discussed by the authors, discrepancies between their study and the two others may be linked to differences in experimental systems. It nonetheless brings a novel, interesting take on the topic of Dicer & antiviral RNAi in bats, and will be of interest to immunologists and virologists. Altogether, I find the manuscript well-written and clear. Experiments are to the point and well interpreted. Below are a few suggestions that will help bolster the authors' conclusions.

Figure 1 relies on transduction of cells and antibiotic selection to obtain mmDicer-expressing cells. Although we would expect that every cell expresses the construct of interest, this is not always the case, depending on the cell type and toxicity of the construct. As the constructs are tagged, I suggest that the authors use flow cytometry to measure expression levels in a single cell manner. While doing so, they can infect with SINV-GFP and correlate GFP signal with construct expression in each cell, providing a more accurate measurement of mmDicer effect on viral infection. Alternatively, the authors could use live microscopy, as done in Fig 2, to obtain similar data.

For Fig 1C and 1F, it would be great to have growth curves with two different MOIs, instead of a single time point, to ensure that a putative antiviral effect is not missed. Same goes for Fig 2C, especially when the authors document quite a big defect on GFP expression (a proxy for SINV infection) when Dicer is knocked down (Fig 2B). There may be a bigger difference in titers at earlier time points. This matter runs throughout the manuscript. I do not suggest that the authors should provide growth curves every time viral titers are measured, but it is still worth doing it for the 2-3 key experiments of the paper.

Figure 4, could the authors provide a proof that the Dicer antibody is specific in the bat context? This can be done by staining Dicer in bat cells knocked down for Dicer and infected with SINV. The apparition of foci upon anti-Dicer antibody staining should be abbrogated or severely impaired by the knock-down.

Fig 5C, please provide a quantification of the images.

l.263, when comparing this work with the recent publications on bat antiviral RNAi, the authors could also provide the percentage identity between Dicers from different species.

Significance

This study by the Pfeffer lab interrogates the role of Dicer during RNA virus infection in bats. This is an interesting and important topic, as bats are well-documented to be a reservoir of viruses that can target humans. The field of bat immunology is gaining momentum, but there is still a lot to be done. This study is thus particularly timely. It also explores more of a niche pathway when it comes to immunity: antiviral RNAi and its entry point, Dicer. This work comes after two recent studies, cited by the authors (Dai 2024, Owolabi 2025), that also explore this concept. Here though, the Pfeffer lab comes to an opposite conclusion, as their results advocate against the existence of antiviral RNAi in bats. As discussed by the authors, discrepancies between their study and the two others may be linked to differences in experimental systems. It nonetheless brings a novel, interesting take on the topic of Dicer & antiviral RNAi in bats, and will be of interest to immunologists and virologists. Altogether, I find the manuscript well-written and clear. Experiments are to the point and well interpreted. Below are a few suggestions that will help bolster the authors' conclusions.

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Referee #1

Evidence, reproducibility and clarity

Bats acts a reservoir for many viruses. While some of these viruses can be pathogenic for humans and other animals, infected bats tolerate these viruses and show little to no pathogenesis. It is therefore key to characterise which immune pathways are active in bats and how do they differ from other mammals to understand how bats can sustain these virus infections. RNA interference (RNAi) acts as an antiviral mechanism in plants, invertebrates and was recently shown to be active in a cell type-dependent manner as a defence mechanism in mammals. Notably, recent findings show that antiviral RNAi activity is high in cells lines from two bats species (P.alecto and T. brasiliensis) and that this pathway might play an important role in bat viral tolerance. In this study, the authors investigate the antiviral role of Dicer in another bat species, Myotis myotis. First they express M. myotis Dicer (mmDicer) or human Dicer (hDicer) in a human epithelial kidney (HEK) 293T cell line knockout for Dicer (NoDice cells) and show that, in a human cell line, expression of mmDicer or hDicer doesn't restrict infections with either Sindbis virus (SINV) or vesicular stomatitis virus (VSV). The authors then tested the role of endogenous bat Dicer in M. myotis nasal epithelial cells and found that mmDicer has a proviral activity since its knockdown reduced the replication of SINV and Semliki Forest virus (SFV), but not of VSV. The authors also show by small RNA deep sequencing analysis that there was only a modest RNAi signature in both HEK293T and M. myotis infected with SINV suggesting that mmDicer does not have increased RNAi activity compared to human cells. Interestingly, the authors then found that in M. myotis cells infected with SINV, SFV but not VSV, mmDicer accumulates into cytoplasmic foci, which also contain double-stranded RNA (dsRNA) derived from viral replication. Finally, the authors showed that this relocalisation of mmDicer into foci was dependent on host factors from M. myotis cells as there was no change in localisation in SINV-infected HEK 293T NoDice cells complemented with mmDicer.

Major comments

• The findings that mmDicer is proviral in bat cells relies exclusively on the observation that the depletion of Dicer in M. myotis cells leads to a reduced accumulation of SFV and SINV at the RNA and protein levels (figure 2). Heterologous expression of mmDicer in HEK 293T NoDice doesn't lead to an increase permissivity to viral infections (figure 1) and the accumulation of Dicer foci is only observed in M. myotis cells but not when mmDicer is expressed in HEK 293 NoDice cells (figure 6). Given that the key finding of this manuscript relies on these knockdown experiments, the authors should ensure that the impact on viral infections is due to the specific silencing of mmDicer and not caused by off-target effects of their siRNA-mediated approach. The authors designed a siRNA pool to efficiently knock-down mmDicer. They should validate their findings by using individual Dicer siRNA and verify whether the decrease SFV/SINV accumulation is observed with at least two individual siRNAs targeting Dicer. It would also strengthen their findings if they could show a complementation experiment in which a mmDicer (designed to not be affected by the siRNA-mediated silencing) is introduced exogenously in Dicer-depleted cells and show that it rescues the observed decrease in viral accumulation to demonstrate that the proviral role is strictly dependent on mmDicer. Alternatively, the authors could consider a CRISPR/Cas9 genome editing approach to knockout Dicer in bat cells to test whether this proviral effect is confirmed.
• Figure 2: the authors knock-downed Dicer in M. myotis nasal epithelial cells and carried out infections with SINV-GFP and SFV. The authors conclude that Dicer is proviral as its depletion causes an decrease in SINV-GFP and SFV accumulation. While this conclusion is supported by the decrease levels of viral RNA and protein levels upon Dicer depletion (figure 2D, 2E, 2G), the effect on the viral titers is non-significant for both viruses (Figure 2C and 2F) based on the statistical analysis. This reviewer appreciates that the titers are lower upon Dicer knockdown, which support the authors' findings at the viral RNA and protein levels. However, as these results are central to the core message of the manuscript, the authors should provide evidence that this proviral effect observed is statistically significant on viral titers by perhaps providing additional repeats and/or comment on this observation.
• In figure 4 and 5, the authors nicely show that mmDicer accumulate to cytoplasmic foci in M. myotis cells upon infection with SFV and SINV and these foci co-localise with double-stranded RNA. The authors used a commercial polyclonal antibody against Dicer (A301-937A, Bethyl according to the Material and Methods section) which is specific to human Dicer to carry out their immunostaining in bat cells. The authors should provide evidence that this antibody indeed recognises/crossreacts with mmDicer as well and that the staining shown is indeed specific to mmDicer localisation especially because the heterologous expression of HA-tagged version of mmDicer in HEK 293T NoDice cells did not show this accumulation of cytoplasmic foci. The authors should verify the specificity of their mmDicer immunostaining by performing the same labelling in bat cells in which Dicer is knock-downed (or knock out) by individual and validated siRNA against mmDicer. The decrease signal of bat Dicer staining using the anti-human Dicer antibody would indicate specificity. Another complementary approach would be to test their Dicer staining between HEK NoDice cells (no Dicer present) versus NoDice complemented with with either mmDicer or human Dicer constructs, which would then indicate how much the anti-human Dicer antibody recognises bat Dicer. In addition, the authors should overexpress HA-tagged mmDicer in M. myotis nasal epithelial cells and test whether HA-mmDicer accumulate into foci upon infection using an anti-HA immunostaining. This would confirm that these accumulation into foci indeed is specific to mmDicer but also would reinforce the authors' findings that host factors within bat cells are important for this formation into foci since mmDicer expression in HEK 293T No Dice cells didn't show this phenotype upon infection (figure 6). OPTIONAL: it would be interesting to overexpress HA-tagged human Dicer into M. myotis nasal epithelial cells as well to then test using anti-HA staining whether human Dicer in presence of host factors from the bat can accumulate into cytoplasmic foci or not upon viral infection.
• This reviewer appreciates that this might be judged as beyond the scope of this study since it is focused on the role of Dicer in M. myotis. However, the observation that mmDicer accumulates into foci containing as well viral dsRNA is very interesting and it would significantly improve the manuscript if the authors would provide further indications that this phenotype is related to the lack of antiviral activity of mmDicer compared to what has been previously shown in other bat species (P.alecto and T. brasiliensis). In other words, is this accumulation of mmDicer into foci responsible for its different impact on virus infection? It would therefore be insightful to compare Dicer localisation upon infection in M. myotis versus P.alecto and/or T. brasiliensis bat cells in which Dicer was shown to be antiviral and test whether this accumulation in foci is only observed in bat cells in which Dicer is proviral (M. myotis) but not in the other bat cells in which Dicer is antiviral (P.alecto and/or T. brasiliensis).
• OPTIONAL: Given the difference between the provial role of mmDicer compared to the antiviral activity of Dicer in cells from P.alecto and T. brasiliensis bat cells, it would strengthen the authors' findings. if additional experiments would be conducted in parallel using M. myotis, P.alecto and/or T. brasiliensis cells. Notably knocking down Dicer in both M. myotis, P.alecto and/or T. brasiliensis cells, compare the impact on viral infections with SINV, SFV, VSV and correlate any observed difference in phenotype with putative variations in the formation of foci.

Minor comments

• Figure 2I: The authors performed a knockdown of Dicer in M. myotis nasal epithelial cells and monitor the impact on VSV-GFP infection. They found that knocking down Dicer leads to an increase in GFP protein and RNA levels suggesting an antiviral role of Dicer while, in contrast, no effect is observed on the production of infectious particles (figure 2H). On the western blot there is only a slight/weak increase of GFP protein level observed upon Dicer knockdown. Yet, the quantification of the band intensity shows a 4-fold increase relative to tubulin and compared to cells treated with siRNA control. This 4-fold increase seems exaggerated given the low increase in the intensity shown on the blot. This discrepancy is most likely due to the lower intensity of tubulin in the western blot analysis of siDicer-treated cells compared to siNeg-treated cells. The authors should reload their western blot with equal amount of protein extract loaded to ensure that the results shown on the western blot are in line with the quantification.
• Figure 3D: the authors mention that in both HEK293T cells and M. myotis nasal epithelial cells infected with SINV-GFP, there was an enrichment of 22-nucleotides (nt) paired positive and negative sense reads that overlapped with a 2-nt overhang, typical of Dicer cleavage. In Figure 3D, the data shows indeed that the duplexes are enriched for reads of 22-nt but it is unclear how this analysis reveals a 3' 2nt overhang within these duplexes. Can the authors clarify this point and if the data provided in that particular analysis indeed doesn't allow to detect these overhangs, please rephrase accordingly or provide additional analysis to support that point.
• Typo: page 5, line 152: the authors mention that Dicer knock down had an antiviral effect against VSV-GFP infection at the RNA and protein levels. However, the data in Figure 2I and 2J show an increase in both GFP RNA and proteins levels upon knockdown of Dicer. Although this data suggests that Dicer is antiviral against VSV, the knockdown of Dicer itself is not antiviral but rather proviral/increase virus accumulation. Please rephrase this sentence to avoid confusions.

Significance

The findings from this study are interesting as they provide further insights into the role of RNAi towards virus infections. Notably, it highlights a putative proviral role of Dicer in M. myotis bat cells in contrast to the antiviral role in mammals (including other bat species) as well as in plants and invertebrates. Another exciting finding of this study is the observation that mmDicer accumulates in cytoplasmic foci upon viral infection and that these foci also contain viral dsRNA replication intermediates. These accumulation of Dicer into foci only appear in bat cells infected with viruses producing large amounts of dsRNA such as SFV and SINV but not with VSV infection where no dsRNA was detected.

While these findings are novel and interesting, this study, as it stands, is rather descriptive and doesn't provide mechanistic insights into the proviral activity of mmDicer and its localisation into cytoplasmic foci upon infections. The importance of the authors' findings would greatly improve if there were some experiments addressing whether this localisation of mmDicer into foci is responsible or at least correlate with its proviral activity/its lack of antiviral activity. Comparative studies between M. myotis cells in which Dicer is proviral and/or P.alecto and T. brasiliensis cells where RNAi was previously shown to be antiviral would likely provide key mechanistic insights.

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Reply to the reviewers

Manuscript number: RC-2025-02946

Corresponding author(s): Margaret, Frame

Roza, Masalmeh

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Reviewer #1

Evidence, reproducibility and clarity

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

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

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

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

Response:

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

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

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

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

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

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

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

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

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

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

Response:

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

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

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

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

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

Significance

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

__Response: __

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

Review #2

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

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

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

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

Response:

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

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

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

__Response: __

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

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

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

Response:

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

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

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

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

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

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Referee #2

Evidence, reproducibility and clarity

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

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

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

Significance

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

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

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

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

Review of Masalmeh et al.

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

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

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

Some questions that would enhance potential impact.

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

Significance

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

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Reply to the reviewers

Manuscript number: RC-2025-02946

Corresponding author(s): Margaret, Frame

Roza, Masalmeh

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Reviewer #1

Evidence, reproducibility and clarity

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

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

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

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

Response:

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

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

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

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

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

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

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

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

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

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

Response:

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

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

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

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

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

Significance

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

__Response: __

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

Review #2

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

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

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

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

Response:

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

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

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

__Response: __

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

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

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

Response:

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

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

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

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

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

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

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

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

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

Significance

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

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

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

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

Review of Masalmeh et al.

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

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

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

Some questions that would enhance potential impact.

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

Significance

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

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Reply to the reviewers

RESPONSE TO REVIEWERS

We thank the reviewers for their thoughtful and constructive feedback, which has been instrumental in improving the overall quality of our manuscript.

In response, we have undertaken a substantial revision that includes new experimental data, refined analyses, and clearer presentation of our findings. Specifically, we have addressed concerns about RNAi efficiency and protein-level validation, expanded our genetic models to include loss-of-function contexts, and clarified the interpretation of mitochondrial morphology using both confocal and electron microscopy. We also incorporated new data on Cyclin E regulation and mitochondrial membrane potential to strengthen the mechanistic link between dPGC1 depletion and Yki-driven tumorigenesis. These revisions not only address the specific points raised by the reviewers but also enhance the coherence and impact of the study. We are confident that the revised manuscript presents a more robust and compelling case for the role of dPGC1 as a context-dependent tumor suppressor and that it will be of broad interest to the fields of developmental biology, cancer metabolism, and mitochondrial dynamics.

Reviewer #1 (Evidence, reproducibility and clarity (Required)): Sew et al. examine the master regulator of mitochondrial biogenesis, dPGC1, in the context of Drosophila wing and larval development. They primarily use confocal imaging to probe the interplay between dPGC1 and an overactive Hippo pathway, driven by overexpression of the main effector protein, Yki. In their study, they find that tumors, driven by overactivity of Yki grow larger when dPGC1 is downregulated, implicating the mitochondrial biogenesis pathway in tumor suppression. Furthermore, in the context of Yki overexpression, they find that levels of Mfn or Opa1 modulate tumor size. Lastly, they show a role of cyclin E in controlling the size of tumors formed by Yki OE + dPGC1 RNAi. The potential role of dPGC1 as a tumor suppressor is interesting because it highlights an emerging recognition of mitochondria in the aetiology of cancer. However, before publication, much of the data in this manuscript should be strengthened by a refinement in the methods/analysis and an increase in orthogonal approaches.

We addressed concerns regarding RNAi efficiency and wing development by incorporating data from a dPGC1 mutant allele and using a ubiquitous driver for qPCR validation of transgene efficiency. We clarified the rationale for EM use. The manuscript now avoids overinterpretation of mitochondrial morphology and focuses on fusion-specific regulators. We also revised the narrative arc to maintain coherence and added loss-of-function models to support our conclusions.

Below, we address each of the reviewer’s points in detail.

Major comments:

The authors indicate that for example, in lines127-28, that neither downregulating or overexpressing dPGC1 affects wing size. However, the quantification in Fig. 1C shows a significant decrease in wing size following RNAi treatment. This decrease is modest, but it is nevertheless significant. It is worth pointing out, too, that the efficiency of the RNAi in Fig. S1C suggests that the conclusions drawn are premature. While a roughly 55% drop in mRNA levels may be statistically significant, it is unclear whether this drop in transcripts corresponds to a commensurate depletion of protein. Moreover, it is unclear, in this context, how much dPGC1 may indeed be necessary to drive a relatively normal program of mitochondrial biogenesis in wing development. To obtain a clear result, it is necessary to show significant depletion of the dPGC1 protein. (Ultimately, if it is the case that dPGC1 is unnecessary for wing development and function, a more coherent line of inquiry would be to find out the reason for this rather than to pivot the story to studying tumorigenesis in larva.)

We agree that the interpretation of the RNAi efficiency data requires clarification.

The qPCR analysis shown in former Fig. S1C was performed using wing discs from flies expressing UAS-dPGC1-RNAi under the control of the MS1096-Gal4 driver. However, as shown in current Fig. 1C, MS1096-Gal4 is not expressed uniformly across the wing disc. Some regions remain RFP-negative, indicating that the RNAi construct is not active in all cells. As a result, the measured mRNA levels likely underestimate the true knockdown efficiency. This is because the qPCR includes mRNA from both RNAi-expressing and non-expressing cells, diluting the apparent reduction in transcript levels.

