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Reply to the reviewers

Reviewers’ comments:

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

This manuscript identifies a potential connection between FASN, endogenous dsRNAs, and innate immune signaling. The authors show that FASN depletion increases cytoplasmic dsRNA staining, enhances IFN transcription and restricts Sindbis virus replication. Overall, the basic observation seems to be solid and well-controlled. Depending on which journal this is being considered for, the central mechanism could be better developed and elucidated to entail more molecular details. As it currently stands, several important questions, especially ones regarding the FASN-RNA interactions remain unresolved.

Major comments

The conclusion that FASN regulates dsRNA accessibility rather than dsRNA abundance requires further support. The authors show increased J2 staining without major changes in the global dsRNA landscape by J2-RIP-seq. However, alternative explanations could be: (1) changes in dsRNA structure or length distribution could affect J2 recognition, i.e. epitope masked by FASN binding; (2) differences in RNA-protein complex assembly could influence J2 accessibility; (3) Altered subcellular localization of dsRNAs could increase immunofluorescence signals without substantially affecting RIP-seq recovery. 2. The nature of the FASN-RNA interaction remains unclear. The authors demonstrate that FASN associates with a subset of endogenous RNAs, but it is not clear whether this interaction is sequence-specific, structure-specific, or largely nonspecific. Are there common sequence motifs, secondary structures, repetitive elements, or specific transcript classes enriched among FASN-associated RNAs? Without a clearer understanding of RNA selectivity, it remains difficult to evaluate the biological significance of the observed interactions. 3. The study would be significantly strengthened by complementation experiments. Although the FASN knockout phenotype is convincing, add-back experiments are needed to demonstrate specificity and probe potential mechanisms. Reconstitution with wild-type FASN should rescue the dsRNA and immune phenotypes. Furthermore, domain-specific mutants or catalytic mutants (e.g., palmitoylation) could help distinguish whether the observed effects depend on FASN enzymatic activity, a specific protein domain, or a non-canonical RNA-binding function. Such experiments would greatly improve the mechanistic depth of the study. It will also address whether the observed dsRNA increase phenotype is irreversible.

The manuscript proposes that increased endogenous dsRNA sensing drives the inflammatory phenotype in FASN-deficient cells. However, direct evidence for enhanced PRR engagement is currently lacking. Although MDA5 and MAVS knockdown experiments suggest a possible contribution of this pathway, the observed knockdown effects are relatively modest and needs to be repeated by CRISPR knockout. Does FASN, MAVS double knockout cells rescue the slow growth phenotype? In addition, direct measurements of PRR activation, such as MDA5-RNA association, MAVS activation, IRF3 phosphorylation, or related downstream signaling events, were not examined. 5. The antiviral phenotype observed during Sindbis virus infection is interesting, but the underlying mechanism remains uncertain. The authors propose that enhanced endogenous dsRNA sensing contributes to viral restriction, yet alternative explanations related to altered lipid metabolism, impaired membrane remodeling, or other consequences of FASN deficiency cannot be excluded. Especially when MDA5 and MAVS knockdown effect appears modest. Additional experiments disrupting interferon signaling or innate immune sensing pathways using the FASN, MAVS double knockout cells would help determine whether the antiviral phenotype is directly linked to the proposed dsRNA sensing mechanism.

Reviewer #1 (Significance (Required)):

This manuscript identifies a potential connection between FASN, endogenous dsRNAs, and innate immune signaling. The authors show that FASN depletion increases cytoplasmic dsRNA staining, enhances IFN transcription and restricts Sindbis virus replication. Overall, the basic observation seems to be solid and well-controlled. Depending on which journal this is being considered for, the central mechanism could be better developed and elucidated to entail more molecular details. As it currently stands, several important questions, especially ones regarding the FASN-RNA interactions remain unresolved.

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

The manuscript by Pasquier and colleagues investigates the role of fatty acid synthase (FASN) in the regulation of innate immune signaling through its interaction with endogenous dsRNAs. The authors build upon their previous study, in which they identified FASN as a potential dsRNA-binding protein. They show that FASN knockout results in increased cytoplasmic dsRNA detection accompanied by the induction of inflammation-related genes. Subsequent multi-omics analyses reveal that FASN associates with dsRNAs derived from nuclear genome-encoded transcripts in multiple contexts. Interestingly, FASN depletion does not alter the overall expression of these dsRNAs but increases their detection by the J2 antibody. Functionally, FASN depletion enhances innate immune responses to dsRNA stimulation and Sindbis virus infection.

While the study provides evidence supporting an proviral role for FASN, the manuscript lacks mechanistic insight into this phenomenon. In particular, it remains unclear how FASN depletion enhances dsRNA detection without altering endogenous dsRNA abundance. The following points should be addressed:

1) The main limitation of the manuscript is the absence of a mechanistic explanation for how FASN depletion leads to increased dsRNA detection without affecting expression. Does the increased dsRNA detection require a direct interaction between FASN and dsRNAs? The authors should provide additional evidence to clarify whether FASN binding masks dsRNA epitopes or regulates dsRNA accessibility to recognition by J2 and innate immune sensors.

2) The authors show that FASN directly binds nuclear genome-encoded transcripts. It would be important to perform RNA-FISH for selected FASN-interacting RNAs to determine whether their cellular localization or J2-detectable signal is altered in FASN-depleted cells.

3) In Figure 2B, the authors demonstrate enrichment of inflammation-related gene signatures in FASN knockout cells. However, the magnitude of induction is not clear. How does the inflammatory response compare with canonical innate immune activation, such as viral infection or poly(I:C) stimulation? Although Figure 2A partially addresses this point, many of the highlighted genes are not directly associated with inflammatory responses.

4) For the transcripts directly associated with FASN, do they contain predicted dsRNA-forming regions or known structured RNA elements? The current data do not sufficiently demonstrate whether these transcripts indeed form dsRNA structures. Although some are enriched in J2 immunoprecipitation, additional structural analyses, including computational prediction of dsRNA regions, would strengthen the conclusion.

5) The authors should further investigate whether the enhanced antiviral activity observed upon FASN depletion is mediated by elevated endogenous dsRNA sensing. Are dsRNA sensors such as PKR, MDA5, or RIG-I more strongly activated in FASN knockout cells? Do these sensors exhibit increased binding to endogenous dsRNAs following FASN depletion?

Reviewer #2 (Significance (Required)):

Main strength: Uncover the proviral role of FASN via regulation of endogenous dsRNAs

Limitations: Molecular mechanism on how FASN depletion increases the accessibility of dsRNAs without affecting their expression. Also, need better characterization of FASN-binding RNAs, especially their secondary structure.

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

Summary The manuscript entitled, "Fatty Acid Synthase associates with nuclear-derived cytoplasmic dsRNA molecules and influences antiviral innate immune response," by Pasquier et al. identifies an unexpected function for FASN as an endogenous dsRNA-associated protein and explores the relationship between FASN, cellular dsRNA homeostasis, and antiviral innate immunity. Using FASN knockout cells, the authors demonstrate that depletion of FASN results in accumulation of cellular dsRNA, characterize the endogenous dsRNA species associated with FASN, and show that loss of FASN is accompanied by increased expression of interferon-stimulated genes and restriction of SINV replication. The biochemical characterization of FASN-associated dsRNAs together with the accompanying transcriptomic analyses provide compelling evidence that FASN interacts with a distinct subset of endogenous dsRNAs, representing a novel function for this metabolic enzyme.

While evidence is presented that FASN can associate with endogenous dsRNA, several aspects of the proposed functional model extend beyond what is directly demonstrated by the data. In particular, the manuscript presents dsRNA accumulation, innate immune activation, and viral restriction as a consequence of FASN-mediated dsRNA regulation. However, it remains unclear whether these downstream phenotypes arise specifically from the newly described RNA-binding activity of FASN or instead reflect broader cellular consequences of FASN deficiency, including alterations in lipid metabolism and protein palmitoylation. Likewise, although the authors identify a population of FASN-associated dsRNAs, the relationship between these transcripts and the dsRNAs that accumulate following FASN depletion remains insufficiently resolved, making it difficult to mechanistically understand how FASN regulates dsRNA homeostasis. Overall, the manuscript provides a number of intriguing observations regarding FASN association with endogenous dsRNA. However, the functional relationship between these findings and the proposed effects on dsRNA homeostasis and innate immunity would benefit from additional clarification before the mechanistic model can be fully supported.

Major Concerns

It remains unclear whether the inflammatory and antiviral phenotypes observed following FASN depletion are attributable to FASN's newly described dsRNA-binding activity or to the broader metabolic consequences of losing FASN. The manuscript presents dsRNA accumulation, induction of ISGs, and restriction of SINV as downstream consequences of FASN-mediated dsRNA regulation. While these observations are compelling, they remain correlative and do not distinguish between effects arising from dsRNA regulation versus the numerous metabolic changes expected following loss of FASN. In particular, reduced palmitate production and altered protein palmitoylation are well-established consequences of FASN depletion and have documented roles in MAVS signaling and antiviral immunity. This distinction is important because the principal claim of the manuscript is not simply that FASN depletion alters innate immunity, but that its RNA-binding activity is proposed to underlie these effects. At present, the data support an association between these phenotypes but fall somewhat short of demonstrating that the observed immune response is specifically driven by FASN-mediated regulation of endogenous dsRNA.

1. While the manuscript does provide evidence that FASN associates with a subset of endogenous dsRNAs, the relationship between these RNAs and those that accumulate following FASN depletion remains unclear. The authors conclude that FASN regulates dsRNA homeostasis, yet also show that transcripts associated with FASN do not measurably accumulate in knockout cells. This creates a disconnect between RNA association and functional regulation that is not adequately resolved.

An overlap analysis comparing the dsRNA populations identified in wt and KO cells would help clarify whether FASN regulates a stable population of transcripts or whether broader remodeling of the dsRNA landscape occurs following FASN loss. More generally, the manuscript would be stronger if it helps clarify or distinguish the observation that FASN binds endogenous dsrna from the conclusion that it regulates cellular dsRNA homeostasis; the latter is not fully supported with the presented data.

Minor concerns

The mitochondrial localization of dsRNA needs additional validation. Specifically, Fig 3A requires quantitative analysis of mitochondrial abundance, while Fig 3C could be strengthened through orthogonal validation of mitochondrial localization (e.g., microscopy-based co-localization or further purification of the mitochondrial fraction). Inclusion of an RNase control would also help demonstrate that the enrichment is specific to dsRNA.

The role of the ADAR depletion experiments within the overall narrative is somewhat unclear. Consider either integrating these data more directly into the proposed model or reducing their emphasis. Along similar lines, Fig 4B should clarify whether the increased FASN-dsRNA association reflects greater binding or simply increased abundance of both FASN and dsRNA following 5-Aza treatment. • Several aspects of the data presentation needs clarification. These include the rationale for selecting IFIT1 for validation (Fig 2A), the relationship between proteins highlighted in the Fig 4 volcano plot and those selected for immunoblot validation, the apparent reduction in tubulin complicating interpretation of the SINV capsid blot (Fig 5B), and the conclusion that J2-positive puncta are distinct from SINV RNA without co-localization analysis. • Several figures could be improved for presentation. Quantification of the J2 signal in Fig S1C (analogous to Fig 1D) and improved labeling of the volcano plots would improve readability. • Several minor editorial revisions are recommended. These include describing ACP as a carrier/tethering rather than catalytic domain, citing Fig S2 in the Results, defining the long form of NES in the Fig 2 legend, removing redundant panel descriptions in the Fig 3G legend, correcting the missing text on page 14, and resolving the duplicated figures and formatting issues present throughout the manuscript.

Reviewer #3 (Significance (Required)):

Strengths Nice extension of FASN biology beyond its canonical metabolic role Introduces FASN as a potential endogenous dsRNA-binding protein Broad interest for the RNA biology and innate immunity communities

Limitations RNA binding not fully demonstrated with higher-resolution approaches such as more precise CLIP approaches

Mechanistic link between FASN dsRNA homeostasis and innate immune activation remains incomplete

Advance Good conceptual advance but is more descritive than mechanistic

Audience: RNA biology RNA-binding proteins Innate immunity Host-virus interactions Moonlighting metabolic enzymes

Revision plan:

1. General Statements:

We thank the three reviewers for their careful evaluation of our manuscript and for their constructive comments. We are encouraged that all reviewers considered the central observations of the study to be robust and appreciated the conceptual advance provided by the identification of a previously unrecognized association between FASN and endogenous dsRNAs, together with its impact on antiviral innate immunity.

We also acknowledge the fact that the main limitation of the current manuscript is the mechanistic understanding of how FASN regulates endogenous dsRNA accessibility and how this relates to innate immune activation. We agree that strengthening the mechanistic aspects of the study will substantially improve the manuscript. Nonetheless, dissecting the full mechanism may require more time which goes beyond the scope of this paper.

Based on the comments of the three reviewers, our revision plan will therefore focus on three major objectives:

• further characterizing the endogenous RNAs associated with FASN,
• strengthening the mechanistic aspects linking increased accessibility of endogenous dsRNAs to FASN depletion,
• providing additional evidence linking endogenous dsRNA accessibility to innate immune priming and antiviral activity. Importantly, we also intend to clarify our proposed model. Our data do not suggest that loss of FASN induces a strong spontaneous interferon response comparable to that triggered by viral infection or poly(I:C) stimulation. We rather propose that FASN depletion establishes a primed state by increasing the accessibility of a subset of endogenous dsRNAs to innate immune sensors, thereby lowering the threshold for antiviral activation upon subsequent challenge. We will revise the manuscript to better communicate this model, improving data presentation throughout the manuscript and discussion to clearly distinguish experimentally supported conclusions from mechanistic interpretations.

__2. __Description of the planned revisions:

Further characterization of FASN-associated endogenous RNAs

To better define the RNA population associated with FASN, we will perform additional bioinformatic analyses using our existing RIP-seq datasets. These analyses will include:

• characterization of transcript classes (coding and non-coding RNAs);
• analysis of sequence composition and motif enrichment;
• prediction of RNA structural features (including GC content, normalized minimum free energy, paired nucleotide fraction and predicted stem length);
• analysis of overlap with repetitive elements (including Alu, LINE and LTR elements);
• comparison of predicted structural and sequence features of FASN-associated RNAs and J2-enriched RNAs;

• additional comparisons between dsRNA populations identified in wild-type and FASN knockout cells. These analyses will help determine whether FASN preferentially associates with specific classes of endogenous RNAs. Based on the shortlisted RNAs, we will also test selected FASN-associated transcripts by RT-qPCR following RNase III treatment, to determine whether they are forming dsRNA with or without FASN depletion.

• Strengthening the link between endogenous dsRNA accessibility and innate immune activation To provide more evidence that increased accessibility of endogenous dsRNAs results in enhanced innate immune sensing, we plan to further examine activation of dsRNA sensing pathways.

Specifically, we will assess activation of downstream signaling components (including IRF3 activation) and further investigate the association of endogenous dsRNAs with innate immune sensors by examining MDA5 recruitment to J2-positive dsRNA complexes. Where technically feasible, we will also evaluate the spatial proximity between endogenous dsRNAs and MDA5 by microscopy-based approaches.

To strengthen the link between endogenous dsRNA sensing and the primed inflammatory phenotype, we also plan to generate polyclonal CRISPR/Cas9 MDA5 or MAVS knockout cell populations in combination with FASN depletion by siRNA treatment, and evaluate the effects on interferon-responsive gene expression such as IFIT1.

• Relationship between RNA binding and the metabolic functions of FASN Several reviewers raised the important question of whether the observed immune phenotypes arise from FASN-mediated regulation of endogenous dsRNAs or from broader metabolic consequences of FASN deficiency.

To address this point, we plan to complement our genetic analyses with pharmacological inhibition of FASN catalytic activity using independent inhibitors and assess their effects on endo-dsRNA accumulation and Sindbis virus replication. We also plan to evaluate whether supplementation with exogenous palmitate rescues the observed phenotypes. These experiments will help distinguish catalytic from non-canonical functions of FASN in regulating endo-dsRNA accessibility and antiviral responses.

Where feasible, we will also attempt complementation experiments using ectopic expression of wild-type FASN in FASN knockout cells.

Additional manuscript improvements

We will incorporate the requested additional quantifications, improve figure presentation and labeling, clarify the rationale for selected validation experiments, expand the discussion of alternative mechanistic models, and address the editorial and presentation issues identified by the reviewers.

__3. __Description of analyses that authors prefer not to carry out:

Although we agree that additional mechanistic studies would further strengthen the manuscript, we believe that several of the experiments suggested by the reviewers extend beyond the scope of this work.

In particular, generation and characterization of multiple FASN domain-specific or RNA-binding mutants is currently not feasible. FASN is a large multifunctional enzyme containing several catalytic domains and no canonical RNA-binding domain has yet been defined. Consequently, designing mutants that specifically disrupt RNA binding while preserving enzymatic activities would be possible but difficult to deliver within the timeframe of this revision. Instead, we propose to address the reviewers' concerns through complementary pharmacological approaches (using FASN inhibitors), palmitate supplementation experiments and wild-type FASN complementation where feasible.

Similarly, while high-resolution CLIP approaches would provide valuable information regarding FASN binding sites on the RNA, these technically demanding experiments fall beyond the scope of the current revision. We believe that the additional computational analyses, biochemical validation and functional experiments described above will substantially strengthen the conclusions regarding the interaction between FASN and endogenous structured RNAs.

Finally, although generation of stable double knockout cell lines (e.g. FASN/MAVS or FASN/MDA5) could provide additional mechanistic insight, we consider that this could take too much time. Instead, we plan to generate polyclonal CRISPR/Cas9 knockout populations of MAVS or MDA5 in combination with siFASN to strengthen the causal relationship between endogenous dsRNA sensing and the observed primed immune phenotype.

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

The manuscript entitled, "Fatty Acid Synthase associates with nuclear-derived cytoplasmic dsRNA molecules and influences antiviral innate immune response," by Pasquier et al. identifies an unexpected function for FASN as an endogenous dsRNA-associated protein and explores the relationship between FASN, cellular dsRNA homeostasis, and antiviral innate immunity. Using FASN knockout cells, the authors demonstrate that depletion of FASN results in accumulation of cellular dsRNA, characterize the endogenous dsRNA species associated with FASN, and show that loss of FASN is accompanied by increased expression of interferon-stimulated genes and restriction of SINV replication. The biochemical characterization of FASN-associated dsRNAs together with the accompanying transcriptomic analyses provide compelling evidence that FASN interacts with a distinct subset of endogenous dsRNAs, representing a novel function for this metabolic enzyme. While evidence is presented that FASN can associate with endogenous dsRNA, several aspects of the proposed functional model extend beyond what is directly demonstrated by the data. In particular, the manuscript presents dsRNA accumulation, innate immune activation, and viral restriction as a consequence of FASN-mediated dsRNA regulation. However, it remains unclear whether these downstream phenotypes arise specifically from the newly described RNA-binding activity of FASN or instead reflect broader cellular consequences of FASN deficiency, including alterations in lipid metabolism and protein palmitoylation. Likewise, although the authors identify a population of FASN-associated dsRNAs, the relationship between these transcripts and the dsRNAs that accumulate following FASN depletion remains insufficiently resolved, making it difficult to mechanistically understand how FASN regulates dsRNA homeostasis. Overall, the manuscript provides a number of intriguing observations regarding FASN association with endogenous dsRNA. However, the functional relationship between these findings and the proposed effects on dsRNA homeostasis and innate immunity would benefit from additional clarification before the mechanistic model can be fully supported.

Major Concerns

1. It remains unclear whether the inflammatory and antiviral phenotypes observed following FASN depletion are attributable to FASN's newly described dsRNA-binding activity or to the broader metabolic consequences of losing FASN. The manuscript presents dsRNA accumulation, induction of ISGs, and restriction of SINV as downstream consequences of FASN-mediated dsRNA regulation. While these observations are compelling, they remain correlative and do not distinguish between effects arising from dsRNA regulation versus the numerous metabolic changes expected following loss of FASN. In particular, reduced palmitate production and altered protein palmitoylation are well-established consequences of FASN depletion and have documented roles in MAVS signaling and antiviral immunity.

This distinction is important because the principal claim of the manuscript is not simply that FASN depletion alters innate immunity, but that its RNA-binding activity is proposed to underlie these effects. At present, the data support an association between these phenotypes but fall somewhat short of demonstrating that the observed immune response is specifically driven by FASN-mediated regulation of endogenous dsRNA. 2. While the manuscript does provide evidence that FASN associates with a subset of endogenous dsRNAs, the relationship between these RNAs and those that accumulate following FASN depletion remains unclear. The authors conclude that FASN regulates dsRNA homeostasis, yet also show that transcripts associated with FASN do not measurably accumulate in knockout cells. This creates a disconnect between RNA association and functional regulation that is not adequately resolved.

An overlap analysis comparing the dsRNA populations identified in wt and KO cells would help clarify whether FASN regulates a stable population of transcripts or whether broader remodeling of the dsRNA landscape occurs following FASN loss. More generally, the manuscript would be stronger if it helps clarify or distinguish the observation that FASN binds endogenous dsrna from the conclusion that it regulates cellular dsRNA homeostasis; the latter is not fully supported with the presented data.

Minor concerns

• The mitochondrial localization of dsRNA needs additional validation. Specifically, Fig 3A requires quantitative analysis of mitochondrial abundance, while Fig 3C could be strengthened through orthogonal validation of mitochondrial localization (e.g., microscopy-based co-localization or further purification of the mitochondrial fraction). Inclusion of an RNase control would also help demonstrate that the enrichment is specific to dsRNA.
• The role of the ADAR depletion experiments within the overall narrative is somewhat unclear. Consider either integrating these data more directly into the proposed model or reducing their emphasis. Along similar lines, Fig 4B should clarify whether the increased FASN-dsRNA association reflects greater binding or simply increased abundance of both FASN and dsRNA following 5-Aza treatment.
• Several aspects of the data presentation needs clarification. These include the rationale for selecting IFIT1 for validation (Fig 2A), the relationship between proteins highlighted in the Fig 4 volcano plot and those selected for immunoblot validation, the apparent reduction in tubulin complicating interpretation of the SINV capsid blot (Fig 5B), and the conclusion that J2-positive puncta are distinct from SINV RNA without co-localization analysis.
• Several figures could be improved for presentation. Quantification of the J2 signal in Fig S1C (analogous to Fig 1D) and improved labeling of the volcano plots would improve readability.
• Several minor editorial revisions are recommended. These include describing ACP as a carrier/tethering rather than catalytic domain, citing Fig S2 in the Results, defining the long form of NES in the Fig 2 legend, removing redundant panel descriptions in the Fig 3G legend, correcting the missing text on page 14, and resolving the duplicated figures and formatting issues present throughout the manuscript.

Significance

Strengths

Nice extension of FASN biology beyond its canonical metabolic role Introduces FASN as a potential endogenous dsRNA-binding protein Broad interest for the RNA biology and innate immunity communities

Limitations

RNA binding not fully demonstrated with higher-resolution approaches such as more precise CLIP approaches Mechanistic link between FASN dsRNA homeostasis and innate immune activation remains incomplete

Advance

Good conceptual advance but is more descritive than mechanistic

Audience

RNA biology RNA-binding proteins Innate immunity Host-virus interactions Moonlighting metabolic enzymes

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

Learn more at Review Commons

Referee #2

Evidence, reproducibility and clarity

The manuscript by Pasquier and colleagues investigates the role of fatty acid synthase (FASN) in the regulation of innate immune signaling through its interaction with endogenous dsRNAs. The authors build upon their previous study, in which they identified FASN as a potential dsRNA-binding protein. They show that FASN knockout results in increased cytoplasmic dsRNA detection accompanied by the induction of inflammation-related genes. Subsequent multi-omics analyses reveal that FASN associates with dsRNAs derived from nuclear genome-encoded transcripts in multiple contexts. Interestingly, FASN depletion does not alter the overall expression of these dsRNAs but increases their detection by the J2 antibody. Functionally, FASN depletion enhances innate immune responses to dsRNA stimulation and Sindbis virus infection.

While the study provides evidence supporting an proviral role for FASN, the manuscript lacks mechanistic insight into this phenomenon. In particular, it remains unclear how FASN depletion enhances dsRNA detection without altering endogenous dsRNA abundance. The following points should be addressed:

1) The main limitation of the manuscript is the absence of a mechanistic explanation for how FASN depletion leads to increased dsRNA detection without affecting expression. Does the increased dsRNA detection require a direct interaction between FASN and dsRNAs? The authors should provide additional evidence to clarify whether FASN binding masks dsRNA epitopes or regulates dsRNA accessibility to recognition by J2 and innate immune sensors.

2) The authors show that FASN directly binds nuclear genome-encoded transcripts. It would be important to perform RNA-FISH for selected FASN-interacting RNAs to determine whether their cellular localization or J2-detectable signal is altered in FASN-depleted cells.

3) In Figure 2B, the authors demonstrate enrichment of inflammation-related gene signatures in FASN knockout cells. However, the magnitude of induction is not clear. How does the inflammatory response compare with canonical innate immune activation, such as viral infection or poly(I:C) stimulation? Although Figure 2A partially addresses this point, many of the highlighted genes are not directly associated with inflammatory responses.

4) For the transcripts directly associated with FASN, do they contain predicted dsRNA-forming regions or known structured RNA elements? The current data do not sufficiently demonstrate whether these transcripts indeed form dsRNA structures. Although some are enriched in J2 immunoprecipitation, additional structural analyses, including computational prediction of dsRNA regions, would strengthen the conclusion.

5) The authors should further investigate whether the enhanced antiviral activity observed upon FASN depletion is mediated by elevated endogenous dsRNA sensing. Are dsRNA sensors such as PKR, MDA5, or RIG-I more strongly activated in FASN knockout cells? Do these sensors exhibit increased binding to endogenous dsRNAs following FASN depletion?

Significance

Main strength: Uncover the proviral role of FASN via regulation of endogenous dsRNAs

Limitations: Molecular mechanism on how FASN depletion increases the accessibility of dsRNAs without affecting their expression. Also, need better characterization of FASN-binding RNAs, especially their secondary structure.

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 manuscript identifies a potential connection between FASN, endogenous dsRNAs, and innate immune signaling. The authors show that FASN depletion increases cytoplasmic dsRNA staining, enhances IFN transcription and restricts Sindbis virus replication. Overall, the basic observation seems to be solid and well-controlled. Depending on which journal this is being considered for, the central mechanism could be better developed and elucidated to entail more molecular details. As it currently stands, several important questions, especially ones regarding the FASN-RNA interactions remain unresolved.

Major comments

1. The conclusion that FASN regulates dsRNA accessibility rather than dsRNA abundance requires further support. The authors show increased J2 staining without major changes in the global dsRNA landscape by J2-RIP-seq. However, alternative explanations could be: (1) changes in dsRNA structure or length distribution could affect J2 recognition, i.e. epitope masked by FASN binding; (2) differences in RNA-protein complex assembly could influence J2 accessibility; (3) Altered subcellular localization of dsRNAs could increase immunofluorescence signals without substantially affecting RIP-seq recovery.
2. The nature of the FASN-RNA interaction remains unclear. The authors demonstrate that FASN associates with a subset of endogenous RNAs, but it is not clear whether this interaction is sequence-specific, structure-specific, or largely nonspecific. Are there common sequence motifs, secondary structures, repetitive elements, or specific transcript classes enriched among FASN-associated RNAs? Without a clearer understanding of RNA selectivity, it remains difficult to evaluate the biological significance of the observed interactions.
3. The study would be significantly strengthened by complementation experiments. Although the FASN knockout phenotype is convincing, add-back experiments are needed to demonstrate specificity and probe potential mechanisms. Reconstitution with wild-type FASN should rescue the dsRNA and immune phenotypes. Furthermore, domain-specific mutants or catalytic mutants (e.g., palmitoylation) could help distinguish whether the observed effects depend on FASN enzymatic activity, a specific protein domain, or a non-canonical RNA-binding function. Such experiments would greatly improve the mechanistic depth of the study. It will also address whether the observed dsRNA increase phenotype is irreversible.
4. The manuscript proposes that increased endogenous dsRNA sensing drives the inflammatory phenotype in FASN-deficient cells. However, direct evidence for enhanced PRR engagement is currently lacking. Although MDA5 and MAVS knockdown experiments suggest a possible contribution of this pathway, the observed knockdown effects are relatively modest and needs to be repeated by CRISPR knockout. Does FASN, MAVS double knockout cells rescue the slow growth phenotype? In addition, direct measurements of PRR activation, such as MDA5-RNA association, MAVS activation, IRF3 phosphorylation, or related downstream signaling events, were not examined.
5. The antiviral phenotype observed during Sindbis virus infection is interesting, but the underlying mechanism remains uncertain. The authors propose that enhanced endogenous dsRNA sensing contributes to viral restriction, yet alternative explanations related to altered lipid metabolism, impaired membrane remodeling, or other consequences of FASN deficiency cannot be excluded. Especially when MDA5 and MAVS knockdown effect appears modest. Additional experiments disrupting interferon signaling or innate immune sensing pathways using the FASN, MAVS double knockout cells would help determine whether the antiviral phenotype is directly linked to the proposed dsRNA sensing mechanism.

Significance

This manuscript identifies a potential connection between FASN, endogenous dsRNAs, and innate immune signaling. The authors show that FASN depletion increases cytoplasmic dsRNA staining, enhances IFN transcription and restricts Sindbis virus replication. Overall, the basic observation seems to be solid and well-controlled. Depending on which journal this is being considered for, the central mechanism could be better developed and elucidated to entail more molecular details. As it currently stands, several important questions, especially ones regarding the FASN-RNA interactions remain unresolved.

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Reply to the reviewers

Response to the points raised by the reviewers.

Once again, we would like to thank the reviewers for their comments. We have systematically addressed their concerns, as detailed below.