To address this limitation and more accurately assess RNAi efficiency, we repeated the qPCR analysis using a ubiquitous driver (actin-Gal4) to ensure uniform expression of the RNAi construct. Under these conditions, we observed a more substantial knockdown, with dPGC1 mRNA levels reduced to approximately 25% of control levels (this is shown in current Fig S2). This result indicates that the RNAi line is more effective than initially suggested by the MS1096-Gal4-based analysis.

To complement our RNAi-based analysis, we additionally used a mutant strain carrying a characterized allele of dPGC1 (dPGC11, also known as dPGC1KG08646; see FlyBase: https://flybase.org/reports/FBal0148128). This genetically distinct approach allowed us to validate and strengthen our findings regarding dPGC1 function. Flies homozygous for this allele exhibited a modest but statistically significant reduction in both wing disc and adult wing size. These results support the conclusion that dPGC1 is required for normal wing growth and development. The new data are now included in Figure 1 and referenced in the main text (lines 144-153).

Additionally, as suggested by the reviewer, we have revised the relevant section to maintain a coherent line of inquiry. The updated text can be found in lines 163–172.

In Figure 3H-K, it is not clear why the authors used electron microscopy to evaluate mitochondrial morphology. The very good confocal images in Figure 3C-G show a clear change in mitochondrial morphology following the knockdown of Mfn, Opa1, and Miro. While it is clear from the electron micrographs in Figure H that the mitochondria are enlarged, it is not obvious that this increase in length is a result of increased mitochondrial fusion. Indeed, if the mean form factor were used to quantify the shape, it is likely that in both conditions, the value would be close to 1, indicating more of a round object, and it not obvious whether there would be a difference between the Yki OE versus the YkI OE + dPGC1 RNAi. Therefore, from this data alone, it cannot be concluded that the YkI OE + dPGC1 RNAi condition leads to mitochondrial hyperfusion.

Our rationale for including electron microscopy (EM) was to overcome specific limitations in imaging mitochondrial morphology within the main epithelium of the wing disc, where Yki-driven tumors arise. These tumors were generated using ap-Gal4, which drives expression specifically in the main epithelium and is not active in the peripodial membrane. This is an important distinction, as the peripodial membrane—used in Figures 3C–G—has a squamous architecture and larger cytoplasmic volume, making it ideal for high-resolution confocal imaging and for assessing the effects of manipulating dMfn, Opa1, and miro. However, because ap-Gal4 is not expressed in the peripodial membrane, this tissue could not be used to analyze mitochondrial morphology in the actual tumorous context.

To directly evaluate mitochondria in the main epithelium, we employed EM, which provides the resolution necessary to visualize ultrastructural changes that are not easily captured by confocal microscopy in this densely packed tissue. While EM does not directly measure fusion events, it allowed us to detect changes in mitochondrial size and shape that support our broader findings.

We acknowledge that mitochondrial enlargement alone does not definitively demonstrate hyperfusion. However, the EM data were interpreted alongside additional evidence: the upregulation of mitochondrial fusion genes (dMfn and Opa1) in Yki + dPGC1-RNAi tumors, and functional data showing that overexpression of these genes promotes fusion in the peripodial membrane. Together, these findings suggest that dPGC1 depletion enhances mitochondrial fusion in Yki-driven tumors.

To further clarify this point, we also imaged mitochondria in the main epithelium using confocal microscopy. However, the resolution was considerably lower than that achieved with EM, limiting our ability to assess fine mitochondrial structures. We have prepared a representative figure for the reviewer (below), showing representative confocal images of wing discs from three genotypes: (A) ap-Gal4, UAS-GFP (control), (B) ap-Gal4, UAS-Yki, and (C) ap-Gal4, UAS-Yki, UAS-dPGC1-RNAi. We used anti-ATP-synthase (Abcam, ab14748, dilution 1:200), to label the mitochondria for this Figure. Despite the lower resolution, mitochondria in the Yki + dPGC1-RNAi tumors appear elongated (yellow arrows) compared to those in the other conditions, consistent with the changes observed by EM. We believe this example illustrates the limitations of confocal imaging in this tissue and reinforces the need for EM to accurately assess mitochondrial morphology in the tumorous epithelium.

While our EM analyses reveal mitochondrial enlargement in wing discs co-expressing Yki and PGC1-RNAi, we acknowledge that these structural features alone do not conclusively demonstrate mitochondrial hyperfusion. To address this, we have revised the manuscript to avoid overinterpreting the EM data and instead emphasize the functional relevance of mitochondrial fusion regulators such as dMfn and Opa1 in promoting tumor growth.

Taken together, the EM analysis provides structural validation in the tumorous epithelium (Fig 4), while the confocal imaging and functional manipulation of fusion genes in the peripodial membrane offer mechanistic insight (Fig 3). This integrated approach strengthens the conclusion that PGC1 depletion in a Yki-overexpressing context promotes changes in mitochondrial morphology and contributes to tumorigenesis, independent of whether these changes reflect hyperfusion.

Figure 4. refers to changes in mitochondrial fusion and fission in tumor formation; however, the authors do not attempt to alter mitochondrial fission factors, so it is not accurate to mention a role of mitochondrial fission, in this context.

As we did not directly manipulate fission-related factors in our experiments, we agree that it would be inappropriate to draw conclusions about the role of mitochondrial fission in this context. Our revised figure (current Fig 5) and accompanying text now focus exclusively on the effects of mitochondrial fusion and the genes directly involved in regulating this process.

It must be noted, too, that the authors have not demonstrated that their genetic interventions have actually affected mitochondrial morphology in these experiments. As noted in the previous figure, the Yki OE + dPGC1 RNAi condition showed enlarged mitochondria, but not necessarily hyperfused organelles. Therefore, the downregulation of Mfn or Opa1 in this set of experiments may not necessarily have altered mitochondrial morphology. Perhaps suppression of Mfn or Opa1 would normalize the areas of these evidently swollen mitochondria, but this is unclear without images. Furthermore, it should be appreciated that both Opa1 and Mfn exhibit pleiotropic attributes - e.g., Opa1 not only regulates IMM fusion, but it also modulates the shape and tightness of cristae membranes, specialized sites of oxidative phosphorylation as well as sequestration of cytochrome c, the release of which influences apoptosis (Frezza et al., 2006). At least in mammalian cells, Mfn2 is thought to regulate contacts between mitochondria and endoplasmic reticulum (Naon et al., 2023), which may serve other functions than OMM fusion, such as stabilization of the MAM.

To directly address this point, we performed EM to assess mitochondrial ultrastructure in Yki + dPGC1-RNAi wing disc tumors, with and without dMfn1 downregulation, the most upregulated mitochondrial fusion gene in this tumor context. In Yki + dPGC1-RNAi tumors, mitochondria appeared more elongated, consistent with increased fusion. Upon dMfn1 depletion, we observed a dramatic shift in mitochondrial morphology: mitochondria became larger and more rounded, with disrupted cristae and onion-like structures, indicative of compromised mitochondrial integrity and function (see current Fig. 4).

As the reviewer rightly notes, these morphological changes are consistent with the pleiotropic roles of Mfn and Opa1, which extend beyond outer and inner membrane fusion to include regulation of cristae architecture and ER-mitochondria contacts (Frezza et al., 2006; Naon et al., 2023). We now discuss these broader roles in the revised manuscript (lines 493–497). Taken together, our EM and confocal analyses, combined with targeted genetic manipulations, provide evidence that mitochondrial morphology is indeed altered in response to dPGC1 depletion and fusion gene deregulation in the wing disc.

Figure 5 highlights a connection between dysregulation of mitochondria and Cyclin E, which allows cells to prematurely enter S phase. The data presented here do not offer clarity on whether the enlargement of the tumors results from increase cellular proliferation and/or cell size. The role of the cell cycle adds a layer of complexity to these results, because it is thought that mitochondria undergo fragmentation during the cell cycle to promote an even distribution of the organelle population after mitosis (Taguchi et al., 2007); however, in this manuscript, the authors contend that the downregulation dPGC1 is promoting mitochondrial hyperfusion. It is unclear how and whether cellular division and proliferation would proceed at an accelerated rate in a situation with mitochondrial hyperfusion.

To address this point, we started by analyzing whether Yki + dPGC1-RNAi tumors exhibit increased proliferation compared to tumors expressing Yki alone. We quantified mitotic activity using the phospho-Histone H3 (PH3) marker of mitotic cells and observed a significant increase in PH3-positive cells in the Yki + dPGC1-RNAi condition. These results indicate an elevated proliferation rate in these tumors and are now presented in Fig 2O–Q. In the text, can be found in lines 221-228.

We agree with the reviewer that our findings challenge the conventional view that mitochondrial fragmentation is a prerequisite for mitosis, as we observe increased expression of gene promoting mitochondrial fusion in the context of dPGC1 downregulation alongside signs of accelerated cell cycle entry. It is important to note that we also show that the levels of the oncogene Cyclin E, a key driver of cell cycle progression and S-phase entry, were elevated in Yki + dPGC1-RNAi tumors compared to those expressing Yki alone, suggesting that the increased proliferation observed is at least in part driven by enhanced cycle activity. To further probe Cyclin E’s role, we used the CycE-05306 heterozygous mutant allele, which reduces Cyclin E levels by ~50% without affecting normal development. Notably, this partial reduction strongly suppressed tumor growth in the Yki + dPGC1-RNAi background (Fig 6), underscoring Cyclin E’s functional importance in supporting oncogenic growth in this context.

These findings support the notion that defects in the expression of mitochondrial genes involved in mitochondrial morphology induced by dPGC1 depletion do not impair but rather coincide with accelerated cell division.

Minor comments:

Lines 69-72 contrast the roles of PGC1α and β. It is not clear whether the comparison is of their respective roles in cancer or in normal physiology. In either case, it is important to note that PGC1β has been shown to drive mitochondrial fusion as well as biogenesis through its control of MFN2, among other factors (Liesa et al., 2008).

In response, we have clarified the comparison between PGC1α and PGC1β in the introduction to specify that it refers to their roles in cancer. Additionally, we now acknowledge that PGC1β has been shown to promote mitochondrial biogenesis and fusion, notably through the regulation of MFN2, as demonstrated by Liesa et al. (2008). This reference has been added to provide a more balanced and accurate representation of PGC1β’s functions. In the text it can be found in lines 77-81.

Although this study focuses on PGC1, the authors do not seem to site the original literature from the Spiegelman lab.

In response to the reviewer’s comment, we have added a new section in the introduction that cites key foundational studies from the Spiegelman lab. This addition can be found in the introduction in lines 68-73.

There are 10-20 grammatical errors throughout the text.

We apologize for this. We have carefully revised the text, and we are very confident those errors have been corrected.

**Referee Cross-commenting**

There is agreement among the referees that the potential role of PGC1 as a tumor suppressor is interesting and significant. However, various aspects of this work require attention prior to publication. For example, there needs to be a complete knock down of PGC1 to come to any conclusion as to its role in wing development. The methods for analyzing mitochondrial morphology need to be clarified and be consistent with standards in the field of mitochondrial dynamics. Also, the authors need to quantify their Western blots to obtain accurate assessments of protein levels. Generally, the study relies too heavily on overexpression experiments; understanding the potential role of mitochondria in regulating the Hippo pathway should include various knockdown and/or knockout models.

Reviewer #1 (Significance (Required)):

Overall, the authors show an interesting dampening effect of dPGC1 on growth of Yki-driven tumors. This data could be relevant for elucidating how dysregulation of the Hippo signalling pathway can underlie tumorigenesis.

The narrative arc of the study, however, appears to lack a focused line of inquiry. Figure 1 highlights an attempt to modulate Drosophila wing size and/or structure by downregulating dPGC1, but to no effect. Although examination of the efficiency of the RNAi revealed that the transcripts were still present in significant quantities; so, the conclusion that dPGC1 is dispensable for wing formation is premature. To have clarity on this point, it would be necessary to completely knockdown the gene, preferably by showing a total loss of protein. This should be feasible for the authors, since they showed Western blotting in Figure 5A. In any event, it seems that this negative data led the authors to study the Hippo pathway in the larval stage. This transition from Figure 1 to 2 seemed somewhat arbitrary and leads to a rather disjointed sense of the main line of inquiry around dPGC1.

It is important to note, too, that the authors highlight a role of mitochondrial dynamics in the pathway of Yki-driven tumor formation; however, they only directly evaluate mitochondrial dynamics in this context in a single assay, namely, Figure 3H-K, and this quantification is likely inaccurate because the mitochondria in the Yki OE + dPGC1 RNAi condition seem to be substantially enlarged, circular structures. It is critical to keep in mind that mitochondrial enlargement does not necessarily stem from hyperfusion. It could come from a decrease in the activity of Drp1 or result from an imbalance between mitochondrial biogenesis and mitophagy.

As noted in our responses above, we have addressed these concerns by clarifying the limitations of our mitochondrial morphology analysis. Additionally, we have expanded the discussion (lines 498-504) to explicitly acknowledge that mitochondrial enlargement does not necessarily indicate hyperfusion. In that paragraph, we consider alternative explanations such as reduced fission or imbalances in mitochondrial biogenesis and mitophagy, and we outline the need for future studies using dynamic assays and additional markers to more precisely dissect mitochondrial remodeling in Yki-driven tumors.

A marked limitation of this study is the overuse of rather artificial manipulations of transcriptional regulatory pathways. The study would benefit a lot from investigation of the loss of function of components of the Hippo pathway rather than just OE of Yki.

We performed additional experiments using Warts (Wts) mutant clones to assess the role of dPGC1 in a loss-of-function context within the Hippo pathway. While our initial analyses were based on Yki overexpression, which allowed us to robustly probe the interaction between Yki and dPGC1, we agree that this approach may not fully reflect physiological conditions. By generating Wts mutant clones, which endogenously activate Yki through loss of upstream inhibition, we were able to evaluate the impact of dPGC1 depletion in a more physiologically relevant setting. These new results confirm and extend our previous findings, showing that dPGC1 limits tissue overgrowth even when Yki is activated through loss of Wts, thereby strengthening the biological relevance of our conclusions.

These results are presented in Fig 2F-I. In the text, those results are presented in lines 181-189.

My expertise is in mitochondrial biology, with specialization in super-resolution imaging, mitochondrial dynamics and membrane architecture. I have also worked in the interface between mitochondrial physiology and cancer. With this perspective, I think that the authors uncover a potentially interesting role of PGC1 as a tumor suppressor.

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

Summary In this manuscript the authors the investigate the role of the mitochondrial regulatory transcription factor dPGC1 in tissue growth and oncogenic transformation. They show that dPGC1 limits hyperplasia mediated by overexpression of Yki in the Drosophila wing disc, while having no effect on normal growth. dPGC1 depletion in discs overexpressing Yki results neoplastic overgrowth and hyperfused mitochondria, which was dependent on the increased expression of genes involved in promoting mitochondrial fusion. Additionally, the authors show that dPGC1 limits CycE levels post-transcriptionally in Yki tumors.

In the revised version of our manuscript, we have clarified the relationship between our findings and prior work by Nagaraj et al., including new experiments that demonstrate the specificity of dPGC1’s role in Yki-driven growth. Specifically, we show that dPGC1 depletion does not enhance tissue overgrowth in EGFR or InR contexts, nor does it affect Yki expression or activity. Furthermore, we tested dPGC1 overexpression in Yki-overexpressing tissues and observed no significant changes in growth or mitochondrial fusion gene expression. Additional controls confirmed that Cyclin E upregulation is specific to the Yki + dPGC1 depletion condition, reinforcing the context-dependent nature of our findings.

Each of the reviewer’s comments is addressed below.

Major comments 1) The authors mention several times in passing in the results a manuscript from the Banerjee lab (Nagaraj et al 2012), which shows that many of the genes the authors of the present manuscript show are upregulated upon Yki overexpression + dPGC1-RNAi compared with Yki overexpression alone are in fact upregulated upon Yki overexpression alone compared with control (dMfn/marf, opa1, miro - while interestingly dPGC1 itself is not affected). Nagaraj et al further show that Yki-overexpressing discs have longer mitochondria suggesting increased fusion even in the absence of dPGC1 depletion. The findings from Nagaraj et al should be mentioned explicitly in the introduction and the relationship between this manuscript and the present work clearly outlined in the discussion.

In the revised manuscript, we have now explicitly referenced the findings of Nagaraj et al. (2012) in the Introduction (lines 106-118), Results (lines 355-360) and Discussion (lines 466-468) sections.

In the revised Introduction, we summarize their key observations that Yki overexpression alone upregulates mitochondrial fusion genes such as dMfn and Opa1, and leads to mitochondrial elongation, while not affecting dPGC1 expression.

In the revised Results section, we mention that, building on that work, our study demonstrates that dPGC1 depletion further amplifies this effect, leading to enhanced mitochondrial elongation and tumor growth.

In the revised Discussion, we now explicitly reference the findings by Nagaraj et al. (2012), which demonstrated that Yki overexpression promotes mitochondrial fusion and upregulates key fusion genes. We build upon this work by showing that dPGC1 depletion in a Yki-overexpressing background further enhances mitochondrial fusion gene expression and tumor growth. This supports a model in which dPGC1 acts as a safeguard against Yki-induced mitochondrial remodeling and oncogenesis, reinforcing its role as a context-dependent tumor suppressor.

Importantly, we show that this effect is context-dependent and not observed in otherwise normal tissues, highlighting a sensitized mitochondrial response to Yki activation when dPGC1 is lost. These additions help delineate the novel contribution of our study in identifying dPGC1 as a critical modulator of mitochondrial dynamics and tumorigenesis downstream of Yki.

2) Given that Yki overexpression alone induces mitochondrial fusion and that dMfn/marf and opa1 depletion suppresses Yki-induced overgrowth (Nagaraj et al), does dPGC1 overexpression also suppress Yki-induced overgrowth?

If so, is this correlated with reduction in dMfn/marf and opa1 compared with Yki overexpression alone?

In response, we performed additional experiments to assess whether dPGC1 overexpression influences Yki-driven overgrowth. We also analyzed the expression of mitochondrial fusion genes (dMfn and Opa1) in this context. As shown in new Fig. S8, dPGC1 overexpression in Yki-overexpressing wing discs did not significantly affect tissue growth, nor did it alter the mRNA levels of key fusion regulators, dMfn and Opa1. These findings suggest that the transcriptional upregulation of mitochondrial fusion genes observed upon dPGC1 depletion is not a general consequence of altered dPGC1 levels, but rather a specific response that emerges in the context of Yki activation. We now present and discuss these results in the revised manuscript (lines 278-285), highlighting the sensitized nature of mitochondrial remodeling in an oncogenic environment driven by Yki signaling.

3) One important question raised by this study is: how specific is the effect of dPGC1 depletion to Yki-driven overgrowth? As Yki-driven overgrowth already have increased mitochondrial length, it is possible that Yki-expressing cells are already sensitised to the effects of dPGC1 depletion. Interestingly, Nagaraj et al show that mitochondrial morphology is not affected upon EGFR activation (hyperplasia) or upon scrib and avl depletion (neoplasia). The authors should therefore test if dPGC1 depletion can potentiate the growth of other hyperplasia drivers such as activated EGFR and InR in the wing disc.

We tested whether the growth-suppressive effect of dPGC1 depletion was specific to Yki-driven overgrowth or could also potentiate tissue growth in other oncogenic contexts. Specifically, we downregulated dPGC1 in wing discs overexpressing either EGFR or InR. In both cases, we did not observe any enhancement of tissue overgrowth upon dPGC1 depletion, in contrast to what we observed in Yki-overexpressing discs. These results suggest that the sensitivity to dPGC1 depletion is specific to Yki-driven overgrowth and is not a general feature of hyperplastic growth induced by other oncogenes.

These results are shown in Fig S4 and in lines 195-202.

4) There are a few simple control experiments the authors should provide to clarify the relationship between Yki and dPGC1: - Are Yki levels affected by dPGC1 depletion?

To address the potential regulation of Yki by dPGC1, we performed quantitative PCR (qPCR) analysis to measure the expression levels of yki and its well-established transcriptional targets—Cyclin E, Diap1, and bantam—in wing discs depleted of dPGC1. As shown in Fig. S3, we did not detect significant changes in the transcript levels of yki or its target genes, suggesting that the enhanced phenotype observed upon dPGC1 depletion is unlikely to be driven by increased Yki expression or activity. These results indicate that dPGC1 does not strongly influence Yki expression or activity. These new results are presented in lines 190-194.

• Does dPGC1 knockdown alone modify the expression of the genes tested in Fig.3A? In other words, is this upregulation specific of the Yki-overexpression context?

We have conducted this analysis, and the results are now presented in new Fig S7. While the trend is similar to that observed in tumors with both Yki depletion and dPGC1 depletion, the magnitude of change is smaller compared to the context of Yki overexpression. This is described in the text in lines 273-277.

• Does dPCG1 knockdown also stabilise CycE in the absence of Yki overexpression or does the stabilisation of CycE occur only in Yki tumors?

To address this, we examined Cyclin E levels in wing imaginal discs mutant for dPGC1 alone. Our analysis did not reveal any detectable changes in Cyclin E levels under these conditions. These findings suggest that the upregulation of Cyclin E is not a general consequence of dPGC1 loss, but rather a feature specific to the context of Yki overactivation. The corresponding data are now included in Fig S14 of the revised manuscript. In the text, it can be found in lines 442-448.

5) Figure 3C-G: it is not clear how the authors can quantify the length of 3D structures like mitochondria from 2D TEM images (unless they have done volume reconstruction from consecutive sections) and no details are provided in the methods. The quantification of mitochondrial length has to be performed rigorously as it is a key part of the paper.

We agree that TEM provides only 2D profiles of 3D mitochondrial structures, and that this does not allow for precise volumetric reconstruction. In our study, we measured the longest axis of mitochondria visible in thin TEM sections, which is a commonly used 2D proxy for mitochondrial length in the literature (e.g., PMID: 36367943 and PMID: 38637532). To avoid misunderstandings, we have clarified in the Material and Methods section that the reported values represent apparent mitochondrial length in 2D sections, not true 3D length. To enhance the accuracy of these estimates, we measured more than three tissues per genotype, multiple regions per tissue, several cells per region, and various fields of view per cell.

Minor Comments:

1) Line 51: "Mitochondria are highly dynamics organelles." should be "Mitochondria are highly dynamic organelles."

We have corrected that mistake. Thanks!

2) Introduction: the authors should summarise the known physiological functions of PGC1α in order to put their findings in context.

We have added a section in the introduction (lines 66-81) summarizing the known physiological functions of PGC1α

3) lines: 121-3: "...depletion of dPGC1...did not have a major impact on adult wing size and shape (Fig 1B, C)." There is a small but statistically significant difference so the authors should state this in the text.

We have revised the text to acknowledge that dPGC1 depletion leads to a modest but statistically significant reduction in wing size. In addition to the original analysis, we have now included further experiments to strengthen this point. Specifically, we analyzed wings from flies homozygous for the dPGC11 allele (also known as dPGC1KG08646; see FlyBase: https://flybase.org/reports/FBal0148128) and confirmed a small but significant reduction in both wing disc and adult wing size compared to controls (this can be found in Fig. 1 and Fig. S1). These results support the conclusion that, although dPGC1 is dispensable for viability and gross morphology, it contributes to normal wing growth. These new results can be found in lines 144-153.

4) Figure 5A (Cyclin E western blot): the authors should show molecular weight markers. In the revised version of our manuscript, we are including the molecular markers as indicated by the reviewer. These can be found in Fig S12.

Reviewer #2 (Significance (Required)):

The manuscript by Sew et al builds on the previous work by Nagaraj et al to explore the role of mitochondrial function in tumors driven by disruption of the Hippo pathway. In particular, the authors identify dPGC1 as a transcription factor that limits Yki-driven mitochondrial fusion and tissue growth. Interestingly, they further show that Yki/PGC1-depleted tumors are highly sensitive to Cyclin E levels, due to post-transcriptional Cyclin E increase. These results further our knowledge of how Yki drives growth and how mitochondria participate in oncogenic transformation. With appropriate revision as outlined above (for example exploring whether the mechanism proposed is Yki-specific), the manuscript will be of broad interest to developmental and cancer biologists.

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

The manuscript presents compelling evidence that dPGC1 acts as a context-dependent tumor suppressor in Drosophila by modulating mitochondrial dynamics and limiting Yorkie (Yki)-induced oncogenic growth. By leveraging the Drosophila wing imaginal disc as a model, the authors investigate how dPGC1 depletion exacerbates Yki-driven tissue overgrowth, mitochondrial hyperfusion, Cyclin E upregulation, and DNA damage, leading to tumorigenesis. The study provides valuable insights into the interplay between mitochondrial dynamics and cancer, with implications for understanding metabolic regulation in oncogenesis. While the findings are significant and well-aligned with the field, certain aspects of the experimental design, data presentation, and mechanistic insights require further attention to enhance clarity, reproducibility, and impact. Below, I outline my major concerns and recommendations.

We addressed concerns about RNAi efficiency and protein-level validation with new qPCR data and mutant analysis. We provided EM and confocal evidence of mitochondrial changes. We clarified non-autonomous effects and quantified Mmp1 and F-actin and added data on miro and Opa1 manipulations. Cyclin E quantification was expanded using multiple Western replicates and a validated mutant allele, and we included new data on mitochondrial membrane potential to assess functional consequences.

Our detailed responses to each point raised by the reviewer are provided below.

Major Points

1. One point is the knock-down efficiency of dPGC1 on the mRNA level, which is between 30 to >50% (Fig. S1C). This is not too strong, so the question arises how severly the protein levels are affected. If possible, an antibody staining with quantification should be performed. From these data it cannot be concluded dPGC1 is not required for normal development, half the dose could be sufficient. How do wings look like when the ap-GAL4 driver is used for dPGC1 knock-down, as this is the driver used in the subsequent experiments? Reviewer 1 also raised concerns about the potential inefficiency of the RNAi treatment in revealing a function during normal wing growth. We agree with both reviewers that the interpretation of the RNAi efficiency data requires clarification.

The qPCR analysis shown in former Fig. S1C was performed using wing discs from flies expressing UAS-dPGC1-RNAi under the control of the MS1096-Gal4 driver. However, as shown in current Fig. 1C, MS1096-Gal4 is not expressed uniformly across the wing disc. Some regions remain RFP-negative, indicating that the RNAi construct is not active in all cells. As a result, the measured mRNA levels likely underestimate the true knockdown efficiency. This is because the qPCR includes mRNA from both RNAi-expressing and non-expressing cells, diluting the apparent reduction in transcript levels.

To address this limitation and more accurately assess RNAi efficiency, we repeated the qPCR analysis using a ubiquitous driver (actin-Gal4) to ensure uniform expression of the RNAi construct. Under these conditions, we observed a more substantial knockdown, with dPGC1 mRNA levels reduced to approximately 25% of control levels (this is shown in current Fig S2). This result indicates that the RNAi line is more effective than initially suggested by the MS1096-Gal4-based analysis.

To complement our RNAi-based analysis, we additionally used a mutant strain carrying a characterized allele of dPGC1 (dPGC11, also known as dPGC1KG08646; see FlyBase: https://flybase.org/reports/FBal0148128). This genetically distinct approach allowed us to validate and strengthen our findings regarding dPGC1 function. Flies homozygous for this allele exhibited a modest but statistically significant reduction in both wing disc and adult wing size. These results support the conclusion that dPGC1 is required for normal wing growth and development. The new data are now included in Figure 1 and referenced in the main text (lines 144-151).

Unfortunately, we cannot perform antibody staining due to the unavailability of antibodies against dPGC1.

How does the wing disc look like when dPGC1 is overepressed together with Yki?

In response, we performed additional experiments to assess whether dPGC1 overexpression influences Yki-driven overgrowth. We also analyzed the expression of mitochondrial fusion genes (dMfn and Opa1) in this context. As shown in new Fig. S8, dPGC1 overexpression in Yki-overexpressing wing discs did not significantly affect tissue growth, nor did it alter the mRNA levels of key fusion regulators, dMfn and Opa1. These findings suggest that the transcriptional upregulation of mitochondrial fusion genes observed upon dPGC1 depletion is not a general consequence of altered dPGC1 levels, but rather a specific response that emerges in the context of Yki activation. We now present and discuss these results in the revised manuscript (lines 278-285), highlighting the sensitized nature of mitochondrial remodeling in an oncogenic environment driven by Yki signaling.

In Fig 2D (but also in Fig. 2C) not only cells in the dorsal but also in the ventral comparmtent seem to overproliferate. Either this is a mis-conception or it is a non-autonomous effect from interfering with Yki and dPGC1 in the vertrnal compartment. In either cases, this has to be clarified.

Ventral cells are not labelled by GFP. Fig 3D shows a tumor in which GFP-negative cells are not present, suggesting that they are not overproliferating but rather being eliminated. This phenomenon is consistent with cell competition, a well-characterized process in which transformed or tumorigenic cells outcompete and eliminate neighboring wild-type cells. We have previously described this behavior in wing disc tumors (PMID: 26853367; DOI: 10.1016/j.cub.2015.12.042), and it likely contributes to the expansion of the tumor mass by removing surrounding normal tissue also in this context.

In Fig. 2F-H quantification of Mmp1 and F-actin is missing. Mmp1 is a JNK target, so the authors could do in addition an anti-phospho JNK antibody staining.

In response, we have performed those quantifications. They are now included in Fig 2M, N.

In Fig. 3: how does the mitochondrial network look like in the wing disc periopodial epithelium using the Gug>Yki+dPGC1 genotype? Is it similar to Gug>dMfn or Gug>miro?

We attempted to perform this analysis; however, Yki overexpression under the control of Gug-GAL4 resulted in larval lethality, likely due to GAL4 activity in essential tissues such as the central nervous system. As a result, we were only able to induce transgene expression for 24 hours before lethality occurred.

At this early point, no detectable changes in mitochondrial morphology were observed in the peripodial membrane, likely because the duration of transgene expression was insufficient to elicit phenotypic alterations in this specific tissue. Therefore, while we aimed to compare this genotype to Gug>dMfn and Gug>miro, the technical limitations prevented a conclusive analysis.

We have prepared a representative figure for the reviewer (below), showing representative confocal images of wing discs showing mito-GFP and Dapi in the three genotypes indicated in the Fig.

In Fig. 3I: what is really the mitochondrion? It would be good to outline the region(s) that was/were measured.

To improve clarity, we have repeated the electron microscopy (EM) analysis and now provide representative images that more clearly illustrate mitochondrial morphology in the different genotypes analyzed. These updated images presented in Fig 4 better highlight the structural alterations observed upon genetic manipulation and help clarify the basis for our morphological assessments.

We have extended our analysis and have assessed mitochondrial ultrastructure in Yki + dPGC1-RNAi wing disc tumors, with and without dMfn1 downregulation—the most upregulated mitochondrial fusion gene in this tumor context. In Yki + dPGC1-RNAi tumors, mitochondria appeared more elongated, consistent with increased fusion. Upon dMfn1 depletion, we observed a dramatic shift in mitochondrial morphology: mitochondria became larger and more rounded, with disrupted cristae and onion-like structures, indicative of compromised mitochondrial integrity and function (see new Fig 4).

A quantification of RNAi and overexpression efficiencies of the different transgenes in Fig. 3 is required.

To assess the efficiency of RNAi-mediated knockdown and transgene overexpression, we performed quantitative PCR (qPCR) using the ubiquitous Actin-Gal4 driver. While we acknowledge that this driver does not replicate the spatial specificity of the periodic membrane Gal4 driver used in the experiments shown in Figure 3 (Gug-Gal4), the latter targets a very limited number of cells within the imaginal disc, making reliable qPCR quantification unfeasible.

Using Actin-Gal4 allows us to obtain a relative and informative measure of transgene efficiency across the different constructs. These data confirm effective knockdown and overexpression of the relevant genes and are now included in Figure S2.

In Fig. 4: what is the phenotype when miro is over-expressed in combination with Yki? Or when it is knocked down in the ap>Yki-dPGC1 background? This was the gene tested in Fig. 3 with a clear mitochondrial phenotype

To address whether miro contributes to Yki-mediated tumor growth, we performed the requested experiments and now include the results in the revised manuscript (see updated Results section, lines 374-377, and new Fig. S11).

Our data show that overexpression of miro in combination with Yki does not lead to a significant increase in tissue growth or tumor-like phenotypes, in contrast to the effects observed with dMfn or Opa1 overexpression. Similarly, knockdown of miro in the ap>Yki-dPGC1-RNAi background did not suppress tumor growth, indicating that miro is not required for the enhanced proliferation observed in this context.

These findings suggest that, although miro influences mitochondrial morphology in normal wing discs (as shown in Fig. 3), its role in tumorigenesis is distinct from that of dMfn and Opa1. We have revised the manuscript to clarify the gene-specific contributions of mitochondrial fusion regulators to Yki-driven tumorigenesis. This distinction underscores the complexity of mitochondrial dynamics and highlights that not all fusion-related genes exert the same functional impact in oncogenic settings.

How does the mitochondrial morphology in the wing disc peripodial epithelium look like in Gug>Opa1RNAi or Gug>Opa1 discs?

To assess the impact of Opa1 on mitochondrial morphology in the peripodial epithelium of the wing disc, we used the Gug-GAL4 driver to either overexpress or knock down Opa1. Our analysis revealed that Opa1 overexpression led to slightly elongated mitochondria, but did not result in extensive network formation, suggesting a modest enhancement of inner membrane fusion. In contrast, Opa1 knockdown caused clear mitochondrial fragmentation, closely resembling the phenotype observed upon dMfn depletion. These results shown in Fig 3 are consistent with the distinct roles of Opa1 and dMfn in regulating mitochondrial fusion: Opa1 primarily modulates inner membrane fusion and cristae architecture, while dMfn drives outer membrane fusion and network connectivity.

The corresponding data are presented in Figure 3F, G, and quantified in Figure S9, alongside experiments manipulating other genes involved in mitochondrial dynamics.

Why have the authors switched between the ap>Yki+dPGCRNAi and the ap>Yki+dPGC1shRNA lines? It would be important to have this series of experiments in the same backgrounds, as KD efficiencies are different (Fig. S1C).

The primary reason for switching between the dPGC1-RNAi and dPGC1-shRNA lines was practical: the chromosomal insertion sites of the transgenes made certain genetic combinations more feasible with one line over the other. This flexibility significantly facilitated our experimental design and analysis.

To address concerns regarding knockdown efficiency, we performed a comparative analysis using the ubiquitous actin-GAL4 driver, rather than MS1096-GAL4, which exhibits patchy and dynamic expression in the wing imaginal disc. This allowed us to obtain a more consistent and interpretable measure of mRNA downregulation for both transgenes. Our results show that both lines achieve comparable levels of knockdown, as shown in Figure S2.

Fig. 5A: proper quantification of Western Blot signals is required. I do not agree that Cyclin E protein levels are elevated in ap>Yki or ap>Yki+dPGC1 discs. Even at the mRNA levels the increase in expression is rather weak. From these results nothing can be concluded.