Reviewer #1

Evidence, reproducibility and clarity

This study demonstrates that BICD2, previously known as an adaptor protein for dynein, is involved in regulating centriole engagement during mitosis. First, using different antibodies, it was shown that BICD2 localizes near the mother centriole, as observed by super-resolution microscopy. During G1 and S phases, BICD2 localizes slightly outside the Cep152 ring, while in G2 to mitosis, it localizes near the cartwheel component SAS-6. Moreover, analysis of deletion mutants revealed that BICD2 localizes to the centrosome in a CC domain-dependent manner at the C-terminal end. The localization pattern resembling a ring in the cytoplasm was also observed through the CC3 domain. Next, BICD2 knockout (KO) cells were generated to investigate centriole dynamics. In BICD2 KO cells, the distance between the mother and daughter centrioles was observed to increase from G2 to mitosis compared to controls. Along with this, early centriole disengagement and centriole amplification phenotypes were observed. The increased distance phenotype between centrioles was rescued in BICD2 wild-type (WT) and mutant forms lacking the CC1 domain at the N-terminus, suggesting that this function of BICD2 is independent of dynein. Additionally, BICD2 mutants mimicking phosphorylation at the C-terminus showed reduced centrosome localization and were unable to rescue the phenotypes seen in BICD2 KO cells.

While the study clearly demonstrates BICD2's contribution to centriole engagement, the underlying mechanisms of how BICD2 is involved in centrosome localization and centriole engagement remain unclear. As it is anticipated that the function of BICD2 is independent of dynein, further exploration of this unknown mechanism would enhance the value of the paper. Below are the concerns that should be addressed, including new experiments.

Main Points:

1. __ Fig. 1-3: Regarding the localization of BICD2 to centrioles, during the G1-S phase, its localization appears to overlap with PCM. Experimental investigation should be performed to examine whether BICD2's centrosomal localization is influenced by knockdown of PCM components like PCNT, Cep192, or Cep152.__ We now show that BICD2 localization does not depend on pericentrin (Supplementary Figure S4B). We also show that the two proteins do not colocalize (Supplementary Figure S4A and S4D) and are functionally independent (Figure 5).

We also show that BICD2 localization does depend on the torus protein CEP152 (Figure 8B). Importantly, our data indicate that BICD2 interacts with the N-terminal region of CEP152, suggesting that this interaction places BICD2 at the outer region of the torus (Figures 8C and 8D). We propose that this provides a mechanistic basis for BICD2 function in maintaining mother-daughter centriole engagement.

__ Fig. 7: The experiments using BICD2 mutants suggest that the function of BICD2 here is independent of dynein. To further investigate whether BICD2's role in centriole engagement is independent of dynein, experiments should be conducted to examine the effect of dynein knockdown on BICD2 localization to the centrosome and centriole engagement.__

Using Dynapyrazole-A, a fast-acting and potent dynein inhibitor, we demonstrate that acute inhibition of dynein motor activity affects neither the centrosomal localization of BICD2 during G2 and M phases (Supplementary Figure S3A) nor centriole engagement (Supplementary Figure S3B). Together with experiments using BICD2 mutants deficient in dynein interaction (Figure 7B), these data compellingly demonstrate that the recruitment and function of BICD2 at the centriole is dynein-independent.

__ Fig. 4: The CC4 domain at the C-terminus of BICD2 is important for its centrosomal localization, but identifying the binder/recruiter responsible for BICD2's centrosome localization would be desirable.__

We thank the reviewer for prompting us to investigate this further. We are delighted that we now identify the torus protein CEP152 as the BICD2 binder/recruiter at the centriole (Figure 8). As we discuss in the manuscript, our observation that the outward-facing N-terminus of CEP152 interacts with the C-terminal region of BICD2 provides a mechanistic basis for understanding BICD2's role in maintaining mother–daughter centriole engagement.

__ Fig. 7: Rescue experiments using BICD2 mutants suggest that BICD2's functional domains are critical. Further experiments by creating mutants missing parts of CC2 or CC3 could identify functionally important domains of BICD2 by observing any loss-of-function phenotypes at the centrosome.__

We fully appreciate the reviewer’s suggestion to examine the roles of the CC2 and CC3 regions. We believe that these domains, and particularly the unstructured loop within CC3, are important for both BICD2 localization, function and regulation at the centrosome. However, given that our current data already establish a clear mechanism for BICD2 centriolar recruitment via CEP152 and the CC4 region, we feel these additional structural studies fall outside the core scope of the present manuscript. We hope the reviewer agrees that the current evidence provides a robust foundation for our conclusions, and we look forward to addressing the roles of CC2 and CC3 in a dedicated future study.

__ Fig. 6: Regarding the BICD2 KO cell phenotype, is there experimental evidence showing an increase in centriole number during mitosis? For instance, while no abnormality in centriole number may occur during G2, a trend of increase in mitosis should be experimentally demonstrated. Also, how should the slight differences in phenotypes between Ndelta4 and Ndelta5 BICD2 KO cells be interpreted?__

We thank the reviewer for highlighting this point, but we would like to clarify that we do indeed observe a significant increase in centriole number during both mitosis and G2 phase across multiple cell lines in our BICD2 KO models and RNAi experiments (Figure 4E, RPE-1 KO cells, and 4G, U2OS cells, RNAi) and G2 (Figure 5C, both RPE-1 and U2OS, RNAi). As the main text was not explicit enough on this point, we have revised the manuscript to describe these observations more clearly.

Regarding the phenotypic differences between BICD2 KO lines, we assign them to the clone-to-clone functional heterogeneity often seen in CRISPR/Cas9-generated cell lines. Importantly both clones show a consistent, statistically significant phenotype (e.g., impaired engagement and increased centriole numbers) compared to wild-type controls, confirming that the overall defect is robust and specific to BICD2 loss. We have added a clarifying note on this in the revised manuscript: “Figure 4F; we assign the differences between BICD2-/- cell lines to standard clone-to-clone phenotypic heterogeneity often seen in CRISPR/Cas9-generated cell lines.”

__ Fig. 8: Regarding the phosphorylation of BICD2 at the C-terminus: The phenotypes of mutants where these two phosphorylation sites are changed to alanine should be experimentally observed. It is expected that the removal of BICD2 from the centrosome during mitosis could be rescued. Additionally, the effect of PLK1 or CDK1 inhibitors on the removal of BICD2 from the centrosome should be investigated.__

We agree with the reviewer that phosphonull mutants should be added to these experiments. As mentioned above we have decided to remove the preliminary data regarding BICD2 phosphorylation from the manuscript data to present a more comprehensive, dedicated study on BICD2 phosphorylation in the near future. In fact, we have already performed the suggested experiments, including the phosphonull mutants and kinase inhibitor treatments, and would be glad to share these additional results if the reviewers would find them helpful. Interestingly, our experiments show that BICD2 centrosomal amounts are not affected by PLK1 inhibition (using BI 2536); CDK1 inhibition (RO-3306), although not significatively changing the amount of BICD2 at the centrosome, slightly diminishes it. We currently favor a model in which BICD2 is predominantly regulated by CDK1, and we are actively defining the precise molecular mechanism governing this regulation.

Minor Points:

__ Fig. 1-3: During G1 and S phases, BICD2 localizes near the mother centriole, and from G2 onward, it colocalizes with SAS-6. How can this be explained?__

We currently do not have a clear explanation for this transition, as our focus has been in understanding BICD2 recruitment to the centriole (and its role in centriole engagement). We view this as a very interesting question that could be studied together with BICD2 regulation through phosphorylation. Our current hypothesis is that most of BICD2 is removed through phosphorylation in late G2 and M, with a pool remaining at the mother-daughter interface, possibly protected by a yet to be understood mechanism. We have added a sentence in the discussion addressing this (“ A pool of protein could be protected and correspond to the observed remnant of BICD2 at the mother-daughter interface.“). This last pool, as we discuss in the manuscript, could be further phosphorylated at the M/G1 transition or cleaved by separase (although this last point is of course highly speculative).

__ Fig. 4: The GFP-BICD2 488-820 fragment forms cytoplasmic rings, which is interesting. This domain contains the CC4 domain, so it can localize near the centriole, but why does it not form a perfect ring there? Also, which other centriole/centrosome markers were used for colocalization studies? Does knockdown of PCM1 affect BICD2's centrosomal localization?__

We show in Figures 6G and 6H that BICD2 488-820 can form a ring around the centriole. Indeed this polypeptide contains the CC4 region, which our results indicate it will guide it to the centriole (through an interaction with CEP152). Once the available CEP152 is occupied with BICD2 we assume that BICD2 488-820 forms oligomers that assemble ring-like structures outside the centriole.

Other centrosomal markers used are SAS-6.

We now show that PCM1 knockdown does not affect BICD2's centrosomal localization (Supplementary Figure S4C). Although our results indicate that partial forms of BICD2 such as BICD2 488-820 can colocalize with PCM-1 (Figure 6D), full length endogenous BICD2 (or GST-BICD2) does not seem to colocalize with this protein and thus the centriole satellites (Supplementary Figure S4A). We note this discrepancy in the text: “The presence of BICD2 at the centriolar satellites has been suggested previously (Quarantotti et al, 2019); we ignore the reason why in the conditions used in this study only C-terminal fragments of BICD2 but not the full-length protein”. The relationship between satellites and BICD2 grants further studies. Our data suggests that centriolar localization of the protein may be regulated, possibly by its intramolecular structure, and that regulated binding of BICD2 to a yet to be identified partner may recruit the protein to satellites either for its transport to the centrosome or in order to perform a specific function at the satellites. We have added a sentence to the text to note this: “This suggests that BICD2 satellite localization is regulated (possibly via intramolecular autoinhibition) to mediate BICD2 transport or a distinct satellite-specific function of this protein.”.

__ Fig. 4A: What are the aggregates observed in the cytoplasm under the GFP-BICD2 + ice condition? Also, does the 1-575 mutant fail to localize to the centrosome upon ice treatment?__

We currently do not know the nature of the GFP-BICD2 full length aggregates observed upon microtubule depolymerization. We also observe GFP-BICD2 aggregates in cells that express high amounts of the polypeptide, leading us to hypothesize that it may be insoluble and the disappearance of microtubules may liberate it from motor complexes resulting in its aggregation -although of course more work would be needed to clarify this.

We now show new data (Supplementary Figure S5), showing that the localization of not only GFP-BICD2 1-575 but also the C-terminal fragments 272-820 and 488-820 are not significantly affected by cold-induced microtubule depolymerization. These last results strongly suggest that BICD2 localization at the centriole is microtubule independent and are compatible with our data showing that BICD2 can directly interact with the centriolar protein CEP152.

__ Can similar phenotypes be observed in other cell types when BICD2 is knocked down? This should be experimentally validated.__

Our current manuscript now shows that similar phenotypes regarding centriole separation and amplification are observed upon BICD2 depletion in RPE-1 cells (non-transformed, p53-wildtype) and U2OS cells (transformed). These are shown in Figure 4 (RPE-1 knockout, U2OS RNAi knockdown) and Figure 5 (RPE-1 and U2OS RNAi knockdown).

__ Are there previous studies suggesting that this function of BICD2 is evolutionarily conserved? This should be addressed.__

To our knowledge there are no previous studies describing BICD2 function at the centrosome, excepting the recent article by Kuang et al., (Kuang W et al. 2025. BICD2 promotes ciliogenesis by facilitating CP110 removal from the mother centriole. EMBO reports 26:5567–5588. DOI: https://doi.org/10.1038/s44319-025-00597-0), that describes a role for BICD2 during ciliogenesis in non-cycling cells. As we mention in our discussion this new role may be related to the distal pool of protein that we observe using ExM, and we don’t think is related to the function of the proximal pool of BICD2 at the torus in cycling cells that we describe in our manuscript.

Regarding functional conservation, BICD2 orthologs are widely distributed across metazoans (as reflected in OrthoDB, which lists ~5,000 ortholog genes across ~2,500 species). They share a remarkably conserved C-terminal domain that acts as a docking interface mediating subcellular targeting independently of dynein motor activity (i.e. through binding to Rab6, RanBP2 and, as shown here, CEP152). Cross-species analyses show that this C-terminal domain is preserved in most eukaryotic orthologs, including Drosophila melanogaster BICD (UniProt P16568) and Caenorhabditis elegans BICD-1 (UniProt V6CJ04). Interestingly, several predicted orthologous sequences in public databases retain high C-terminal similarity while completely lacking the N-terminal regions containing the CC1 box motif (residues 29–57 in human BICD2) required for dynein interaction (e.g., predicted isoforms in mouse or camels). Thus, dynein-independent scaffolding functions may represent an ancient, foundational role of the BICD protein family, or alternatively (and perhaps most probably, given that basal metazoans like sponges or Cnidaria do show a conserved N-terminus), these truncated forms may have evolved to fulfill distinct cellular roles operating independently of motor-adaptor activity. We have added a passage at the end of the discussion to reflect this.

Significance

In this paper, the identification of BICD2 as a novel factor regulating centriole engagement is of significant importance. However, the mechanisms through which BICD2 controls its localization to the centrosome and regulates centriole engagement remain largely undefined. Further exploration of these mechanisms would likely enhance the value of the paper.

The findings are likely to be of great interest to researchers in the field of cell biology, particularly those focusing on centrosome biology.

The above feedback comes from a researcher specializing in centrosome studies.

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Reviewer #2

Evidence, reproducibility and clarity

Montez-Ruiz and colleagues explore the role of a dynein adaptor BICD2 in the engagement of mother and daughter centrioles. Cells need to maintain centriole engagement in interphase to prevent centriole reduplication and in early mitosis to prevent the formation of aberrant mitosis spindles. The authors demonstrate that BICD2 is a centriolar protein that surrounds the mother centriole adjacent to the daughter centriole. It is removed from centrosomes in mitosis, which, in turn, is responsible for centriole disengagement. Further, they suggest that in BICD2 knock-out G2 and early mitotic cells, centrioles disengage prematurely. By conducting rescue experiments, the authors conclude that BICD2 regions CC2, CC3, and CC4, which are dynein-independent, are essential for their function at the centrosome. Finally, they show that the phosphorylation of S817 and S819 of BICD1 controls its centrosome localization.

Major comments:

1. __ Based on F1 and SF1, BICD2 is reduced from centrosomes already in early G2. So, it is hard to square how removing a factor that is not present at the centrosomes at the time of disengagement would dysregulate disengagement. The study at this stage does not explain how BICD2 contributes to centriole engagement only in mitosis, while it does not affect centrioles in S.__ We now present new data obtained using expansion microscopy (ExM) that, together with our super-resolution observations, clarifies this point. As shown in the new Figure 3 and Figure EV2 (and supported by Figures EV3 and EV4), although the total amount of BICD2 at centrosomes is significantly reduced from G2 to M, a pool of BICD2 persists at the mother centriole until late mitosis. Importantly, this pool tends to localize close to the daughter centriole. We note this in the text (“BICD2 remained visible in both diplosomes, associated with the SAS-6 foci (Figure 3, Figures EV2-3). Around anaphase, BICD2 was not detectable in some diplosomes, while others retained some protein (again, close to the SAS-6 foci, which at this point were disappearing from the centrioles as the result of the disassembly of the cartwheel).”). Supported by our BICD2 depletion experiments, we propose that this centriolar pool enables BICD2 to contribute to engagement until late mitosis, when the remaining protein at the centrosome is ultimately removed. We highlight this model in the Discussion section (“In mitosis, when the protein progressively disappears from the centrosomes, BICD2 remains functionally relevant -likely via the small pool that persists at the mother–daughter centriole interface.”).

Based on our new data demonstrating an interaction with CEP152, we propose that BICD2 forms an outer component of the centriolar torus. Centriole engagement is known to be maintained during S phase by the cartwheel (Huang F et al. 2022. Cartwheel disassembly regulated by CDK1-Cyclin B kinase allows human centriole disengagement and licensing. The Journal of Biological Chemistry 298:102658. DOI: https://doi.org/10.1016/j.jbc.2022.102658; Ito KK et al. 2025. Multimodal mechanisms of human centriole engagement and disengagement. The EMBO journal 44:1294–1321. DOI: https://doi.org/10.1038/s44318-024-00350-8), with the torus playing a role in cohesion later in the cell cycle. We note in our manuscript that this is consistent with our observations and supports a model in which BICD2 functions as part of the torus: “During S phase, mother–daughter centriole cohesion is maintained by the cartwheel (Huang et al, 2022; Ito et al, 2025) and, consistently, does not depend on BICD2.”

__ The interpretation that the longitudinal localization of the BICD2 signal coincides with SAS-6 and procentrioles requires further evidence. BICD2 seems largely localized to the other regions around the mother centriole, and in some examples, it does not colocalize with the site of the daughter centriole or SAS-6 (for instance: F2B second row; SF4B, second row; SF5, fourth row; SF6 upper row).__

We have added an ExM characterization of BICD2 centrosomal localization in the revised manuscript (Figures 2 and 3), that we think further clarify this point, showing that BICD2 longitudinally coincides with the torus and the daughter centriole. This is supported by new additional superresolution images (Figure 2, Figure EV2).

Note that ExM revealed an additional stable pool of BICD2 at the distal end of the centrioles that is not detected using standard methanol fixation combined with 3D-SIM. As discussed in the text this distal pool may reflect additional centriolar functions of BICD2.

__ BICD2 is important for centrosome-nucleus tethering during centrosome separation in G2, and its global removal likely affects the dynamics of the spindle assembly. Is G2 and mitotic progression affected in knockouts? Do the knockout cells show issues with chromosome alignment? Such analyses are critically missing from the manuscript.__

BICD2 knockout cells indeed show a slightly higher mitotic index than their wild type counterparts, and a higher frequency of lagging chromosomes in anaphase and telophase as well (new data, shown in Figure EV5C). We agree with the reviewer that these might result from the role of BICD2 tethering centrosomes to the nuclear envelope to facilitate their separation during the initial steps of spindle formation. We have added a sentence in the text noting this: “As expected from cells with supernumerary centrioles, BICD2-/- cells showed a slightly higher mitotic index and a higher frequency of lagging chromosomes in anaphase and telophase (Figure EV5C), although these mitotic defects might also be partially attributed to the role of BICD2 in centrosome separation (Splinter et al, 2010; Gallisà-Suñé et al, 2023).”

__ In general, SCLT experiments are ambiguous. Centriole disengagement spontaneously occurs during prolonged prometaphase induced by SCLT. Accordingly, F6D shows that many centriole pairs in the control sample are disengaged after 16h of SCLT treatment. Although the distance between centrioles in knockout cells is, on average, larger, without knowing how BICD2 perturbations affect the dynamics of the mitotic spindles and mitosis progression, SCLT experiments do not provide enough insight.__

After 16h of SCLT treatment, the authors regularly measure centriole distances in mitosis smaller than 500 nm in all samples. This suggests that the used method (which also needs to be described) cannot reliably assess centriole engagement status. Centrioles can be disengaged but adjacent. The authors reference Shukla et al. 2015 to compare the centriole-to-centriole distances here with those from that publication. However, in Shukla 2015, centriole-to-centriole distances increase from S to M. But here, in F6, the control centriole distances in S, G2, and early M are almost identical and less than 500 nm. This discrepancy needs to be addressed.

We thank the reviewer for these constructive comments. We appreciate the opportunity to further clarify our methodology and experimental rationale.

Validity and necessity of STLC treatment (Figures 4D and 7)

We fully agree with the reviewer that prolonged STLC treatment (16 hours) carries inherent limitations and should not serve as the sole experimental system for studying centriole engagement. As the reviewer notes, 16 hours of STLC treatment results in a baseline population of control cells displaying disengaged centrioles. This population likely represents cells that entered mitosis early during the treatment and remained arrested for the longest duration, or cells with inherently less robust engagement machinery.

However, we would like to highlight two key observations that validate STLC as a useful comparative tool in our study:

• The significative increase in the number of cells with higher intercentriolar distances that indicate disengagement in particular experimental conditions. We show that depletion of BICD2 consistently leads to a statistically significant increase in mean intercentriolar distances compared to controls under identical STLC conditions, indicating a distinct weakening of centriole engagement in a substantial number of cells (and thus suggesting that BICD2 is part of the engagement mechanism).

• Validation in unarrested cells: Crucially, this effect is not an artifact of mitotic arrest. Unarrested, normally cycling mitotic cells also display significantly increased intercentriolar distances in the absence of BICD2 (Figure 4C).

Following the initial characterization in Figure 4D, we restricted the use of STLC exclusively to experiments requiring cell transfection and recombinant protein expression (Figure 7). Human RPE-1 cells offer the key advantage of being an untransformed, p53-wild-type model. However, they also present technical challenges, including lower transfection efficiencies and sensitivity to experimental manipulation. Capturing a statistically robust sample of transfected, unarrested mitotic cells proved technically challenging. STLC treatment provided a necessary tool to enrich for mitotic cells while allowing clear observation of rescue effects.

We have explicitly clarified this technical rationale in the manuscript text:

"Although this treatment inherently increased mean intercentriolar distances, it nevertheless enabled clear observation of the effects of BICD2 ablation, while yielding a sufficient number of mitotic cells expressing the recombinant proteins."

Assessment of centriole engagement

We agree that centrioles can occasionally be disengaged while still remaining adjacent. To avoid oversimplifying the observed phenotypes, we chose to report raw intercentriolar distances rather than applying an arbitrary binary classification of "engaged" versus "disengaged." Furthermore, we do not rely solely on distance measurements to assess engagement status. We complemented these data by quantifying c-NAP1-positive centrioles in unarrested, cycling mitotic cells (Figure 4E, F). Because c-NAP1 loading marks centriole-to-centrosome conversion (and thus licensing), this functional readout independently confirms that BICD2 loss promotes premature centriole disengagement.

Intercentriolar distances across the cell cycle and cell-type variation

Regarding the comparison with Shukla et al. (2015), we note that their study was conducted in HeLa cells, whereas our primary model is RPE-1 (alongside U2OS cells). Variations in centriole engagement dynamics and distance kinetics can likely be attributed to intrinsic differences among these cell types:

RPE-1 cells: baseline intercentriolar distances in S-phase control RPE-1 cells (0.4–0.5 µm, measured using centrin) match those reported for HeLa cells in S-phase by Shukla et al. However, in RPE-1 control cells, these distances remain relatively constant from S phase through early M phase (Figure 4).

U2OS cells: U2OS cells exhibit a slight increase from 0.43±0.01 µm in G2 to 0.50±0.01 µm in M (Figure 5), illustrating that slight variations occur between cell lines.

Other studies similarly report persistent baseline distances around 0.5 µm through early cell cycle stages. For example, Yaguchi et al. (Yaguchi K et al. 2018. Uncoordinated centrosome cycle underlies the instability of non-diploid somatic cells in mammals. The Journal of Cell Biology 217:2463–2483. DOI: https://doi.org/10.1083/jcb.201701151) observed intercentriolar distances close to 0.5 µm in diploid HAP1 cells throughout mitosis and into early G1 phase, with substantial disengagement (>0.8 µm) occurring only well after cytokinesis onset.

To address this discrepancy, we have added the following sentence to the manuscript text: "Note that in wild-type S-phase RPE-1 cells, intercentriolar distances measured using centrin as a marker were similar to those described in S-phase HeLa cells (Shukla et al., 2015), namely 0.4–0.5 µm; however, in contrast to HeLa cells, these distances remained fairly constant from S to early M phase in RPE-1 cells." We have also updated the Materials and Methods section to provide a precise description of how intercentriolar distances were measured: “Intercentriolar distances were assessed as the distance between centrin foci of the same diplosome in maximum projections of z-stacks”

__ The authors suggest that BICD2's functions at the centrosome are independent of its dynein functions. They show that GFP-BICD2 1-820 DD rescues centriole engagement among several other mutants. However, it is still possible that the expression of the mutants affects some yet uncovered BICD2 function outside of centrosomes. At least, T821A and S823A should be mutated to Ala. From what I gathered, such mutant should remain associated with mitotic centrosomes. The authors should analyze whether mitotic progression remains unperturbed, and centriole engagement status should be analyzed without SCLT treatment in G2, M, and in ensuing G1.__

We agree with the reviewer that phosphonull mutants should be added to these experiments. In fact, and as mentioned in the responses to Reviewer 1, we have already performed experiments with the phosphonull mutants, observing that they are more retained at centrosomes than the phosphomimetic counterparts. We would be happy to share these results with the reviewers upon request if helpful. Nevertheless, and as mentioned above, we have decided to remove the preliminary data regarding BICD2 phosphorylation from the manuscript data in order to present a separate and more comprehensive study on BICD2 phosphorylation in the near future.

Significance

The question explored is relevant to the centrosome field and beyond since the processes leading to premature centriole disengagement and amplification are not fully understood. The study provides some novel insights. However, at the current stage, the study is preliminary. Additional experiments would be needed to strengthen the conclusion that BICD2 directly regulates centriole disengagement.

My expertise is in centriole and centrosome assembly and the mechanisms that regulate centrosome homeostasis in human cells.

__ __

__Reviewer #3 __

Evidence, reproducibility and clarity (Required):

Centrosome duplication is tightly control during cell cycle to prevent loss or amplification of centrosome numbers, which are detrimental for cell proliferation. In preparation for centriole duplication in S-phase, mother and daughter centrioles disengaged late mitosis, a process that functions as a licensing factor for duplication. While several mechanism have been proposed to be important for centriole disengagement, differences between systems and organisms exist, suggesting alternative pathways may play a role.

In this manuscript, Montes-Ruiz and colleagues investigate the role of the dynein adaptor protein BICD2 during centriole disengagement. They found that BICD2 localises to the centrioles, with a peak in S-Phase. Super resolution microscopy suggests that BICD2 localises to the mother centrioles and is mostly absent in mitosis cells after anaphase, when centrioles are disengaging. KO of BICD2 in REP-1 cells does not some t have strong phenotypes, but the authors found that centriole separation is increased, suggesting a role in centriole cohesion. While there is limited mechanist insight about the regulation of BICD2 and its function at the centrosomes, the data presented suggests a role for BICD2 in centriole cohesion that is independent of dynein interaction. There are however several issues with data presentation, image analyses and data interpretation the authors could improve.

Major comments

- On page 5, the authors state that figure 1 and supplementary figure1 data strongly suggest that BICD2 associates with mother centrioles and not the PCM. This is not very clear from the images on these figures. In fact, PCM is often associated with mother centriole as well, thus I am not sure they can make these conclusions based on the data presented in these 2 figures. Also, the fact that PCM is more abundant in G2/M, when BICD2 is not, does not mean it does not localize to the PCM. Higher resolution of expansion will be needed.

The data presented in supplementary figure 3 does not help the conclusion above as it seems form the images that there is co-localization between BICD2 and pericentrin. It is impossible to conclude also that there is co-localization with the satellite marker PCM-1. In fact, they seem to have no overlap from the images provided. Higher resolution of expansion will be needed.

Following the reviewer’s suggestion we embarked in a full characterization of BICD2 localization using expansion microscopy (ExM). We think that our new data further clarifies this together with new superresolution data.

Additionally we now have a figure (Supplementary Figure S4) addressing the relation between pericentrin and the localization of BICD2. We show that pericentrin downregulation does not affect centrosomal BICD2 levels. And that both proteins do not colocalize as observed using 3D-SIM.

Also regarding pericentrin, the revised version of the manuscript now includes a figure that functionally compares the results of its depletion to those of BICD2 (Figure 5).

We also provide data showing that BICD2 localization does not significatively change upon PCM-1 depletion (Supplementary Figure S4C). As we mention in the text, previous reports have suggested that BICD2 is indeed in the satellites (Quarantotti V et al. 2019. Centriolar satellites are acentriolar assemblies of centrosomal proteins. The EMBO Journal e101082. DOI: https://doi.org/10.15252/embj.2018101082) . But we only observed clear colocalization of PCM-1 with C-terminal fragments of BICD2. Thus, while GFP-BICD2 488–820 strongly colocalizes with satellites, endogenous BICD2 and full-length GFP-BICD2 do not (Figure 6D). We ignore the reason for this, but the data suggests that satellite localization is regulated (possibly via intramolecular autoinhibition) to mediate BICD2 transport or a distinct satellite-specific function of this protein. To address this we have added a sentence to the text that now reads: “The presence of BICD2 at the centriolar satellites has been suggested previously (Quarantotti et al, 2019); we ignore the reason why in the conditions used in this study only C-terminal fragments of BICD2 (but not the full-length protein, see Supplementary Figure S4) colocalize with satellites. This suggests that BICD2 satellite localization is regulated (possibly via intramolecular autoinhibition) to mediate BICD2 transport or a distinct satellite-specific function of this protein.”.

- In figure 2, to confirm localization to the mother centrioles, could the authors use a mother centriole marker? Such as a distal appendage protein of ninein? CEP152 localizes to both centrioles in the images provided.

I was surprised that BICD2 localizes to both distal appendages and linker? These are not close to each other. Can the authors comment on this? In supplementary figure 4C orthogonal view it seems like BICD2 is in between distal appendages and linker?

We believe that the new ExM data (Figures 2 and 3) directly address the reviewer's concerns.

Regarding the original supplementary figure S4C, indeed in the orthogonal projections of 3D-SIM images the signal corresponding to BICD2 was observed between distal appendages and linker and was quite broadly distributed. We recognize that this could lead to confusion. We have now removed part of this figure (original Figures 4B and 4C) from the manuscript, as we think that the data is made redundant with our new ExM data. Our new data, with a much higher resolution shows that BICD2 localization corresponds to that of the proximal torus (see new Figures 2D and 2E, and Figure 3). Note that in our new ExM images we use a daughter centriole marker (SAS-6) that (in addition to CEP152) we think helps confirm that BICD2 localizes around the mother centriole.

-The IF data suggests that BICD2 localization to the centrosome is dynamically regulated during cell cycle. Did the authors consider that this protein could be degraded? Is it a matter of recruitment or total protein levels?

We agree that protein degradation has to be considered when analyzing cell cycle-dependent localization. However, our data suggest that the dynamic behaviour of BICD2 at the centrosomes does not reflect changes in its total protein amount. We have previously shown that total BICD2 levels are not reduced in mitosis, as assessed by western blot (Gallisà-Suñé N et al. 2023. BICD2 phosphorylation regulates dynein function and centrosome separation in G2 and M. Nature Communications 14:2434. DOI: https://doi.org/10.1038/s41467-023-38116-1). To make this clear in the current manuscript, we have additionally added Figure EV1B depicting BICD2 levels in S, G2 and M phase, and the following note to the text : “Total levels of BICD2 remained constant during the different phases of the cell cycle (Figure EV1B and (Gallisà-Suñé et al, 2023))“.

- The authors propose that the dynamic localization of BICD2 is associated with licensing. However, it is rather surprising that the phenotype of centriole separation they describe is only observe in mitosis when BICD2 in knockdown and not in S-phase when the levels of BICD2 are higher? If the role of BICD2 is to prevent premature centiole disengagement, shouldn't that be observed in S-phase as well? Why only in mitosis when in control cells BICD2 levels are already very low?

Recent data supports the notion that in S phase centriole cohesion is maintained by the cartwheel (Huang F et al. 2022. Cartwheel disassembly regulated by CDK1-Cyclin B kinase allows human centriole disengagement and licensing. The Journal of Biological Chemistry 298:102658. DOI: https://doi.org/10.1016/j.jbc.2022.102658; Ito et al. 2025. Multimodal mechanisms of human centriole engagement and disengagement. The EMBO journal 44:1294–1321. DOI: https://doi.org/10.1038/s44318-024-00350-8). Our data, including the new results showing that BICD2 interacts with CEP152, suggests that BICD2 is a dynamic part of the mother centriole torus, a structure that does not seem to be implicated in maintaining cohesion in S. We now note this in the manuscript’s text: “During S phase, mother-daughter centriole cohesion is maintained by the cartwheel (Huang et al, 2022; Ito et al, 2025), and, consistently, does not depend on BICD2.”. Of note, after Ito etl al. BICD2 (and the torus) may have a role in late S if the cartwheel is compromised, something that could be tested in future studies by downregulating cartwheel components and BICD2 simultaneously.

- The images of C-Nap1 localization in figure 6E are not very convincing to illustrate the pint the authors are making in the main text (additional C-Nap1 foci are visible in the KO cells)

We would like to note that visualizing C-NAP1 in mitosis is technically challenging, as a significant pool of the protein is displaced from the centrioles after phosphorylation in G2. However, the protein has been widely used as a marker of centriole disengagement (e.g. in the seminal Tsou M-FB et al. 2006. Mechanism limiting centrosome duplication to once per cell cycle. Nature 442:947–951. DOI: https://doi.org/10.1038/nature04985). We therefore consider it a valuable tool to support our conclusions regarding centriole engagement. Regarding extra c-NAP1 foci in BICD2 knockout cells, these may reflect additional centrioles that appear in these cells, as a result of abnormal disengagement and early licensing. To have this into account our data quantifies both c-NAP-1 positive centrioles (increased in KO cells, Figure 4E) and number of c-NAP-1 positive centrioles /total centriole number (with an increase in the abnormal >2:4 configuration in BICD2 KO cells, Figure 4F).

- The authors propose that PLK1 and CDK1 phosphorylation sites regulate the association of BICD2 with the centrioles. Could this be tested with a PLK1 inhibitor?

As noted above, we have removed the phosphorylation data from the manuscript, as we aim to report these findings in a dedicated upcoming study. Nevertheless, to address the reviewer's query, we now consider BICD2 to be predominantly regulated by CDK1, supported by data using BI 2536 showing that BICD2 centrosomal levels are unaffected by PLK1 inhibition. In contrast, CDK1 inhibition slightly reduces these levels, though this effect does not reach statistical significance under the tested conditions. We would be glad to share these additional results with the reviewers upon request.

- On page 13, the authors state that their results do not agree with previous literature showing that pericentrin cleavage can result in disengagement. However, it was unclear from this manuscript what is the evidence to demonstrate that this is the case? The data presented in figure 5B for example only demonstrates that pericentrin levels do not change in the absence of BICD2 in what looks like S-phase cells. Did the authors look at pericentrin levels when they observe centriole disengagement in the ko cells? In G2 or early M-phase?

We recognize that pericentrin is widely considered a crucial factor in centriole engagement, and have added new data in the manuscript studying the relationship between it and BICD2 (the partially new Supplementary Figure S4), and their relative importances for engagement both in G2 and M (the new Figure 5). Our data suggests that both proteins act independently in a partially redundant manner, BICD2 as part of the torus (key for engagement in G2) and pericentrin of the PCM (more important in M).

We have updated the Discussion to present this and our view on pericentrin importance for engagement more clearly, specially our concerns that its importance may have been overestimated. Specifically we write that “BICD2 depletion reduces its centrosomal levels to a degree that mirrors those naturally observed during late M and early G1 in unperturbed cells. In contrast, experimental depletion of pericentrin reduces its levels far below physiological baselines across any phase of the cell cycle. This severe reduction produces marked centriole separation in mitosis that is likely amplified by spindle-derived forces. Consequently, the individual contribution of pericentrin to regulating physiological centriole cohesion may be somewhat overestimated under standard experimental knockdowns, and this regulation may rely more heavily on torus components, such as BICD2, than previously appreciated.”

Regarding the phases of the cell cycle in which we quantify pericentrin levels in the original Figure 5B (now Figure EV5B), we realize that the figure could lead to confusion as it was, as they were measured in M (when its amount is maximal, as specified in the figure legend) but the figure did not show examples in this cell cycle phase. We have added new examples of mitotic cells to the figure, and modified the figure labels and wording of the figure legend to clarify this.

Minor comments

- A more general reference (review) missing in the second paragraph of the introduction that describe the centrosomes.

We have added a recent general reference when introducing centrioles (Gönczy P. 2025. Critical constituents and assembly principles of centriole biogenesis in human cells. Nature Reviews Molecular Cell Biology 1–18. DOI: https://doi.org/10.1038/s41580-025-00921-5). Later in the paragraph, when centriole duplication is introduced, we now use this reference plus the also recent Fernandes-Mariano C et al. 2025. Centrosome biogenesis and maintenance in homeostasis and disease. Current Opinion in Cell Biology 94:102485. DOI: https://doi.org/10.1016/j.ceb.2025.102485.

- Some figures are not well organized, difficult to see which panel they correspond to? The authors could consider labelling panels better to make this clear. For example, figure 4 and 6 could benefit from additional panel labels.

We have added additional panel labels to Figure 4 (now Figure 6) and Figure 6 (now Figure 4), that we have also slightly reorganized with the aim of making it clearer).

- On page 7, what the authors mean by: "... we ignore the reason why in the conditions used in this study only C-terminal fragments of BICD2 but not the fill-length protein co-localize with these pericentriolar structures"?

By "pericentriolar structures” we were referring to the centriolar satellites. We realize that that was not clear and updated the wording of the sentence that now reads “we ignore the reason why in the conditions used in this study only C-terminal fragments of BICD2 (but not the full-length protein, see Supplementary Figure S4) colocalize with satellites.”. We subsequently propose a possible a possible explanation for this: "This suggests that BICD2 satellite localization is regulated (possibly via intramolecular autoinhibition) to mediate BICD2 transport or a distinct satellite-specific function of this protein.".

Reviewer #3 (Significance (Required)):

In general this work has limited mechanistic insight and BICD2 localization to the centrosomes was known. However, the authors do go into more detail description of the centriole localization of BICD2 . In addition, their established KO cell lines provide some insights into the role of BICD2 in centriole disengagement, which is of interest to the field. But the limited scope of the conclusions does not advance the field significantly as it is.

this work will interest a specialized audience.

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Referee #3

Evidence, reproducibility and clarity

Centrosome duplication is tightly control during cell cycle to prevent loss or amplification of centrosome numbers, which are detrimental for cell proliferation. In preparation for centriole duplication in S-phase, mother and daughter centrioles disengaged late mitosis, a process that functions as a licensing factor for duplication. While several mechanism have been proposed to be important for centriole disengagement, differences between systems and organisms exist, suggesting alternative pathways may play a role. In this manuscript, Montes-Ruiz and colleagues investigate the role of the dynein adaptor protein BICD2 during centriole disengagement. They found that BICD2 localises to the centrioles, with a peak in S-Phase. Super resolution microscopy suggests that BICD2 localises to the mother centrioles and is mostly absent in mitosis cells after anaphase, when centrioles are disengaging. KO of BICD2 in REP-1 cells does not some t have strong phenotypes, but the authors found that centriole separation is increased, suggesting a role in centriole cohesion. While there is limited mechanist insight about the regulation of BICD2 and its function at the centrosomes, the data presented suggests a role for BICD2 in centriole cohesion that is independent of dynein interaction. There are however several issues with data presentation, image analyses and data interpretation the authors could improve.

Major comments

On page 5, the authors state that figure 1 and supplementary figure1 data strongly suggest that BICD2 associates with mother centrioles and not the PCM. This is not very clear from the images on these figures. In fact, PCM is often associated with mother centriole as well, thus I am not sure they can make these conclusions based on the data presented in these 2 figures. Also, the fact that PCM is more abundant in G2/M, when BICD2 is not, does not mean it does not localize to the PCM. Higher resolution of expansion will be needed. The data presented in supplementary figure 3 does not help the conclusion above as it seems form the images that there is co-localization between BICD2 and pericentrin. It is impossible to conclude also that there is co-localization with the satellite marker PCM-1. In fact, they seem to have no overlap from the images provided. Higher resolution of expansion will be needed. In figure 2, to confirm localization to the mother centrioles, could the authors use a mother centriole marker? Such as a distal appendage protein of ninein? CEP152 localizes to both centrioles in the images provided. I was surprised that BICD2 localizes to both distal appendages and linker? These are not close to each other. Can the authors comment on this? In supplementary figure 4C orthogonal view it seems like BICD2 is in between distal appendages and linker? The IF data suggests that BICD2 localization to the centrosome is dynamically regulated during cell cycle. Did the authors consider that this protein could be degraded? Is it a matter of recruitment or total protein levels? The authors propose that the dynamic localization of BICD2 is associated with licensing. However, it is rather surprising that the phenotype of centriole separation they describe is only observe in mitosis when BICD2 in knockdown and not in S-phase when the levels of BICD2 are higher? If the role of BICD2 is to prevent premature centiole disengagement, shouldn't that be observed in S-phase as well? Why only in mitosis when in control cells BICD2 levels are already very low? The images of C-Nap1 localization in figure 6E are not very convincing to illustrate the pint the authors are making in the main text (additional C-Nap1 foci are visible in the KO cells) The authors propose that PLK1 and CDK1 phosphorylation sites regulate the association of BICD2 with the centrioles. Could this be tested with a PLK1 inhibitor? On page 13, the authors state that their results do not agree with previous literature showing that pericentrin cleavage can result in disengagement. However, it was unclear from this manuscript what is the evidence to demonstrate that this is the case? The data presented in figure 5B for example only demonstrates that pericentrin levels do not change in the absence of BICD2 in what looks like S-phase cells. Did the authors look at pericentrin levels when they observe centriole disengagement in the ko cells? In G2 or early M-phase?

Minor comments

A more general reference (review) missing in the second paragraph of the introduction that describe the centrosomes. Some figures are not well organized, difficult to see which panel they correspond to? The authors could consider labelling panels better to make this clear. For example, figure 4 and 6 could benefit from additional panel labels. On page 7, what the authors mean by: "... we ignore the reason why in the conditions used in this study only C-terminal fragments of BICD2 but not the fill-length protein co-localize with these pericentriolar structures"?

Significance

In general this work has limited mechanistic insight and BICD2 localization to the centrosomes was known. However, the authors do go into more detail description of the centriole localization of BICD2 . In addition, their established KO cell lines provide some insights into the role of BICD2 in centriole disengagement, which is of interest to the field. But the limited scope of the conclusions does not advance the field significantly as it is.

this work will interest a specialized audience.

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Referee #2

Evidence, reproducibility and clarity

Montez-Ruiz and colleagues explore the role of a dynein adaptor BICD2 in the engagement of mother and daughter centrioles. Cells need to maintain centriole engagement in interphase to prevent centriole reduplication and in early mitosis to prevent the formation of aberrant mitosis spindles. The authors demonstrate that BICD2 is a centriolar protein that surrounds the mother centriole adjacent to the daughter centriole. It is removed from centrosomes in mitosis, which, in turn, is responsible for centriole disengagement. Further, they suggest that in BICD2 knock-out G2 and early mitotic cells, centrioles disengage prematurely. By conducting rescue experiments, the authors conclude that BICD2 regions CC2, CC3, and CC4, which are dynein-independent, are essential for their function at the centrosome. Finally, they show that the phosphorylation of S817 and S819 of BICD1 controls its centrosome localization.

Major comments:

1. Based on F1 and SF1, BICD2 is reduced from centrosomes already in early G2. So, it is hard to square how removing a factor that is not present at the centrosomes at the time of disengagement would dysregulate disengagement. The study at this stage does not explain how BICD2 contributes to centriole engagement only in mitosis, while it does not affect centrioles in S.
2. The interpretation that the longitudinal localization of the BICD2 signal coincides with SAS-6 and procentrioles requires further evidence. BICD2 seems largely localized to the other regions around the mother centriole, and in some examples, it does not colocalize with the site of the daughter centriole or SAS-6 (for instance: F2B second row; SF4B, second row; SF5, fourth row; SF6 upper row).
3. BICD2 is important for centrosome-nucleus tethering during centrosome separation in G2, and its global removal likely affects the dynamics of the spindle assembly. Is G2 and mitotic progression affected in knockouts? Do the knockout cells show issues with chromosome alignment? Such analyses are critically missing from the manuscript.
4. In general, SCLT experiments are ambiguous. Centriole disengagement spontaneously occurs during prolonged prometaphase induced by SCLT. Accordingly, F6D shows that many centriole pairs in the control sample are disengaged after 16h of SCLT treatment. Although the distance between centrioles in knockout cells is, on average, larger, without knowing how BICD2 perturbations affect the dynamics of the mitotic spindles and mitosis progression, SCLT experiments do not provide enough insight. After 16h of SCLT treatment, the authors regularly measure centriole distances in mitosis smaller than 500 nm in all samples. This suggests that the used method (which also needs to be described) cannot reliably assess centriole engagement status. Centrioles can be disengaged but adjacent. The authors reference Shukla et al. 2015 to compare the centriole-to-centriole distances here with those from that publication. However, in Shukla 2015, centriole-to-centriole distances increase from S to M. But here, in F6, the control centriole distances in S, G2, and early M are almost identical and less than 500 nm. This discrepancy needs to be addressed.
5. The authors suggest that BICD2's functions at the centrosome are independent of its dynein functions. They show that GFP-BICD2 1-820 DD rescues centriole engagement among several other mutants. However, it is still possible that the expression of the mutants affects some yet uncovered BICD2 function outside of centrosomes. At least, T821A and S823A should be mutated to Ala. From what I gathered, such mutant should remain associated with mitotic centrosomes. The authors should analyze whether mitotic progression remains unperturbed, and centriole engagement status should be analyzed without SCLT treatment in G2, M, and in ensuing G1.

Significance

The question explored is relevant to the centrosome field and beyond since the processes leading to premature centriole disengagement and amplification are not fully understood. The study provides some novel insights. However, at the current stage, the study is preliminary. Additional experiments would be needed to strengthen the conclusion that BICD2 directly regulates centriole disengagement.

My expertise is in centriole and centrosome assembly and the mechanisms that regulate centrosome homeostasis in human cells.

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Referee #1

Evidence, reproducibility and clarity

This study demonstrates that BICD2, previously known as an adaptor protein for dynein, is involved in regulating centriole engagement during mitosis. First, using different antibodies, it was shown that BICD2 localizes near the mother centriole, as observed by super-resolution microscopy. During G1 and S phases, BICD2 localizes slightly outside the Cep152 ring, while in G2 to mitosis, it localizes near the cartwheel component SAS-6. Moreover, analysis of deletion mutants revealed that BICD2 localizes to the centrosome in a CC domain-dependent manner at the C-terminal end. The localization pattern resembling a ring in the cytoplasm was also observed through the CC3 domain. Next, BICD2 knockout (KO) cells were generated to investigate centriole dynamics. In BICD2 KO cells, the distance between the mother and daughter centrioles was observed to increase from G2 to mitosis compared to controls. Along with this, early centriole disengagement and centriole amplification phenotypes were observed. The increased distance phenotype between centrioles was rescued in BICD2 wild-type (WT) and mutant forms lacking the CC1 domain at the N-terminus, suggesting that this function of BICD2 is independent of dynein. Additionally, BICD2 mutants mimicking phosphorylation at the C-terminus showed reduced centrosome localization and were unable to rescue the phenotypes seen in BICD2 KO cells. While the study clearly demonstrates BICD2's contribution to centriole engagement, the underlying mechanisms of how BICD2 is involved in centrosome localization and centriole engagement remain unclear. As it is anticipated that the function of BICD2 is independent of dynein, further exploration of this unknown mechanism would enhance the value of the paper. Below are the concerns that should be addressed, including new experiments.

Main Points:

1. Fig. 1-3: Regarding the localization of BICD2 to centrioles, during the G1-S phase, its localization appears to overlap with PCM. Experimental investigation should be performed to examine whether BICD2's centrosomal localization is influenced by knockdown of PCM components like PCNT, Cep192, or Cep152.
2. Fig. 7: The experiments using BICD2 mutants suggest that the function of BICD2 here is independent of dynein. To further investigate whether BICD2's role in centriole engagement is independent of dynein, experiments should be conducted to examine the effect of dynein knockdown on BICD2 localization to the centrosome and centriole engagement.
3. Fig. 4: The CC4 domain at the C-terminus of BICD2 is important for its centrosomal localization, but identifying the binder/recruiter responsible for BICD2's centrosome localization would be desirable.
4. Fig. 7: Rescue experiments using BICD2 mutants suggest that BICD2's functional domains are critical. Further experiments by creating mutants missing parts of CC2 or CC3 could identify functionally important domains of BICD2 by observing any loss-of-function phenotypes at the centrosome.
5. Fig. 6: Regarding the BICD2 KO cell phenotype, is there experimental evidence showing an increase in centriole number during mitosis? For instance, while no abnormality in centriole number may occur during G2, a trend of increase in mitosis should be experimentally demonstrated. Also, how should the slight differences in phenotypes between Ndelta4 and Ndelta5 BICD2 KO cells be interpreted?
6. Fig. 8: Regarding the phosphorylation of BICD2 at the C-terminus: The phenotypes of mutants where these two phosphorylation sites are changed to alanine should be experimentally observed. It is expected that the removal of BICD2 from the centrosome during mitosis could be rescued. Additionally, the effect of PLK1 or CDK1 inhibitors on the removal of BICD2 from the centrosome should be investigated.

Minor Points:

1. Fig. 1-3: During G1 and S phases, BICD2 localizes near the mother centriole, and from G2 onward, it colocalizes with SAS-6. How can this be explained?
2. Fig. 4: The GFP-BICD2 488-820 fragment forms cytoplasmic rings, which is interesting. This domain contains the CC4 domain, so it can localize near the centriole, but why does it not form a perfect ring there? Also, which other centriole/centrosome markers were used for colocalization studies? Does knockdown of PCM1 affect BICD2's centrosomal localization?
3. Fig. 4A: What are the aggregates observed in the cytoplasm under the GFP-BICD2 + ice condition? Also, does the 1-575 mutant fail to localize to the centrosome upon ice treatment?
4. Can similar phenotypes be observed in other cell types when BICD2 is knocked down? This should be experimentally validated.
5. Are there previous studies suggesting that this function of BICD2 is evolutionarily conserved? This should be addressed.

Significance

In this paper, the identification of BICD2 as a novel factor regulating centriole engagement is of significant importance. However, the mechanisms through which BICD2 controls its localization to the centrosome and regulates centriole engagement remain largely undefined. Further exploration of these mechanisms would likely enhance the value of the paper.

The findings are likely to be of great interest to researchers in the field of cell biology, particularly those focusing on centrosome biology.

The above feedback comes from a researcher specializing in centrosome studies.

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Reply to the reviewers

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

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Referee #4

Evidence, reproducibility and clarity

In this manuscript, Dilbaz-Gunden, et al. investigate the localization and function of CSPP1 in multiciliated cells (MCCs). Using a combination of mouse tracheal cell cultures and Xenopus embryos, the authors characterize the localization of CSPP1 in MCCs and use gene knockdowns to analyze CSPP1 function. They find similar protein localization in both models and that loss of CSPP1 disrupts centriole organization, basal body migration/docking, basal body polarity, and cilia formation. Overall, the data is high quality and the presentation is clear. The main conclusion that CSPP1 is a conserved regulator of ciliogenesis in MCCs is supported by the evidence presented.

Major comments:

1. For each of the CSPP1 protein localization studies presented in Figure 1, to gauge reproducibility, it would be useful to indicate how many cells were analyzed and how many looked like the representative images.
2. The conclusion that CSPP1 is required for centriole amplification is confusing since CSPP1 depletion does not alter centriole number (Fig. 2D-E). The centriole defect appears to be due to a MCC morphogenesis defect.
3. In CSPP1 loss-of-function treatments, the authors find defects in centriole organization, basal body migration, basal body polarization, cilia formation, cilia length, and cilia motility in MCCs. It is not clear whether the authors propose that CSPP1 has distinct functions in each of these processes or these are pleiotropic phenotypes due to earlier defects in MCC morphogenesis. This is particularly confusing since previous work indicates CSPP1 is a regulator of the cell/cytoplasmic cytoskeleton.

Significance

Mutations in CSPP1 have been identified in patients with the ciliopathies Joubert syndrome and Meckel-Gruber syndrome, so the significance of studying CSPP1 is high. How mutations in CSPP1 can cause two distinct ciliopathies remains unclear. Previous work has identified CSPP1 as a microtubule-associated protein that is localized to the basal body and ciliary tip of primary cilia and is involved in cilia length regulation. In this context, the finding in the current manuscript that CSPP1 is important for establishing ciliary structure is not new or unexpected. However, this is the first analysis of CSPP1 localization and function in MCCs. This new evidence that loss of CSPP1 can disrupt both primary cilia and motile cilia in MCCs supports a model for how mutations affecting core cilia assembly proteins can underlie multiple ciliopathy phenotypes. This work will appeal to a broad audience in the fields of cell biology and ciliopathy. A limitation to the significance of this work is that it stops short of investigating how CSPP1 mechanistically regulates MCCs.

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Referee #3

Evidence, reproducibility and clarity

The report by Dilbaz-Gunden et al characterizes the roles of Joubert syndrome protein CSPP1 in multiciliogenesis. Joubert syndrome is commonly thought of as a sensory ciliopathy as many regions in the brain that are affected in this disorder do not possess motile cilia. However, the authors note in their introduction that there are pathogenic variants in several "cilia" genes that cause both sensory and motile cilia phenotype in the same individuals. This motivates the study to evaluate the role of CSPP1 in multiciliated cell contexts.

The strengths of this report are the analyses in multiple systems and the beautiful imaging and quantifications of these images. However, some of the conclusions are less convincing than others as written and this weakens the paper. My suggestions for strengthening this report are as follows:

1) One major conclusion is that CSPP1 is required for "efficient centriole amplification". This doesn't seem supported by the results in figure 2 as presented. In 2D the conclusion seems to be that the cells have similar number of centrioles, but loss of Cspp1 results in cells with larger apical surfaces that do not fill with centrioles. This doesn't appear to be an inability to make centrioles, but an inability of a cell lacking Cspp1 to recognize that it needs to make more centrioles to fill the larger surface area. Are there other manipulations that increase apical surface area yet the cells compensate appropriately with more centrioles? Given the later results that Cspp1 loss affects the apical microtubule networks, how many of the subsequent defects, (defective basal body docking, apical organization, establishment of rotational polarity, ciliogenesis, and failure of MCCs to integrate properly in the epithelium) are due to that defect alone? The presentation and the interpretations would benefit from thinking about which loss of Cspp1 phenotypes are likely direct roles of Cspp1, versus indirect consequences of an earlier Cspp1 role. The statement on page 20 that "CSPP1 depletion is consistent with a role for CSPP1 in coordinating centriole amplification with apical remodeling" seems more accurate and could be the way to think about reframing the results.

2) Another major issue is that how quantifications are conducted aren't always clear. For example, saying a control cell has "dense and uniform" centriole distribution and a Cspp1 depletion cell is abnormal and disorganized doesn't clarify how the person doing the analysis decided what was normal versus abnormal. In some cases this can be found in figure legends, but it would be helpful to include an analysis section in materials and methods that explains how decisions were made regarding normal and abnormal for each analysis.

3) Minor - It would be nice to add some thought to the discussion about why some mutations cause both sensory and motile cilia defects, while others do not.

4) Figure 1A - please add the ALI stages to the diagram outlining the stages of MCC formation.

5) Figure 2 B-J it would be helpful to add these category labels to the panels to help the reader understand what each group of stainings is meant to analyze.

6) Figure 1E bottom panel - the inset isn't from the outlined cell? Why is this?

7) Figure 1F and S1B - in detached cilia, CSPP1 expression is throughout the axoneme and at the tip, but in other images the concentration at the tip is emphasized as the localization for this protein. Is the staining in detached cilia an artefact? Or is it just less obvious that CSPP1 is throughout the cilia body in intact MCCs?

8) Figure 2B - As per the major comment above - how did the researcher set the threshold for amplified versus less amplified?

9) Was there rationale for using the SB versus TB morpholino?

10) In Figure 3A, why is there so much less ZO1 in the shCspp1 image? Is this a defect with loss of CSPP1 or an imaging plane issue?

11) Figure 4A add the stage of analysis to the images.

12) Figure S2A How was quantification of CSPP1 protein levels conducted?

13) Figure S2E was the new product produced by SB MO sequenced to confirm this is intron retention as opposed to some other splicing defect?

14) Define GFP-GPI in material and methods. I assume membrane associated GFP marker?

15) Figure S2F - the traced outlines do not look like the cells indicated by the boxes.

16) Figure S3B - Which cells is which of the callouts? Why are there no traced outlines as in other figures?

Significance

This work is important and will be of interest to the cilia community. The images are fantastic and the ultimate findings of CSPP1 affecting multiciliated cells is novel and intriguing. My issues with the paper have to do with interpretation of the results which seems to be incomplete. The authors should be able to fix the issues I have with text edits and I do not think they need to do additional experiments.

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Referee #2

Evidence, reproducibility and clarity

The paper by Dilbaz-Gunden and colleagues describe the results of experiment to understand the function of the CSPP1 protein in multiciliated cells (MCCs). Mutations CSPP1 have been identified in Joubert syndrome patients and although the protein has been studied with reference to primary cilia, there are clinical issues reported in these patients that suggest functions in motile ciliated cells as well. The authors first describe a detailed localization pattern of CSPP1 in differentiating MCCs, using mouse trachea and Xenopus epidermal MCCs. Then they use knockdown studies to uncover apparently multiple roles of CSPP1 in basal body biogenesis, apical migration and docking as well as axoneme formation and cilia motility. While the localization studies provide solid data, I am not convinced with the loss-of-functions approaches adopted in this study. A stable genetic knockout is essential to properly dissect the role of CSPP1 in MCCs: Either a mouse mutant or knockout in cultured cells then differentiated into MCCs. There are many papers with knockdown studies in cultured cells and Xenopus embryos which do not even up with findings from stable knock outs. Of relevance to this work is the initial description of Deup1 as a protein essential for basal body generation in MCCs using similar knock down studies in mammalian cells and Xenopus embryos (PMID: 24240477), which has been subsequently refuted using stable knockout mice (PMID: 31792378). The other shortcoming is that the data are largely descriptive, with no new or mechanistic insights into CSPP1 function in centriole or cilia formation. Furthermore, the knockdown effects seem to produce pleiotropic effects, so it is not easy to appreciate if CSPP1 indeed has multiple functions or it is principally required for generating proper basal bodies, for example, and failure in this early event in the knockdown conditions triggers other downstream manifestations like problem in their migration and docking and axonemal extension.

Significance

The study provides limited conceptual novelty and does not substantially advance mechanistic understanding of CSPP1 function.

I have expertise in cilia and ciliopathies, particularly multiciliated cells

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Referee #1

Evidence, reproducibility and clarity

The Joubert syndrome protein CSPP1 is a conserved regulator of vertebrate multiciliogenesis and motile cilia function

By: Irem S. Dilbaz-Gunden, Clothilde Boitel, Jovana Deretic, Marine Touret, Mehmet S. Aydin, Esra N. Yigit, Ozgecan Kayalar, Hasan Bayram, Virginie Thomé, Olivier Rosnet, Nicolas Brouilly, Laurent Kodjabachian, Camille Boutin and Elif Nur FiratKaralar

I have only some Minor remarks:

Introduction:

• Motile cilia not always have 9+2 configuration.
• Authors present a excellent introduction explaining how a number of findings suggest that ciliogenesis relies on shared molecular modules, including microtubule-associated proteins, that govern organelle biogenesis and function across both primary and motile cilia.

Results:

• The authors establish CSPP1 as a conserved component of the multiciliogenesis machinery in mouse, human and Xenopus. Its localization to fibrous granules and deuterosomes during centriole amplification, and to basal bodies and ciliary axonemes in mature cells.

• Figure 1: is flawless.

• Figure 2: data from 2 animal models strongly supports that CSPP1 depletion reduced the efficiency of centriole amplification and disrupted formation of the dense centriole arrays characteristic of MCCs.
• Figure 3: data is robust and presents an excellent quantification in 3 axis of milder defects for centrin signal spacing and stronger defects for polarity direction.

I would ask the authors to make the figures even more clear by iserting a small diagram of the animal model being used in each case. In all images presented.

• Figure 4 title: CSPP1 loss leads to defective cilia formation, axonemal structure, and motility (please add in which cells from which animal model) I like the way the authord show the "normal defects" in the control figures and make the comparison with the treatment defects in all cases. Transparency is important. Congratulations. Again, here if one does not read the main text cannot undestand which model is being used. Legends also ommit the model. Please make sure each figure is understandable on its own. Images are of high quality. The number of methodologies used to reach their conclusions is impressive and data is well quantified. The TEM data (h) supports the claims and images were taken at the same cilia longitudinal focus planes supporting sh Cspp1 cilia are indeed very deffective.