We have repeated the Western blot analysis using seven independent membranes to ensure robust quantification of Cyclin E levels in ap>Yki and ap>Yki+dPGC1-RNAi wing discs (Fig 6).

Although the increase in Cyclin E protein levels is subtle, it is consistent across replicates and statistically significant. We have now included the quantification of these Western blot signals in the revised Figure 6, which supports the conclusion that Cyclin E levels are elevated in ap>Yki+dPGC1 discs.

We hope this additional data addresses the reviewer’s concern and strengthens the interpretation of our results.

Knock-down efficiencies for dap and CycE needs to be quantifiec (Fig. 5H-N). Although the rescue experiment with CycE knock down is from the phenotype convincing, it is nonetheless puzzling, as CycE is accodring to Fig. 5A+B hardly upregulated. An independent CycE RNAi line would be useful.

We have quantified the knockdown efficiency of the dap-RNAi line, and the results are included in Figure S13.

Regarding Cyclin E, we would like to clarify that we did not use an RNAi line in this experiment. Instead, we employed the CycE-05306 mutant allele in a heterozygous background, which is expected to reduce Cyclin E levels by approximately 50%. The CycE-05306 allele in Drosophila melanogaster is a loss-of-function allele of the Cyclin E gene. This allele carries a P-element insertion in the first intron of the CycE gene, which disrupts normal transcription and reduces Cyclin E expression. In a heterozygous background, as used in your experiments, CycE-05306/+ is expected to reduce Cyclin E levels by approximately 50%, which is typically sufficient to observe genetic interactions or sensitized phenotypes without affecting normal development. This makes it a valuable tool for studying gene dosage effects, particularly in tumor models where Cyclin E activity may be rate-limiting.

Importantly, this partial reduction does not impair normal tissue growth, but it strongly limits tumor growth in the context of Yki overexpression combined with dPGC1 downregulation, as shown in Figure 6. This selective sensitivity highlights the functional importance of Cyclin E in supporting oncogenic growth driven by Yki and dPGC1 depletion. We believe this provides compelling evidence for Cyclin E’s role in this tumor model.

Reviewer #3 (Significance (Required)):

Strengths and Limitations of the Study Strengths Innovative Focus on Mitochondrial Dynamics and Oncogenesis: The study provides compelling evidence linking mitochondrial dynamics, particularly hyperfusion, to tumorigenesis in Drosophila. The identification of dPGC1 as a context-dependent tumor suppressor adds novel insights into the interplay between metabolism and oncogenesis. Comprehensive Use of Drosophila as a Model System: The study leverages the genetic tractability of Drosophila, allowing precise manipulation of mitochondrial regulators and signaling pathways. The use of wing imaginal discs as a model for tumor growth is well-established and appropriate. Integration of Morphological and Genetic Data: The manuscript combines confocal imaging, electron microscopy, and genetic tools to demonstrate the role of dPGC1 in regulating mitochondrial dynamics, Cyclin E levels, and tissue overgrowth. Relevance to Cancer Biology: The findings address key hallmarks of cancer, including deregulated metabolism, genomic instability, and cell cycle misregulation. The study's exploration of these processes in a simple model organism provides a strong basis for translating findings to mammalian systems.

Limitations Validation of RNAi and Overexpression Efficiency: The knockdown efficiency of dPGC1 on the mRNA level is only moderate (30-50%), and protein-level validation is missing. Without this, the study cannot conclusively demonstrate the role of dPGC1 in normal development or tumorigenesis. Incomplete Mechanistic Insights: The manuscript identifies Cyclin E as a potential driver of tumor growth but does not adequately explore how mitochondrial hyperfusion leads to Cyclin E regulation (e.g., post-transcriptional mechanisms or protein stability). Inconsistencies in Experimental Backgrounds: The study uses different RNAi/shRNA lines and driver combinations inconsistently across experiments, making it difficult to compare results directly. This variability undermines the robustness of the conclusions. Limited Functional Analysis of Mitochondria: While mitochondrial morphology is well-characterized, functional assays (e.g., membrane potential or ATP production) are missing. These would confirm the impact of hyperfusion on cellular energetics and oncogenesis.

In the revised manuscript, we have addressed each of the concerns raised.

In addition to that, in the revised version of the manuscript, we have included new experiments to assess mitochondrial functionality in tumors co-expressing Yki and dPGC1-RNAi. Specifically, we analyzed the Mitochondrial Membrane Potential (MMP). We used TMRE staining to evaluate MMP, a key indicator of mitochondrial integrity and oxidative phosphorylation capacity. Our analysis revealed no significant differences in MMP between Yki tumors and Yki + dPGC1-RNAi tumors, suggesting that mitochondrial membrane potential is preserved despite the observed morphological abnormalities. These results are shown in Fig S6. In the text it is discussed in lines 233-243.

Contribution to Existing Literature The study makes a significant contribution to the growing body of literature on the metabolic regulation of cancer by identifying dPGC1 as a tumor suppressor modulating mitochondrial dynamics. Previous work has established the dual roles of mammalian PGC1α in promoting or suppressing cancer depending on context. This study adds depth by demonstrating similar context-dependent effects in a simpler model organism, facilitating further exploration of the molecular mechanisms involved.

By linking mitochondrial fusion, Yki signaling, and Cyclin E regulation, the manuscript aligns with and expands upon research on Hippo pathway regulation, cancer metabolism, and mitochondrial biology. The findings highlight the importance of integrating metabolic and signaling networks in understanding oncogenesis.

Community Selection The current form of the manuscript is best suited for a specialized audience, particularly mitochondrial biologists, Drosophila researchers, and Hippo pathway specialists. To engage a broader community, additional work linking these findings to mammalian models or human cancer biology would be necessary.

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Referee #3

Evidence, reproducibility and clarity

The manuscript presents compelling evidence that dPGC1 acts as a context-dependent tumor suppressor in Drosophila by modulating mitochondrial dynamics and limiting Yorkie (Yki)-induced oncogenic growth. By leveraging the Drosophila wing imaginal disc as a model, the authors investigate how dPGC1 depletion exacerbates Yki-driven tissue overgrowth, mitochondrial hyperfusion, Cyclin E upregulation, and DNA damage, leading to tumorigenesis. The study provides valuable insights into the interplay between mitochondrial dynamics and cancer, with implications for understanding metabolic regulation in oncogenesis. While the findings are significant and well-aligned with the field, certain aspects of the experimental design, data presentation, and mechanistic insights require further attention to enhance clarity, reproducibility, and impact. Below, I outline my major concerns and recommendations.

Major Points

1. One point is the knock-down efficiency of dPGC1 on the mRNA level, which is between 30 to >50% (Fig. S1C). This is not too strong, so the question arises how severly the protein levels are affected. If possible, an antibody staining with quantification should be performed. From these data it cannot be concluded dPGC1 is not required for normal development, half the dose could be sufficient. How do wings look like when the ap-GAL4 driver is used for dPGC1 knock-down, as this is the driver used in the subsequent experiments?
2. How does the wing disc look like when dPGC1 is overepressed together with Yki?
3. In Fig 2D (but also in Fig. 2C) not only cells in the dorsal but also in the ventral comparmtent seem to overproliferate. Either this is a mis-conception or it is a non-autonomous effect from interfering with Yki and dPGC1 in the vertrnal compartment. In either cases, this has to be clarified.
4. In Fig. 2F-H quantification of Mmp1 and F-actin is missing. Mmp1 is a JNK target, so the authors could do in addition an anti-phospho JNK antibody staining.
5. In Fig. 3: how does the mitochondrial network look like in the wing disc periopodial epithelium using the Gug>Yki+dPGC1 genotype? Is it similar to Gug>dMfn or Gug>miro?
6. In Fig. 3I: what is really the mitochondrion? It would be good to outline the region(s) that was/were measured.
7. A quantification of RNAi and overexpression efficiencies of the different transgenes in Fig. 3 is required.
8. In Fig. 4: what is the phenotype when miro is over-expressed in combination with Yki? Or when it is knocked down in the ap>Yki-dPGC1 background? This was the gene tested in Fig. 3 with a clear mitochondrial phenotype. How does the mitochondrial morphology in the wing disc peripodial epithelium look like in Gug>Opa1RNAi or Gug>Opa1 discs? Why have the authors switched between the ap>Yki+dPGCRNAi and the ap>Yki+dPGC1shRNA lines? It would be important to have this series of experiments in the same backgrounds, as KD efficiencies are different (Fig. S1C).
9. Fig. 5A: proper quantification of Western Blot signals is required. I do not agree that Cyclin E protein levels are elevated in ap>Yki or ap>Yki+dPGC1 discs. Even at the mRNA levels the increase in expression is rather weak. From these results nothing can be concluded.
10. Knock-down efficincies for dap and CycE needs to be quantifiec (Fig. 5H-N). Although the rescue experiment with CycE knock down is from the phenotype convincing, it is nonetheless puzzling, as CycE is accodring to Fig. 5A+B hardly upregulated. An independent CycE RNAi line would be useful.

Significance

Strengths and Limitations of the Study

Strengths

Innovative Focus on Mitochondrial Dynamics and Oncogenesis: The study provides compelling evidence linking mitochondrial dynamics, particularly hyperfusion, to tumorigenesis in Drosophila. The identification of dPGC1 as a context-dependent tumor suppressor adds novel insights into the interplay between metabolism and oncogenesis. Comprehensive Use of Drosophila as a Model System: The study leverages the genetic tractability of Drosophila, allowing precise manipulation of mitochondrial regulators and signaling pathways. The use of wing imaginal discs as a model for tumor growth is well-established and appropriate. Integration of Morphological and Genetic Data: The manuscript combines confocal imaging, electron microscopy, and genetic tools to demonstrate the role of dPGC1 in regulating mitochondrial dynamics, Cyclin E levels, and tissue overgrowth. Relevance to Cancer Biology: The findings address key hallmarks of cancer, including deregulated metabolism, genomic instability, and cell cycle misregulation. The study's exploration of these processes in a simple model organism provides a strong basis for translating findings to mammalian systems.

Limitations

Validation of RNAi and Overexpression Efficiency: The knockdown efficiency of dPGC1 on the mRNA level is only moderate (30-50%), and protein-level validation is missing. Without this, the study cannot conclusively demonstrate the role of dPGC1 in normal development or tumorigenesis. Incomplete Mechanistic Insights: The manuscript identifies Cyclin E as a potential driver of tumor growth but does not adequately explore how mitochondrial hyperfusion leads to Cyclin E regulation (e.g., post-transcriptional mechanisms or protein stability). Inconsistencies in Experimental Backgrounds: The study uses different RNAi/shRNA lines and driver combinations inconsistently across experiments, making it difficult to compare results directly. This variability undermines the robustness of the conclusions. Limited Functional Analysis of Mitochondria: While mitochondrial morphology is well-characterized, functional assays (e.g., membrane potential or ATP production) are missing. These would confirm the impact of hyperfusion on cellular energetics and oncogenesis.

Contribution to Existing Literature

The study makes a significant contribution to the growing body of literature on the metabolic regulation of cancer by identifying dPGC1 as a tumor suppressor modulating mitochondrial dynamics. Previous work has established the dual roles of mammalian PGC1α in promoting or suppressing cancer depending on context. This study adds depth by demonstrating similar context-dependent effects in a simpler model organism, facilitating further exploration of the molecular mechanisms involved.

By linking mitochondrial fusion, Yki signaling, and Cyclin E regulation, the manuscript aligns with and expands upon research on Hippo pathway regulation, cancer metabolism, and mitochondrial biology. The findings highlight the importance of integrating metabolic and signaling networks in understanding oncogenesis.

Community Selection

The current form of the manuscript is best suited for a specialized audience, particularly mitochondrial biologists, Drosophila researchers, and Hippo pathway specialists. To engage a broader community, additional work linking these findings to mammalian models or human cancer biology would be necessary.

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

In this manuscript the authors the investigate the role of the mitochondrial regulatory transcription factor dPGC1 in tissue growth and oncogenic transformation. They show that dPGC1 limits hyperplasia mediated by overexpression of Yki in the Drosophila wing disc, while having no effect on normal growth. dPGC1 depletion in discs overexpressing Yki results neoplastic overgrowth and hyperfused mitochondria, which was dependent on the increased expression of genes involved in promoting mitochondrial fusion. Additionally, the authors show that dPGC1 limits CycE levels post-transcriptionally in Yki tumors.

Major comments

1. The authors mention several times in passing in the results a manuscript from the Banerjee lab (Nagaraj et al 2012), which shows that many of the genes the authors of the present manuscript show are upregulated upon Yki overexpression + dPGC1-RNAi compared with Yki overexpression alone are in fact upregulated upon Yki overexpression alone compared with control (dMfn/marf, opa1, miro - while interestingly dPGC1 itself is not affected). Nagaraj et al further show that Yki-overexpressing discs have longer mitochondria suggesting increased fusion even in the absence of dPGC1 depletion. The findings from Nagaraj et al should be mentioned explicitly in the introduction and the relationship between this manuscript and the present work clearly outlined in the discussion.
2. Given that Yki overexpression alone induces mitochondrial fusion and that dMfn/marf and opa1 depletion suppresses Yki-induced overgrowth (Nagaraj et al), does dPGC1 overexpression also suppress Yki-induced overgrowth? If so, is this correlated with reduction in dMfn/marf and opa1 compared with Yki overexpression alone?
3. One important question raised by this study is: how specific is the effect of dPGC1 depletion to Yki-driven overgrowth? As Yki-driven overgrowth already have increased mitochondrial length, it is possible that Yki-expressing cells are already sensitised to the effects of dPGC1 depletion. Interestingly, Nagaraj et al show that mitochondrial morphology is not affected upon EGFR activation (hyperplasia) or upon scrib and avl depletion (neoplasia). The authors should therefore test if dPGC1 depletion can potentiate the growth of other hyperplasia drivers such as activated EGFR and InR in the wing disc.
4. There are a few simple control experiments the authors should provide to clarify the relationship between Yki and dPGC1:
   • Are Yki levels affected by dPGC1 depletion?
   • Does dPGC1 knockdown alone modify the expression of the genes tested in Fig.3A? In other words, is this upregulation specific of the Yki-overexpression context?
   • Does dPCG1 knockdown also stabilise CycE in the absence of Yki overexpression or does the stabilisation of CycE occur only in Yki tumors?
5. Figure 3C-G: it is not clear how the authors can quantify the length of 3D structures like mitochondria from 2D TEM images (unless they have done volume reconstruction from consecutive sections) and no details are provided in the methods. The quantification of mitochondrial length has to be performed rigorously as it is a key part of the paper.

Minor Comments:

1. Line 51: "Mitochondria are highly dynamics organelles." should be "Mitochondria are highly dynamic organelles."
2. Introduction: the authors should summarise the known physiological functions of PGC1α in order to put their findings in context.
3. lines: 121-3: "...depletion of dPGC1...did not have a major impact on adult wing size and shape (Fig 1B, C)." There is a small but statistically significant difference so the authors should state this in the text.
4. Figure 5A (Cyclin E western blot): the authors should show molecular weight markers.

Significance

The manuscript by Sew et al builds on the previous work by Nagaraj et al to explore the role of mitochondrial function in tumors driven by disruption of the Hippo pathway. In particular, the authors identify dPGC1 as a transcription factor that limits Yki-driven mitochondrial fusion and tissue growth. Interestingly, they further show that Yki/PGC1-depleted tumors are highly sensitive to Cyclin E levels, due to post-transcriptional Cyclin E increase. These results further our knowledge of how Yki drives growth and how mitochondria participate in oncogenic transformation. With appropriate revision as outlined above (for example exploring whether the mechanism proposed is Yki-specific), the manuscript will be of broad interest to developmental and cancer biologists.

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Referee #1

Evidence, reproducibility and clarity

Sew et al. examine the master regulator of mitochondrial biogenesis, dPGC1, in the context of Drosophila wing and larval development. They primarily use confocal imaging to probe the interplay between dPGC1 and an overactive Hippo pathway, driven by overexpression of the main effector protein, Yki. In their study, they find that tumors, driven by overactivity of Yki grow larger when dPGC1 is downregulated, implicating the mitochondrial biogenesis pathway in tumor suppression. Furthermore, in the context of Yki overexpression, they find that levels of Mfn or Opa1 modulate tumor size. Lastly, they show a role of cyclin E in controlling the size of tumors formed by Yki OE + dPGC1 RNAi. The potential role of dPGC1 as a tumor suppressor is interesting because it highlights an emerging recognition of mitochondria in the aetiology of cancer. However, before publication, much of the data in this manuscript should be strengthened by a refinement in the methods/analysis and an increase in orthogonal approaches.

Major comments:

The authors indicate that for example, in lines127-28, that neither downregulating or overexpressing dPGC1 affects wing size. However, the quantification in Fig. 1C shows a significant decrease in wing size following RNAi treatment. This decrease is modest, but it is nevertheless significant. It is worth pointing out, too, that the efficiency of the RNAi in Fig. S1C suggests that the conclusions drawn are premature. While a roughly 55% drop in mRNA levels may be statistically significant, it is unclear whether this drop in transcripts corresponds to a commensurate depletion of protein. Moreover, it is unclear, in this context, how much dPGC1 may indeed be necessary to drive a relatively normal program of mitochondrial biogenesis in wing development. To obtain a clear result, it is necessary to show significant depletion of the dPGC1 protein. (Ultimately, if it is the case that dPGC1 is unnecessary for wing development and function, a more coherent line of inquiry would be to find out the reason for this rather than to pivot the story to studying tumorigenesis in larva.)