• Figure 5:

The xenopus experiments are very convincing and robust as cells were stained for the MO lineage tracer (green), the Rescue tracer (RFP, magenta), and cilia (Acetylated alphatubulin, yellow). All images are impecably presented. The authors provide a detailed framework along MCC development for understanding how a Joubert syndrome-associated gene can contribute to respiratory phenotypes.

Discussion:

• In the discussion (final paragraph) please add a reference for the HH signalling defects in seen in primary cilia as these were not evaluated here. Are these for the same gene or for other genes? Please specify to make it clearer. In JS patients is there any reason why the symptoms are more related to the upper airways? Perhaps discuss this here. Any data from bronchoscopy available? is this a very mild phenotype in humans?

Significance

The manuscript is very well written, supported by great imaging and beautiful figures. I agree that the findings support a model in which disruption of a shared cytoskeletal assembly pathway can link primary and motile ciliopathy phenotypes across multiple ciliary tissues and species. I have some minor remarks that would improve the clariry of the manuscript but I think the work is of excellent quality and will be an important contribution to the field. Publication should be fast.

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Reply to the reviewers

Note to readers on BioRxiv: In this response to reviewer comments, we have drafted some display items to illustrate the preliminary analyses that we have performed. If the reader sees a reference to a display item and wishes to view it in its original format, please see the original revision response PDF file. Our response begins below:

Manuscript number: RC-2026-03518

Corresponding author(s): Tijana, Ivanovic

General Statements

We first provide the general statements from Reviewers #1, 2, and 3 to give a holistic view of their impressions of the paper. Afterwards, we describe our plan to address their comments and the structure of this document.

Reviewer #1(Evidence, reproducibility and clarity (Required)): Planitzer et al. have developed a clever flow cytometry assay to monitor hemagglutinin (HA)-mediated membrane fusion. This novel approach provides several advantages over bulk and single-particle fusion assays, including dramatically higher throughput and detection of lipid mixing under low efficiency conditions. As such, on purely technical grounds, this manuscript provides a significant advance to the field. The authors then apply their new approach to probe the role of HA-sialic acid binding in the membrane fusion reaction. This reflects an important open question in the field, which, as the authors point out, has been elusive. They conclude that sialic acid binding promotes efficient membrane fusion, probably by increasing the likelihood of the fusion peptide engaging the target membrane after acid-induced conformational changes. Overall, the manuscript is very well written; the data are rigorously analyzed and nicely presented; and the results are important and informative. My comments are, for the most part, minor.

__Reviewer #1 (Significance (Required)): Planitzer et al. have developed a clever flow cytometry assay to monitor hemagglutinin (HA)-mediated membrane fusion. This novel approach provides several advantages over bulk and single-particle fusion assays, including dramatically higher throughput and detection of lipid mixing under low efficiency conditions. As such, on purely technical grounds, this manuscript provides a significant advance to the field. The authors then apply their new approach to probe the role of HA-sialic acid binding in the membrane fusion reaction. This reflects an important open question in the field, which, as the authors point out, has been elusive. They conclude that sialic acid binding promotes efficient membrane fusion, probably by increasing the likelihood of the fusion peptide engaging the target membrane after acid-induced conformational changes. Overall, the manuscript is very well written; the data are rigorously analyzed and nicely presented; and the results are important and informative.

__

Reviewer #2 (Evidence, reproducibility and clarity (Required)): This manuscript by Planitzer et al. investigates how NA activity, HA receptor binding avidity, and the identity and density of sialic acid receptors within the target membrane influence membrane fusion. This is an important question, as functional balance between HA and NA drives the antigenic evolution of seasonal influenza viruses and contributes to the pandemic potential of zoonotic viruses. As discussed in this manuscript, prior studies of how sialic acid receptors contribute to fusion following initial viral attachment are relatively few, and these have frequently reached different conclusions. Many of these discrepancies are likely attributable to details of the experimental system used to address the question, highlighting the importance of approaches in which the receptor identity and density are precisely controlled. Within this context, the sensitive and quantitative method the authors have developed to measure the efficiency and kinetics of virion fusion using flow cytometry ('spCALM') stands out as an important contribution of this manuscript. Using this approach, the authors convincingly demonstrate that engagement of HA with sialic acid receptors during the fusion process promotes efficient fusion, and that conditions that disrupt this engagement (low receptor densities combined with NA activity or receptor-HA mismatch) lead to reduced fusion efficiency by reducing the probability of fusion peptide insertion. Overall, the methods and findings of this paper are a strong contribution to the field and will be of interest to researchers studying viral membrane fusion as well as HA-NA balance. The manuscript is well-written, and the figures are very clear. The supporting figures provide additional context that is valuable. Addressing the comments below would strengthen the manuscript further.

Reviewer #2 (Significance (Required)): This study establishes a powerful experimental approach to quantitatively dissect fusion between influenza viruses and target membranes across a wide range of experimental conditions. This approach represents a significant methodological advance and its high throughput allows the authors to quantify rare events. Additionally, the manuscript presents convincing data showing that, within the regimes tested here, sustained receptor engagement promotes membrane fusion by increasing the likelihood of fusion peptide insertion. The observation that this is reduced by NA activity at low receptor densities carries implications for HA-NA functional balance.

While the specific findings may be restricted to the range of experimental conditions tested here, the results will be of interest to researchers studying virus-membrane fusion and functional balance between the influenza virus glycoproteins.

__Reviewer #3 (Evidence, reproducibility and clarity (Required)): Summary: The manuscript by Plamitzer et al. investigates influenza A virus hemagglutinin (HA)-mediated membrane fusion using bulk flow cytometry analysis. In the assay, they use red blood cells and liposomes carrying defined, variable densities of sialic acid residues. They used H3N2 and H1N1 model viruses with spherical morphology. The liposomes were produced using double-stranded DNA to attach sialic acid. Similar studies have been done using DNA-tethers to study membrane fusion between liposomes and influenza virions (PMID: 35143209, PMID: 27410740). Some previous studies have shown that reduced HA binding does not influence membrane fusion, while others have shown that binding increases membrane fusion. This work aims to reconcile prior conflicting observations. Based on their results, they conclude that HA-receptor binding avidity and the extent of neuraminidase (NA)-mediated receptor cleavage directly influence lipid mixing, which is used here as a proxy for membrane fusion and allows monitoring of the first step of fusion, namely the hemifusion intermediate. The results of the test whether receptor binding modulates the HA extended intermediate should be interpreted with more caution. The manuscript would benefit from more data on the characterisation of liposome carrying dsDNA sialic acid receptors and from using the TIRF SBP method to validate the flow cytometry.

__

__Reviewer #3 (Significance (Required)):

__

__Significance: The study attempts to answer an important question and is of interest to the membrane fusion field and the virology field. It provides flow cytometry to study membrane fusion and a method for DNA-based sialic acid receptors that can be displayed at control density.

Limitations and Advances: 1) Flow cytometry is a high throughput methods which allows to analyze many conditions. Recently published methods on flow virometry are promising methods that allow to study viron morphology. However, it might not be suitable to address specific mechanistic questions of membrane fusion to the molecular details presented in the model and discussed in the discussion. Overall, TIRF microscopy and SBP (Fig S6) present a much more accurate method than flow cytometry as it allows to study individaul events and provides additional information on virus size, fluorescence signal etc. In addition, single-molecule FRET methods could be used to monitor HA conformational changes at varying concentrations of sialic acid receptors. Previous studies have already shown that binding to sialic acid allosterically regulates HA2 conformational dynamics (PMID: 29961575). 2) A limitation is that only lipid mixing is monitored and no full fusion. Hence, one cannot conclude that all lipid mixing here leads to a full fusion pore opening. This should be addressed in the manuscript or at least noted as a limitation noted in the manuscript as a limitation.__

We thank the reviewers for their careful evaluation of our manuscript and for their thoughtful and constructive comments. We are encouraged that Reviewers 1 and 2 recognized both the methodological advances afforded by the spCALM assay and the importance of the biological insights into the role of HA-receptor interactions in influenza membrane fusion. We also appreciate the critical perspective of Reviewer 3, whose comments prompted us to more carefully articulate the capabilities and limitations of the assay, clarify aspects of its implementation that may not be immediately apparent to readers more familiar with conventional bulk fusion assays or supported planar bilayer/TIRF approaches, and consider alternative mechanistic interpretations of our findings.

Overall, we believe the reviewers have identified several opportunities to substantially strengthen the manuscript. Briefly, prompted by Reviewer 1 and Reviewer 3, we have developed improved analyses of virion recovery, binding, and liposome occupancy that refine our assessment of virion attachment, reveal previously unrecognized nonspecific particle losses, and will provide more rigorous quality-control metrics throughout the study. These new analyses also strengthen the inference that receptor interactions similarly influence both virion attachment and the lipid-mixing efficiency of bound virions, although the two processes exhibit distinct quantitative dependencies across multiple experiments. In response to Reviewer 2, we will extend the experimental parameter space by attempting measurements at higher receptor densities and with longer DNA receptor linkers. If these experiments cannot be completed successfully, we will better define the experimental regimes over which our conclusions are expected to apply and discuss the corresponding limitations. In response to Reviewer 3, we will revise the manuscript to more clearly describe the single-particle nature and unique advantages of the spCALM assay, explicitly discuss alternative mechanistic interpretations of the receptor-density dependence, attempt experiments to distinguish between competing mechanistic models, and evaluate the effects of soluble receptor on binding and lipid mixing to further probe the role of receptor engagement during membrane fusion.

In summary, we believe all reviewer comments can be satisfactorily addressed. The revised manuscript will include new analyses, expanded discussion, clarification of the experimental methodology, and even new experiments where feasible. Together, these revisions will strengthen both the technical presentation of the spCALM assay and the mechanistic conclusions regarding the role of receptor engagement in regulating influenza virus lipid mixing.

We have organized our responses to reviewer comments according to the Revision Plan template, separating planned revisions (Section 2), revisions that are already complete (Section 3), and revisions which we prefer not to carry out (Section 4). Within each section, we present our responses in order from reviewer #1 to reviewer #3 in the original order that they appear in the compiled reviews document. We have included line numbers in this revision plan to indicate where text revisions can be found in the (partially) revised manuscript and have tracked those changes in Microsoft Word. We also cite several publications in our responses and have included a list of references at the end of this revision plan.

Description of the planned revisions

Insert here a point-by-point reply that explains what revisions, additional experimentations and analyses are planned to address the points raised by the referees.

Reviewer #1: “In the spCALM assay, the authors indicate that labeled virions were incubated with cells or liposomes at a ratio of "0.15 virions per target". How were the numbers of virions determined for these experiments? The Methods refer to MOIs in units of PFU/cell but do not indicate how the number of physical particles were determined.”

Thank you for pointing out this omission. We have for now extended our description of the “Viruses and reagents” subsection of Materials and Methods in lines 457-463 to refer to our previous study describing how physical virus particle and vesicle counts were determined.

However, since this is a relatively new method, in the revision we will add supplemental panels to Figure S1 to show how we count free virions and assess whether they are monodisperse and uniform in both size (mostly spherical) and R18-dye incorporation by flow virometry. Then, these figures will also be referenced in the Methods.

Reviewer #1: “The authors indicate that the MEDI antibody "increased binding across all tested conditions." But this was not mentioned again. By what mechanism do they expect the antibody enhances virus binding?”

We thank Reviewer #1 for prompting us to reevaluate this unexpected observation. Upon additional analysis, we found that our original interpretation was incorrect. Rather than increasing receptor-mediated attachment, MEDI increases the recovery of virions in our assay, including both free and liposome-attached particles, while the total liposome concentration remains unchanged (Display Item 1A,B). Consistent with this interpretation, the fraction of virions bound to liposomes is not meaningfully changed by the presence of MEDI (Display Item 1E). We therefore infer that MEDI reduces nonspecific losses of virions, likely through decreased adsorption to plastic surfaces, rather than enhancing receptor-mediated binding. We have added a mention of this point in lines 314-317 and will incorporate these additional analyses in the manuscript revision.

Display Item 1 caption: MEDI reduces virion losses but does not improve virion attachment. In the experiment presented in Fig 5C and S15, MEDI8852-Fab (MEDI) increased the fraction of liposomes with bound virions because it reduced particle losses. We extracted total virion counts (A), total liposome counts (B), the ratio of total recovered virions to liposomes (C), the percentage of liposomes with bound virions (D), and the percentage of virions bound to liposomes (E) before pH drop. MEDI increased total virion counts (A) but did not affect total liposome counts (B). This increased the actual virion-to-liposome ratio in MEDI relative to no-MEDI condition (C). By instead analyzing attachment efficiency as the percentage of recovered virions which are attached to liposomes (note the liposomes are always in access) (E), we control for differential particle loss with or without MEDI and find no meaningful difference in virion attachment efficiency in the presence or absence of MEDI, as expected. Error bars indicate standard error of the mean.

While investigating this effect, we also identified an error in our description of a subset of the experimental conditions. Specifically, the experiments shown in Figs. 5A and 5B were performed using 0.5 virions per liposome rather than the previously stated ratio of 0.15. This higher input was intentionally used to increase the number of bound virion-liposome pairs under conditions of very low lipid-mixing efficiency. We will correct the manuscript to accurately report these experimental conditions. Importantly, this did not increase the number of virions bound per liposome (see our response to reviewer 3 #2, Display Item 3).

Finally, these analyses prompted us to systematically evaluate particle recovery and liposome binding in other experiments in the study (Display Item 2, Display Item 6). We found that low-input virions are subject to nonspecific adsorption losses, explaining why the observed fraction of bound liposomes is often lower than expected from the nominal input ratio (Display Item 2). We will incorporate these new particle recovery and liposome binding analyses into the revised manuscript and extend this systematic evaluation across all experiments.

Display Item 2 caption: Particle recovery and attachment analysis for the experiment presented in Fig. 4B. From events detected before pH drop, we derive particle recovery metrics, including total virion counts (A), total liposome counts (B), and total virion-to-liposome ratio (C), as well as attachment metrics, including the fraction of liposomes with bound virions (D), the fraction of total virions attached to liposomes (E).

Reviewer #2: “Related to my first point, a tradeoff in the approach described here is that the observations may be specific to the regime that is being tested. Any effort to expand the range of conditions tested would therefore be valuable. For example, the authors discuss prior work at higher receptor densities (line 364); it seems that this higher-density regime could be evaluated here for direct comparison. Similarly, it is interesting that the authors do not observe differences when they use 12nt vs 24nt for the display of sialic acid on DNA tethers. I would imagine that sustained receptor binding could be detrimental to fusion peptide insertion only if it occurs at too large of a distance from the target membrane. It seems likely that the distances involved here (~4nm vs. 8nm) may not be sufficient to observe this, but testing larger DNA anchors seems feasible. If not, additional discussion of contexts where the findings described here may no longer be applicable would strengthen the manuscript.”

Thank you for this valuable suggestion. We agree that extending the range of receptor densities and spacer lengths would strengthen this manuscript by more directly comparing our result with previous studies and by testing our proposed mechanism at the high end of receptor densities. We therefore plan to extend our analysis to receptor incorporations of at least 5 mol% and to compare lipid mixing using receptor mimetics displayed on 12 (+4.08 nm), 24 (+8.16 nm), and 32 (+10.88 nm)-nucleotide oligo linkers.

If these experiments cannot be completed successfully within the revision, we will expand the Discussion to more clearly define the range of conditions over which we expect our conclusions to apply and where they may not.

Reviewer #3: “1) The conclusions are drawn from a flow cytometry, which allows to analyse samples in bulk. On one hand, it allows analysis of a large number of fusion events; on the other hand, it cannot resolve individual events or the relationship between binding and membrane fusion in individual binding states. The flow cytometry method used in the manuscript should be validated against single-particle fusion events in microscopy-based assays, which would also allow investigation of both the binding area and fusion (as done in the Fig S6). Here, authors could evaluate the effect of neutralizing antibody, NA inhibitor or the presence of soluble sialic acid pretreated virions at receptor concentrations higher than 16%.”

Thank you for revealing this potential point of confusion. Fundamentally, flow cytometry does measure individual particles which are sampled from a particle suspension; from this, we derive the distribution of liposome-bound virus particles that have undergone R18 dye dequenching within discrete time intervals. It is true that we do not track a single virion from binding to fusion, but we instead measure the distribution of single virions (in virion-liposome pairs) in sampled time bins. In other words, this is not a single-particle tracking experiment (which SPB/TIRF is), but it is nonetheless a single-particle experiment well suited to derive single-particle kinetics and especially efficiencies under attenuation. To address this reviewer’s comment, we will improve our description of this assay to make sure this distinction is clearly made in writing.

We have developed this novel assay after much experimentation using SPB/TIRF, our key area of expertise (Ivanovic, Choi et al. 2013, Li, Li et al. 2021, Li, Li et al. 2022) and realizing that this more standard approach is critically limited. Some of these limitations can be gleaned from the presented results as follows. Based on the decreases in particle attachment that we observed on supported planar bilayers with 16% receptor saturation with TIRF microscopy in Fig. S6, it would be impractical to evaluate differential effects on lipid mixing from receptor binding when receptor saturation is further reduced. In the spCALM experiment presented in Fig. 4B, which tests lipid mixing by the same virus strain used in the TIRF experiment presented in Fig. S6, the 6’SL receptor did not reduce lipid mixing efficiency until receptor saturation was decreased to values lower than 8%. Therefore, we are unable to assess the relevant receptor saturation regimes using TIRF microscopy; we expect that other treatments which influence receptor binding will likewise restrict virion attachment too severely to be practical. Finally, diffraction-limited optical microscopy methods do not provide any more information on virion-target membrane contact area than our flow cytometry-based method.

We presented several layers of validation of our assay and summarize them in order. Attachment of PR8 virions to erythrocyte membranes is inhibited by the neutralizing antibody SbH36-26 in the expected concentration range (Fig. 2C, (Partlow, Jaeggi-Wong et al. 2025)). As in SPB/TIRF, PR8 has lower baseline efficiency than X31 in spCALM (Fig. S2, (Otterstrom, Brandenburg et al. 2014)). As is well established including by SPB/TIRF, fusion kinetics and efficiency are pH-dependent in spCALM (Fig. 3E, (Floyd, Ragains et al. 2008, Ivanovic, Choi et al. 2013)). As in SPB/TIRF, Gamma cumulative distribution fitting of lipid mixing vs. time trajectories in spCALM revealed 3-4 underlying steps (Fig. S8, (Floyd, Ragains et al. 2008, Ivanovic, Choi et al. 2013, Otterstrom, Brandenburg et al. 2014, Ivanovic and Harrison 2015, Li, Li et al. 2021, Li, Li et al. 2022).

Reviewer #3: “2) In particular, authors do not provide data showing that flow cytometry can quantify time-resolved distributions of lipid mixing states among single virions bound to individual cells or vesicles, as claimed in the introduction (Page 3, line 85). Flow cytometry can not distinguish a single virion bound to a 1µm vesicle from multiple virions bound to a 1µm vesicle. Liposomes often can bind to multiple virions, as shown by previous cryo-EM studies. Since authors use liposomes extruded via a 1µm filter, it is expected that these liposomes will be heterogeneous in size and shape, and thus single liposomes can bind a variable amount of viruses, leading to a variable amount of dequnching. In addition, this will lead to aggregation - analogous to a hemagglutination assay, which will complicate the interpretation of flow cytometry results.”

We thank Reviewer #3 for raising this point – in response, we have performed additional analyses which, as we demonstrate in what follows, formalize our claims. Since flow virometry can readily distinguish single virions from pairs or groups of associated virions by virion fluorescence intensity (bioRxiv: https://doi.org/10.64898/2026.06.15.729605), we decided to analyze fluorescence distributions of free and liposome-associated virions in our experiments to probe whether multi-virion binding to single liposomes occurs with notable frequency. Liposomes with more than one bound virion would, just like clumped virions do, shift upward in fluorescence intensity. We illustrate here with the results of this analysis for the experiment shown in Fig. 5A,B, where virion-liposome input was the highest (0.5 vs. 0.15 in the remaining experiments; also see our response regarding the MEDI8852 experiment to Reviewer 1). We used virus-only and liposome-only controls to define cytometry gates for unbound virions and virion-free liposomes. We extracted the R18 fluorescence distributions for liposomes with and without bound virions, and for unbound virions in the same sample (Display Item 3). The fluorescence distributions for virions and liposome-virion bound complexes strongly overlap and are both considerably higher than the distribution for liposomes without virions. This is consistent with liposomes not appreciably binding more than one virion. We will extend this analysis to the remaining samples in this experiment and to other experiments and present it as a supplementary figure in the revised manuscript. This analysis furthermore excludes the existence of aggregates such as in a hemagglutination assay.

Display Item 3 caption: Liposomes do not bind multiple particles. (A) Representative sample from the experiment presented in Fig. 5A,B showing that liposome-virion complexes have nearly overlapping R18 fluorescence distribution to unbound virions, and both have higher intensity than liposomes without bound virions. (B) Violin plots showing the distribution of median R18 fluorescence distributions for the specified populations representing all samples from the experiment presented in Fig. 5A,B.

Reviewer #3: 3) Liposomes with variying concentration of receptors should be characterized by cryo-EM as a quality check. It is not clear what the size distribution of liposomes and multilamellarity is. A fraction of small liposomes can skew the analysis as they would not be gated in the flow cytometry. In addition, cryo-ET could be used to analyze the contact zone area at different concentrations of DNA-linked sialic acid receptors.

We agree that the size distribution of the liposome preparations used in our study is likely heterogeneous to some extent and that an analysis of the efficiency of lipid mixing for liposomes of different sizes is therefore useful. We thank this reviewer for suggesting we explore this further. In spCALM, liposomes are detected with a range of DiD membrane dye fluorescence and 488-nm side-scatter intensities. For the experiment presented in Fig. 4B, we separately gated subsets of liposomes with low DiD fluorescence and side-scatter intensity, which would comprise smaller liposomes on average, and of liposomes with high DiD fluorescence and side-scatter, which would comprise larger liposomes (Display Item 4A). We compared lipid-mixing efficiency of bound virion-liposomes pairs between the small and large liposome subpopulations to the total liposome population. Differences in efficiency across liposome subpopulations within each replicate were small relative to differences across replicates (Display Item 4B). The smallest ~7-9% of liposomes fused slightly more efficiently at very low or no receptor saturation whereas the largest ~1-3% liposomes tended to fuse somewhat less efficiently overall. The results of the experiment with respect to the effect of receptor density, NA-inhibition, and receptor type are thus practically indistinguishable between the liposome size subpopulations (Display Item 4C). From this, we infer that size heterogeneity in our liposome preparations neither explains nor confounds our interpretations of the regulatory effect of receptor binding on lipid mixing. We will present this analysis as a supplementary figure in the revised manuscript.

Display Item 4 caption: Liposome size heterogeneity does not produce meaningful differences in lipid-mixing efficiency. (A) We re-analyzed the experiment presented in Fig. 4B by separately analyzing lipid mixing for liposomes with low (Small liposomes) or high (Big liposomes) 488-nm side-scatter (SSC-A) and DiD membrane fluorescence (APC-A). (B) Lipid mixing efficiency for liposomes displaying 3’SL or 6’SL receptors at the indicated range of saturations in the presence or absence of 100 nM NAI; analyses with each liposome size subpopulation are connected by lines for each replicate. (C) For each liposome size subpopulation, logistic curves with a shared Hill slope were fit to the combined data from each condition, with shaded 95% confidence intervals. The overall effect of receptor saturation, receptor type, and NA-inhibition is not meaningfully different between the liposome size subpopulations.

Reviewer 3: “4) Data on receptor binding promote HA insertion is not cleanly explained and not experimentally justified. Increased binding of virion and liposomes, will potentially lead to an extended binding zone, which could give rise to multiple fusion pores, which could accelerate dequenching and the R18 fluorescence burst. Previous cryo-ET work has shown that interaction with liposomes can engage one to seven HA glycoproteins when 5 mol% gangliosides are present in 200 nm liposomes (PMID: 27572837). This should be considered in the model and the manuscript would largely benefit from having a resolution analysis of the liposomes at varying concentrations of the DNA-sialic acid and the binding area with a virus.”

We thank reviewer #3 for raising the alternative hypothesis that receptor binding could deform the target membrane, thereby increasing the virion-target contact area and the number of HAs contained within. We agree that this is a plausible mechanism that merits consideration. Our current data do not distinguish between this possibility and the hypothesis that receptor binding promotes HA fusion peptide insertion, and we will revise the interpretation of Figure 5A, B results and the Discussion to more explicitly acknowledge these alternative interpretations.

To discriminate between these two mechanistic models, we will evaluate whether receptor density differentially affects lipid mixing of spherical and filamentous virions. We hypothesize that if receptor binding promotes lipid mixing by increasing membrane wrapping and thereby expanding the virion-target contact area, this effect would be more pronounced for spherical virions than for filaments. For a spherical particle, relatively small increases in the extent of membrane wrapping produce comparatively large increases in the buried contact area and, consequently, in the number of HA molecules within the virion-target contact zone. In contrast, for a filament, comparable increases in membrane wrapping produce substantially smaller relative changes in buried contact area. Moreover, membrane wrapping around a sphere is expected to incur greater membrane deformation costs than wrapping around a filament, such that increasing receptor density may produce a relatively sharp transition to extensive wrapping for spherical virions, whereas the corresponding response for filaments would be expected to be more gradual. Thus, if receptor density primarily regulates lipid mixing by modulating the extent of membrane wrapping, we would expect the receptor-density dependence to be steeper for spherical virions than for filaments.

We note that this experiment presents technical challenges. Filamentous virions require larger target membranes to generate sufficient R18 dequenching to resolve unfused and lipid-mixed virion-target pairs, and we therefore anticipate using erythrocyte ghosts rather than liposomes as targets. Receptor density on erythrocyte ghosts would be modulated with bacterial neuraminidase under varying conditions. If these experiments can be completed in time for the revision, we will include them in the revised manuscript. Regardless, we will revise our discussion to explicitly consider membrane deformation as an alternative mechanism underlying the receptor-density dependence observed in Fig. 5AB.

Can strong binding induce liposome membrane rupture?”

To test if liposomes are rupturing or aggregating, we examined the total number of detected liposomes before pH drop for the experiment presented in Fig. 4B (Display Item 2B). The total liposome count decreased somewhat at high receptor saturation for liposomes bearing 3’SL but not 6’SL. This effect was associated with a small increase in the fraction of brighter liposomes for 3’SL but not 6’SL liposomes (Display Item 5). From this, we infer that this apparent loss of liposomes is due to aggregation and not rupture. Importantly, the effect on total liposome counts was relatively small and only present for 3’SL-bearing liposomes, for which efficient lipid mixing required greater receptor density than for 6’SL-bearing liposomes. We therefore conclude that this putative aggregation effect is inconsequential for our lipid mixing results.

Display Item 5 caption: Mild liposome aggregation at high receptor saturation. Representative scatter plots of DiD membrane fluorescence (y-axis) and 488-nm side-scatter (x-axis) before pH drop for liposomes decorated with 0, 16, or 100% saturation with either 3’SL (top) or 6’SL (bottom) receptor mimetics. Gates for overall liposomes, small liposomes, and large liposomes are provided to illustrate the emergence of a larger subpopulation for 3’SL 100%.

and

“6) As in 3D space, viruses can also bind several vesicles; membrane fusion would lead to an increase in the size of the vesicles. Can this be detected by flow cytometry? If not, what is the benefit of the flow cytometer over the classical fluorimeter, which has been routinely used to monitor membrane fusion in bulk?”

As we demonstrate in Display Item 3 and Fig. 2A-B, virions bound to vesicles are distinguishable from vesicles without virions and virion-vesicle pairs that have undergone lipid mixing are distinguishable from pairs which have not. Flow cytometry thus offers a fundamental advantage over bulk fluorimetry because it measures membrane fusion on individual virion-liposome pairs rather than as an ensemble average. Each detected event reports whether a virion is bound to a liposome and whether that virion has undergone lipid mixing. This allows us to determine the probability of lipid mixing among bound virions while independently quantifying binding efficiency. In contrast, bulk fluorimetry reports only the summed fluorescence of the entire sample, making it impossible to distinguish changes in membrane fusion efficiency from changes in the number of virion-target interactions.

“Also, please comment on the sensitivity of the instrument and required volumes, as well as how acid is added. How was the final pH of the mixture determined so precisely?”

We thank the reviewer for pointing out that this description was ambiguous. The reported pH values correspond to the fusion-triggering buffer rather than the final reaction mixture, and we have revised the text to make this explicit on lines 116-118, 189, 194, 299, 737-738, 754, 769, 773, 786-787, 801-802, 807-808. Because the neutral pH virion-liposome mixture is diluted approximately 10-fold into the acidic triggering buffer, the final reaction pH is expected to be very close to that of the triggering buffer. We will experimentally verify this and report the result in the revised manuscript.

Reviewer #3: “7) How efficient is the membrane fusion compared to total disassembly included by a detergent? Normalisation to total dequnching should be used. “

We thank Reviewer #3 for this comment. We believe there may be a misunderstanding regarding the readout of the spCALM assay. Unlike conventional bulk fluorimetry experiments, spCALM does not quantify the magnitude of ensemble R18 fluorescence dequenching. Instead, it analyzes individual virion-liposome pairs and classifies each virion as either quenched or dequenched within discrete sampling intervals. Thus, the question addressed by spCALM is, "What fraction of virion-liposome pairs have undergone lipid mixing?", whereas bulk fluorimetry asks, "How much total R18 dequenching has occurred?" Lipid-mixing efficiency is therefore determined from the fraction of individual virions occupying the dequenched population and is independent of the absolute fluorescence intensity of the R18 signal. Consequently, normalization to detergent-induced total dequenching, which is appropriate for bulk fluorescence assays, is not applicable to the single-particle measurements reported here because complete lipid mixing is intrinsically represented by complete occupancy of the dequenched state. We will revise the manuscript to make this distinction clearer and avoid potential confusion for readers more familiar with ensemble fusion assays.

Reviewer #3: “8) HA/NA functional balance is not only constrained by the distribution of sialic species but also by the ratio of the HA/NA and by the NA spatial distribution, which is clustered only at one end and hence it cannot interfere in the binding zone. This is not discussed in the manuscript or introduced.”

We agree that the spatial organization of HA and NA is an important consideration when interpreting HA/NA functional balance. However, the polarized distribution of NA observed on mature virions might not persist under the low-pH conditions of membrane fusion; polarized NA organization on the virion surface is maintained by the interactions with the underlying M1 matrix which restrict NA mobility (Vahey and Fletcher 2019), and acidification is known to dissociate the underlying M1 matrix layer (Calder, Wasilewski et al. 2010). We had discussed in the original submission that in the context of its polarized distribution, NA might limit receptor availability before the virion-target contact interface is established or, alternatively, it might become mobile at the pH of fusion and contribute from within the interface (lines 400-408). In the revision, we will ensure that the concept of HA/NA polarization is clearly introduced so that it is not overlooked.

Reviewer #3: “9) Conclusions in the manuscript could be strengthened by providing data on binding and fusion using viruses that were pre-treated with different amounts of soluble sialic acid prior to the fusion kinetics measurement.”

We thank Reviewer #3 for this interesting suggestion. While soluble receptor (kd for monomeric binding is ~1 - 4 mM) might not effectively compete with the multivalent receptor displays on the target membrane, this experiment is relatively simple to implement, and a positive outcome has a potential to further hone the mechanistic interpretations of our findings. We will perform experiments measuring virion binding and lipid mixing in the presence of varying concentrations of soluble sialyllactose and include the results in the revised manuscript. Depending on the outcome, these experiments may help distinguish whether receptor binding primarily acts through membrane-associated interactions or by directly modulating HA conformation or function. We will discuss the implications of these results for the proposed mechanism by which receptor binding promotes lipid mixing. A negative result (i.e. no effect from the soluble receptors) will be difficult to interpret and will be simply reported as such.

Reviewer #3: “1) Figure 2 lacks information on time fo the three plots. A time stemp could be also included to the video.”

We will revise Fig. 2 and Movies 1 and 2 to include information on time.

Reviewer #3: “2) It is not clear why the model is presented as figure 1 and the density of spikes does not reflect the density on the viruses - it is not drawn to the scale, which in this study might be important.”

We thank Reviewer #3 for this comment. The purpose of Figure 1 is to provide a schematic illustration of the local conformational changes associated with membrane fusion rather than to accurately represent the surface density or number of HA molecules on influenza virions. We recognize that this was not sufficiently clear in the original figure. To avoid any confusion, we will explicitly indicate in the figure that the illustration is not drawn to scale. We will also revise the legend to clarify that the virion-target contact patch for a representative particle in our experiments is expected to contain on the order of 100 HA molecules, and that the simplified depiction is intended solely to illustrate the key molecular events within the virion-target interface, specifically the fusion cluster and ways HA might be rendered nonparticipating. Depicting the full complement of HA molecules expected within the contact patch would substantially obscure the illustration of the fusion cluster in Fig. 1B and of inhibitor or antibody binding and nonproductive HA refolding in Fig. 1C.

Reviewer #3: “3) The manuscript structure could be improved, although it is understandable that the final format depends on the journal. Some information on methods is present in the main text, and some in the extended methods in the supplementary data. This makes the manuscript harder to review. Authors could consider redistributing some supplementary information to the main data, and consider publishing the first method and its validation, and another manuscript on biology analysis.”

We will certainly rearrange the structure of the methods to accommodate the guidelines of the eventual journal of publication. We aimed to structure our main figures to convey the most essential findings of the work but are open to promoting supplementary content to main figures if it can be accommodated within journal guidelines.

Reviewer #3: “Overall, TIRF microscopy and SBP (Fig S6) present a much more accurate method than flow cytometry as it allows to study individaul events and provides additional information on virus size, fluorescence signal etc. In addition, single-molecule FRET methods could be used to monitor HA conformational changes at varying concentrations of sialic acid receptors. Previous studies have already shown that binding to sialic acid allosterically regulates HA2 conformational dynamics (PMID: 29961575).”

We respectfully disagree that TIRF microscopy of supported planar bilayers is inherently more accurate than flow cytometry in the ways described in this comment. As we detail in other responses in this document (see our responses to “Reviewer #3: “2) In particular, authors do not provide data showing that…” __and “6) As in 3D space, viruses can also bind several vesicles; …”), flow cytometry in the form of spCALM permits analysis of lipid mixing deriving from fluorescence measurements of single, membrane-attached virions. For analysis of virus particles with sizes below the diffraction limit of visible light, which are the sizes that we study here, flow cytometry provides as much size information per particle as TIRF microscopy. Please see our response to reviewer 3 (“1) The conclusions are drawn from a flow cytometry, …”__) regarding the suitability of SPB/TIRF for the current mechanistic questions.

We agree that single-molecule FRET has provided important insight into HA conformational dynamics, including the observation that receptor binding shifts HA toward downstream conformational intermediates (Das, Govindan et al. 2018). However, smFRET addresses a fundamentally different mechanistic question than the present study. smFRET reports on the conformational dynamics of individual labeled HA molecules, whereas our experiments measure the functional outcome of the collective action of many HAs during membrane fusion. Moreover, interpretation of smFRET measurements relies on site-specific fluorophore labeling within conformationally sensitive regions of HA, an experimental strategy that may itself influence the native conformational landscape. Thus, while highly complementary, smFRET cannot directly establish how receptor binding alters the probability of productive lipid mixing.

Implementing and validating an smFRET assay for our virus-membrane fusion system would require substantial development of a highly specialized methodology and is therefore beyond the scope of the present study. Instead, we will expand the Discussion to place our findings in the context of previous smFRET studies. Specifically, we will discuss that, although previous work indicates that receptor binding increases occupancy of later HA conformational intermediates, our data support a different mechanistic interpretation: receptor engagement does not primarily drive HA further along its conformational pathway toward HA extension but instead alters the probability that receptor-bound HAs proceed to membrane insertion following low-pH triggering. In sum, smFRET provides an indication that receptor binding influences conformational HA dynamics whereas our study evaluates the effect of receptor binding on lipid mixing by virions. Both approaches are important, but neither can fully recapitulate the value of the other, nor are they necessarily in conflict.

__ __

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 #1: “A couple points in the text, the authors use the term "distributional dynamics". This term is not defined and could use clarification.”

We agree that this wording was unclear and have revised our wording for clarity on lines 105-106, 204, 801, and 807.

Reviewer #1: “Why have the authors used this technique using lipid-ssDNA and receptor-DNA to display sialic acid on the liposomes? In principle, this allows control over the distance between the sialic acid and the membrane. But in the spCALM assay the length of the spacer DNA (12 or 24 nt) had not effect. So, why then not use the simpler approach of incorporating sialylated lipids (e.g. GD1a, GD1b) in the membrane?”

We thank this reviewer for the opportunity to clarify two additional key advantages of our approach. Our system allows us to display glycans of precisely defined structure, with either α2,3 or α2,6 sialic acid linkage, on identical carbohydrate-lipid conjugates, which ensures identical chemistry and display geometry with only the intended differences. This is not possible with gangliosides familiar to us including GD1a (displays a terminal alpha2,3-linked sialic acid) and GD1b (contains only internal sialic acids, alpha2,8-linked in tandem). Furthermore, to alter receptor density using gangliosides, one must alter membrane lipid composition, while our system allows tuning of receptor density without changing lipid composition.

We have added a description of these key advantages in lines 161-163. We have furthermore restructured the introductory paragraph in the Results section “Programmable glycan-receptor displays for membrane-fusion studies” to first emphasize programmability of the receptor type, then tunability of density without altering lipid or display chemistry, and the spacer component is now mentioned last (as this, indeed, turned out inconsequential for lipid mixing under our current assay conditions).

__Reviewer #2: “____While the precise control of receptor identity and density is a strength of this experimental approach, more discussion of how the conditions tested here compare to physiological conditions would strengthen the manuscript. The receptor densities tested here are We agree that placing the tested receptor densities into a physiological context is valuable. Estimates of the density of influenza receptors in the endosomal compartments where membrane fusion takes place are not available, so we instead compare our system with the plasma membrane of human erythrocytes in the Discussion section, lines 361-372. The maximum receptor density used in our experiments is approximately 15-fold lower than the total sialic acid content of the human erythrocyte glycocalyx. However, this comparison almost certainly overestimates the density of physiologically relevant influenza receptors because it includes all sialic acid regardless of glycosidic linkage, underlying glycan structure, or accessibility. Consequently, the density of functional influenza receptors may be substantially closer to the receptor densities explored in our chemically defined liposome system. Moreover, the receptor composition and density within the endosomal lumen remain unknown and might differ considerably from those of the erythrocyte surface. Finally, receptor density may vary widely across potential cell targets in complex systems of natural infections.

Our aim was to identify the mechanisms by which receptor binding regulates HA-mediated lipid mixing using a molecularly defined receptor display. This approach allowed us to systematically vary receptor density over a controlled range while avoiding the compositional complexity of native membranes, thereby enabling mechanistic interpretation of receptor density-dependent effects.

Reviewer #2: Regarding the experiments in Figure 4 and S13: what is the anticipated phenotype for the A227T variant? It appears to have the opposite effect of the avidity-increasing E246G mutation, restoring WT avidity in the double mutant (line 245), and forming larger plaques in MDCK cells when introduced alone (in contrast to the smaller plaques formed by E246G). However, in spCALM measurements (Fig 4C), it behaves similarly to WT. The authors mention that this result is surprising (line 259), but more context for this observation would be helpful. Similarly, it is interesting that all of the variants tested exhibit higher peak fusion efficiency than the WT (50-75% vs. 25%). I would be interested how the authors interpret this result.

We agree that these observations merit additional discussion. We have revised the manuscript to more carefully interpret the plaque assay results, acknowledging that plaque size reflects the combined effects of virus attachment, entry, membrane fusion, replication, and release, and therefore cannot be directly attributed to altered receptor binding or fusion alone (lines 249-256).

Our reanalysis of the spCALM attachment data (prompted by the Reviewer 1 comment regarding MEDI8852-Fab’s effects on virion attachment) provides additional context for interpreting HA mutants. The attachment phenotypes closely parallel the lipid-mixing results: E246G exhibits the greatest increase in virion binding, A227T alone behaves similarly to WT (maybe slightly reduced binding), and the A227T mutation partially or fully reverses the enhanced binding conferred by E246G (see Display Item 6 below). We have incorporated these observations into the revised Results (lines 256-265) and expanded our interpretations to emphasize that receptor binding and lipid mixing exhibit similar qualitative trends but distinct quantitative dependencies on receptor density (lines 265-271).

Display Item 6 caption: Trends in virion attachment efficiency mirror those of lipid-mixing efficiency, but attachment is sensitive to receptor density at greater values than for lipid mixing. (A) The percentage of total recovered virions which are attached to liposomes. (B) Efficiency of lipid mixing among bound virion-liposome pairs, replotted from Fig. 4C for ease of comparison.

Finally, we agree that the increased maximal lipid-mixing efficiencies observed for all three HA variants relative to WT are intriguing. At present, we do not know the molecular basis for this effect, and we do not believe it can be reliably inferred from the available data. We will therefore discuss this as an interesting observation that warrants future investigation while emphasizing that it does not affect the principal conclusion of the study that HA-receptor interactions regulate lipid-mixing efficiency through receptor avidity.

Reviewer #2: “Line 49: "3-4 neighboring HA2 molecules" should be clarified to indicate that this means 3-4 trimers (as stated a few lines later).”

Thank you, we have clarified the wording in this clause on line 49.

__Reviewer #2: “Line 278: "presence of absence" should read "presence or absence".” __

We thank Reviewer #2 for pointing this out; we found and revised a total of three instances of this typographical error in the main manuscript (lines 289, 309, 769) and one in the supplementary appendix (Fig. S9 legend).

Reviewer #2: “Line 296: I am surprised that 450nM MEDI8852 is a sub-neutralizing dose; this seems higher than what has been reported elsewhere, although it may be a specific feature of the virus used here. Can the authors clarify how this was determined, i.e., is this based on an infection assay or a lipid mixing assay?”

Our intended meaning is that the tested dose of MEDI8852-Fab reduces lipid-mixing efficiency and does not fully inhibit it. We agree that this was unclear and have clarified our language on lines 308-309. As an aside, we note here that in vitro membrane fusion experiments seem to be less susceptible to inhibition by MEDI-Fab than infection experiments (i.e. neutralization), as was reported by our lab in 2021 (Li, Li et al. 2021).

__Reviewer #3: __

__“5) How does 60% receptor saturation compare to the physiological concentration of receptor density? __

We agree that placing the tested receptor densities in a physiological context is valuable. As discussed in response to Reviewer #2, we have expanded the Discussion to compare our receptor densities with estimates for the erythrocyte glycocalyx (see lines 362-378). The maximum receptor density used in this study is approximately 15-fold lower than the total sialic acid density on the erythrocyte surface, although this comparison likely overestimates the number of physiologically relevant influenza receptors because it includes all sialic acid species irrespective of glycosidic linkage, glycan structure, or accessibility. The density of accessible influenza receptors within the endosomal lumen, where fusion occurs in vivo, is not known.

Reviewer #3: “4) Webster ER et al, PMID: 35143209 should be referenced as it showed similar approaches using DNA as a tether to study influenza membrane fusion.”

We thank Reviewer #3 for pointing out that we did not reference this study. We have modified the text to reference this study on lines 71-73 and 152.

Reviewer #3: “____A limitation is that only lipid mixing is monitored and no full fusion. Hence, one cannot conclude that all lipid mixing here leads to a full fusion pore opening. This should be addressed in the manuscript or at least noted as a limitation noted in the manuscript as a limitation. “

We thank Reviewer #3 for highlighting this important distinction. We agree that lipid mixing does not necessarily imply subsequent fusion pore formation and that our assay specifically reports on the lipid-mixing (hemifusion) intermediate rather than full fusion. We have revised the manuscript to make this point more explicit on lines 110–114 and 329-330. Specifically, we now state that our approach probes the lipid-mixing fusion intermediate (i.e., hemifusion), which reports on the preceding HA conformational changes and is an obligate intermediate on the pathway to fusion pore formation.

__ __

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 #1: “The authors raise the interesting possibility that neuraminidase (NA) may contribute to virion attachment in the presence of NAI. Would it be worthwhile to test fusion of virions in the absence of NA? Or in the presence of NA where the sialic acid binding site has been mutated?”

We thank Reviewer #1 for this thoughtful suggestion. We agree that comparing lipid mixing of virions lacking NA or carrying mutations in the NA sialic acid-binding site would provide a direct test of whether receptor-NA interactions contribute to virion attachment and/or lipid mixing. Although NA is a relatively low-abundance virion glycoprotein (there are 4-5 HAs for each NA on the virion surface), it is possible that receptor-NA binding contributes in some way to lipid mixing. We are interested in exploring this in future work. However, production of virions without NA or with defective NA is expected to be challenging because of reduced viral fitness and infectivity. Moreover, this could lead to unintended (e.g. compensatory) differences in virion morphology or glycoprotein composition that would complicate interpretations of any observed effects on lipid mixing. We therefore believe that this represents a substantial follow-up study that is beyond the scope of the current manuscript.

References to works cited in this revision plan

Calder, L. J., S. Wasilewski, J. A. Berriman and P. B. Rosenthal (2010). "Structural organization of a filamentous influenza A virus." Proc Natl Acad Sci U S A 107(23): 10685–10690.

Das, D. K., R. Govindan, I. Nikic-Spiegel, F. Krammer, E. A. Lemke and J. B. Munro (2018). "Direct Visualization of the Conformational Dynamics of Single Influenza Hemagglutinin Trimers." Cell 174(4): 926–937 e912.

Floyd, D. L., J. R. Ragains, J. J. Skehel, S. C. Harrison and A. M. van Oijen (2008). "Single-particle kinetics of influenza virus membrane fusion." Proc Natl Acad Sci U S A 105(40): 15382–15387.

Ivanovic, T., J. L. Choi, S. P. Whelan, A. M. van Oijen and S. C. Harrison (2013). "Influenza-virus membrane fusion by cooperative fold-back of stochastically induced hemagglutinin intermediates." Elife 2: e00333.

Ivanovic, T. and S. C. Harrison (2015). "Distinct functional determinants of influenza hemagglutinin-mediated membrane fusion." Elife 4: e11009.

Li, T., Z. Li, E. E. Deans, E. Mittler, M. Liu, K. Chandran and T. Ivanovic (2021). "The shape of pleomorphic virions determines resistance to cell-entry pressure." Nat Microbiol 6(5): 617–629.

Li, Z., T. Li, M. Liu and T. Ivanovic (2022). "Hemagglutinin Stability Determines Influenza A Virus Susceptibility to a Broad-Spectrum Fusion Inhibitor Arbidol." ACS Infect Dis 8(8): 1543–1552.

Otterstrom, J. J., B. Brandenburg, M. H. Koldijk, J. Juraszek, C. Tang, S. Mashaghi, T. Kwaks, J. Goudsmit, R. Vogels, R. H. Friesen and A. M. van Oijen (2014). "Relating influenza virus membrane fusion kinetics to stoichiometry of neutralizing antibodies at the single-particle level." Proc Natl Acad Sci U S A 111(48): E5143–5148.

Partlow, E. A., A. Jaeggi-Wong, S. D. Planitzer, N. Berg, Z. Li and T. Ivanovic (2025). "Influenza A virus rapidly adapts particle shape to environmental pressures." Nat Microbiol 10(3): 784–794.

Vahey, M. D. and D. A. Fletcher (2019). "Influenza A virus surface proteins are organized to help penetrate host mucus." Elife 8.

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Referee #3

Evidence, reproducibility and clarity

Summary: The manuscript by Plamitzer et al. investigates influenza A virus hemagglutinin (HA)-mediated membrane fusion using bulk flow cytometry analysis. In the assay, they use red blood cells and liposomes carrying defined, variable densities of sialic acid residues. They used H3N2 and H1N1 model viruses with spherical morphology. The liposomes were produced using double-stranded DNA to attach sialic acid. Similar studies have been done using DNA-tethers to study membrane fusion between liposomes and influenza virions (PMID: 35143209, PMID: 27410740). Some previous studies have shown that reduced HA binding does not influence membrane fusion, while others have shown that binding increases membrane fusion. This work aims to reconcile prior conflicting observations. Based on their results, they conclude that HA-receptor binding avidity and the extent of neuraminidase (NA)-mediated receptor cleavage directly influence lipid mixing, which is used here as a proxy for membrane fusion and allows monitoring of the first step of fusion, namely the hemifusion intermediate. The results of the test whether receptor binding modulates the HA extended intermediate should be interpreted with more caution. The manuscript would benefit from more data on the characterisation of liposome carrying dsDNA sialic acid receptors and from using the TIRF SBP method to validate the flow cytometry. Major comments: 1) The conclusions are drawn from a flow cytometry, which allows to analyse samples in bulk. On one hand, it allows analysis of a large number of fusion events; on the other hand, it cannot resolve individual events or the relationship between binding and membrane fusion in individual binding states. The flow cytometry method used in the manuscript should be validated against single-particle fusion events in microscopy-based assays, which would also allow investigation of both the binding area and fusion (as done in the Fig S6). Here, authors could evaluate the effect of neutralizing antibody, NA inhibitor or the presence of soluble sialic acid pretreated virions at receptor concentrations higher than 16%. 2) In particular, authors do not provide data showing that flow cytometry can quantify time-resolved distributions of lipid mixing states among single virions bound to individual cells or vesicles, as claimed in the introduction (Page 3, line 85). Flow cytometry can not distinguish a single virion bound to a 1µm vesicle from multiple virions bound to a 1µm vesicle. Liposomes often can bind to multiple virions, as shown by previous cryo-EM studies. Since authors use liposomes extruded via a 1µm filter, it is expected that these liposomes will be heterogeneous in size and shape, and thus single liposomes can bind a variable amount of viruses, leading to a variable amount of dequnching. In addition, this will lead to aggregation - analogous to a hemagglutination assay, which will complicate the interpretation of flow cytometry results. 3) Liposomes with variying concentration of receptors should be characterized by cryo-EM as a quality check. It is not clear what the size distribution of liposomes and multilamellarity is. A fraction of small liposomes can skew the analysis as they would not be gated in the flow cytometry. In addition, cryo-ET could be used to analyze the contact zone area at different concentrations of DNA-linked sialic acid receptors. 4) Data on receptor binding promote HA insertion is not cleanly explained and not experimentally justified. Increased binding of virion and liposomes, will potentially lead to an extended binding zone, which could give rise to multiple fusion pores, which could accelerate dequenching and the R18 fluorescence burst. Previous cryo-ET work has shown that interaction with liposomes can engage one to seven HA glycoproteins when 5 mol% gangliosides are present in 200 nm liposomes (PMID: 27572837). This should be considered in the model and the manuscript would largely benefit from having a resolution analysis of the liposomes at varying concentrations of the DNA-sialic acid and the binding area with a virus. 5) How does 60% receptor saturation compare to the physiological concentration of receptor density? Can strong binding induce liposome membrane rupture? 6) As in 3D space, viruses can also bind several vesicles; membrane fusion would lead to an increase in the size of the vesicles. Can this be detected by flow cytometry? If not, what is the benefit of the flow cytometer over the classical fluorimeter, which has been routinely used to monitor membrane fusion in bulk? Also, please comment on the sensitivity of the instrument and required volumes, as well as how acid is added. How was the final pH of the mixture determined so precisely? 7) How efficient is the membrane fusion compared to total disassembly included by a detergent? Normalisation to total dequnching should be used. 8) HA/NA functional balance is not only constrained by the distribution of sialic species but also by the ratio of the HA/NA and by the NA spatial distribution, which is clustered only at one end and hence it cannot interfere in the binding zone. This is not discussed in the manuscript or introduced. 9) Conclusions in the manuscript could be strengthened by providing data on binding and fusion using viruses that were pre-treated with different amounts of soluble sialic acid prior to the fusion kinetics measurement.<br /> Minor comments: 1) Figure 2 lacks information on time fo the three plots. A time stemp could be also included to the video. 2) It is not clear why the model is presented as figure 1 and the density of spikes does not reflect the density on the viruses - it is not drawn to the scale, which in this study might be important. 3) The manuscript structure could be improved, although it is understandable that the final format depends on the journal. Some information on methods is present in the main text, and some in the extended methods in the supplementary data. This makes the manuscript harder to review. Authors could consider redistributing some supplementary information to the main data, and consider publishing the first method and its validation, and another manuscript on biology analysis. 4) Webster ER et al, PMID: 35143209 should be referenced as it showed similar approaches using DNA as a tether to study influenza membrane fusion.

Significance

The study attempts to answer an important question and is of interest to the membrane fusion field and the virology field. It provides flow cytometry to study membrane fusion and a method for DNA-based sialic acid receptors that can be displayed at control density.

Limitations and Advances:

1. Flow cytometry is a high throughput methods which allows to analyze many conditions. Recently published methods on flow virometry are promising methods that allow to study viron morphology. However, it might not be suitable to address specific mechanistic questions of membrane fusion to the molecular details presented in the model and discussed in the discussion. Overall, TIRF microscopy and SBP (Fig S6) present a much more accurate method than flow cytometry as it allows to study individaul events and provides additional information on virus size, fluorescence signal etc. In addition, single-molecule FRET methods could be used to monitor HA conformational changes at varying concentrations of sialic acid receptors. Previous studies have already shown that binding to sialic acid allosterically regulates HA2 conformational dynamics (PMID: 29961575).
2. A limitation is that only lipid mixing is monitored and no full fusion. Hence, one cannot conclude that all lipid mixing here leads to a full fusion pore opening. This should be addressed in the manuscript or at least noted as a limitation noted in the manuscript as a limitation.

Expertise: virology, membrane fusion, cryo-EM

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Referee #2

Evidence, reproducibility and clarity

This manuscript by Planitzer et al. investigates how NA activity, HA receptor binding avidity, and the identity and density of sialic acid receptors within the target membrane influence membrane fusion. This is an important question, as functional balance between HA and NA drives the antigenic evolution of seasonal influenza viruses and contributes to the pandemic potential of zoonotic viruses. As discussed in this manuscript, prior studies of how sialic acid receptors contribute to fusion following initial viral attachment are relatively few, and these have frequently reached different conclusions. Many of these discrepancies are likely attributable to details of the experimental system used to address the question, highlighting the importance of approaches in which the receptor identity and density are precisely controlled. Within this context, the sensitive and quantitative method the authors have developed to measure the efficiency and kinetics of virion fusion using flow cytometry ('spCALM') stands out as an important contribution of this manuscript. Using this approach, the authors convincingly demonstrate that engagement of HA with sialic acid receptors during the fusion process promotes efficient fusion, and that conditions that disrupt this engagement (low receptor densities combined with NA activity or receptor-HA mismatch) lead to reduced fusion efficiency by reducing the probability of fusion peptide insertion. Overall, the methods and findings of this paper are a strong contribution to the field and will be of interest to researchers studying viral membrane fusion as well as HA-NA balance. The manuscript is well-written, and the figures are very clear. The supporting figures provide additional context that is valuable. Addressing the comments below would strengthen the manuscript further.

Major comments:

• While the precise control of receptor identity and density is a strength of this experimental approach, more discussion of how the conditions tested here compare to physiological conditions would strengthen the manuscript. The receptor densities tested here are <1 mol%. I suspect that this is lower than physiological densities of sialic acid on the cell surface or in the endosome, but it would be helpful to have a direct (approximate) comparison in units of receptors per unit area.
• Related to my first point, a tradeoff in the approach described here is that the observations may be specific to the regime that is being tested. Any effort to expand the range of conditions tested would therefore be valuable. For example, the authors discuss prior work at higher receptor densities (line 364); it seems that this higher-density regime could be evaluated here for direct comparison. Similarly, it is interesting that the authors do not observe differences when they use 12nt vs 24nt for the display of sialic acid on DNA tethers. I would imagine that sustained receptor binding could be detrimental to fusion peptide insertion only if it occurs at too large of a distance from the target membrane. It seems likely that the distances involved here (~4nm vs. 8nm) may not be sufficient to observe this, but testing larger DNA anchors seems feasible. If not, additional discussion of contexts where the findings described here may no longer be applicable would strengthen the manuscript.
• Regarding the experiments in Figure 4 and S13: what is the anticipated phenotype for the A227T variant? It appears to have the opposite effect of the avidity-increasing E246G mutation, restoring WT avidity in the double mutant (line 245), and forming larger plaques in MDCK cells when introduced alone (in contrast to the smaller plaques formed by E246G). However, in spCALM measurements (Fig 4C), it behaves similarly to WT. The authors mention that this result is surprising (line 259), but more context for this observation would be helpful. Similarly, it is interesting that all of the variants tested exhibit higher peak fusion efficiency than the WT (50-75% vs. 25%). I would be interested how the authors interpret this result.

Minor comments:

Line 49: "3-4 neighboring HA2 molecules" should be clarified to indicate that this means 3-4 trimers (as stated a few lines later).

Line 278: "presence of absence" should read "presence or absence".

Line 296: I am surprised that 450nM MEDI8852 is a sub-neutralizing dose; this seems higher than what has been reported elsewhere, although it may be a specific feature of the virus used here. Can the authors clarify how this was determined, i.e., is this based on an infection assay or a lipid mixing assay?

Significance

This study establishes a powerful experimental approach to quantitatively dissect fusion between influenza viruses and target membranes across a wide range of experimental conditions. This approach represents a significant methodological advance and its high throughput allows the authors to quantify rare events. Additionally, the manuscript presents convincing data showing that, within the regimes tested here, sustained receptor engagement promotes membrane fusion by increasing the likelihood of fusion peptide insertion. The observation that this is reduced by NA activity at low receptor densities carries implications for HA-NA functional balance.

While the specific findings may be restricted to the range of experimental conditions tested here, the results will be of interest to researchers studying virus-membrane fusion and functional balance between the influenza virus glycoproteins.

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Referee #1

Evidence, reproducibility and clarity

Planitzer et al. have developed a clever flow cytometry assay to monitor hemagglutinin (HA)-mediated membrane fusion. This novel approach provides several advantages over bulk and single-particle fusion assays, including dramatically higher throughput and detection of lipid mixing under low efficiency conditions. As such, on purely technical grounds, this manuscript provides a significant advance to the field. The authors then apply their new approach to probe the role of HA-sialic acid binding in the membrane fusion reaction. This reflects an important open question in the field, which, as the authors point out, has been elusive. They conclude that sialic acid binding promotes efficient membrane fusion, probably by increasing the likelihood of the fusion peptide engaging the target membrane after acid-induced conformational changes. Overall, the manuscript is very well written; the data are rigorously analyzed and nicely presented; and the results are important and informative. My comments are, for the most part, minor.

A couple points in the text, the authors use the term "distributional dynamics". This term is not defined and could use clarification.

In the spCALM assay, the authors indicate that labeled virions were incubated with cells or liposomes at a ratio of "0.15 virions per target". How were the numbers of virions determined for these experiments? The Methods refer to MOIs in units of PFU/cell but do not indicate how the number of physical particles were determined.

Why have the authors used this technique using lipid-ssDNA and receptor-DNA to display sialic acid on the liposomes? In principle, this allows control over the distance between the sialic acid and the membrane. But in the spCALM assay the length of the spacer DNA (12 or 24 nt) had not effect. So, why then not use the simpler approach of incorporating sialylated lipids (e.g. GD1a, GD1b) in the membrane?

The authors raise the interesting possibility that neuraminidase (NA) may contribute to virion attachment in the presence of NAI. Would it be worthwhile to test fusion of virions in the absence of NA? Or in the presence of NA where the sialic acid binding site has been mutated?

The authors indicate that the MEDI antibody "increased binding across all tested conditions." But this was not mentioned again. By what mechanism do they expect the antibody enhances virus binding?