In Figure 3H-K, it is not clear why the authors used electron microscopy to evaluate mitochondrial morphology. The very good confocal images in Figure 3C-G show a clear change in mitochondrial morphology following the knockdown of Mfn, Opa1, and Miro. While it is clear from the electron micrographs in Figure H that the mitochondria are enlarged, it is not obvious that this increase in length is a result of increased mitochondrial fusion. Indeed, if the mean form factor were used to quantify the shape, it is likely that in both conditions, the value would be close to 1, indicating more of a round object, and it not obvious whether there would be a difference between the Yki OE versus the YkI OE + dPGC1 RNAi. Therefore, from this data alone, it cannot be concluded that the YkI OE + dPGC1 RNAi condition leads to mitochondrial hyperfusion.

Figure 4. refers to changes in mitochondrial fusion and fission in tumor formation; however, the authors do not attempt to alter mitochondrial fission factors, so it is not accurate to mention a role of mitochondrial fission, in this context. It must be noted, too, that the authors have not demonstrated that their genetic interventions have actually affected mitochondrial morphology in these experiments. As noted in the previous figure, the Yki OE + dPGC1 RNAi condition showed enlarged mitochondria, but not necessarily hyperfused organelles. Therefore, the downregulation of Mfn or Opa1 in this set of experiments may not necessarily have altered mitochondrial morphology. Perhaps suppression of Mfn or Opa1 would normalize the areas of these evidently swollen mitochondria, but this is unclear without images. Furthermore, it should be appreciated that both Opa1 and Mfn exhibit pleiotropic attributes - e.g., Opa1 not only regulates IMM fusion, but it also modulates the shape and tightness of cristae membranes, specialized sites of oxidative phosphorylation as well as sequestration of cytochrome c, the release of which influences apoptosis (Frezza et al., 2006). At least in mammalian cells, Mfn2 is thought to regulate contacts between mitochondria and endoplasmic reticulum (Naon et al., 2023), which may serve other functions than OMM fusion, such as stabilization of the MAM.

Figure 5 highlights a connection between dysregulation of mitochondria and Cyclin E, which allows cells to prematurely enter S phase. The data presented here do not offer clarity on whether the enlargement of the tumors results from increase cellular proliferation and/or cell size. The role of the cell cycle adds a layer of complexity to these results, because it is thought that mitochondria undergo fragmentation during the cell cycle to promote an even distribution of the organelle population after mitosis (Taguchi et al., 2007); however, in this manuscript, the authors contend that the downregulation dPGC1 is promoting mitochondrial hyperfusion. It is unclear how and whether cellular division and proliferation would proceed at an accelerated rate in a situation with mitochondrial hyperfusion.

Minor comments:

Lines 69-72 contrast the roles of PGC1α and β. It is not clear whether the comparison is of their respective roles in cancer or in normal physiology. In either case, it is important to note that PGC1β has been shown to drive mitochondrial fusion as well as biogenesis through its control of MFN2, among other factors (Liesa et al., 2008).

Although this study focuses on PGC1, the authors do not seem to site the original literature from the Spiegelman lab.

There are 10-20 grammatical errors throughout the text.

Referee Cross-commenting

There is agreement among the referees that the potential role of PGC1 as a tumor suppressor is interesting and significant. However, various aspects of this work require attention prior to publication. For example, there needs to be a complete knock down of PGC1 to come to any conclusion as to its role in wing development. The methods for analyzing mitochondrial morphology need to be clarified and be consistent with standards in the field of mitochondrial dynamics. Also, the authors need to quantify their Western blots to obtain accurate assessments of protein levels. Generally, the study relies too heavily on overexpression experiments; understanding the potential role of mitochondria in regulating the Hippo pathway should include various knockdown and/or knockout models.

Significance

Overall, the authors show an interesting dampening effect of dPGC1 on growth of Yki-driven tumors. This data could be relevant for elucidating how dysregulation of the Hippo signalling pathway can underlie tumorigenesis.

The narrative arc of the study, however, appears to lack a focused line of inquiry. Figure 1 highlights an attempt to modulate Drosophila wing size and/or structure by downregulating dPGC1, but to no effect. Although examination of the efficiency of the RNAi revealed that the transcripts were still present in significant quantities; so, the conclusion that dPGC1 is dispensable for wing formation is premature. To have clarity on this point, it would be necessary to completely knockdown the gene, preferably by showing a total loss of protein. This should be feasible for the authors, since they showed Western blotting in Figure 5A. In any event, it seems that this negative data led the authors to study the Hippo pathway in the larval stage. This transition from Figure 1 to 2 seemed somewhat arbitrary and leads to a rather disjointed sense of the main line of inquiry around dPGC1.

It is important to note, too, that the authors highlight a role of mitochondrial dynamics in the pathway of Yki-driven tumor formation; however, they only directly evaluate mitochondrial dynamics in this context in a single assay, namely, Figure 3H-K, and this quantification is likely inaccurate because the mitochondria in the Yki OE + dPGC1 RNAi condition seem to be substantially enlarged, circular structures. It is critical to keep in mind that mitochondrial enlargement does not necessarily stem from hyperfusion. It could come from a decrease in the activity of Drp1 or result from an imbalance between mitochondrial biogenesis and mitophagy.

A marked limitation of this study is the overuse of rather artificial manipulations of transcriptional regulatory pathways. The study would benefit a lot from investigation of the loss of function of components of the Hippo pathway rather than just OE of Yki.

My expertise is in mitochondrial biology, with specialization in super-resolution imaging, mitochondrial dynamics and membrane architecture. I have also worked in the interface between mitochondrial physiology and cancer. With this perspective, I think that the authors uncover a potentially interesting role of PGC1 as a tumor suppressor.

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Reply to the reviewers

Manuscript number: RC- 2025-03073

Corresponding author(s): Shaul Yogev

1. General Statements [optional]

We kindly thank our reviewers for their enthusiasm, thoughtful feedback, and constructive suggestions on how to strengthen our manuscript. Below, we provide a point-by-point response to reviewer comments and outline the experiments we will do to address every concern that has been raised.

2. Description of the planned revisions

• *

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

This interesting study uses an unbiased genetic screen in C. elegans to identify SAX-1/NDR kinase as a regulator of dendritic branch elimination. Loss of SAX-1 results in an excess branching phenotype that is striking and highly penetrant. The authors identify several additional regulators of branch elimination (SAX-2, MOB-1, RABI-1, RAB-11.2) by using a candidate genetic screen aimed at factors that interact physically or genetically with SAX-1. They propose that SAX-1 acts by promoting membrane retrieval based on the nature of these interactors and the results of an imaging-based in vivo assay for endocytic puncta.

Major comments.

1. My biggest concern is that the phenotypes are only observed in temperature-sensitive dauer-constitutive mutant backgrounds, and not in wild-type dauers. That is, wild-type animals exiting dauer do not require SAX-1 for dendrite elimination. While this does not undermine the importance of the results, it does require more explanation. The authors write that "the requirement for sax-1... relies on specific physiological states of the dauer stage," but I do not understand what this means. Are they saying that daf-7 and daf-2 dauers are in a different "physiological state" than wild-type dauers? In what way? What is the evidence for this? A more rigorous explanation is needed. We agree that this is puzzling, and we thank the reviewer for recognizing that this does not undermine the importance of the results. There is ample evidence that daf-2 and daf-7 differ from starvation-induced dauers. For example, a recent preprint finds that the transcriptomes of these two mutants at dauer cluster much closer to each other than to starvation-induced dauers (Corchado et al. 2024). Older work has noted other differences, such as the time the dauer entry decision is made (Swanson and Riddle 1981), the synchronicity of dauer exit, the ability to force dauer entry in daf-d mutants, as well as additional dauer-unrelated phenotypes (reviewed in Karp 2018). We agree with the reviewer that this merits further clarifications and will perform the experiments suggested by the reviewer below:

To me, the simplest genetic explanation is that daf-7 and daf-2 are partially required for branch retraction in a manner redundant with sax-1, and the ts mutants are not fully wild-type at 15C. Thus, the sax-1 requirement is revealed only in these mutant backgrounds. Can the authors examine starvation-induced dauers of daf-7 or daf-2 raised continuously at 15C?

We will do this experiment.

daf-7 and daf-2 ts strains can form "partial dauers" that have a dauer-like appearance but are not SDS resistant. Could the difference between partial dauers and full dauers account for the difference in sax-1-dependence? The authors could use SDS selection of the daf-7 strain at 25C to ensure they are examining full dauers.

We tested daf-7 mutants with 1% SDS when we set up the system – they are fully dauer at 25°C and are SDS sensitive after exit. We will repeat this important control with daf-7; sax-1 double mutants.

The Bargmann lab has created a daf-2 FLP-OUT strain (ky1095ky1087) that allows cell-type-specific removal of daf-2. Could this be used to test for a cell-autonomous role of daf-2 in IL2Q related to branch elimination?

We can attempt this experiment. However, since IL2 promoters turn on prior to dauer, the interpretation would not be straightforward – it would be hard to exclude that a cell autonomous defect in dauer entry does not account for the IL2 dauer exit phenotype, even if branching appears normal.

These ideas are not a list of specific experiments the authors need to complete, rather they are meant to illustrate some possible approaches to the question. Whatever approach they use, it is important for them to more rigorously explain why SAX-1 is not required for branch removal in wild-type animals.

We completely agree. We will carry out the 15°C experiment, examine morphological characteristics and test SDS resistance. In addition, we will test neuronal markers that differ between dauers and non-dauers to determine whether the mutants are full or partial dauers at the relevant timepoints.

The SAX-2 localization (Fig. 4) and endocytosis assay (Fig. 6) results were not clear to me from the data shown. Overall a more rigorous analysis and presentation of the data would be important to make these conclusions convincing. This may involve refining the data presentation in the figures, modifying the claims (e.g., "we propose" vs "we find"), or saving some of the data to be more fully explored in a future paper. In my view, these figures are the biggest weak point of the manuscript and also are not important for the central conclusions (which are well supported and convincing), indeed these results are barely mentioned in the Abstract or last paragraph of Introduction.

We agree that the analysis and presentation of Figures 4 and 6 need to be improved. The presentation has already been updated, and the figures are clearer now. In the revision, we will increase sample size to provide stronger conclusions, consolidate some of the analysis and further improve presentation. While we agree with the reviewer that conclusions from these figures are not as strong as those drawn from genetic experiments, they do complement and support the conclusions of those other figures.

• In Fig. 4D, why is SAX-2 visible throughout the entire neuron and why is the "punctum" marked with an arrow also seen in the tagRFP channel? One gets the impression that some of the puncta may be background, bleed-through, or artifacts due to cell varicosities.

There is no bleed-through: this is most evident by looking at the brightest signals in the cell body (now labelled with an asterisk in a zoomed-out image) and noting that they do not bleed between channels. In sax-1 mutants, the SAX-2::GFP puncta are very obvious and distinguishable from the tagRFP channel. In control, SAX-2::GFP is very faint in the dendrite, so we increased the contrast to allow visualization. The reviewer is correct that under these conditions, some puncta look like the cytosolic fill. In the revision, we will re-analyze the data and will not consider these as bona-fide SAX-2 puncta, but rather cytosolic SAX-2 that accumulates due to constrictions and varicosities in the dendrite.

• Related to both Fig. 4 and Fig. 6, where does SAX-1 localize in IL2Q in dauer and post-dauer? Does its expression or localization change during branch retraction? Does it co-localize with SAX-2 or endocytic puncta?

We generated an endogenously tagged sax-1 with a 7xspGFP11 tag; however, this was below detection in the IL2s. For the revisions, we can test an overexpressed cDNA construct.

**Referee cross-commenting**

I think we all touched on similar points. I wanted to follow up on Reviewer 3's comment, "Is the failure to eliminate branches an indication of incomplete dauer recovery? Do sax-1 mutants retain additional characteristics of dauer morphology in post dauer adults." I thought this was an excellent point. It made me wonder if that might explain why the defect is only seen in daf-7 and daf-2 mutant backgrounds - maybe these strains retain partial dauer traits even after exit. Is there a specific experiment that they could do? Did you have specific characteristics of dauer morphology in mind for them to check? (Ideally something in the nervous system that can be scored quantitatively.)

Please see response to point #1 regarding experiments we will do to confirm the “dauer state” of daf-7 and daf-7; sax-1 double mutants.

Reviewer #1 (Significance (Required)):

A major strength of this work is the pioneering use of a novel system to study neuronal branch retraction. C. elegans has provided a powerful model for studying how dendrite branches form, but much less attention has been paid to how excess neuronal branches are removed. The post-dauer remodeling of IL2Q neurons provides an exciting and dramatic physiological example to explore this question.

This paper is notable for taking the first steps towards developing this innovative model. It does exactly what is needed at the outset of a new exploration - a forward genetic screen to discover the main regulators of the process. Using a combination of classical and modern genetic approaches, the authors bootstrap their way to a sizeable list of factors and a solid understanding of the properties of this system, for example that retraction of higher vs lower order dendrites show different genetic requirements.

We thank the reviewer for recognizing the novelty and significance of our work.

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

In this manuscript, the authors establish C. elegans IL2 neurons as a system in which to study dendrite pruning. They use the system to perform a genetic screen for pruning regulators and find an allele of sax-1. Unexpectedly sax-1 is only required for post-dauer pruning in two different genetic backgrounds that induce dauer formation, but not starvation-induced dauer formation. Sax-1/NDR kinase reduction has previously been associated with increased outgrowth and branching in other systems, so this is a new role for this protein. However, the authors show that proteins that work with Sax-1 in other systems, like sax-2/fry, also play a role in this pathway. The genetic experiments are beautiful and the findings are all clearly explained and strongly supported. The authors also examine sax-2 localization, which localizes sax-1 in other systems, and show it in puncta in dendrites that increase with dauer exit, consistent with function at the time of pruning. They also show that membrane trafficking regulators associated with NDR kinases function in the same pathway here, hinting that endocytosis may play a role during pruning as in Drosophila. The link to endocytosis was a little weak (see Major point below). Overall, this study describes a new system to study pruning and identifies NDR/fry/Rabs as regulators of pruning during dauer exit. The work is very high quality and both the imaging and genetics are extremely well done.

We thank the reviewer for their positive assessment of the manuscript.

Major points

1. The only place where there were any questions about the data was the last figure (6G and I). Here they use uptake of GFP secreted from muscle as a readout of endocytosis in IL2 neurons. They nicely show that more internalized puncta accumulate as animals exit dauer. The claim that this is reduced in sax-1 mutants doesn't seem to match the images shown well. In the image there are many more puncta in the GFP channel and much more accumulation of the RFP-tagged receptor everywhere. It seems like some additional analysis of this data is important to fully capture what is going on and whether this really represents an endocytic defect. We agree and will provide additional data in Figure 6. The specific discrepancy between the image and the quantification is because we showed a single focal plane rather than a projection. This does not capture all the puncta in a neurite. The current version shows a projection, making it evident that the mutants has fewer puncta compared to the control.

Reviewer #2 (Significance (Required)):

Neurite pruning is important in all animals with neurons. Genetic approaches have primarily been applied to the problem using Drosophila, so identifying a new model system in which to study it is an important step. Using this system, a pathway known to function in a different context is linked to pruning. Thus the study provides new insights into both pruning and this pathway.

We thank the reviewer for the positive assessment of our study’s significance.

__Reviewer #3 (Evidence, reproducibility and clarity (Required)): __

Summary: Figueroa-Delgado et al. use a C. elegans neuro plasticity model to examine how dendrites are eliminated upon recovery from the stress induced larval stage, dauer. The authors performed a mutagenesis screen to identify novel regulators of dendrite elimination and revealed some surprising results. Branch elimination mechanism varies between 2{degree sign}, 3{degree sign}, and 4{degree sign} branches. The NDR kinase, SAX-1 and it's interactors (SAX-2 and MOB-2) are required for elimination of second and third order branches but not fourth order branches. Interestingly they showed that branch elimination varies depending on the stimulus of dendrite outgrowth such that the NDR kinase is required for branch elimination after genetically inducing the dauer stage but is not required if dauers are produced through food deprivation. The authors go a step further to include a small candidate screen looking at various pathways of membrane remodeling and identify additional regulators of dendrite elimination related to membrane trafficking including RABI-1, RAB-8, RAB-10, and RAB-11.2.

We thank the reviewer for their time and suggestions below

Major comments:

• While I find the data promising and exciting, several of the experiments have concerningly low sample sizes. Fig 3G, Fig 4G, Fig 5J and L, and Fig 6I all contain data sets that are fewer than 10 animals. Sample sizes should be stated specifically in the figure legends for all data represented in the graphs. We thank the reviewer for finding the data exciting. We agree that the sample sizes in some panels is low and will increase it in the revised version. Sample sizes are now specifically listed in the figure legends.

• All statements based on data not shown should be amended to include the data as a supplemental figure or edited to omit the statement based on withheld data. We agree. Some “not shown” data are already added to the current version of the manuscript and the rest will be added to the fully revised version, or the statements will be omitted.

• Rescue experiments (Fig 2J) should demonstrate failure to rescue from neighboring tissue types (hypodermis and muscle) to conclude cell autonomous rescue rather than a broadly acting factor. Thank you for the suggestion. We will use a hypodermal promoter and a muscle promoter driving SAX-1 cDNA expression to strengthen the claim of cell autonomy.

• Fig 4 needs quantification of higher order branches and SAX-2 proximity to branch nodes as these are discussed in the text. We will add this quantification.

Minor comments:

• Fig 1C-F, It appears like the shy87 allele produces animals of significantly different body sizes. It would improve rigor to normalize the dendrite coverage to body size in the quantification. We do not see a biologically meaningful size difference between shy87 and control, it may be the specific image shown. We will confirm this by measuring animal size for the final revision.