Significance

Planitzer et al. have developed a clever flow cytometry assay to monitor hemagglutinin (HA)-mediated membrane fusion. This novel approach provides several advantages over bulk and single-particle fusion assays, including dramatically higher throughput and detection of lipid mixing under low efficiency conditions. As such, on purely technical grounds, this manuscript provides a significant advance to the field. The authors then apply their new approach to probe the role of HA-sialic acid binding in the membrane fusion reaction. This reflects an important open question in the field, which, as the authors point out, has been elusive. They conclude that sialic acid binding promotes efficient membrane fusion, probably by increasing the likelihood of the fusion peptide engaging the target membrane after acid-induced conformational changes. Overall, the manuscript is very well written; the data are rigorously analyzed and nicely presented; and the results are important and informative.

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Reply to the reviewers

We thank the two reviewers for their constructive comments regarding our manuscript. Below is our point-by-point response (un-bold) to each reviewer’s comments together with the experiments we propose to carry-out in order to strengthen our main conclusions.

Reviewer #1

In this study, the authors investigate the effects of pharmacological inhibition of the spliceosome using the SF3B1 inhibitor pladienolide B in models of platinum-resistant non-small cell lung cancer (NSCLC). Using a combination of cell lines, platinum-resistant derivatives, and patient-derived xenograft (PDX) models, the authors show that spliceosome inhibition sensitizes platinum-resistant tumors to treatment and leads to increased DNA damage accumulation and impaired DNA damage response signaling. Transcriptomic analyses indicate that transcripts encoding DNA damage regulators are particularly sensitive to alternative splicing perturbations, and selected mechanistic experiments suggest involvement of specific regulators such as MLH3. The study further explores links between splicing inhibition, transcriptional activity, and cell cycle progression. Overall, the manuscript presents extensive datasets across multiple experimental systems and provides strong evidence that spliceosome inhibition can sensitize platinum-resistant tumors to DNA damage. However, several aspects of the mechanistic interpretation, data consistency, and presentation require clarification or strengthening to fully support the central claims.

We thank the reviewer for his/her positive comments on our work and we agree that the manuscript requires clarification to support our main claims.

Major comments* *

Conceptual clarity and synthesis of mechanistic model

The manuscript presents multiple mechanistic observations-including altered splicing of DNA repair genes, increased DNA damage accumulation, transcriptional perturbation, and cell cycle changes-but these are not integrated into a coherent conceptual framework. While it is reasonable that not all mechanistic details are fully resolved, the current presentation leaves the reader uncertain about the relative contributions of these processes. A clearer synthesis of the proposed mechanism, possibly including a summary model figure, would substantially improve the conceptual clarity of the study.

__We thank the reviewer for his/her comment. We acknowledge that our study provides multiple mechanistic observations. However, all these observations converge towards a more global mechanism by which pladienolide B induces cell death in NSCLC. Hence, we demonstrate that pladienolide B, which targets the SF3B1 protein, a core component of the spliceosome machinery, induces a massive shutdown of the DNA Damage Response signaling pathway, both at the transcriptional and splicing levels, which leads to enhanced genomic instability and cell death notably in NSCLC cells with acquired resistance to platinum salts. More specifically, we identified ATR, DNA-PKcs and MLH3 as novel targets of SF3B1 in NSCLC cell lines, as well as more importantly, in NSCLC Patient-Derived Xenografts. To our knowledge, and as also highlighted by the reviewer, this is the first evidence that pladienolide B slows-down tumor growth by negatively impacting DNA Damage Response in patient-derived xenografts. We agree with the reviewer that providing a summary model figure would improve the clarity of the study. We will provide such a graphical abstract in our revised manuscript. __

Biological specificity of platinum-resistant cell sensitivity

A central premise of the study is that platinum-resistant cells exhibit enhanced sensitivity to spliceosome inhibition. However, in several experiments (e.g., cell cycle analysis in Figure 2A), similar responses to pladienolide B appear to occur in both platinum-sensitive and resistant cells. This observation complicates the interpretation that resistant cells exhibit uniquely distinct vulnerability. The authors should clarify how these findings align with the proposed model and more explicitly distinguish shared versus resistance-specific responses.

__We thank the reviewer for this remark. In this study, we did not want to claim that platinum-salts resistant cells exhibit unique vulnerability to pladienolide B as we fully agree with the reviewer that pladienolide B also exhibits cytotoxic effects in parental sensitive cells, although with a delayed kinetic. We acknowledge that the way we introduced our results section in the former manuscript could have contributed to such a misunderstanding. Rather, we propose a model in which pladienolide B induces cell death in NSCLC cells by massively impairing the expression of key components of the DNA damage and repair signaling pathways, at the transcriptional and/or splicing level. As NSCLC cells with acquired resistance to platinum salts are likely more dependent to these pathways for their survival than parental cells, this explains enhanced susceptibility of these resistant cells to pladienolide B-induced cell death. We think that these results highlight spliceosome targeting compounds as an alternative therapeutic strategy in NSCLC patients who escape chemotherapy. According to the remark of the reviewer, we will modify the way we introduce our results and we will clarify all these points in the discussion section of the revised manuscript. __

Heterogeneity in PDX responses and lack of platinum-sensitive controls

The PDX experiments represent a major strength of the study. However, resistant tumors display heterogeneous responses to pladienolide treatment, suggesting the presence of additional determinants of sensitivity.

__We thank the rewiever for this remark. In this study, we used seven distinct NSCLC PDXs We initially selected these PDXs based on their low responsive rate to cisplatin rather than their mutational status. As discussed in the discussion section, we did not find any common mutation(s) that could predict the differential response of these PDXs to pladienolide B. We only noticed that the LCIM10 PDX, which is the most responsive to pladienolide B, exhibits ATRX mutation. ATRX has been shown to protect stalled replication forks from collapsing. As we found that pladienolide B induces early replicative stress in NSCLC cells, it is tempting to speculate that ATRX mutation might interfere with the replicative stress response and potentiates pladienolide B’s cytotoxic effects. Noteworthy, LCIM10 PDX also displayed higher basal levels of both P-DNA-PKcs(Ser2056) and P-ATR(Thr1989) proteins as compared to LCF26, ML1 and LCIM1 PDXs that were less responsive to pladienolide B (data to be added in the revised version of the manuscript as supplementary data). Therefore, and although this remains to be further clarified, this suggests that NSCLC patients with higher basal level of replicative stress, such as those who escape chemotherapy, might be more susceptible to SF3B1 inhibition. __

Including platinum-sensitive PDX tumors, if available, would provide valuable baseline comparison and strengthen interpretation of resistance-specific effects. If not feasible, the limitations should be acknowledged and discussed.

To our knowledge, and as also mentioned by the reviewer, our study provides the first demonstration of the effects of pladienolide B on the growth of NSCLC PDXs. We think that these results pave the way for further investigations in additional NSCLC PDXs and we agree with the reviewer that adding platinum-sensitive PDX tumors would be interesting. However, due to cost limitations and time constraints, we will be unable to repeat them for this specific study. Based on the results we already obtained in 7 platinum salts-resistant PDXs as regard to their response heterogeneity, one might also speculate that the comparisons between numerous sensitive and resistant PDXs should be complicated as sensitive PDXs might also display distinct mutational status. According to the remark of the reviewer, we will discuss these aspects in the discussion section of the revised manuscript.

Consistency between pharmacological inhibition and genetic depletion

In Figure 4, the authors compare pladienolide treatment with SF3B1 knockdown to demonstrate target specificity. However, the effects observed with the two perturbations are not entirely consistent-for example, pladienolide affects phosphorylation of DNA-PKcs, while SF3B1 knockdown appears to produce broader effects at both protein and mRNA levels. Additionally, differences are observed between resistant cell lines in the response to SF3B1 knockdown. These discrepancies should be addressed and discussed, as they may reflect mechanistic differences between acute pharmacological inhibition and genetic depletion.

__We thank the reviewer for this remark and we agree that acute pharmacological inhibition using pladienolide B and genetic depletion using SF3B1 siRNA might produce distinct effects as they do not exhibit the same mechanism of action. Hence, pharmacological inhibitors target the protein while siRNA targets mRNA with effects depending on the basal mRNA level/stability. This could explain why we did not exactly observe the same effects on ATR/DNA-PKcs mRNA and protein levels using both approachs in H460/A549 parental and resistant cells (Fig 3-4). For pladienolide B treatment, the effects were analyzed at “early” timepoint [i.e. after 4-6 hours treatment (Fig 3a-d)] or at a “later timepoint” [i.e. after 24-48 hours treatment (Fig 3e-f)]. At early timepoint, pladienolide B induced replicative stress that correlated with DNA-PKcs phosphorylation, while at later timepoints it decreased ATR and DNA-PKcs mRNA/protein levels. The biological consequences of SF3B1 knock-down were analyzed after 72 hours of transfection in resistant cells. This could explain why SF3B1 knock-down appears to produce broader effects at both protein and mRNA levels. However, we acknowledge the existence of differences between SF3B1 knocked-down-H460 and -A549 cells as regard to the downregulation of ATR and DNA-PKcs that occurs at the mRNA and/or protein level depending on the cell line. Again, this could depend on the time as well as the efficiency of SF3B1 knock-down which was more prominent in H460 resistant cells compared to A549 cells. Nevertheless, and despite these mechanistic differences in cell lines and between pladienolide B and SF3B1 siRNA, our results identify ATR and DNA-PKcs as novel targets of SF3B1 in NSCLC cell lines, including cells with acquired resistance to cisplatin, as well as more importantly in NSCLC PDXs (Fig 9c). To our knowledge, this is the first evidence that pladienolide B or SF3B1 knock-down negatively targets ATR or DNA-PKcs in solid tumors. Owing to the crucial role played by both kinases in the maintenance of genomic stability in cancer cells, we think that this result is of importance. Nevertheless, as suggested by the reviewer, we propose to acknowledge and discuss more in details the discrepancies between cellular models and pladienolide B / SF3B1 knock-down in the revised version of the manuscript. __

Selection and interpretation of splicing-sensitive transcripts

Transcriptomic analyses in Figure 5 identify both shared and differential splicing changes between sensitive and resistant cells. However, much of the analysis focuses on transcripts that are commonly affected in both conditions, rather than those uniquely altered in resistant cells. Given that the central phenotype is resistance-specific sensitivity, transcripts uniquely mis-spliced in resistant cells may represent more informative candidates. The authors should clarify the rationale behind focusing on shared events and discuss the implications of resistance-specific versus common splicing changes.

We thank the reviewer for this remark. Indeed, after obtaining RNA-Seq data, we initially looked for genes which differential expression and/or splicing upon pladienolide B treatment could only be observed in resistant cells but not parental ones. We focused first on the 121 genes belonging to the DNA repair pathways full network (WikiPathway WP4946) since Gene-Ontology analyses based on RNA-Seq data demonstrated enrichment of genes involved in DNA metabolic process, which includes DNA repair, among genes down-regulated after pladienolide B treatment (Fig S3). The focus on DNA repair was also justified by our observation showing accumulation of DNA double strand breaks upon pladienolide B treatment in H460 resistant cells (Fig 2d-f). Doing this comparison, we showed that pladienolide B regulates the expression of 41 (33%) and 47 (39%) genes of this network in H460S and H460R cells respectively, ____which were mostly down-regulated in both H460S (33/41) and H460R (33/47) cells (Table 3). Fifteen genes involved in all DNA repair processes were found to be specifically down-regulated in H460R cells upon pladienolide B treatment, including PARP-1. As a whole, these results demonstrated that pladienolide B down-regulates the expression of numerous DNA repair genes in both NSCLC parental and resistant cells. As discussed above, we propose that the enhanced sensitivity of resistant cells to pladienolide B is related to their increased dependency for survival to functional DNA repair pathways.

When differentially spliced genes were considered, and focusing on exon skipping events, as they were the more prominent (Fig 5e), we found that pladienolide B regulates the splicing of 107 and 87 genes of the WikiPathway WP4946 in H460 parental and resistant cells, respectively (Table 5). Forty five genes were predicted to be regulated in both cell lines. Only 3 genes, namely DCLRE1C, POLD3 and PNKP, were predicted to be differentially spliced upon pladienolide B treatment in H460R cells only. Trying to increase the number of genes to study, we extended our analysis to genes belonging to another DNA repair database (Human DNA Repair Genes, Resources from Wood laboratory, UT MD Anderson), and we found six additional genes, namely MLH3, MSH5, RAD54L, EME1, SETMAR and SMC6, that were also predicted to be differentially spliced upon pladienolide B treatment in H460R cells only. However, four of these exon skipping events (i.e. PNKP-Ex9, DCLRE1C-Ex11, SETMAR-Ex2, SMC6-Ex6) were not validated and we did not observe clear difference between H460 resistant and parental cells for the others (Fig 5g and Fig S6). Skipping of MLH3-Ex8 was the sole event displaying a slight difference between both cell lines, mainly in term of kinetic of recovery. This is why we decided to further analyze this specific splicing event. Noteworthy, we focused only on genes involved in DNA damage and repair signaling pathways. Therefore, we cannot exclude that genes involved in other biological processes might be differentially transcribed or spliced in response to pladienolide B in H460 parental and resistant cells.

Transient nature of splicing effects

The authors report transient alternative splicing effects upon prolonged pladienolide treatment. This observation is counterintuitive, as continued spliceosome inhibition might be expected to produce cumulative splicing defects. While the authors reference studies showing that transient inhibition can produce lasting effects, the current observations involve continuous exposure. This apparent discrepancy should be clarified and discussed.

We thank the reviewer for this remark. We agree with him/her that the transient effect of pladienolide B on most of the splicing events we studied was unexpected as pladienolide B treatment was prolonged. We do not have a clear explanation for that. One possibility is that pladienolide B is not stable in the cell culture supernatant and is degraded rapidly. Another, not exclusive, possibility relies on the structure of studied transcripts. As discussed in the discussion section, it is possible that the nature of the transcripts involved in DNA damage response/DNA repair which have a long length, a large number of small exons per transcript, and an elevated number of introns could explain why they recover very rapidly from pladienolide B inhibition. Alternatively, upon SF3B1 inhibition, compensatory regulations by other splicing factors might occur. We will discuss these aspects in the revised version of the manuscript.

Use of unrelated cell lines in reporter assays

The DNA damage reporter assays (Figure 6A-D) appear to be performed in cell lines not directly linked to platinum sensitivity or resistance. Given the central importance of resistance-specific responses, repeating key reporter assays in both sensitive and resistant paired models would strengthen the conclusions.

__We initially engineered these cellular models to assess the role of SRSF2, a splicing factor, in DNA repair ____(Khalife M. et al., NAR Cancer, 2025). In these models derived of either H1299 or A549 NSCLC cell lines, DNA double strand breaks (DSBs) are produced after cleavage by the SceI enzyme and the efficiency of repair is assessed based on the expression of either GFP (for homologous recombination) or CD4 (for c-NHEJ). These cellular models were difficult to engineer and to work with as they require a first stable transfection with either PBL174 pDR-GFP (for HR analysis) or PBL230 (for c-NHEJ) plasmid followed by a second transient transfection with the PLBL133 plasmid that encodes SceI enzyme. As an example, we tried to generate stable A549 cells with PBL174 plasmid but we never succeeded. The reverse was true for H1299 cells and transfection with PBL230. In addition, during the time course of this project, we also tried to transiently transfect plasmid encoding MLH3 or MLH3 protein devoid of exon 8-encoding amino acids in H460 or A549 resistant cells but we never obtained good efficiency of transfection, although we tested several transfection reagents. So, it looks like that resistant cells are hardly transfectable. This is why repeating these experiments in resistant models will not be possible. However, and although we agree with the reviewer that the cell lines we used were not directly linked to platinum sensitivity or resistance, the idea behind these experiments was to test whether pladienolide B could have a general impact on DNA repair by homologous recombination or c-NHEJ using these SceI-induced DSBs systems that are already widely used in the DNA repair field. As shown in Fig 6b and 6d, pladienolide B prevented DNA repair in these cellular models, confirming that it widely negatively impacts DNA repair pathways. __

Interpretation of MLH3 splicing results

In Figure 7, differences between pharmacological inhibition and SF3B1 knockdown in MLH3 exon 8 regulation are not entirely consistent.

We do not strictly agree with this comment. __As also discussed above, the differences seen between pharmacological inhibition of SF3B1 using pladienolide B and SF3B1 knock-down in term of MLH3-exon 8 regulation could be related to differences in term of mechanism of action and/or the fact that the effects of SF3B1 knockdown were analyzed after 72 hours treatment (as we obtained the best knock-down efficiency at this time point) while those of pladienolide B were studied between 6 to 48 hours treatment. However, as illustrated in Fig 7a and 7c (right panel), we showed that both pladienolide B and SF3B1 knock-down promote MLH3-exon 8 exclusion in H460 and A549 resistant cells. The effects of SF3B1 knock-down were less pronounced in A549R cells which could be consistent with the decreased efficiency of SF3B1 knockdown as depicted in Fig 7c (left panel). Pladienolide B also promoted MLH3-Ex8 exclusion in H460 and A549 parental cells but the recovery was faster in parental cells as compared to resistant cells (Fig 7a). __

Furthermore, inclusion levels of regulated and non-regulated exons appear similarly correlated with SF3B1 expression, potentially weakening the argument for exon-specific regulation. These observations should be clarified.

__As regard to MLH3-exon 5 exclusion, we observed its exclusion in A549 parental and resistant cells upon pladienolide B treatment, while this was not observed in H460 parental and resistant cells (Fig 7a-b). In SF3B1 knocked-down H460R and A549R cells, the exclusion of MLH3-exon 5 was seen in A549R cells. When analyzing MLH3 exon 8 or exon 5 usage in lung adenocarcinoma patients (Fig 7e), we agree with the reviewer that there was a significant correlation between SF3B1 mRNA level and MLH3 exons 5 and 8 usage. Therefore, these and our data indicate that both MLH3 exons 5 and 8 could be regulated by SF3B1 in NSCLC although differences might occur depending on the cell line. To make this point clearer, we will clarify the text of the results for Figure 7 and our conclusion. __

Combination treatment logic

In Figure 8, co-treatment experiments with pladienolide B and cisplatin are performed primarily in resistant cells. Performing similar experiments in platinum-sensitive cells would provide an important reference point to distinguish additive versus resistance-specific effects.

__We thank the reviewer for this important remark. The objective of figure 8 was to investigate whether pladienolide B that induces a shutdown of numerous DNA damage response-related genes could resensitize NSCLC cells with acquired resistance to cisplatin-induced apoptosis. The results presented in Figures 8a and 8b show that this is indeed the case. However, and according to the remark of the reviewer, we propose to illustrate in the revised version of the manuscript the results of the co-treatment experiments in sensitive parental cells also. Indeed, we already had the results for H460 parental cells. They did not show any additive or synergistic effects of the combination in these cells. Rather adding pladienolide B to cisplatin tended to decrease apoptosis as compared to cisplatin alone. We will reiterate these experiments in A549 cells. If confirmed, and to a translational point of view, these results would support the idea that treating NSCLC patients who relapse from chemotherapy with a combination of platinum salts and pladienolide B could provide therapeutic benefits, whereas NSCLC patients that primary respond to platinum salts could less benefit from this combination. __

Minor comments

• In Figure 1, pladienolide treatment in platinum-sensitive cells appears to plateau at approximately 50% cell killing. Extending the concentration range may help clarify whether maximal efficacy was reached.

__ We agree with this remark. We will reiterate our MTS experiments increasing the dose of pladienolide B. __

In Figure 1H, the difference between 2.5 mg/kg and 5 mg/kg pladienolide in PDX models appears disproportionately large relative to the dose change. This should be discussed or experimentally clarified.

We agree with the reviewer but these are the results we obtained. In Figure 1h, we illustrated the probability of progression based on Relative Tumor Volume (RTV) = 2. The difference between the two doses was less, although remaining significant, when considering RTV = 4 as a marker of progression (Fig S2d).

In Figure 5, differential expression and splicing analyses are presented using multiple cutoffs (e.g., log₂FC > 0.4 and >1; ΔPSI thresholds). This introduces redundancy and may obscure key findings. A single well-justified cutoff would improve clarity.

We agree with the reviewer that in initial Figure 5 we provided graphs illustrating different analysis thresholds based on our transcriptomic analyses. We will select one cut-off for Differentially Expressed Genes [absolute Log2Fold Change ≥ 0.4 and p ≤ 0.05 (Fig 5a)] and Differentially Spliced Genes [absolute percent splice in (PSI) ≥ 0.2 and p ≤ 0.05 (Fig 5e)]. We will remove Fig 5b and 5d for more clarity.

Several isoform-specific RT-PCR gels are difficult to interpret due to low image clarity. Improving gel presentation or focusing on key timepoints would strengthen data readability.

We will improve gel presentation.

Some figure panels appear redundant, showing similar datasets under different analysis thresholds.

We agree with the reviewer that in Figure 5 we provided graphs illustrating different analysis thresholds based on our transcriptomic analyses. We will select one cut-off for Differentially Expressed Genes [absolute Log2Fold Change ≥ 0.4 and p ≤ 0.05] and for Differentially Spliced Genes [absolute percent splice in (PSI) ≥ 0.2 and p ≤ 0.05]. We will remove Fig 5b and 5d for more clarity.

A graphical summary model illustrating the proposed mechanism would improve reader comprehension.

We agree with the reviewer. We will provide such a graphical abstract in the revised version of our manuscript.

In Figure 3D, representative images of γH2AX foci appear visually similar across conditions, whereas quantification shows large differences. The authors should ensure that representative images accurately reflect quantified trends and clarify selection criteria for displayed images.

We agree with the reviewer. We will select additional images illustrating more the differences we highlighted after quantification of more than 500 nuclei (Figure 3D, right panel).

Reviewer #1 (Significance (Required)):

This study represents a comprehensive investigation of spliceosome inhibition as a therapeutic strategy to overcome platinum resistance in NSCLC. The use of resistant cell lines, PDX models, and functional reporters provides strong experimental depth. The most compelling aspects of the study include the demonstration that spliceosome inhibition enhances DNA damage accumulation and sensitizes resistant tumors to platinum-based therapies. However, several mechanistic interpretations require clarification, and data presentation could be streamlined to improve logical coherence.

We thank the reviewer for his/her constructive remarks. We hope that our answers and the additional works we now propose to carry-out in order to revise the manuscript will get agreement to him/her and will strengthen our main claims

Advance

The work provides evidence that targeting spliceosome function-specifically via SF3B1 inhibition-can sensitize platinum-resistant tumors to DNA-damaging agents. To my knowledge, this represents one of the first comprehensive demonstrations that spliceosome-targeting compounds can effectively overcome acquired platinum resistance in solid tumor models. The study also contributes to the emerging understanding that DNA damage response transcripts may represent particularly sensitive targets of splicing perturbation.

Audience

The study will be of interest to researchers in RNA biology, cancer therapeutics, DNA damage response, and translational oncology. It is particularly relevant to scientists investigating therapeutic vulnerabilities in drug-resistant cancers and those exploring RNA processing as a therapeutic target.

Expertise I have expertise in RNA biology, alternative splicing and cancer models. My expertise is more limited in pharmacological dosing strategies and some aspects of in vivo xenograft modeling.

Keywords: RNA biology, alternative splicing, spliceosome function, cancer biology, DNA damage response, transcriptomics

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

Summary

In the manuscript by Jamal-El-Hussein et al., the authors demonstrated that pladienolide B, an inhibitor of splicing factor 3B subunit 1 (SF3B1), inhibits cell viability in NSCLC cells and PDXs with resistance to platinum-based chemotherapy. Mechanistically, they identified that pladienolide B regulates splicing events of genes associated with DNA damage signaling and repair, specifically through exon skipping of MLH3, thus increasing vulnerability to chemotherapy. This study provides therapeutic insights into combining pladienolide B with chemotherapy for overcoming therapy resistance.

__Major comments __

The authors showed that both H460R and A549R cell lines are sensitive to pladienolide B; however, they exhibit distinct molecular responses. For example, SF3B1 knockdown downregulates the mRNA expression of ATR and PRKDC in H460R cells, while the expression of these genes remains unchanged in A549R cells (Fig. 4b). Furthermore, exon 8 skipping of MLH3 is not observed in A549R cells with pladienolide B treatment (Fig. 7a). These discrepancies suggest that the two cell lines respond to pladienolide B through different mechanisms. The authors should also perform a bulk RNA-seq on A549 cell line to better understand the different behavior of the two cell lines.

We disagree with the remark regarding Fig 7a as this figure demonstrated MLH3 exon 8 skipping in A549R cells also after 6 and 24 hours pladienolide B treatment. __Although we agree with the reviewer that some differences exist in term of molecular mechanisms regulated by pladienolide B or SF3B1 knock-down in H460R and A549R cell lines, we identified in this study ATR, DNA-PKcs and MLH3 as novel targets of SF3B1 in both cell lines as well as more importantly in NSCLC PDXs. To our knowledge, this is the first evidence that SF3B1 inhibition negatively impacts ATR or DNA-PKcs and regulates MLH3 alternative splicing in solid tumors. In addition, we found a significant correlation between SF3B1 and DNA-PKCs or ATR protein levels in 77 NSCLC cell lines (Fig 4c) which supports a close relationship between these proteins in lung cancer. As also discussed in the response to reviewer 1, the differences between pladienolide B and SF3B1 knock-down could be related to the distinct timepoints at which we analyzed their effects as well as to the different mechanisms of action between pharmacological and siRNA inhibition. Nevertheless, we propose to acknowledge and discuss more in details the discrepancies between cellular models and pladienolide B or SF3B1 knock-down in the revised version of the manuscript. __

The authors' central claim is that platinum-based chemotherapy-resistant cells are more sensitive to pladienolide B treatment.

__We thank the reviewer for this remark. In this study, we did not want to claim that platinum-salts resistant cells exhibit unique vulnerability to pladienolide B as we fully agree with the reviewer that pladienolide B also exhibits cytotoxic effects in parental sensitive cells, although with a delayed kinetic. We acknowledge that the way we introduced our results section in the former manuscript could have contributed to such a misunderstanding. Rather, we propose a model in which pladienolide B induces cell death in NSCLC cells by massively impairing the expression of key components of the DNA damage and repair signaling pathways, at the transcriptional and/or splicing level. As NSCLC cells with acquired resistance to platinum salts are likely more “addict” to these pathways for their survival than parental cells, this might explain enhanced susceptibility of these resistant cells to pladienolide B-induced cell death. We think that these results highlight spliceosome targeting compounds as an alternative therapeutic strategy in NSCLC patients who escape chemotherapy. According to the remark of the reviewer, we will modify the way we introduce our results and we will clarify all these points in the discussion section of the revised manuscript. __

In their bulk RNA-seq analysis, the authors selected genes commonly regulated by pladienolide B in both parental and resistant cells for further validation. This approach raises a critical concern: the observed sensitivity to pladienolide B may already be present in parental cells rather than representing a mechanism uniquely acquired by the resistant cells. To substantiate their central claim, the authors should analyze the differentially expressed genes between parental and resistant cells to identify resistance-specific molecular alterations that may confer enhanced sensitivity to pladienolide B, thereby providing a more mechanistically rigorous basis for their conclusions.

We thank the reviewer for this remark and we agree with him/her. Indeed, after obtaining RNA-Seq data, we initially looked for genes which differential expression and/or splicing upon pladienolide B treatment could be only observed in resistant cells but not parental ones. We initially focused on the 121 genes belonging to the DNA repair pathways full network (WikiPathway WP4946) since Gene-Ontology analyses demonstrated enrichment of genes involved in DNA metabolic process, which includes DNA repair, among genes down-regulated after pladienolide B treatment (Fig S3). The focus on DNA repair was also justified by our observation showing accumulation of DNA double strand breaks upon pladienolide B treatment in H460 resistant cells (Fig 2d-f). Doing this comparison, we showed that pladienolide B regulates the expression of 41 (33%) and 47 (39%) genes of this network in H460S and H460R cells respectively, ____which were mostly down-regulated in both H460S (33/41) and H460R (33/47) cells (Table 3). Fifteen genes involved in all DNA repair processes were found to be specifically down-regulated in H460R cells upon pladienolide B treatment, including PARP-1. As a whole, these results demonstrated that pladienolide B down-regulates the expression of numerous DNA repair genes in both NSCLC parental and resistant cells. However, and as discussed above, we propose that the enhanced sensitivity of resistant cells to pladienolide B is related to their increased dependency for their survival to functional DNA repair pathways.

__When differentially spliced genes were considered, and focusing on exon skipping events, as they were the more prominent (Fig 5e), we found that pladienolide B regulates the splicing of 107 and 87 genes of the WikiPathway WP4946 in H460 parental and resistant cells, respectively (Table 5). Forty five genes were predicted to be regulated in both cell lines. Only 3 genes, namely DCLRE1C, POLD3 and PNKP, were predicted to be differentially spliced upon pladienolide B treatment in H460R cells only. Trying to increase the number of genes to study, we extended our analysis to genes belonging to another DNA repair database (Human DNA Repair Genes, Resources from Wood laboratory, UT MD Anderson), and we found six additional genes, namely MLH3, MSH5, RAD54L, EME1, SETMAR and SMC6, that were also predicted to be differentially spliced in H460R cells only. However, four of these exon skipping events (i.e. PNKP-Ex9, DCLRE1C-Ex11, SETMAR-Ex2, SMC6-Ex6) were not validated and we did not observe clear difference between H460 resistant and parental cells for the others (Fig 5g and Fig S6). Skipping of MLH3-Ex8 was the sole event displaying a slight difference between both cell lines, mainly in term of kinetic of recovery. This is why we decided to further analyze this specific splicing event. Noteworthy, we focused only on genes involved in DNA damage and repair signaling pathways. Therefore, we cannot exclude that genes involved in other biological processes might be differentially transcribed or spliced in response to pladienolide B in H460 parental and resistant cells. __

The authors conclude that pladienolide B treatment correlates with activation of DNA-PKcs signaling followed by a shutdown of ATR and DNA-PKcs pathways. However, the data presented do not fully support this interpretation. P-ATR levels are already elevated in resistant cells and remain unchanged following pladienolide B treatment (Fig. 3a). However, prolonged pladienolide B treatment leads to decreased total ATR protein and mRNA expression (Fig. 3e-f), suggesting that pladienolide B maintains an initial constitutive ATR activation followed by transcriptional downregulation. Since pladienolide B is a splicing inhibitor, the authors should determine whether ATR and DNA-PKcs mRNA downregulation is a direct consequence of aberrant splicing of their transcripts, or a non-specific effect of prolonged cellular toxicity. To strengthen their mechanistic conclusions, the authors should perform time-course experiments to establish the temporal relationship between these signaling events, analyze splicing changes specifically in ATR and DNA-PKcs transcripts (are they in the differential genes from the bulk RNA-seq analysis?), and also check the downstream targets of the ATR and DNA-PKcs signaling.

__We thank the reviewer for his/her comment. In our RNA-Seq analyses, we did not recover PRKDC among the differential genes expressed or spliced upon pladienolide B treatment whatever the cell line. However, PRKDC was also not in the full RNA-Seq data list of not significant genes. Therefore, it remains unclear whether PRKDC splicing could account for the decrease of PRKDC mRNA level upon pladienolide B treatment. Concerning ATR, it was not in the RNA-Seq data list of the genes significantly up- or down-regulated upon pladienolide B treatment in either H460 parental or resistant cells. However, transcriptomic analyses were performed after 8 hours pladienolide B treatment while the decrease of ATR mRNA was observed after 24 hours (Fig 3f). Regarding splicing, ATR was predicted to be spliced, skipping of exon 30, upon pladienolide B treatment in both H460 parental and resistant cells. We validated this splicing event after 8 hours treatment with pladienolide B in both H460 cellular models but we did not analyze this splicing event at later timepoints, nor in the A549 parental or resistant cells. Therefore, and according to the remarks of the reviewer, we propose to deepen the temporal relationships between all these signaling events by performing time-course experiments for analysis of ATR exon 30 splicing by RT-PCR, ATR and PRKDC mRNA levels by RT-qPCR, and expression of downstream targets of ATR and DNA-PKcs, such as P-CHK1(Ser345) or P-RPA32(Ser4/8) by immunoblotting. __

The authors report that skipping of exon 8 of MLH3 leads to the complete absence of the protein (Fig. 7d). However, this observation needs further clarification, as at least two alternative explanations exist. First, the antibody used to detect MLH3 may specifically recognize an epitope encoded by exon 8 or downstream exons, in which case the loss of signal would reflect antibody incompatibility rather than true protein absence.

__We thank the reviewer for this remark. The anti-MLH3 antibody recognizes the C-terminal part of the MLH3 full-length protein (between amino acids 1228-1453). MLH3 exon 8 is 72 base pair and does not encode for the amino acids recognized by the anti-MLH3 antibody. In ENSEMBL, the MLH3-201 transcript encodes for the full-length protein (1453 amino acids) and the MLH3-202 transcript encodes for a MLH3 protein (1429 amino acids) devoid of the amino acids encoded by exon 8. Nevertheless, the two products have the same C-terminus recognized by the anti-MLH3 antibody used in this study. So, the loss of the signal depicted in Figure 7d is not due to antibody incompatibility. __

Second, skipping of exon 8 may introduce a premature stop codon, triggering nonsense-mediated mRNA decay (NMD) and consequent loss of the transcript. To distinguish between these possibilities, the authors should perform qPCR using primers targeting sequences both upstream and downstream of the skipped exon, as well as consider NMD inhibition experiments, to clarify whether the observed protein loss occurs at the transcriptional or translational level.

__As shown in Figure 8f, we demonstrated by RT-qPCR that pladienolide B alone or the combination of pladienolide B with cisplatin does not negatively impact MLH3 mRNA level in both H460R and A549R cells. These results were confirmed in a time-course experiment of pladienolide B treatment performed in H460 and A549 parental and resistant cells, as well as in NSCLC PDXs. Similar results were obtained in H460R or A549R cells deprived of SF3B1. These new data will be added in the revised version of the manuscript. The couple of primers we used for MLH3 amplification was located downstream of exon 8, respectively on constitutive MLH3-exon 9 (forward primer) and MLH3-exon 10 (reverse primer). These results indicate that pladienolide B regulates MLH3 splicing but not MLH3 total mRNA level. Considering NMD, in the FASTER DB database, none of the MLH3 transcripts devoid of exon 8 are predicted to be degraded by NMD. So we do not think that pladienolide B-induced MLH3 exon 8 skipping promotes the synthesis of transcripts recognized by the NMD machinery. As discussed above, the anti-MLH3 antibody does not allow to distinguish between the full length MLH3 protein and the MLH3 product encoded by transcript devoid of exon 8. In addition, only 24 amino acids (around 2-3KDa) differentiate both products which could render difficult their specific detection in SDS-PAGE. So, we speculate that the decrease of MLH3 signal detected by immunoblotting in pladienolide B-treated and SF3B1 knocked-down cells is mostly related to the decrease of MLH3 full-length protein due to the decreased level of MLH3 transcript retaining exon 8 and encoding MLH3 full-length protein. Alternatively, and not exclusively, MLH3 product devoid of exon 8 might also be less stable. __

The difference shown in Fig. 6b after pladienolide B treatment decreases from 2.2% to 1%. This raises concern about whether the observed difference reflects a true biological effect or is confounded by technical limitations such as low transfection efficiency. The authors should consider optimizing their transfection conditions to achieve a more robust and convincing result.

We agree with the reviewer’s comment. However, using this SceI-inducible system to analyze DNA double strand breaks repair by homologous recombination, it is very frequent to have only a very low percentage of cells able to perform homologous recombination thereby expressing the GFP protein ____(as examples: Yoshino Y et al., Sci Reports, 2019; Brustel et al., Sci Rep., 2018; Croglio et al., Oncotarget, 2016; Mamouni et al., Mol Cell Biol., 2014). This is why the difference is low between each condition but it is significant. Indeed, these engineered cellular models are not easy to manipulate as we first need to obtain stable clones having incorporated the PBL174 pDR-GFP-plasmid and then to transiently transfect them using a second plasmid encoding the SceI enzyme which creates DNA Double Strand Breaks. The efficiency of the second round of transfection might therefore be decreased as the cells already experienced a first round of transfection.

__Minor comments __

The abbreviation "S" in H460S and A549S cells is not defined in the manuscript. As this designation is used throughout the text, the authors should clarify what "S" denotes upon its first appearance.

__We thank the reviewer for this remark. We will correct the text. __

The current presentation of Figure S1a does not clearly demonstrate that different NSCLC cell lines exhibit differential sensitivity to pladienolide B. The authors should calculate and report IC50 values for each cell line to enable a more rigorous and quantitative comparison of their respective dose-response relationships.

We thank the reviewer for this remark and agree with it. We will calculate and report in the revised version of Fig S1a the IC50 for pladienolide B for each cell line.

In Figure 4c, two dashed black lines are present in the plot but are not described or explained in the figure legend or the main text.

We thank the reviewer for this remark. The two dashed black lines represent the upper and lower boundaries of the 95% confidence interval for the fitted linear regression line. We have now clarified their meaning in the revised figure legend and indicated section of the main text also.

In Figure 5a, the authors combine the downregulated and upregulated genes in a single Venn diagram. This approach may obscure biologically meaningful differences, as overlapping genes between conditions could reflect opposing directions of regulation. The authors should separate upregulated and downregulated genes into distinct Venn diagrams to provide a more accurate and interpretable comparison.

We thank the reviewer for this remark and agree with it. Hence, in Fig 5a-b and Fig S3, we already highlighted the number of genes down-regulated or up-regulated upon pladienolide B treatment in either H460 parental and resistant cells using bar graphs. We will provide new Venn diagrams separating up-regulated and down-regulated genes for both cell lines.

In the figure legend of Fig. 6a, the panel is incorrectly described as a "quantification." As the panel depicts a schematic representation of the experimental construct rather than numerical data, the term "illustration" or "schematic" would be more accurate and should be used instead.

We thank the reviewer for this remark and we agree with it. We will modify the legend of Figure 6a accordingly.

Reviewer #2 (Significance (Required)):

This manuscript provides evidence that pladienolide B can overcome chemotherapy resistance in NSCLC by modulating splicing events of genes associated with DNA damage signaling and repair. Although the underlying mechanism requires further elucidation, this study offers valuable mechanistic insights into how aberrant splicing regulates therapy resistance, with potential implications for the development of novel therapeutic strategies targeting splicing factors in chemotherapy-resistant cancers.

My research field is in tumor heterogeneity and tumor microenvironment.

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Referee #2

Evidence, reproducibility and clarity

Summary

In the manuscript by Jamal-El-Hussein et al., the authors demonstrated that pladienolide B, an inhibitor of splicing factor 3B subunit 1 (SF3B1), inhibits cell viability in NSCLC cells and PDXs with resistance to platinum-based chemotherapy. Mechanistically, they identified that pladienolide B regulates splicing events of genes associated with DNA damage signaling and repair, specifically through exon skipping of MLH3, thus increasing vulnerability to chemotherapy. This study provides therapeutic insights into combining pladienolide B with chemotherapy for overcoming therapy resistance.

Major comments

1. The authors showed that both H460R and A549R cell lines are sensitive to pladienolide B; however, they exhibit distinct molecular responses. For example, SF3B1 knockdown downregulates the mRNA expression of ATR and PRKDC in H460R cells, while the expression of these genes remains unchanged in A549R cells (Fig. 4b). Furthermore, exon 8 skipping of MLH3 is not observed in A549R cells with pladienolide B treatment (Fig. 7a). These discrepancies suggest that the two cell lines respond to pladienolide B through different mechanisms. The authors should also perform a bulk RNA-seq on A549 cell line to better understand the different behavior of the two cell lines.
2. The authors' central claim is that platinum-based chemotherapy-resistant cells are more sensitive to pladienolide B treatment. However, in their bulk RNA-seq analysis, the authors selected genes commonly regulated by pladienolide B in both parental and resistant cells for further validation. This approach raises a critical concern: the observed sensitivity to pladienolide B may already be present in parental cells rather than representing a mechanism uniquely acquired by the resistant cells. To substantiate their central claim, the authors should analyze the differentially expressed genes between parental and resistant cells to identify resistance-specific molecular alterations that may confer enhanced sensitivity to pladienolide B, thereby providing a more mechanistically rigorous basis for their conclusions.
3. The authors conclude that pladienolide B treatment correlates with activation of DNA-PKcs signaling followed by a shutdown of ATR and DNA-PKcs pathways. However, the data presented do not fully support this interpretation. P-ATR levels are already elevated in resistant cells and remain unchanged following pladienolide B treatment (Fig. 3a). However, prolonged pladienolide B treatment leads to decreased total ATR protein and mRNA expression (Fig. 3e-f), suggesting that pladienolide B maintains an initial constitutive ATR activation followed by transcriptional downregulation. Since pladienolide B is a splicing inhibitor, the authors should determine whether ATR and DNA-PKcs mRNA downregulation is a direct consequence of aberrant splicing of their transcripts, or a non-specific effect of prolonged cellular toxicity. To strengthen their mechanistic conclusions, the authors should perform time-course experiments to establish the temporal relationship between these signaling events, analyze splicing changes specifically in ATR and DNA-PKcs transcripts (are they in the differential genes from the bulk RNA-seq analysis?), and also check the downstream targets of the ATR and DNA-PKcs signaling.
4. The authors report that skipping of exon 8 of MLH3 leads to the complete absence of the protein (Fig. 7d). However, this observation needs further clarification, as at least two alternative explanations exist. First, the antibody used to detect MLH3 may specifically recognize an epitope encoded by exon 8 or downstream exons, in which case the loss of signal would reflect antibody incompatibility rather than true protein absence. Second, skipping of exon 8 may introduce a premature stop codon, triggering nonsense-mediated mRNA decay (NMD) and consequent loss of the transcript. To distinguish between these possibilities, the authors should perform qPCR using primers targeting sequences both upstream and downstream of the skipped exon, as well as consider NMD inhibition experiments, to clarify whether the observed protein loss occurs at the transcriptional or translational level.
5. The difference shown in Fig. 6b after pladienolide B treatment decreases from 2.2% to 1%. This raises concern about whether the observed difference reflects a true biological effect or is confounded by technical limitations such as low transfection efficiency. The authors should consider optimizing their transfection conditions to achieve a more robust and convincing result.

Minor comments

1. The abbreviation "S" in H460S and A549S cells is not defined in the manuscript. As this designation is used throughout the text, the authors should clarify what "S" denotes upon its first appearance.
2. The current presentation of Figure S1a does not clearly demonstrate that different NSCLC cell lines exhibit differential sensitivity to pladienolide B. The authors should calculate and report IC50 values for each cell line to enable a more rigorous and quantitative comparison of their respective dose-response relationships.
3. In Figure 4c, two dashed black lines are present in the plot but are not described or explained in the figure legend or the main text.
4. In Figure 5a, the authors combine the downregulated and upregulated genes in a single Venn diagram. This approach may obscure biologically meaningful differences, as overlapping genes between conditions could reflect opposing directions of regulation. The authors should separate upregulated and downregulated genes into distinct Venn diagrams to provide a more accurate and interpretable comparison.
5. In the figure legend of Fig. 6a, the panel is incorrectly described as a "quantification." As the panel depicts a schematic representation of the experimental construct rather than numerical data, the term "illustration" or "schematic" would be more accurate and should be used instead.

Significance

This manuscript provides evidence that pladienolide B can overcome chemotherapy resistance in NSCLC by modulating splicing events of genes associated with DNA damage signaling and repair. Although the underlying mechanism requires further elucidation, this study offers valuable mechanistic insights into how aberrant splicing regulates therapy resistance, with potential implications for the development of novel therapeutic strategies targeting splicing factors in chemotherapy-resistant cancers.

My research field is in tumor heterogeneity and tumor microenvironment.

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Referee #1

Evidence, reproducibility and clarity

In this study, the authors investigate the effects of pharmacological inhibition of the spliceosome using the SF3B1 inhibitor pladienolide B in models of platinum-resistant non-small cell lung cancer (NSCLC). Using a combination of cell lines, platinum-resistant derivatives, and patient-derived xenograft (PDX) models, the authors show that spliceosome inhibition sensitizes platinum-resistant tumors to treatment and leads to increased DNA damage accumulation and impaired DNA damage response signaling. Transcriptomic analyses indicate that transcripts encoding DNA damage regulators are particularly sensitive to alternative splicing perturbations, and selected mechanistic experiments suggest involvement of specific regulators such as MLH3. The study further explores links between splicing inhibition, transcriptional activity, and cell cycle progression.

Overall, the manuscript presents extensive datasets across multiple experimental systems and provides strong evidence that spliceosome inhibition can sensitize platinum-resistant tumors to DNA damage. However, several aspects of the mechanistic interpretation, data consistency, and presentation require clarification or strengthening to fully support the central claims.

Major comments

Conceptual clarity and synthesis of mechanistic model

The manuscript presents multiple mechanistic observations-including altered splicing of DNA repair genes, increased DNA damage accumulation, transcriptional perturbation, and cell cycle changes-but these are not integrated into a coherent conceptual framework. While it is reasonable that not all mechanistic details are fully resolved, the current presentation leaves the reader uncertain about the relative contributions of these processes. A clearer synthesis of the proposed mechanism, possibly including a summary model figure, would substantially improve the conceptual clarity of the study.

Biological specificity of platinum-resistant cell sensitivity

A central premise of the study is that platinum-resistant cells exhibit enhanced sensitivity to spliceosome inhibition. However, in several experiments (e.g., cell cycle analysis in Figure 2A), similar responses to pladienolide B appear to occur in both platinum-sensitive and resistant cells. This observation complicates the interpretation that resistant cells exhibit uniquely distinct vulnerability. The authors should clarify how these findings align with the proposed model and more explicitly distinguish shared versus resistance-specific responses.

Heterogeneity in PDX responses and lack of platinum-sensitive controls

The PDX experiments represent a major strength of the study. However, resistant tumors display heterogeneous responses to pladienolide treatment, suggesting the presence of additional determinants of sensitivity. Including platinum-sensitive PDX tumors, if available, would provide valuable baseline comparison and strengthen interpretation of resistance-specific effects. If not feasible, the limitations should be acknowledged and discussed.

(OPTIONAL - would strengthen study but may require substantial additional work.)

Consistency between pharmacological inhibition and genetic depletion

In Figure 4, the authors compare pladienolide treatment with SF3B1 knockdown to demonstrate target specificity. However, the effects observed with the two perturbations are not entirely consistent-for example, pladienolide affects phosphorylation of DNA-PKcs, while SF3B1 knockdown appears to produce broader effects at both protein and mRNA levels. Additionally, differences are observed between resistant cell lines in the response to SF3B1 knockdown. These discrepancies should be addressed and discussed, as they may reflect mechanistic differences between acute pharmacological inhibition and genetic depletion.

Selection and interpretation of splicing-sensitive transcripts

Transcriptomic analyses in Figure 5 identify both shared and differential splicing changes between sensitive and resistant cells. However, much of the analysis focuses on transcripts that are commonly affected in both conditions, rather than those uniquely altered in resistant cells. Given that the central phenotype is resistance-specific sensitivity, transcripts uniquely mis-spliced in resistant cells may represent more informative candidates. The authors should clarify the rationale behind focusing on shared events and discuss the implications of resistance-specific versus common splicing changes.

Transient nature of splicing effects

The authors report transient alternative splicing effects upon prolonged pladienolide treatment. This observation is counterintuitive, as continued spliceosome inhibition might be expected to produce cumulative splicing defects. While the authors reference studies showing that transient inhibition can produce lasting effects, the current observations involve continuous exposure. This apparent discrepancy should be clarified and discussed.

Use of unrelated cell lines in reporter assays

The DNA damage reporter assays (Figure 6A-D) appear to be performed in cell lines not directly linked to platinum sensitivity or resistance. Given the central importance of resistance-specific responses, repeating key reporter assays in both sensitive and resistant paired models would strengthen the conclusions.

(OPTIONAL - likely moderate experimental effort.)

Interpretation of MLH3 splicing results

In Figure 7, differences between pharmacological inhibition and SF3B1 knockdown in MLH3 exon 8 regulation are not entirely consistent. Furthermore, inclusion levels of regulated and non-regulated exons appear similarly correlated with SF3B1 expression, potentially weakening the argument for exon-specific regulation. These observations should be clarified.

Combination treatment logic

In Figure 8, co-treatment experiments with pladienolide B and cisplatin are performed primarily in resistant cells. Performing similar experiments in platinum-sensitive cells would provide an important reference point to distinguish additive versus resistance-specific effects.

(OPTIONAL - moderate experimental effort.)

Minor comments

• In Figure 1, pladienolide treatment in platinum-sensitive cells appears to plateau at approximately 50% cell killing. Extending the concentration range may help clarify whether maximal efficacy was reached.
• In Figure 1H, the difference between 2.5 mg/kg and 5 mg/kg pladienolide in PDX models appears disproportionately large relative to the dose change. This should be discussed or experimentally clarified.
• In Figure 5, differential expression and splicing analyses are presented using multiple cutoffs (e.g., log₂FC > 0.4 and >1; ΔPSI thresholds). This introduces redundancy and may obscure key findings. A single well-justified cutoff would improve clarity.
• Several isoform-specific RT-PCR gels are difficult to interpret due to low image clarity. Improving gel presentation or focusing on key timepoints would strengthen data readability.
• Some figure panels appear redundant, showing similar datasets under different analysis thresholds.
• A graphical summary model illustrating the proposed mechanism would improve reader comprehension.
• In Figure 3D, representative images of γH2AX foci appear visually similar across conditions, whereas quantification shows large differences. The authors should ensure that representative images accurately reflect quantified trends and clarify selection criteria for displayed images.

Significance

This study represents a comprehensive investigation of spliceosome inhibition as a therapeutic strategy to overcome platinum resistance in NSCLC. The use of resistant cell lines, PDX models, and functional reporters provides strong experimental depth. The most compelling aspects of the study include the demonstration that spliceosome inhibition enhances DNA damage accumulation and sensitizes resistant tumors to platinum-based therapies. However, several mechanistic interpretations require clarification, and data presentation could be streamlined to improve logical coherence.

Advance

The work provides evidence that targeting spliceosome function-specifically via SF3B1 inhibition-can sensitize platinum-resistant tumors to DNA-damaging agents. To my knowledge, this represents one of the first comprehensive demonstrations that spliceosome-targeting compounds can effectively overcome acquired platinum resistance in solid tumor models. The study also contributes to the emerging understanding that DNA damage response transcripts may represent particularly sensitive targets of splicing perturbation.

Audience

The study will be of interest to researchers in RNA biology, cancer therapeutics, DNA damage response, and translational oncology. It is particularly relevant to scientists investigating therapeutic vulnerabilities in drug-resistant cancers and those exploring RNA processing as a therapeutic target.

Expertise

I have expertise in RNA biology, alternative splicing and cancer models. My expertise is more limited in pharmacological dosing strategies and some aspects of in vivo xenograft modeling.

Keywords:

RNA biology, alternative splicing, spliceosome function, cancer biology, DNA damage response, transcriptomics

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Reply to the reviewers

Reviewer #1:

Major comments:

1. Lines 103-116 (first paragraph of the results section) describe mainly published data that is more suitable for the introduction section. It is annoying to refer to different published articles in the Results section to strengthen the results instead of showing them. The same goes for paragraphs two and three. Why mention those data in the Results section if they are already published and known?

We have reorganized this material by moving some background information to the Introduction. Our intention was not to incorporate published data to strengthen our results, but rather to provide essential context for interpreting our findings. We have therefore left some of this foundational information in the results section to create a clear narrative flow, enabling readers to understand the basis for our experimental design and interpretations without needing to recall details from earlier paragraphs in the Introduction. For example, we considered it crucial to restate the earlier report of the BiP:sfGFP:HDEL phenotype in Atlastin mutants, since our results supporting luminal ER protein displacement contradict the previous fragmentation model.

The following concept was in line 103 in the Results section, and is now in the introduction in lines 82-92: "Conventional light microscopy, commonly used in studies of neuronal ER structure, lacks the resolution necessary to visualize individual ER tubules in small structures, such as presynaptic terminals. The ER is highly sensitive to fixation, and live imaging experiments in neurons in vivo have been conducted on upright microscopes using water dipping objectives with a typical axial resolution limit of >300 nm, which cannot distinguish the densely packed ER tubules at presynaptic terminals (3,8,21,28,39-42). Electron microscopy offers higher resolution, but cannot be used in live samples and has typically been limited to thin 2D sampling (in which it is difficult to distinguish ER cross-sections from synaptic vesicles) (8,20,22)."

Figure Legends-(in all Figures): The number of experimental repeats must be mentioned in the figure legends.

This information is provided in Supplementary Table 1, which contains detailed information about the genotype, statistical analysis, and number of larvae and NMJs analyzed. If the journal requires this information in figure legends, we can move it.

The way the figures are labeled is worrisome; supplementary figures are not ordered numerically.

We will be happy to rename supplementary figures according to journal guidelines.

The tubule extension in Figure 2D is not convincing. Is there a movie showing those changes? Better images are needed. It is essential to show which supplemental movie corresponds to which panel.

We have now included a corresponding video of the same neuron used as an example of tubule extension. We also added another frame to the figure to provide further information on the tubule event we captured. (Figure 2D, Movie S10)

This is unnecessary in the results section: "To investigate the relationship between ER structure and function at synapses, we examined mutants of Atlastin, a GTPase that regulates ER tubule fusion. Drosophila has a single homolog while mammals have three Atlastin homologs, with Atlastin-1 enriched in the brain (Rismanchi et al., 2008)."

This information was moved to the introduction.

"This reduction in ER membrane marker intensity has also been observed in other HSP mutants, suggesting this is a common feature of ER shaping mutants and could indicate changes in ER membrane composition, integrity, or tubule thickness (Perez-Moreno et al., 2023)." This comparison is important and should be shown in the same settings as for the Atlastin mutant rather than referring to published data.

We agree with the reviewer that it is important to determine whether other ER-shaping proteins, besides Atlastin, also show a decrease in tdTomato:Sec61b to support our claim that this could be a common feature among ER-shaping mutants. To do this, we examined mutants of another ER-shaping protein, Reticulon 1, which regulates membrane bending and stabilization in ER tubules. These loss-of-function mutants were a gift from Dr. Cahir O'Kane at the University of Cambridge and were used in his lab's Pérez-Moreno et al., 2023 publication. We found that in our hands tdTomato:Sec61b levels were reduced in Reticulon 1 mutants, consistent with the results reported by Pérez-Moreno et al. (2023). These results are in Figure 3E-F. We also examined the synaptic distribution of the luminal ER marker, BiP:sfGFP:HDEL, in Reticulon 1 mutants to see if it is displaced to the cytosol. Notably, it remained ER-associated, unlike in Atlastin mutants. These results are in Figure 6F-G, results lines 267-270, and discussion lines 542-545.

Does the distribution of the luminal ER marker in Figure 6F diffuse due to mislocalization or reflux after being localized to the ER and then refluxed to the cytosol as was previously shown for the ER to Cytosol signaling (ERCYS) mechanism? Could you assess other ER-luminal protein localization biochemically? It is highly recommended to look at another soluble ER-protein localization in the Atlastin mutant without overexpression, which can be an artifact.

ER stressors can induce ERCYS, in which some luminal proteins, including PDIA3, DNAJB11, ERp29, and an eroGFP reporter, reflux by 30-70% to the cytoplasm without subsequent degradation (unlike ERAD (ER-associated degradation). This phenomenon has only previously been observed in yeast and glioblastoma tumor cells from mice and human . We believe that our work provide the first suggestion that this may occur in neurons, and particularly in a neurological disease model.

We do not believe that the reflux phenotype for BiP:sfGFP:HDEL is due to its overexpression for two reasons: (1) we observe reflux in our neuronal Atlastin knockdown experiments, even when the levels of BiP:sfGFP:HDEL are significantly reduced artificially because of titration of the GAL4 between the RNAi and the reporter (Figure 7A), and (2) BiP:sfGFP:HDEL overexpression somewhat suppresses endogenous BiP upregulation ((Figure 10 and see Reviewer 1.10), arguing that the transgene does not induce ER stress). We included a new "limitations of the study" section to be transparent about the caveats of the BiP:sfGFP:HDEL reporter (lines 639-664).

Identifying potential endogenous neuronal ERCYS substrates in our in vivo preparation poses several challenges. First, biochemical approaches, such as fractionation, are not possible in our complex in vivo sample because neuronal ER proteins would mix with ER from other tissues upon homogenization. Second, detecting endogenous proteins with antibodies requires fixation and permeabilization, which notoriously disrupts ER structure and even causes our reporter BiP:sfGFP:HDEL to collapse from a smooth distribution, as visualized by live imaging and FRAP, to a punctate distribution. Third, using antibodies rather than neuronally restricted transgenes makes it challenging to determine whether the signal originates from the neuron or from dense ER structures in the surrounding muscle. Fourth, some ER luminal proteins can displace as little as 30% in the ERCYS examples cited above, and the sensitivity of our imaging assays may limit our ability to detect these small changes. Finally, the limited availability of tagged transgenes and antibodies specific to Drosophila luminal ER proteins (see next paragraph) poses additional challenges. These limitations highlight the need for future studies to develop novel tools and techniques to more definitively test whether we are indeed observing ERCYS. We have included a paragraph on these future challenges in our discussion in lines 639-664. Identifying endogenous targets of ERCYS in fly neurons is a worthwhile goal, but beyond the scope of the current study. These next steps will particularly benefit from identifying the machinery involved in the reflux of our BiP:sfGFP:HDEL reporter.

Tools we tested: We investigated several options: (1) a tagged PDI transgene (a gift from Karen Hibbard), which was not detectable at presynaptic terminals, (2) a tagged BiP (FlyORF; F000956) that did not localize to the ER, and (3) full-length endogenous BiP detected by antibody staining. We did not detect obvious reflux of endogenous BiP to the cytoplasm (Figure 9), with the caveat that in fixed samples, the BiP signal was not tightly co-localized with the ER marker even under control conditions. However, we did use this antibody to detect an increase in BiP in Atlastin mutant presynaptic terminals, indicating ER stress (see Reviewer 1.10).

Though we have not identified endogenous targets, we believe that our studies with the exogenous reporter will be of great interest to the field, as they clarify the previously reported Atlastin phenotype and provide the first report of a new defect in a human disease animal model.

In comparison to Summerville et al. (2016) in Figure 7, the experiment was not done in the same way. It is important to keep the same settings for comparison

In Figure 7D-E, we compare the distribution of BiP:sfGFP:HDEL in cell bodies, axons, and muscles between controls and Atlastin mutants. To clarify the experimental approach relative to Summerville et al. (2016): while both our studies examined the same cellular compartments (cell bodies, axons and nerve terminals) using the BiP:sfGFP:HDEL reporter, we employed super-resolution Airyscan microscopy. This enhanced resolution was critical for definitively demonstrating that this is a functional rather than a structural phenotype and that ER displacement is progressive, and repeating this experiment at lower resolution as previously reported does not provide any new information. We identified two distinct distribution phenotypes in Atlastin mutants expressing BiP:sfGFP:HDEL, which were not described in the Summerville et al., 2016 paper. From our manuscript (lines 249-251): "We identified two distinct ER network phenotypes in Atlastin mutants expressing BiP:sfGFP:HDEL: "Partial loss" NMJs retained both diffuse signal and identifiable ER network structures, while "Complete loss" NMJs showed no visible ER network structures. Note that the "Complete loss" phenotype in Atlastin mutants reflects the absence of detectable luminal marker signal in organized ER structures, but not the complete absence of ER membranes, as demonstrated by our ER membrane marker tdTomato:Sec61β results."

Does the Atlastin mutant induce the unfolded protein response and stress within the ER? It is necessary to look for UPR markers in those settings. It was shown previously that ER stress leads to protein reflux from the ER to the cytosol. Is there a difference in the ER stress markers in the presynaptic terminal?

The reviewer suggested that Atlastin mutant synapses may exhibit ER stress. To address this, we examined levels of the ER chaperone BiP, a well-established ER stress marker whose expression increases during UPR activation. We first validated that our BiP antibody can detect changes in ER stress by feeding control larvae with 50mM DTT for 24 hours. These results are in the new Figure 10A. Note that we were unable to test sensitivity to ER stress in this way in Atlastin mutant larvae because they did not consume the DTT-treated food, as assessed by blue food coloring in the larvae's guts.