• Is the failure to eliminate branches an indication of incomplete dauer recovery? Do sax-1 mutants retain additional characteristics of dauer morphology in post dauer adults. This important point was also raised by Reviewer 1. We will test SDS sensitivity, morphological markers, and molecular markers to determine the dauer “state” of the mutants used in this study. The results will be included in the final revision.

• The text references multiple transgenic lines tested in Fig 2I-J but only one line is shown. Additional lines were visually examined under a fluorescent compound microscope but not imaged or quantified. We will add this quantification to the final revision.

• Fig 4F, Additional timepoints would enhance the sax-1 localization result and might provide insight into mechanism of action for sax-1. We will add the localization in post-dauer adults.

• Fig 6I Control and sax-1(ky491) example images should be provided in the supplement. We will add these images to the final revision.

**Referee cross-commenting**

I agree that we shared many of the same concerns.

There are several general assays for dauer characteristics that could be used here to determine if the post-dauer animals retain other characteristics of the dauer stage in addition to IL2 branches (SDS resistance, alae remodeling, pharyngeal bulb morphology, nictation behavior). The nictation behavior has been connected very nicely with IL2 neurons (Junho Lee's group). Additionally, FLP dendrites occupy the same space as the IL2 branches and outgrowth in post-dauers occurs in coordination with IL2 branch elimination - this might be another optional experiment, to check if FLP growth is impeded by persistent IL2 branches. All of these could be quantified similar to how the authors have already established with their IL2 model (FLP dendrite branches) or with a binary statistic.

Please see responses to Reviewer 1 and 3 above for the list of experiments to determine whether the animals fail to completely enter or exit dauer.

Reviewer #3 (Significance (Required)):

SIGNIFICANCE ============ These results describe a new role for the NDR kinase complex in dendrite pruning that has clinical significance to our understanding of human brain development and human health concerns in which pruning is dysregulated, such as observed in the case of autism. The authors use an established neuro-plasticity, C. elegans model (Schroeder et al. 2013) which provides a tractable and reproduceable platform for discovering the mechanism of dendrite pruning. These results would influence future work in the fields of cell biology of the neuron and disease models of brain development.

My expertise is in the field of C. elegans neuroscience and stress biology and have sufficient expertise to evaluate all aspects of this work.

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

Reviewer #1

• In Fig. 4C, the distinction between puncta in the primary or higher-order dendrites is not clear to me, and several puncta that I would have scored as primary are marked as higher-order.

We apologize for a mistake in the arrowhead color and overall presentation of this figure. It has been fixed in the current version.

• Related to this, in Fig. 4B are the two arrows meant to be white as in the top panel, or yellow as in the bottom panel?

We thank Reviewer #1 for their observation, and we apologize for our oversight. We fixed this in the current version.

• In Fig. 4, where in the head are we looking? It would help to show a more low-magnification view of the entire cell.

We added zoomed-out images and indicated where the zoomed in insets are taken from. We thank the reviewer for helping us improve the clarity of the data.

• The main sax-1 phenotype is increased SAX-2 puncta in dauer, but the branch retraction defect is in post-dauers. How is this relevant to the phenotype?

This is a very good point. The increase in SAX-2 puncta in sax-1 mutants is stronger during dauer-exit than in dauer, consistent with this being the time when SAX-1 functions. We agree that some earlier activity of SAX-1 cannot be excluded, and we do not assume that the effect on SAX-2 completely accounts for the pruning defects. This is now acknowledged in the text. However, given that both proteins function together in pruning, and given that the effect is strongest during dauer exit, we do believe that this data is informative and worth showing.

• The number of SAX-2 puncta in sax-1 mutants decreases almost to normal in post dauers. Is there a correlation between the number of remaining branches and the number of SAX-2 puncta? That is, do the many wild-type animals with "excess" SAX-2 puncta also fail to retract branches?

There is no correlation. In other words, the number of SAX-2 puncta does not instruct the extent of pruning. Please note the quantifications underestimate the number of SAX-2 puncta in the mutants, since they were only done on the primary dendrite. This is necessary because the mutant and control have different arbor size, so only branch order that can be appropriately compared are primary dendrites.

• The control post-dauer data in Fig. 4F and 4H are identical (re-used data) but the corresponding control dauer data in Fig. 4F and 4G are different. What is going on here?

We thank the reviewer for raising this point and apologize for the oversight in data presentation. In the revised manuscript, we now show all control and experimental data integrated into a single graph, ensuring that each dataset is represented accurately to provide a comparison between dauer and post dauer recovery conditions.

• Why are sample sizes so small for both strains in Fig. 4G compared to Fig. 4F and 4H?

We sincerely apologize for this mistake, some of the data was erroneously grouped in the original submission. The revised version contains an updated number of neurons, presented on the same graph, and in the final revision we will further increase sample size. We apologize again for this error.

• In Fig. 6C, why are the tagRFP (blue) puncta larger than the neurite? Aren't these meant to represent vesicles inside the surrounding neurite? One gets the impression that this is bleed-through from the GFP channel.

Based on EM, both an endocytic punctum and the diameter of the neuron are smaller than a single pixel. The apparent difference in size in fluorescence microscopy is because the puncta are brighter (they contain more membrane) and thus appear larger. In the current version, the improved presentation of the figure contains zoomed out images that clearly show that there is no bleed-through.

• In Fig. 6E and 6F, why are there no tagRFP (blue) puncta? Is CD8 not endocytosed at all if it lacks the nanobody sequence? One would expect the tagRFP (blue) signal to be the same in both strains and simply to lack yellow if the nanobody is not present.

CD8 lacks clear endocytosis motifs, which is why it is advantageous for labelling neurites and testing endocytosis when paired with an endocytic signal (Lee and Luo 1999; Kozik et al. 2010). Conversely, extracellular GFP binding to a membrane GFP antibody can induce endocytosis (for example, see (Tang et al., 2020)), likely by inducing clustering, although we are not familiar with work that explored the mechanism. In the updated version we included a rare example of an mCD8 punctum.

• The authors report a decrease in endocytic events in sax-1, but qualitatively it looks like there are vastly more puncta inside the neuron in Fig. 6H than in 6G.

We apologize for the presentation in the original version of Figure 6. This impression was because we showed single focal planes that only captured some of the signal. In the revised version we show projections, which makes it evident that there are fewer endocytic events in the mutant.

• In Fig. 6E and 6H, why are there so many GFP (yellow) puncta outside the neuron? What are these structures and why are they absent in the strain with the nanobody?

These puncta are secreted or muscle-associated GFP that has not been internalized by IL2Q neurons. They are present in all strains in this figure, this can be clearly seen in the zoomed-out images that have been added to the updated figure.

• What is the large central blue structure in Fig. 6H - is this the soma? - and why are puncta in this region not counted?

This is indeed the soma. In the updated version this can be clearly seen in the zoom-out. The large puncta in the soma were not counted because they may arise from the fusion of an unknown number of smaller puncta, and their precise number cannot be determined at the resolution of fluorescence microscopy.

• minor: there is text reading "40-" in the bottom panel of Fig. 6H. It is visible when printed but not on screen - adjust levels in Photoshop to reveal it.

We thank the reviewer for catching this oversight, it is now fixed.

Minor points:

1. At several points the authors emphasize the relationship of neurite remodeling to stress, e.g. Abstract and Discussion: "we adapted C. elegans IL2 sensory dendrites as a model [of...] stress-mediated dendrite pruning". It seems unnecessary and potentially misleading to treat this as a neuronal stress response. First, it conflates organismal and cellular stress - there is no reason to think that IL2 neurons are under cellular stress in dauer. In fact parasitic nematodes go through dauer-like stages as part of healthy development and probably have similar remodeling of IL2. Second, dendrite pruning occurs during dauer exit, which is the opposite of a stress response - it reflects a return to favorable conditions. We agree. We modified the abstract and discussion to avoid conflating organismal stress (the alleviation of which is relevant for triggering pruning) and cellular stress. Thank you for pointing this out.

In Fig. 1A, C. elegans is shown going directly from L1 to dauer in response to unfavorable conditions, which is incorrect. Animals proceed through L2 (in many cases actually an alternative L2d pre-dauer) and then molt into dauer (an alternative L3 stage) after completing L2.

We updated the schematic to include the L2d stage where commitment to dauer entry or resumption to reproductive development is made.

In Fig. 1B, please check if it is correct that hypodermis contacts the pharynx basement membrane as drawn. The schematic in the top panel makes it look like there is a single secondary branch and the quaternary branches are similar in length to the primary dendrite. The schematic in the bottom panel makes it look like the entire neuron is a small fraction of the length of the pharynx. Could these be drawn closer to scale?

The hypodermis does contact the pharynx basement membrane. We redrew the schematic for clarity.

Reviewer #2

For context, it might be helpful to know whether branching of other dendrites is increased in sax-1 mutants (as expected based on phenotypes in other animals) or decreased like IL2 neurons.

We examined the branching pattern of PVD, a polymodal nociceptive neuron (new Supplemental Figure 3). We find no significant difference between control and sax-1 or sax-2 mutants, suggesting that these genes function in the context of pruning. Recent work (Zhao et al. 2022) confirms that sax-1 is not required for PVD branching.

Minor:

"shy87 mutant dauers showed a minor reduction in secondary and tertiary branches compared to control (Figure 1G). These results indicate that shy87 is specifically required for the elimination of dauer-generated dendrite branches." Maybe temper the specificity claim some as the reduction in branches is definitely there.

We agree, the claim was tempered.

"three complimentary approaches" should be complementary

Thank you for noticing. We fixed this.

"In control animals, SAX-2 was mostly concentrated in the cell body (data not shown)" It might be nice to include some overview images that show the cell body for completeness.

We added zoomed-out images to the revised figure, thank you for the suggestion.

Reviewer #3

Minor comments:

• Fig 1G-H, are shy87 second and third order branch counts statistically different between dauer and post dauer adults? This comparison would strengthen the claim that these order branches fail to eliminate all together rather than undergo a partial elimination. We added this to Figure S2. The shy87 mutants show a complete failure in eliminating secondary branches (i.e. no difference between dauer and post-dauer) and a strong but incomplete defect in eliminating tertiary branches.

• Fig 4B-E Indicate branch order in the images, this is unclear and a point that is focused on in the text. Done.

• Discussion of Fig 1G from the text claims that shy87 is specifically required for branch elimination yet the data shows significant defects in branch outgrowth as well. This raises the question, are the branches abnormally stabilized that results in early underdevelopment and late atrophy? Authors should acknowledge alternative hypotheses. We agree and will revise the text accordingly. The difference between shy87 and control dauers, while statistically significant, is relatively minor and can only be detected by careful quantification, it is not apparent from looking at the images (in contrast for example to rab-8 and rab-10 mutants, where we acknowledge in the text that their branching defects might affect subsequent pruning.

• Authors reference a branch elimination process but don't outline what this would entail and where their results fit in. We apologize for being unclear. Given that sax-1 and sax-2 function together, one would intuitively expect to see SAX-2 being reduced in sax-1 mutants, yet the opposite is observed. On potential explanation is that SAX-1 does not directly control SAX-2 abundance, but that clearance of SAX-2 is part of the pruning process that both proteins regulate. This would explain the enrichment of SAX-2 in sax-1 mutants. However, additional models cannot be excluded, and we acknowledge this in the revised text.

References:

Corchado, Johnny Cruz, Abhishiktha Godthi, Kavinila Selvarasu, and Veena Prahlad. 2024. “Robustness and Variability in Caenorhabditis Elegans Dauer Gene Expression.” Preprint, bioRxiv, August 26. https://doi.org/10.1101/2024.08.15.608164.

Karp, Xantha. 2018. “Working with Dauer Larvae.” WormBook, August 9, 1–19. https://doi.org/10.1895/wormbook.1.180.1.

Kozik, Patrycja, Richard W Francis, Matthew N J Seaman, and Margaret S Robinson. 2010. “A Screen for Endocytic Motifs.” Traffic (Copenhagen, Denmark) 11 (6): 843–55. https://doi.org/10.1111/j.1600-0854.2010.01056.x.

Lee, T., and L. Luo. 1999. “Mosaic Analysis with a Repressible Cell Marker for Studies of Gene Function in Neuronal Morphogenesis.” Neuron 22 (3): 451–61.

Swanson, M. M., and D. L. Riddle. 1981. “Critical Periods in the Development of the Caenorhabditis Elegans Dauer Larva.” Developmental Biology 84 (1): 27–40. https://doi.org/10.1016/0012-1606(81)90367-5.

Tang, Rui, Christopher W Murray, Ian L Linde, et al. n.d. “A Versatile System to Record Cell-Cell Interactions.” eLife 9: e61080. https://doi.org/10.7554/eLife.61080.

Zhao, Ting, Liying Guan, Xuehua Ma, Baohui Chen, Mei Ding, and Wei Zou. 2022. “The Cell Cortex-Localized Protein CHDP-1 Is Required for Dendritic Development and Transport in C. Elegans Neurons.” PLOS Genetics 18 (9): e1010381. https://doi.org/10.1371/journal.pgen.1010381.

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

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Referee #3

Evidence, reproducibility and clarity

Summary:

Figueroa-Delgado et al. use a C. elegans neuro plasticity model to examine how dendrites are eliminated upon recovery from the stress induced larval stage, dauer. The authors performed a mutagenesis screen to identify novel regulators of dendrite elimination and revealed some surprising results. Branch elimination mechanism varies between 2{degree sign}, 3{degree sign}, and 4{degree sign} branches. The NDR kinase, SAX-1 and it's interactors (SAX-2 and MOB-2) are required for elimination of second and third order branches but not fourth order branches. Interestingly they showed that branch elimination varies depending on the stimulus of dendrite outgrowth such that the NDR kinase is required for branch elimination after genetically inducing the dauer stage but is not required if dauers are produced through food deprivation. The authors go a step further to include a small candidate screen looking at various pathways of membrane remodeling and identify additional regulators of dendrite elimination related to membrane trafficking including RABI-1, RAB-8, RAB-10, and RAB-11.2.

Major comments:

• While I find the data promising and exciting, several of the experiments have concerningly low sample sizes. Fig 3G, Fig 4G, Fig 5J and L, and Fig 6I all contain data sets that are fewer than 10 animals. Sample sizes should be stated specifically in the figure legends for all data represented in the graphs.
• All statements based on data not shown should be amended to include the data as a supplemental figure or edited to omit the statement based on withheld data.
• Rescue experiments (Fig 2J) should demonstrate failure to rescue from neighboring tissue types (hypodermis and muscle) to conclude cell autonomous rescue rather than a broadly acting factor.
• Fig 4 needs quantification of higher order branches and SAX-2 proximity to branch nodes as these are discussed in the text.

Minor comments:

• Fig 1C-F, It appears like the shy87 allele produces animals of significantly different body sizes. It would improve rigor to normalize the dendrite coverage to body size in the quantification.
• Fig 1G-H, are shy87 second and third order branch counts statistically different between dauer and post dauer adults? This comparison would strengthen the claim that these order branches fail to eliminate all together rather than undergo a partial elimination.
• Discussion of Fig 1G from the text claims that shy87 is specifically required for branch elimination yet the data shows significant defects in branch outgrowth as well. This raises the question, are the branches abnormally stabilized that results in early underdevelopment and late atrophy? Authors should acknowledge alternative hypotheses.
• Is the failure to eliminate branches an indication of incomplete dauer recovery? Do sax-1 mutants retain additional characteristics of dauer morphology in post dauer adults.
• The text references multiple transgenic lines tested in Fig 2I-J but only one line is shown.
• Fig 4B-E Indicate branch order in the images, this is unclear and a point that is focused on in the text.
• Fig 4F, Additional timepoints would enhance the sax-1 localization result and might provide insight into mechanism of action for sax-1.
• Authors reference a branch elimination process but don't outline what this would entail and where their results fit in.
• Fig 6I Control and sax-1(ky491) example images should be provided in the supplement.

Referee cross-commenting

I agree that we shared many of the same concerns.

There are several general assays for dauer characteristics that could be used here to determine if the post-dauer animals retain other characteristics of the dauer stage in addition to IL2 branches (SDS resistance, alae remodeling, pharyngeal bulb morphology, nictation behavior). The nictation behavior has been connected very nicely with IL2 neurons (Junho Lee's group). Additionally, FLP dendrites occupy the same space as the IL2 branches and outgrowth in post-dauers occurs in coordination with IL2 branch elimination - this might be another optional experiment, to check if FLP growth is impeded by persistent IL2 branches. All of these could be quantified similar to how the authors have already established with their IL2 model (FLP dendrite branches) or with a binary statistic.

Significance

These results describe a new role for the NDR kinase complex in dendrite pruning that has clinical significance to our understanding of human brain development and human health concerns in which pruning is dysregulated, such as observed in the case of autism. The authors use an established neuro-plasticity, C. elegans model (Schroeder et al. 2013) which provides a tractable and reproduceable platform for discovering the mechanism of dendrite pruning. These results would influence future work in the fields of cell biology of the neuron and disease models of brain development.

My expertise is in the field of C. elegans neuroscience and stress biology and have sufficient expertise to evaluate all aspects of this work.

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 establish C. elegans IL2 neurons as a system in which to study dendrite pruning. They use the system to perform a genetic screen for pruning regulators and find an allele of sax-1. Unexpectedly sax-1 is only required for post-dauer pruning in two different genetic backgrounds that induce dauer formation, but not starvation-induced dauer formation. Sax-1/NDR kinase reduction has previously been associated with increased outgrowth and branching in other systems, so this is a new role for this protein. However, the authors show that proteins that work with Sax-1 in other systems, like sax-2/fry, also play a role in this pathway. The genetic experiments are beautiful and the findings are all clearly explained and strongly supported. The authors also examine sax-2 localization, which localizes sax-1 in other systems, and show it in puncta in dendrites that increase with dauer exit, consistent with function at the time of pruning. They also show that membrane trafficking regulators associated with NDR kinases function in the same pathway here, hinting that endocytosis may play a role during pruning as in Drosophila. The link to endocytosis was a little weak (see Major point below). Overall, this study describes a new system to study pruning and identifies NDR/fry/Rabs as regulators of pruning during dauer exit. The work is very high quality and both the imaging and genetics are extremely well done.

Major points

1. The only place where there were any questions about the data was the last figure (6G and I). Here they use uptake of GFP secreted from muscle as a readout of endocytosis in IL2 neurons. They nicely show that more internalized puncta accumulate as animals exit dauer. The claim that this is reduced in sax-1 mutants doesn't seem to match the images shown well. In the image there are many more puncta in the GFP channel and much more accumulation of the RFP-tagged receptor everywhere. It seems like some additional analysis of this data is important to fully capture what is going on and whether this really represents an endocytic defect.
2. For context, it might be helpful to know whether branching of other dendrites is increased in sax-1 mutants (as expected based on phenotypes in other animals) or decreased like IL@ neurons.

Minor:

"shy87 mutant dauers showed a minor reduction in secondary and tertiary branches compared to control (Figure 1G). These results indicate that shy87 is specifically required for the elimination of dauer-generated dendrite branches." Maybe temper the specificity claim some as the reduction in branches is definitely there.

"three complimentary approaches" should be complementary

"In control animals, SAX-2 was mostly concentrated in the cell body (data not shown)" It might be nice to include some overview images that show the cell body for completeness.

Significance

Neurite pruning is important in all animals with neurons. Genetic approaches have primarily been applied to the problem using Drosophila, so identifying a new model system in which to study it is an important step. Using this system, a pathway known to function in a different context is linked to pruning. Thus the study provides new insights into both pruning and this pathway.

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 interesting study uses an unbiased genetic screen in C. elegans to identify SAX-1/NDR kinase as a regulator of dendritic branch elimination. Loss of SAX-1 results in an excess branching phenotype that is striking and highly penetrant. The authors identify several additional regulators of branch elimination (SAX-2, MOB-1, RABI-1, RAB-11.2) by using a candidate genetic screen aimed at factors that interact physically or genetically with SAX-1. They propose that SAX-1 acts by promoting membrane retrieval based on the nature of these interactors and the results of an imaging-based in vivo assay for endocytic puncta.

Major comments.

1. My biggest concern is that the phenotypes are only observed in temperature-sensitive dauer-constitutive mutant backgrounds, and not in wild-type dauers. That is, wild-type animals exiting dauer do not require SAX-1 for dendrite elimination.

While this does not undermine the importance of the results, it does require more explanation. The authors write that "the requirement for sax-1... relies on specific physiological states of the dauer stage," but I do not understand what this means. Are they saying that daf-7 and daf-2 dauers are in a different "physiological state" than wild-type dauers? In what way? What is the evidence for this? A more rigorous explanation is needed.

To me, the simplest genetic explanation is that daf-7 and daf-2 are partially required for branch retraction in a manner redundant with sax-1, and the ts mutants are not fully wild-type at 15C. Thus, the sax-1 requirement is revealed only in these mutant backgrounds. Can the authors examine starvation-induced dauers of daf-7 or daf-2 raised continuously at 15C?

daf-7 and daf-2 ts strains can form "partial dauers" that have a dauer-like appearance but are not SDS resistant. Could the difference between partial dauers and full dauers account for the difference in sax-1-dependence? The authors could use SDS selection of the daf-7 strain at 25C to ensure they are examining full dauers.

The Bargmann lab has created a daf-2 FLP-OUT strain (ky1095ky1087) that allows cell-type-specific removal of daf-2. Could this be used to test for a cell-autonomous role of daf-2 in IL2Q related to branch elimination?

These ideas are not a list of specific experiments the authors need to complete, rather they are meant to illustrate some possible approaches to the question. Whatever approach they use, it is important for them to more rigorously explain why SAX-1 is not required for branch removal in wild-type animals. 2. The SAX-2 localization (Fig. 4) and endocytosis assay (Fig. 6) results were not clear to me from the data shown. Overall a more rigorous analysis and presentation of the data would be important to make these conclusions convincing. This may involve refining the data presentation in the figures, modifying the claims (e.g., "we propose" vs "we find"), or saving some of the data to be more fully explored in a future paper. In my view, these figures are the biggest weak point of the manuscript and also are not important for the central conclusions (which are well supported and convincing), indeed these results are barely mentioned in the Abstract or last paragraph of Introduction.

• In Fig. 4, where in the head are we looking? It would help to show a more low-magnification view of the entire cell.
• In Fig. 4D, why is SAX-2 visible throughout the entire neuron and why is the "punctum" marked with an arrow also seen in the tagRFP channel? One gets the impression that some of the puncta may be background, bleed-through, or artifacts due to cell varicosities.
• In Fig. 4C, the distinction between puncta in the primary or higher-order dendrites is not clear to me, and several puncta that I would have scored as primary are marked as higher-order.
• Related to this, in Fig. 4B are the two arrows meant to be white as in the top panel, or yellow as in the bottom panel?
• The main sax-1 phenotype is increased SAX-2 puncta in dauer, but the branch retraction defect is in post-dauers. How is this relevant to the phenotype?
• The number of SAX-2 puncta in sax-1 mutants decreases almost to normal in post dauers. Is there a correlation between the number of remaining branches and the number of SAX-2 puncta? That is, do the many wild-type animals with "excess" SAX-2 puncta also fail to retract branches?
• The control post-dauer data in Fig. 4F and 4H are identical (re-used data) but the corresponding control dauer data in Fig. 4F and 4G are different. What is going on here?
• Why are sample sizes so small for both strains in Fig. 4G compared to Fig. 4F and 4H?
• In Fig. 6C, why are the tagRFP (blue) puncta larger than the neurite? Aren't these meant to represent vesicles inside the surrounding neurite? One gets the impression that this is bleed-through from the GFP channel.
• In Fig. 6E and 6F, why are there no tagRFP (blue) puncta? Is CD8 not endocytosed at all if it lacks the nanobody sequence? One would expect the tagRFP (blue) signal to be the same in both strains and simply to lack yellow if the nanobody is not present.
• In Fig. 6E and 6H, why are there so many GFP (yellow) puncta outside the neuron? What are these structures and why are they absent in the strain with the nanobody?
• What is the large central blue structure in Fig. 6H - is this the soma? - and why are puncta in this region not counted?
• The authors report a decrease in endocytic events in sax-1, but qualitatively it looks like there are vastly more puncta inside the neuron in Fig. 6H than in 6G.
• minor: there is text reading "40-" in the bottom panel of Fig. 6H. It is visible when printed but not on screen - adjust levels in Photoshop to reveal it.
• Related to both Fig. 4 and Fig. 6, where does SAX-1 localize in IL2Q in dauer and post-dauer? Does its expression or localization change during branch retraction? Does it co-localize with SAX-2 or endocytic puncta?

Minor points:

1. At several points the authors emphasize the relationship of neurite remodeling to stress, e.g. Abstract and Discussion: "we adapted C. elegans IL2 sensory dendrites as a model [of...] stress-mediated dendrite pruning". It seems unnecessary and potentially misleading to treat this as a neuronal stress response. First, it conflates organismal and cellular stress - there is no reason to think that IL2 neurons are under cellular stress in dauer. In fact parasitic nematodes go through dauer-like stages as part of healthy development and probably have similar remodeling of IL2. Second, dendrite pruning occurs during dauer exit, which is the opposite of a stress response - it reflects a return to favorable conditions.
2. In Fig. 1A, C. elegans is shown going directly from L1 to dauer in response to unfavorable conditions, which is incorrect. Animals proceed through L2 (in many cases actually an alternative L2d pre-dauer) and then molt into dauer (an alternative L3 stage) after completing L2.
3. In Fig. 1B, please check if it is correct that hypodermis contacts the pharynx basement membrane as drawn. The schematic in the top panel makes it look like there is a single secondary branch and the quartenary branches are similar in length to the primary dendrite. The schematic in the bottom panel makes it look like the entire neuron is a small fraction of the length of the pharynx. Could these be drawn closer to scale?

Referee cross-commenting

I think we all touched on similar points. I wanted to follow up on Reviewer 3's comment, "Is the failure to eliminate branches an indication of incomplete dauer recovery? Do sax-1 mutants retain additional characteristics of dauer morphology in post dauer adults." I thought this was an excellent point. It made me wonder if that might explain why the defect is only seen in daf-7 and daf-2 mutant backgrounds - maybe these strains retain partial dauer traits even after exit. Is there a specific experiment that they could do? Did you have specific characteristics of dauer morphology in mind for them to check? (Ideally something in the nervous system that can be scored quantitatively.)

Significance

A major strength of this work is the pioneering use of a novel system to study neuronal branch retraction. C. elegans has provided a powerful model for studying how dendrite branches form, but much less attention has been paid to how excess neuronal branches are removed. The post-dauer remodeling of IL2Q neurons provides an exciting and dramatic physiological example to explore this question.

This paper is notable for taking the first steps towards developing this innovative model. It does exactly what is needed at the outset of a new exploration - a forward genetic screen to discover the main regulators of the process. Using a combination of classical and modern genetic approaches, the authors bootstrap their way to a sizeable list of factors and a solid understanding of the properties of this system, for example that retraction of higher vs lower order dendrites show different genetic requirements.

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Reply to the reviewers

We thank the reviewers for their positive comments. Our manuscript is to our knowledge the first to investigate the role of VAIL (V-ATPase—ATG16L1 induced LC3 lipidation), a form of CASM (Conjugation of ATG8s to single membranes) in SARS-CoV-2 replication. We demonstrate that SARS-CoV-2 Envelope (E) induces VAIL and this contributes to viral replication, including by using a reverse genetics system to make an E mutant virus. There have been many high quality studies examining the role of canonical autophagy in SARS-CoV-2 replication and our manuscript does not argue that all or even most LC3 lipidation during infection is via VAIL. We will try to make this point more clearly in the text. We do not think this detracts from the novelty and importance of our manuscript.

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

• Figueras-Novoa et al present a short report demonstrating the induction of LC3 lipidation on single membranes by SARS-CoV-2 through a noncanonical autophagy pathway referred to as VAIL. The authors utilize elegant genetic tools to show that the induction of LC3 lipidation upon viral infection is mainly due to VAIL rather than canonical autophagy. They demonstrate that the activity of the viral E protein that can cause neutralization of acidic vesicles leads to the activation of non-canonical LC3 lipidation on single membranes. Interestingly, the authors also conclude that the impairment of VAIL leads to a reduction of viral load as a result of a defect in later stages of viral infection, although the underlying mechanism was not further explored. *

• Overall, this is an elegant and well controlled study that provides a clear conclusion. I only have some minor comments.*

We thank the reviewer for their assessment of our manuscript.

In some experiments, LC3 lipidation does not appear to be fully disrupted upon VAIL inhibition (e.g. Fig.'s 1H, 3D, 4A). As other labs have shown that SARS-CoV2 blocks autophagic flux, this could be further clarified in this manuscript as both VAIL and autophagy may be co-induced upon viral infection.

We agree with the reviewer that there is a contribution of canonical macroautophagy to the LC3B lipidation observed in SARS-CoV-2. We will extend the discussion in the manuscript to clarify this point for the readers.

Can the authors test the induction of LC3 lipidation in cells expressing K490 mutant of ATG16L1 in ATG16L1 KO cells to compare them with ATG16L1-ATG13 double knockouts?

The western blot in figure 3F (quantified in Figure 3G) shows LC3B lipidation in response to E expression in ATG16L1-ATG13 double knock out cells reconstituted with wild type ATG16L1 but not in cells complimented with ATG16L1 K490A mutant. We agree that the referee’s suggestion to perform these experiments in the context of infection would be informative. However in spite of numerous attempts, we have so far been unable to generate a cell clone fully devoid of ATG16L1 in a cell line that can be productively infected with SARS-CoV-2. For reasons unclear to us there appears to be a very low level of residual ATG16L1 activity despite multiple different CRISPR/Cas9 targeting attempts. The suggested complementation experiments might still be informative in the context of low level ATG16L1 expression so we will pursue this. Alternatively, as a contingency we can try to produce SARS-CoV-2 infectable cells with mutations in ATG16L1’s binding partner V1H, this interaction is required for VAIL. A further contingency could be to assess LC3B lipidation during infection and treatment with a Vps34 inhibitor, which inhibits canonical autophagy.

Minor points: * * The difference between Fig. 1F&G is unclear and why the authors are including both analyses. Similarly figures 4G&H.

We included both metrics to show that the decrease in LC3B lipidation in cells expressing SopF during infection is robust and observed in two separate readouts. While spot area measures the area of infected cells covered by GFP-LC3B fluorescence, spot intensity is a reading of the intensity of the area defined in an infected cell as being LC3 positive. Theoretically, these measurements could change in different ways. For example, if the same amount of lipidated LC3 were to distribute over a larger area of the cell. We prefer to keep both measurements in the manuscript.

The authors should show boxed colocalisation of all images, including negative controls. For examples, the authors have shown boxed magnifications in only the lowest panel in Figure 2A but not the upper two panels. Figures 4E&F should include boxed examples. This serves to clarify both positive and negative colocalisation events.

Boxed magnifications will be added to all images.

• Reviewer #1 (Significance (Required)): *

• Overall an elegant and well controlled study demonstrating the induction of non-canonical LC3 conjugation on single membranes (VAIL) during SARS-CoV2 infection. A further exploration of canonical autophagy (as previously published by others) in addition to VAIL would enhance this study.*

As the reviewer noted, several excellent studies have explored canonical autophagy during SARS-CoV-2 infection, many of which we cite in our manuscript. Our focus, however, is to demonstrate that SARS-CoV-2 E induces LC3 lipidation via VAIL. We believe that exploring the diverse roles of canonical autophagy mechanisms in SARS-CoV-2 infection is beyond the scope of this study.

*This study is of interest to researchers studying autophagy, viruses, immunology, single membrane LC3 lipidation, and lysosomes as well as potentially clinicians treating SARS-CoV2 infecteted individuals. *

• This reviewer is experienced in autophagy research.*

We thank the reviewer for this assessment of our manuscript.

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

• Major Comments *

• Figure 1D does not very clearly show an overlap between V1D and LC3B. Both proteins seem broadly present across the cell and there is no easily identifiable change in V1D distribution upon infection. As such the overlay may be purely stochastic. The authors should quantify the observed co-localization events across multiple cells and biological replicates and compare them to other protein(s) with a similar cellular distribution pattern.*

We agree there is no obvious change in V1D staining on infection. The images in Figure 1D are purely intended to illustrate that LC3 and the V-ATPase can colocalise, not to demonstrate a change in V-ATPase distribution or to suggest a direct interaction. We will make this point more clearly in the text. We will also carry out analyses of the kind (see also response to the first two Minor Comments). We would be happy to provide an alternative method of visualising the V-ATPase (we could use any suitable antibody to the V-ATPase, or the bacterial effector SidK) if required. In response to reviewer 3’s comments, we will carry out a pull-down experiment to test the association of the V-ATPase and ATG16L1 during E expression, as this is a key interaction during VAIL activation.

Based on Figure 2F the authors suggest that virus entry is unaffected by the inhibition of VAIL in early timepoints. However, according to the figure legend, the timepoint used is 7hpi, while 2D uses 24hpi. Some SARS-CoV-2 papers suggest 7-10 hours is sufficient time to release new virions (Ban-On et al., 2020). As such 7hpi can not necessarily be seen as an early time point. Did the authors test earlier ones? Also, based on this, would it be possible that the effects observed at 24hpi are actually secondary infections, meaning that the virus utilizes pathway components for virion production and a lack thereof reduces infectivity of newly formed virions? In this case it would be interesting to set up an assay that can distinguish between primary and secondary infection to study both individually more closely.

Whereas 7 hours may be sufficient to release new virions, it is not sufficient to establish infections in other cells – this is why we chose that time point. The observation that there is no difference in the percentage of infected cells at 7 h p.i. (figure 2F) led us to suggest that viral entry is unaffected . We then confirmed this through the pseudovirus assay in Figure 2G, where no difference is found between SopF and mCherry expressing cells. For this assay, GFP-expressing, replication incompetent, lentiviral particles pseudotyped with Spike from different SARS-CoV-2 lineages were used to transduce mCherry and SopF expressing cells. A change in the percentage of GFP-positive cells would indicate an effect on viral entry, but no such change was observed in SopF-expressing cells.

We agree with the reviewer that the effects observed at 24 hpi are likely due to a defect in subsequent rounds of infection, since no difference was observed at 7 hpi or with our pseudovirus assay. We will attempt to make this point in the text as clearly as possible.

The authors nicely show in their study an involvement of VAIL in SARS-CoV-2 mediated LC3 lipidation. However, the observed effects are relatively moderate in several experiments, indicating that there may be another contributor to the observed phenotype. It would be nice to highlight this in the discussion and debate potential mechanisms that are causing the observed effects during infection.

We agree with the reviewer’s analysis. We have discussed the contribution of canonical autophagy in the second paragraph of the discussion, but we will expand on this in a revised manuscript. E expression levels are moderate during infection, other structural proteins such as N and M are present in much higher amounts. Since E is the key protein in VAIL initiation, a moderate effect of VAIL inhibition in perhaps expected. Nonetheless this still plays a crucial role in the viral life cycle.

*Minor Comments *

• The re-localization events shown in Fig 3A should be quantified.*

This quantification of GFP-LC3 relocalisation will be carried out and included.

• The co-localization events displayed in Fig 4A should be quantified.*

The quantification of V1D, E and GFP-LC3 will be carried out and included.

For Figure 2H-K the authors perform KDs of ATG16L1 and ATG13. While the results for the two specific proteins are certainly convincing, the authors would strengthen their argument by testing additional proteins in the autophagy pathway to support their claim that VAIL but not autophagy affects protein abundance of N (OPTIONAL).

As discussed in response to reviewer 1, we will attempt to infect ATG16L1 KO cells reconstituted with a K490A ATG16L1 mutant, which is an established tool and has been validated to be deficient in VAIL but not canonical autophagy.

***Referee cross-commenting** *

• Overall I agree with the comments of my co-reviewers and I think the suggested experiments/comments are sensible. *
• I in part already eluted to it my analysis, but I tend to agree with reviewer 3 on the limited effect VAIL seems to have on LC3b lipidation.*

As outlined above in response to reviewer 1 and below to reviewer 3, we agree that there is a modest contribution of VAIL to overall LC3 lipidation, which correlates with a modest amount of E expression in SARS-CoV-2 infection. VAIL is clearly important for the viral life cycle, thus whatever the proportion of LC3 lipidation attributable to this pathway it must be biologically significant.

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

• While previous publications have shown interaction between SARS-CoV2 and autophagy, the authors of this manuscript demonstrate that V-ATPase-ATG16L1 induced LC3 lipidation (VAIL) is activated during infection and affects viral replication. *

• This study provides an interesting new aspect to host-SARS_CoV-2 interactions. *

• The manuscript is of interest for people studying virus-host cell interaction, as well as for researchers in the fields of infectious diseases, specifically SARS-CoV2, and autophagy/VAIL*.

We thank the reviewer for their assessment of our manuscript.

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

• The interaction of SARS-CoV-2 with canonical autophagy has been well documented. However, whether SARS-CoV-2 infection induces and benefits from non-canonical autophagy is unclear. In this manuscript, the authors demonstrated that SARS-CoV-2 infection induces V-ATPase-ATG16L1-induced LC3 lipidation (VAIL), a form of non-canonical autophagy in which LC3 is conjugated to single membranes. The SARS-CoV-2 envelope protein, through its ion channel activity, triggers the V-ATPase proton pump and induces VAIL during SARS-CoV-2 infection. Inhibiting VAIL during SARS-CoV-2 infection with SopF, a Salmonella effector, attenuates SARS-CoV-2 egress. *

• While these findings are interesting and demonstrate that SARS-CoV-2 infection triggers VAIL for its own benefit, the mechanism by which VAIL promotes SARS-CoV-2 replication remains unclear. Moreover, the contribution of VAIL to LC3 lipidation during SARS-CoV-2 infection appears to be minimal, as blocking VAIL through SoPF expression only marginally reduced LC3B lipidation (Fig. 1H). Therefore, the contribution of VAIL to LC3 lipidation during SARS-CoV-2 infection is minimal.*

We thank the reviewer for their assessment of our manuscript. As we have already alluded to in our response, we agree that only part of the LC3 lipidation observed during infection can be attributed to VAIL. There is a reproducible effect on viral replication which we have demonstrated in multiple ways, therefore the contribution of VAIL is of biological importance.

*Comments: *

• The authors show that the ion channel activity of E is essential for VAIL induction during SARS-CoV-2 infection. Since V-ATPase recruits the ATG16L complex to induce VAIL, and to clarify how SARS-CoV-2 infection triggers VAIL, the authors should examine whether SARS-CoV-2 infection or the expression of E induces V-ATPase-ATG16L interaction and whether this interaction is disrupted when SopF is expressed.*

We agree with the reviewer that this would be an informative experiment. We can carry out this experiment in an E expression system, rather than infection. This is due to the difficulty of getting enough material to carry out this kind of pull-down experiment in infected cells (at the time of writing these experiments still have to be carried out in CL3).

• Since the authors suggest that expression of SopF attenuates viral exit, one would expect that the number of N-positive cells will increase in SopF-expressing cells compared to the mCherry control cells. However, as shown in Figure 2D, this is not the case. Could the authors discuss why N-positive cells will be reduced in SopF-expressing cells when viral egress is impeded in these cells*?

This is a reflection of multi-cycle kinetics. N is still very strongly expressed in infected cells, even after virions have egressed. SARS-CoV-2 can infect VAIL-deficient cells and expresses the same levels of N prior to subsequent rounds of infection (at 7 hours after infection for example). Egress in VAIL-deficient, SopF-expressing cells is defective. Therefore, fewer cells will be infected in subsequent rounds of infection in SopF expressing cells, resulting in fewer N-positive cells in the SopF expressing cell population (most obvious after 24 hours).

Figure 2H. The authors show that knockdown of ATG16L1 reduces the expression of N during SARS-CoV-2 infection compared to the controls. To confirm that knockdown of ATG16L1, which is required for both canonical autophagy and VAIL, reduces N staining via VAIL, the authors should examine the impact of SopF expression on N levels in ATG16L KD cells. This experiment will confirm if the reduction in N staining in ATG16L1 KD cells is due to VAIL.

As stated in the response to reviewer 1, we can attempt this experiment in an ATG16L1 KO system complemented with K490A ATG16L1, which is deficient in VAIL and not canonical autophagy.

• Figure 2J. The quality of the Western blot data is poor.*

In this western the exposure is deliberately turned up to show that minimal ATG13 was left after knock down. We will also show the full blot with less exposure – this will demonstrate high quality.

Also, N appears as a single band in Figure 2J, but appears as double bands in Figures 2A and H. Could the authors explain this?

An extra band can be seen in 2J for N. However, as the reviewer points out, the intensity of the lower band is fainter than in 2A or 2H. The biology of SARS-CoV-2 N is interesting and complicated, with different truncated isoforms and phosphorylation patterns observed (see for example Mears et al., 2025 PMID:39836705). We observed changes in abundance of the second band between experiments, but this did not obviously depend on VAIL. We therefore consider this to be beyond the scope of this investigation.

*Reviewer #3 (Significance (Required)): *

• This manuscript proposes a role for VAIL in LC3 lipidation during SARS-CoV-2 infection. While the findings are interesting, VAIL only marginally contributes to LC3 lipidation during SARS-CoV-2 infection. Therefore, the significance of VAIL to LC3B lipidation during SARS-CoV-2 infection is unclear.*

Our experiments show unambiguously that VAIL contributes to viral replication. Therefore even if As alluded to above, we do not think a further investigation of canonical macroautophagy and SARS-CoV-2 would enhance the quality of our manuscript. We will try to make our description of the contribution of macroautophagy clearer in the revised manuscript (without providing a full literature review). We also do not think that exploring the nature of the multiple N bands on western blot is within the scope of this paper.

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Referee #3

Evidence, reproducibility and clarity

The interaction of SARS-CoV-2 with canonical autophagy has been well documented. However, whether SARS-CoV-2 infection induces and benefits from non-canonical autophagy is unclear. In this manuscript, the authors demonstrated that SARS-CoV-2 infection induces V-ATPase-ATG16L1-induced LC3 lipidation (VAIL), a form of non-canonical autophagy in which LC3 is conjugated to single membranes. The SARS-CoV-2 envelope protein, through its ion channel activity, triggers the V-ATPase proton pump and induces VAIL during SARS-CoV-2 infection. Inhibiting VAIL during SARS-CoV-2 infection with SopF, a Salmonella effector, attenuates SARS-CoV-2 egress.

While these findings are interesting and demonstrate that SARS-CoV-2 infection triggers VAIL for its own benefit, the mechanism by which VAIL promotes SARS-CoV-2 replication remains unclear. Moreover, the contribution of VAIL to LC3 lipidation during SARS-CoV-2 infection appears to be minimal, as blocking VAIL through SoPF expression only marginally reduced LC3B lipidation (Fig. 1H). Therefore, the contribution of VAIL to LC3 lipidation during SARS-CoV-2 infection is minimal.

Comments:

The authors show that the ion channel activity of E is essential for VAIL induction during SARS-CoV-2 infection. Since V-ATPase recruits the ATG16L complex to induce VAIL, and to clarify how SARS-CoV-2 infection triggers VAIL, the authors should examine whether SARS-CoV-2 infection or the expression of E induces V-ATPase-ATG16L interaction and whether this interaction is disrupted when SopF is expressed.

Since the authors suggest that expression of SopF attenuates viral exit, one would expect that the number of N-positive cells will increase in SopF-expressing cells compared to the mCherry control cells. However, as shown in Figure 2D, this is not the case. Could the authors discuss why N-positive cells will be reduced in SopF-expressing cells when viral egress is impeded in these cells?

Figure 2H. The authors show that knockdown of ATG16L1 reduces the expression of N during SARS-CoV-2 infection compared to the controls. To confirm that knockdown of ATG16L1, which is required for both canonical autophagy and VAIL, reduces N staining via VAIL, the authors should examine the impact of SopF expression on N levels in ATG16L KD cells. This experiment will confirm if the reduction in N staining in ATG16L1 KD cells is due to VAIL.

Figure 2J. The quality of the Western blot data is poor. Also, N appears as a single band in Figure 2J, but appears as double bands in Figures 2A and H. Could the authors explain this?

Significance

This manuscript proposes a role for VAIL in LC3 lipidation during SARS-CoV-2 infection. While the findings are interesting, VAIL only marginally contributes to LC3 lipidation during SARS-CoV-2 infection. Therefore, the significance of VAIL to LC3B lipidation during SARS-CoV-2 infection is unclear.

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Referee #2

Evidence, reproducibility and clarity

Major Comments

Figure 1D does not very clearly show an overlap between V1D and LC3B. Both proteins seem broadly present across the cell and there is no easily identifiable change in V1D distribution upon infection. As such the overlay may be purely stochastic. The authors should quantify the observed co-localization events across multiple cells and biological replicates and compare them to other protein(s) with a similar cellular distribution pattern.

Based on Figure 2F the authors suggest that virus entry is unaffected by the inhibition of VAIL in early timepoints. However, according to the figure legend, the timepoint used is 7hpi, while 2D uses 24hpi. Some SARS-CoV-2 papers suggest 7-10 hours is sufficient time to release new virions (Ban-On et al., 2020). As such 7hpi can not necessarily be seen as an early time point. Did the authors test earlier ones? Also, based on this, would it be possible that the effects observed at 24hpi are actually secondary infections, meaning that the virus utilizes pathway components for virion production and a lack thereof reduces infectivity of newly formed virions? In this case it would be interesting to set up an assay that can distinguish between primary and secondary infection to study both individually more closely.

The authors nicely show in their study an involvement of VAIL in SARS-CoV-2 mediated LC3 lipidation. However, the observed effects are relatively moderate in several experiments, indicating that there may be another contributor to the observed phenotype. It would be nice to highlight this in the discussion and debate potential mechanisms that are causing the observed effects during infection.

Minor Comments

The re-localization events shown in Fig 3A should be quantified.

The co-localization events displayed in Fig 4A should be quantified.

For Figure 2H-K the authors perform KDs of ATG16L1 and ATG13. While the results for the two specific proteins are certainly convincing, the authors would strengthen their argument by testing additional proteins in the autophagy pathway to support their claim that VAIL but not autophagy affects protein abundance of N (OPTIONAL).

Referee cross-commenting

Overall I agree with the comments of my co-reviewers and I think the suggested experiments/comments are sensible. I in part already eluted to it my analysis, but I tend to agree with reviewer 3 on the limited effect VAIL seems to have on LC3b lipidation.

Significance

While previous publications have shown interaction between SARS-CoV2 and autophagy, the authors of this manuscript demonstrate that V-ATPase-ATG16L1 induced LC3 lipidation (VAIL) is activated during infection and affects viral replication.

This study provides an interesting new aspect to host-SARS_CoV-2 interactions.

The manuscript is of interest for people studying virus-host cell interaction, as well as for researchers in the fields of infectious diseases, specifically SARS-CoV2, and autophagy/VAIL.

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

Figueras-Novoa et al present a short report demonstrating the induction of LC3 lipidation on single membranes by SARS-CoV-2 through a noncanonical autophagy pathway referred to as VAIL. The authors utilize elegant genetic tools to show that the induction of LC3 lipidation upon viral infection is mainly due to VAIL rather than canonical autophagy. They demonstrate that the activity of the viral E protein that can cause neutralization of acidic vesicles leads to the activation of non-canonical LC3 lipidation on single membranes. Interestingly, the authors also conclude that the impairment of VAIL leads to a reduction of viral load as a result of a defect in later stages of viral infection, although the underlying mechanism was not further explored.

Overall, this is an elegant and well controlled study that provides a clear conclusion. I only have some minor comments.

In some experiments, LC3 lipidation does not appear to be fully disrupted upon VAIL inhibition (e.g. Fig.'s 1H, 3D, 4A). As other labs have shown that SARS-CoV2 blocks autophagic flux, this could be further clarified in this manuscript as both VAIL and autophagy may be co-induced upon viral infection. Can the authors test the induction of LC3 lipidation in cells expressing K490 mutant of ATG16L1 in ATG16L1 KO cells to compare them with ATG16L1-ATG13 double knockouts?

Minor points:

The difference between Fig. 1F&G is unclear and why the authors are including both analyses. Similarly figures 4G&H.

The authors should show boxed colocalisation of all images, including negative controls. For examples, the authors have shown boxed magnifications in only the lowest panel in Figure 2A but not the upper two panels. Figures 4E&F should include boxed examples. This serves to clarify both positive and negative colocalisation events.

Significance

Overall an elegant and well controlled study demonstrating the induction of non-canonical LC3 conjugation on single membranes (VAIL) during SARS-CoV2 infection. A further exploration of canonical autophagy (as previously published by others) in addition to VAIL would enhance this study.

This study is of interest to researchers studying autophagy, viruses, immunology, single membrane LC3 lipidation, and lysosomes as well as potentially clinicians treating SARS-CoV2 infecteted individuals.

This reviewer is experienced in autophagy research.

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Reply to the reviewers

We appreciate the constructive and supportive feedback on our manuscript. All three reviewers acknowledged the significance and novelty of our work on bacterial telomere protection. In response to their suggestions, we have conducted the requested experiments and revised the manuscript accordingly. These changes have enhanced the rigor of our study and clarified our interpretations and explanations.

Moreover, we characterized an additional truncation mutant of TelN (TelN Δ445–631), which lacks the two C-terminal domains. Despite this deletion, the mutant retained protection activity (Supplementary Figure S4B), indicating that the remaining regions of the protein are sufficient to confer efficient protection in this assay.

Finally, we removed three sequence alignments (previously Supplementary Figures S6A and S7), as we recognized that the high degree of sequence divergence could hinder proper alignment and potentially lead to misinterpretation.

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

This study addresses how the bacterial telomere protein TelN protects telomere ends against the action of the Mre11-Rad50 nuclease (MR). This protection is essential for the stability of hairpin-ended linear plasmid and chromosomes in bacteria but had not been explored before. The authors demonstrate that TelN is necessary and sufficient to block MR-dependent DNA cleavage when bound to its specific telomere sequence. By combining elegant genetics and biochemical approaches, it convincingly shows that TelN-dependent inhibition likely involves a specific interaction between TelN and the MR complex. The manuscript is well written, easy to read and focused on the relevant information. The claims and the conclusions are supported by the data. There is no over-interpretation.

Comments: - Figure 1B, unnormalized transformation efficiency would be useful to show in SI

The unnormalized B. subtilis transformation efficiency has now been added as new figure panel S1B.

• Figures 2B, 2C, 3C, 3D, 4C, 5A and 5B: quantification of independent experiments should be added

While these DNA protection experiments show a clearly reproducible pattern of DNA degradation, the exact response to TelN titration varies somewhat between experimental replicates. We initially included the quantification of remaining full-length DNA because the corresponding band is hard to discern in the gel image due to pixel saturation. However, we realize now that this may mislead readers to think that the degradation occurs always with the exact same dosage response.

To avoid this, we have decided to remove the quantification and instead show the relevant part of the gel also at higher contrast to better visualize the loss of full-length DNA due to DNA degradation. In addition, we have included replicate experiments carried out at the same MR concentration (125 nM M₂R₂) or at higher concentration (500 nM M₂R₂) in the supplementary material. These examples demonstrate the general reproducibility of the assay.

**Referee cross-commenting**

Perfect for me. It seems that there is a consensus.

Reviewer #1 (Significance (Required)):

This pioneering study provides a very strong basis for a new understanding of telomeres in bacteria and offers fascinating evolutionary perspectives when compared to similar mechanisms active at telomeres in eukaryotic cells.

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

The paper is well-presented and well-written throughout. The paper shows convincingly that TelN protects hairpin DNA ends from the activity of SbcCD, presumably providing a protection mechanism for N15 phage DNA in vivo. Furthermore, this protection activity is shown not to require the catalytic (resolvase) activity of TelN, nor its poorly characterised C-terminal domain. The paper also suggests that this inhibition acts both at the level of competition for the DNA hairpin end and at the level of a direct protein:protein interaction between TelN and MR. An (acknowledged) weakness is that there is no real insight into the protein:protein interaction suggested by the experiments shown in Figure 5. Ideally, the protein:protein interaction interface would be identified and mutations in this interface would be shown to reduce hairpin protection.

Specific comments/questions

(1) What pathway (in vivo) leads to inactivation of linear hairpin DNA - one suspects that cleavage by SbcCD at the hairpins is probably not the full story. Presumably SbcCD cleavage facilitates further processing by other long range resection systems such as RecBCD, Exo1, RecQ/J etc. Would it be appropriate to view the hairpin as an adaption to protect against these nucleases, which then must be complemented with a mechanism to suppress SbcCD?