Using this antibody, we measured baseline BiP levels at NMJs of Atlastin mutants on normal food, and found they were slightly increased compared to controls. We conclude from these experiments that Atlastin mutant synapses have mild ER stress. Notably however, Atlastin mutants co-expressing UAS-BiP:sfGFP:HDEL or UAS-tdTomato:Sec61b did not show significantly increased endogenous BiP levels, suggesting that transgene expression at least partly suppresses the mild ER stress response, even though there is extensive cytosolic displacement. These results argue (1) that the mild ER stress in Atl mutants does not strictly correlate with the reflux phenotype, and (2) that the reflux phenotype is not an artifact of overexpression-induced stress. These results are described on lines 430-436 in the results section and shown in Figure 10B-E, and their implications discussed on lines 585-598.

We also explored another strategy to detect ER stress by assessing eIF2α phosphorylation, a key event in the Unfolded Protein Response (UPR) pathway. We obtained a phospho-eIF2α antibody (Cell Signaling; #3597) that was reported to work in Drosophila. However, when we tested this antibody by Western blot, we were unable to detect a band at the expected molecular weight for phosphorylated eIF2α, even in positive-control samples treated with DTT to induce ER stress. We therefore concluded that this antibody is not suitable for reliably detecting ER stress in our experimental system. The failure of this antibody highlights the challenges of finding robust tools to measure ER stress in Drosophila.

It is important to add biochemical experiments to show that no fragmentation of the ER membrane occurred. It can be simply demonstrated by looking at the redox state of the ER, which would change if it were mixed with the reducing cytosol. Moreover, this can be shown by using an ER-targeted redox-sensitive fluorescent protein that is tethered to the ER membrane to follow changes in the redox state of the ER.

The reviewer asked us to test whether the redox state of the ER is disrupted, which could indicate exchange between the cytosol and ER due to membrane rupture. As noted above, biochemical approaches such as fractionation are not possible in this in vivo sample. We attempted to address this concern by creating a UAS-Sec61β:roGFP construct, using the roGFP sequence from Igbaria et al. (2019) to monitor the ER lumen redox environment in Atlastin mutants. Since Sec61β is membrane-tethered, it should remain in the ER and not undergo reflux, making it an ideal sensor for detecting any mixing between the reducing cytosolic environment and the oxidizing ER lumen that would occur if membrane fragmentation and/or ruptures were present. We tested this approach in wild-type Drosophila S2 cells and used the Gal4-UAS binary expression system to co-express Actin-Gal4 (to drive expression of UAS constructs), UAS-Sec61β:roGFP (redox sensor), and UAS-BiP:Halo:HDEL (as a control reporter insensitive to DTT treatment).

Our experiments showed no detectable changes in the fluorescent properties of UAS-Sec61β:roGFP following 30 min 10mM DTT treatment compared to DMSO vehicle control, including no increase in 405-nm excitation fluorescence or changes in 488nm/405nm excitation ratios. These results suggest that either the roGFP sensor requires further optimization for sensitivity in this cellular system or that additional controls and calibration steps are needed to establish the dynamic range of the assay. We believe this experiment falls beyond the scope of the current study, given the extensive optimization required. However, it represents an important future direction for testing membrane fragmentation as a mechanism underlying the phenotypes observed in Atlastin mutants. The possibility of ER integrity defects is mentioned in the discussion on lines 547-559.

Minor comments:

1. It is important to call figures by order. Figure 2C is called before 2A-B. Figure 2B is called before Figure 2A.

The revised manuscript has all figures in order of appearance in the text.

Figure legends (Figure 2): "The same control dataset used in E-G was used in Figure 5 and Figure 5_Supplement." Why is this relevant?

We wanted to be transparent about reusing the same control dataset across multiple figures to avoid any appearance of data duplication. This notation clarifies that, although the data appear in different contexts (Figures 2 and 5. This version does not contain a Figure 5_Supplement), it represents the same biological samples analyzed for different parameters, ensuring readers understand that these are not independent datasets.

Figure 4F is called before Figure-4D-E which are not called.

We revised our manuscript and reorganized Figure 4 to ensure that all figure panels are referenced in sequential order and that panels 4D-E, which were previously not cited in the text, are now properly referenced when discussing their corresponding results.

Figure 5B is called before the previous ones. Same for Figure 5A supplement.

We referenced Figure 5A in lines 211-212, which precedes our discussion of Figure 5B. To clarify the figure order, we removed the early references to Figures 2D-G and Movies 7-14, which were mentioned only to indicate that we were analyzing the same dataset in different ways.

The revised manuscript has all figures in order of appearance in the text.

Referees cross-commenting

I agree with the comments raised by reviewer2 and 3. Basically it is highly important to validate those data by genetic rescue. Moreover, it is essential to know the source of the displaced luminal marker to the cytosol. Is it mislocalization or it is a reflux of pre-existing protein to the cytosol after insertion to the ER. It is also recommended by me and the reviewers and me to test the endogenous protein rather than overexpression.

We have addressed these points in our responses to the following reviewer questions:

• Genetic rescue: Please see our responses to Reviewer 1/Question #10 and Reviewer 2/Question #1.
• Source of displaced luminal marker: We provide some evidence addressing this in our response to Reviewer 3/Question #1.
• Endogenous protein localization: We have examined this and detailed our findings in our responses to Reviewer 1/Question #7 and Reviewer 2/Question #6.

  Reviewer #1 (Significance (Required)):

General assessment: This interesting paper shows that proteins can escape the ER under special conditions. However, the authors need more evidence to show that and rely less on the overexpression system, especially of BIP-GFP, which can cause proteostasis stress within the ER. Advance: The results have been oversimplified in their explanations, and some points and complexities of the study need to be addressed further to make the most of them. These are often some of the more interesting concepts in the paper. I think many points can be addressed in the text by the authors being clear and concise with their reporting. At the same time, other experiments would turn this paper from an observational one into a very interesting mechanistic one. This paper is based on previously published articles from the group and other groups, and it is a nice progression. However, as mentioned, this paper depends primarily on published data, and the novelty is somehow lost between all the comparisons to other published data instead of emphasizing that. Without a substantial mechanistic improvement, the paper would remain observatory.

Audience: The microscopy tools can be great addition to researchers in the field to monitor protein trafficking especially Cell biologists (basic research)

My expertise: ER homeostasis, protein trafficking, cell biology

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

Summary The endoplasmic reticulum (ER) is a continuous organelle that extends throughout neurons to regulate fundamental processes. The analysis of ER dynamics at synaptic terminals is limited by the challenge of imaging these structures at high resolution. In this manuscript, the authors use super-resolution (~170 nm) live imaging and a combination of membrane and luminal ER markers at the Drosophila larval NMJ, an important model synapse, to investigate dynamic ER architecture in vivo. They report a detailed characterization of the presynaptic ER organization and dynamics at wild-type and GTPase Atlastin mutant NMJs. Their analysis using the ER membrane marker tdTomato:Sec61b reveals the presence of an intact ER network in Atlastin mutants. This contrasts with the apparent ER fragmentation phenotype previously reported and replicated here when using a luminal marker. Their findings instead point to the progressive displacement of luminal proteins to the cytosol in Atlastin mutants specifically at synapses. The authors propose that the disruption of ER protein dynamics at synapses is a compartment-specific ER stress response. The manuscript is well written, results are clearly presented, and experiments are technically rigorous.

Major comments

1. The baseline ER phenotypes in Atlastin mutants are mild with complete loss of ER network only observed in terminal boutons. This interesting and unexpected result should be further confirmed by genetic rescue. The authors can use a UAS rescue line previously reported in PMID: 19341724.

We tested the UAS-Atl-myc rescue line and unfortunately found that even in wild-type neurons, overexpression of Atlastin produced strong ER organization defects that precluded the rescue experiment. Instead, to confirm the cell autonomy of the phenotype and to test it wth an independent tool, we performed a presynaptic knockdown of Atlastin by RNAi and found that BiP:sfGFP:HDEL is displaced, as observed in the Atlastin null mutant. These results are in now shown in Figure 7A-C.

Lines 204-7: It's not clear how a greater coefficient of variation indicates that the marker is more concentrated in subsynaptic structures or what is meant by 'subsynaptic structures.'

We added the following text to explain, in lines 181-183: "A higher CoV indicates an uneven distribution of tdTomato:Sec61β within the presynaptic terminal, with some areas showing higher concentrations than others (in contrast to the uniform, diffuse signal expected from fragmentation)." To avoid confusion with postsynaptic structures called the subsynaptic reticulum, we have removed the term "subsynaptic". The intended meaning is distinct structures found within the presynaptic terminal.

There's a mistake in Figure 6C and the associated text. The summed percentage of the three phenotypic categories adds up to 110% for Atlastin mutants.

The reviewer noted that the summed percentage of the three phenotypic categories in Figure 6C adds up to 110% for Atlastin mutants, which appears to be a mathematical error. However, this is not an error, but rather a reflection of our quantification methodology, in which a single bouton can exhibit more than one type of ER dynamics per movie recorded. Our quantification counts each phenotype independently, so boutons displaying multiple phenotypes contribute to more than one category. This approach provides a more comprehensive view of the range of ER dynamics present in Atlastin mutants, as restricting the analysis to mutually exclusive categories would underrepresent the complexity of the phenotypes observed. To make this point clear, we made the following change to the text in lines 257-259: "We note that the sum of these percentages exceeds 100% because one NMJ exhibited multiple phenotypes: one branch had a complete loss, while the other branch had no phenotype. These phenotypes were counted separately."

Figure 8: the ER looks fragmented in 1st instar controls and mutants. The authors should address this difference from more mature NMJs.

We would like to clarify that the bulk of experiments in this manuscript (including all ER dynamics, luminal marker redistribution, and membrane marker analyses discussed throughout the Results) were performed in 3rd instar larvae, which are more mature larval NMJ preparations standard in the field. Figure 8 was included specifically to test whether the Atlastin mutant phenotype we describe throughout the paper is also detectable at an earlier developmental stage, not to replace or reinterpret our primary findings.

Regarding the specific observation that the ER appears more fragmented in Figure 7F-H relative to the more mature NMJs shown elsewhere: this fragmentation, observed similarly in both control and Atlastin mutant 1st instar larvae, likely reflects technical challenges associated with dissecting these smaller, more delicate early-stage specimens rather than a genotype-specific effect. Because fragmentation occurred similarly in both genotypes, we could still reliably assess the redistribution of BiP:sfGFP:HDEL as our primary phenotypic readout in this experiment. We have added the following text (lines 306-309) to clarify this point: "Note that in 1st instar larvae, both normal networks in controls and residual networks in Atlastin mutants appeared more fragmented than in 3rd instar preparations, likely due to the technical challenges of dissecting these smaller, more delicate specimens. Since ER fragmentation occurred similarly in both genotypes, we could still reliably assess the redistribution of BiP:sfGFP:HDEL as our primary phenotypic readout.

The images in figure 9B do not seem representative of the quantification in Figure 9D. Specifically, the partial loss Atlastin NMJ appears to have recovered as fully as the complete loss Atlastin NMJ.

The images showed FRAP recovery across the entire bouton, but we photobleached only a small region within each bouton and quantified only this region. We have now added outlines to clearly delineate the specific FRAP regions that were analyzed in each image, which clarify that the partial loss Atlastin showed less recovery than the overall bouton. We have also reordered the figures to more clearly convey our message (Figure 9 is now Figure 8).

We also made a few changes to the paragraph on lines 347-350 to clarify our experimental reasoning: "We photobleached en passant boutons using a defined region of 6.8 x 7.8 microns (dashed box in Figure 8D) to ensure that BiP:sfGFP:HDEL could recover from the ER networks surrounding the FRAP region (Movies S20-S23)."

We also added this sentence to the figure legends of Figure 8: "The dashed boxes in (D) indicate areas that were photobleached and analyzed for recovery quantification in (E-F)."

Optional: An overexpressed luminal marker is displaced to the cytoplasm in Atlastin mutants. It would be interesting to know and increase the significance of the findings if the same is true of endogenous luminal proteins under biological stress conditions.

As noted in our response to Reviewer #1 suggested that Atlastin mutant synapses may exhibit ER stress. To address this, we examined levels of the ER chaperone BiP, a well-established ER stress marker whose expression increases during UPR activation. We first validated that our BiP antibody can detect changes in ER stress by feeding control larvae with 50mM DTT for 24 hours. We were unable to perform this experiment in Atlastin mutant larvae because they did not consume the DTT-treated food, as assessed by blue food coloring in the larvae's guts. These results are in Figure 10A. In the future, it will be of interest to establish a protocol to examine Atlastin mutants by feeding or treating larval fillets with DTT.

We measured BiP levels at NMJs of Atlastin mutants and found they were slightly increased compared to controls. Atlastin mutants co-expressing UAS-BiP:sfGFP:HDEL or UAS-tdTomato:Sec61b did not show significantly increased endogenous BiP levels, suggesting that transgene expression suppresses the mild ER stress response. We conclude from these experiments that Atlastin mutant synapses have mild ER stress. These results are in Figure 10B-E).

Optional: Applying this approach in stimulated conditions (high potassium, increased temperature) might reveal a greater activity-dependent role for Atlastin at synaptic terminals.

This is a very interesting idea, as we have only examined synapses at rest. However, this is beyond the scope of this paper.

Minor Comments

1. Line 16: Atlastin should be italicized.

Thank you for catching this typo. We have fixed it.

Figure 5A: Based on the relative intensities, it appears that control and mutant images are not contrast matched but this isn't stated.

Thank you for catching this omission. We added to the figure legend: "Control and Atlastin mutant images are not contrast matched."

Line 822: The number of static Atlastin mutant boutons used for analysis is missing.

Thank you for catching this omission. We have fixed this supplementary table.

Figure 9: The blue arrows are not annotated in the figure legend.

Thank you for catching this omission. We have fixed this figure legend.

Reviewer #2 (Significance (Required)):

Atlastin is linked to Hereditary Spastic Paraplegia (HSP) and this study changes our understanding of the compartment-specific impacts of its loss. This study reveals the importance of using both membrane and luminal ER markers to accurately interpret phenotypes as well as the importance of considering compartment-specific effects on ER. These findings represent significant mechanistic and conceptual advances. The lack of genetic rescue is a limitation and adding an investigation of an endogenous luminal protein under basal and stress conditions would add significantly to our understanding of Atlastin dysfunction in HSP. Notably, the in vivo imaging approach introduced here can be adapted broadly for live imaging of Drosophila larvae. Thus, this work will be of interest to both neuronal cell biologists and the wider Drosophila community. This review is based on our expertise in neuronal cell biology.

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

In this manuscript, the authors investigate the structural dynamics of the endoplasmic reticulum (ER) in Drosophila neurons and examine the role of the ER-shaping protein Atlastin in ER morphology. Their discovery on the neuromuscular junction (NMJ)-specific contribution of Atlastin to ER integrity is intriguing and may provide valuable insights into the pathological mechanisms underlying Atlastin mutations associated with hereditary spastic paraplegia (HSP) and hereditary sensory neuropathy. The key observation on ER protein showing an aberrant cytoplasmic localisation in mutant cells appears convincing. Though this phenomenon's characterisation stays at the point of primary observation with its mechanics unclarified, establishing this new and unexpected functional rather than structural Atl effect is important and useful for the field. The observation that ER is structurally preserved in this mutant with absolute lack of Atl are also extremely useful.

It is unclear if the cytoplasmic localisation affects an exogenous overexpressed ER marker or endogenous protein would also appear in cytoplams, the authors should consider adding an immunostaining data to test that.

Authors offer speculations on potential reasons for the cyto localisation of the ER marker suggesting that relocation at the cell periphery specifically combined with slow clearance there is the most likely explanation (still unclear what stops the marker from spreading through the entire cell). They suggest that decrease in cotranslational translocation is unlikely as this would result in somatic accumulation of the marker. However, if the clearance in the periphery is less efficient than in soma, the accumulation there might reflect a compromised translocation. Any clarifying experiments, if practical, to directly demonstrate how ER proteins in relocates to the cytoplasm in atl mutant would help understanding better the phenomenon. For example, would proteasomal inhibition make the marker accumulate more across the cell? Authors also suggest links to ER stress. Would stress induction phenocopy the mutant?

Reviewer #3 asked whether defective proteasomal clearance underlies the cytosolic accumulation of BiP:sfGFP:HDEL in Atlastin mutants. We addressed this directly. First, proteasome function appears intact in the mutants: baseline ubiquitinated protein levels (FK1 antibody) were comparable between control and Atlastin mutants, and MG132 treatment produced a similar increase in ubiquitination in both genotypes, confirming both antibody specificity and normal proteasome activity. We then examined BiP:sfGFP:HDEL directly. In controls, MG132 caused the marker to accumulate at axons and presynaptic terminals, showing that it is normally cleared from these compartments by the proteasome. Critically, this accumulated marker remained associated with intact ER networks: MG132 did not induce diffuse cytosolic BiP:sfGFP:HDEL in any compartment (cell bodies, axons, or presynaptic terminals), even where levels rose substantially. Thus, blocking proteasomal clearance raises ER-localized marker but does not generate the cytosolic pool seen in Atlastin mutants, indicating that impaired clearance is not sufficient to cause the displacement phenotype. We separately noted that BiP:sfGFP:HDEL was already elevated in Atlastin mutant axons without MG132, paralleling the axonal tdTomato:Sec61β accumulation in Figure 4, consistent with reduced baseline clearance specifically in mutant axons, but this does not lead to cytosolic displacement. This experiment is now shown in Figure 11, described in Results (lines 445-475), and discussed in lines 576-581.

Minor comments:

Line 146:

"fast dynamics (Thank you for catching this mistake. We have corrected it.

Fig. 2D: The data representation of "Tubule displacement" image is unclear. The ER tubule indicated by the red arrow does not seem to show any changes over time (like static). time 0 in stamp appears behind the image.

Thank you for catching the typo. We have fixed it. Additionally, we added black arrows to highlight a tubule that is not moving, allowing the reader to compare it with the moving tubule. We also included a video of all types of ER tubule dynamics to ensure the reader can also look at the raw data (Movies S9-11).

Line 157-158 (and relevant method sections):

The definition of static and dynamic boutons is ambiguous. The author should describe in more detail this point including how long they observed the structure to define the changes in ER tubule dynamics.

We provide in the methods (lines 779-791) a detailed explanation of how we categorized boutons as dynamic or static. In addition, we added the following to explain in the results section how we defined static vs dynamic:

Old sentence: We qualitatively categorized boutons as "static" if we observed no change in ER network structure or "dynamic" if we observed at least one change.

New sentence in lines 143-147: "We imaged boutons for 40 sec at 0.92 sec intervals to capture ER dynamics over this observation period. Boutons were qualitatively categorized as "static" if we observed no detectable changes in ER network structure throughout the entire 40 sec imaging session, or "dynamic" if we observed at least one of the three defined dynamic events during this time window."

Fig. 2E: What n=75 and n=29 represent is unclear, are these the number of boutons in en passant and terminal subjected for qualitative analysis?

We removed these n values from the figure and added this information to the Supplementary Table 1, which contains detailed information about the genotype, statistical analysis, and number of larvae and NMJs analyzed.

Fig. 2: What the qualitative analysis represents is unclear, are the points pulled from different experiments?

The data in Fig. 2 E-F comes from movies acquired in the same experiment. The number of independent animals and NMJs imaged is described in Table 1.

* *Line 231: Regarding "...we found a small but significant reduction in dynamic boutons in Atlastin mutants (76%), ...", how do the authors assess significance. If proportion of static/dynamic ER in boutons was obtained from multiple experiments, it should be presented e.g. as in average {plus minus} standard deviation, or clarify that the proportion is representative of x independent experiments.

The videos used for this figure were acquired from a single experiment. We use a chi-square test to determine significance relative to the "expected" distribution of dynamics types from controls, as these are categorical rather than continuous data (see PMID 31145670). Information regarding genotype, statistical analysis and number of larvae and NMJs can also be found in Supplementary Table 1.

Line 267-269 and Fig. 6B: The author's conclusion that "Complete loss of ER network structure in NMJ of BiP:sfGFP:HDEL overexpressing Atl mutant" seem to be based on the lack of signal from luminal marker, which may be undetectable due to changes to tubular volume or marker loss to the cytoplasm, as suggested by the authors, while the membranous ER structure is intact. It would be useful to discuss this point and potentially add ER membrane-stained control.

We agree with the reviewer that Atlastin mutants categorized as 'complete loss mutants' do not actually lack ER at synapses. We think this is an important point so we added the following to the results in lines 251-254: "Note that the "Complete loss" phenotype in Atlastin mutants reflects the absence of detectable luminal marker signal in organized ER structures, not the complete absence of ER membranes, as demonstrated by our ER membrane marker tdTomato:Sec61β results."

We attempted to co-label the ER membrane and ER lumen, but these crosses yielded very few live larvae (in either controls or Atlastin mutants, and those that survived had severely deformed NMJs. We added Figure 6-Supplement showing the results of this experiment, and described them on lines 270-273.

Fig. 6C: In Atl mutant, why does the total of the proportion exceed 100% (10 + 45 + 55)?

The reviewer noted that the summed percentage of the three phenotypic categories in Figure 6C adds up to 110% for Atlastin mutants. This is not an error, but rather a reflection of our quantification methodology because a single bouton can exhibit more than one type of ER dynamics per movie recorded. Our quantification counts each phenotype independently, so boutons displaying multiple phenotypes contribute to more than one category. This approach provides a more comprehensive view of the range of ER dynamics present in Atlastin mutants, as restricting the analysis to mutually exclusive categories would underrepresent the complexity of the phenotypes observed. To make this point clear, we made the following change to the text in lines 257-259: "We note that the sum of these percentages exceeds 100% because one NMJ exhibited multiple phenotypes: one branch had a complete loss, while the other branch had no phenotype. These phenotypes were counted separately."

Fig. 9C, line 342-344: In FRAP experiment using CD8, it seems that the Partial loss Atl mutant shows slower recovery that control. There seems to be a mismatch in triangle symbols of Partial loss Atl mutant between legend and plot (one is filled and the other is empty). This should be clarified.

Thank you for catching this mistake. We have fixed the figure.

fig. 10 is a clever way to verify the cytoplasmic localization of the ER marker; however, its description and annotation can be improved, and it would be stronger if 4 curves in F for mutant and controls with the trap and normal were shown.

The reviewer suggested merging our graphs but we believe that keeping them separate is clearer.

Line 495: Drosophila have ReepA and ReepB, but not Reep1-4. If the authors discuss their speculation based on their observation (using Drosophila), the gene names should be unified in the same species, and explain the corresponding genes to mammalian cells.

We made the following changes to address the reviewer's concern about gene nomenclature consistency (lines 502-506): "These ER-derived vesicles are likely to involve ReepA and ReepB, the Drosophila orthologs of mammalian REEP1-4, which regulate ER vesicle formation in mammalian cells (67). Notably, while overexpression of Atlastin can regulate REEP vesicle fusion in mammalian systems (67), it is not essential for vesicle formation, suggesting similar regulatory relationships may exist between Atlastin and Reep genes in Drosophila."

Line 548; should UPR be Unfolded Protein Response?

Thank you for catching the typo. We have fixed it.

Reviewer #3 (Significance (Required)):

This study advances the understanding of how ER morphogens affect neuronal cells specifically, the lack of which limits researchers ability to comprehend the neuronal pathologies associated with ER structure-function. The observation on ER content aberrant localisation caused by the lack of key structural protein should be of a great interest for cell and neuronal biologists and researchers of the associated diseases and shows the field a new direction. Though, mechanistic details remain to be unraveled, it constitutes a fundamental, conceptual advance.

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

Learn more at Review Commons

Referee #3

Evidence, reproducibility and clarity

In this manuscript, the authors investigate the structural dynamics of the endoplasmic reticulum (ER) in Drosophila neurons and examine the role of the ER-shaping protein Atlastin in ER morphology. Their discovery on the neuromuscular junction (NMJ)-specific contribution of Atlastin to ER integrity is intriguing and may provide valuable insights into the pathological mechanisms underlying Atlastin mutations associated with hereditary spastic paraplegia (HSP) and hereditary sensory neuropathy. The key observation on ER protein showing an aberrant cytoplasmic localisation in mutant cells appears convincing. Though this phenomenon's characterisation stays at the point of primary observation with its mechanics unclarified, establishing this new and unexpected functional rather than structural Atl effect is important and useful for the field. The observation that ER is structurally preserved in this mutant with absolute lack of Atl are also extremely useful.

It is unclear if the cytoplasmic localisation affects an exogenous overexpressed ER marker or endogenous protein would also appear in cytoplams, the authors should consider adding an immunostaining data to test that.

Authors offer speculations on potential reasons for the cyto localisation of the ER marker suggesting that relocation at the cell periphery specifically combined with slow clearance there is the most likely explanation (still unclear what stops the marker from spreading through the entire cell). They suggest that decrease in cotranslational translocation is unlikely as this would result in somatic accumulation of the marker. However, if the clearance in the periphery is less efficient than in soma, the accumulation there might reflect a compromised translocation. Any clarifying experiments, if practical, to directly demonstrate how ER proteins in relocates to the cytoplasm in atl mutant would help understanding better the phenomenon. For example, would proteasomal inhibition make the marker accumulate more across the cell? Authors also suggest links to ER stress. Would stress induction phenocopy the mutant?

Minor comments:

Line 146: "fast dynamics (<1 sec)" a velocity should be presented as distance/time

Fig. 2D: The data representation of "Tubule displacement" image is unclear. The ER tubule indicated by the red arrow does not seem to show any changes over time (like static). time 0 in stamp appears behind the image.

Line 157-158 (and relevant method sections): The definition of static and dynamic boutons is ambiguous. The author should describe in more detail this point including how long they observed the structure to define the changes in ER tubule dynamics.

Fig. 2E: What n=75 and n=29 represent is unclear, are these the number of boutons in en passant and terminal subjected for qualitative analysis?

Fig. 2: What the qualitative analysis represents is unclear, are the points pulled from different experiments?

Line 231: Regarding "...we found a small but significant reduction in dynamic boutons in Atlastin mutants (76%), ...", how do the authors assess significance. If proportion of static/dynamic ER in boutons was obtained from multiple experiments, it should be presented e.g. as in average {plus minus} standard deviation, or clarify that the proportion is representative of x independent experiments.

Line 267-269 and Fig. 6B: The author's conclusion that "Complete loss of ER network structure in NMJ of BiP:sfGFP:HDEL overexpressing Atl mutant" seem to be based on the lack of signal from luminal marker, which may be undetectable due to changes to tubular volume or marker loss to the cytoplasm, as suggested by the authors, while the membranous ER structure is intact. It would be useful to discuss this point and potentially add ER membrane-stained control.

Fig. 6C: In Atl mutant, why does the total of the proportion exceed 100% (10 + 45 + 55)?

Fig. 9C, line 342-344: In FRAP experiment using CD8, it seems that the Partial loss Atl mutant shows slower recovery that control. There seems to be a mismatch in triangle symbols of Partial loss Atl mutant between legend and plot (one is filled and the other is empty). This should be clarified

fig. 10 is a clever way to verify the cytoplasmic localisatoin of the ER marker, however its description and annotation can be improved, and it would be stronger if 4 curves in F for mutant and controls with the trap and normal were shown.

Line 495: Drosophila have ReepA and ReepB, but not Reep1-4. If the authors discuss their speculation based on their observation (using Drosophila), the gene names should be unified in the same species, and explain the corresponding genes to mammalian cells.

Line 548; should UPR be Unfolded Protein Response?

Significance

This study advances the understanding of how ER morphogens affect neuronal cells specifically, the lack of which limits researchers ability to comprehend the neuronal pathologies associated with ER structure-function. The observation on ER content aberrant localisation caused by the lack of key structural protein should be of a great interest for cell and neuronal biologists and researchers of the associated diseases and shows the field a new direction. Though, mechanistic details remain to be unraveled, it constitutes a fundamental, conceptual advance.

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

Learn more at Review Commons

Referee #2

Evidence, reproducibility and clarity

Summary

The endoplasmic reticulum (ER) is a continuous organelle that extends throughout neurons to regulate fundamental processes. The analysis of ER dynamics at synaptic terminals is limited by the challenge of imaging these structures at high resolution. In this manuscript, the authors use super-resolution (~170 nm) live imaging and a combination of membrane and luminal ER markers at the Drosophila larval NMJ, an important model synapse, to investigate dynamic ER architecture in vivo. They report a detailed characterization of the presynaptic ER organization and dynamics at wild-type and GTPase Atlastin mutant NMJs. Their analysis using the ER membrane marker tdTomato:Sec61b reveals the presence of an intact ER network in Atlastin mutants. This contrasts with the apparent ER fragmentation phenotype previously reported and replicated here when using a luminal marker. Their findings instead point to the progressive displacement of luminal proteins to the cytosol in Atlastin mutants specifically at synapses. The authors propose that the disruption of ER protein dynamics at synapses is a compartment-specific ER stress response. The manuscript is well written, results are clearly presented, and experiments are technically rigorous.

Major comments

1. The baseline ER phenotypes in Atlastin mutants are mild with complete loss of ER network only observed in terminal boutons. This interesting and unexpected result should be further confirmed by genetic rescue. The authors can use a UAS rescue line previously reported in PMID: 19341724.
2. Lines 204-7: It's not clear how a greater coefficient of variation indicates that the marker is more concentrated in subsynaptic structures or what is meant by 'subsynaptic structures.'
3. There's a mistake in Figure 6C and the associated text. The summed percentage of the three phenotypic categories adds up to 110% for Atlastin mutants.
4. Figure 8: the ER looks fragmented in 1st instar controls and mutants. The authors should address this difference from more mature NMJs.
5. The images in figure 9B do not seem representative of the quantification in Figure 9D. Specifically, the partial loss Atlastin NMJ appears to have recovered as fully as the complete loss Atlastin NMJ.
6. Optional: An overexpressed luminal marker is displaced to the cytoplasm in Atlastin mutants. It would be interesting to know and increase the significance of the findings if the same is true of endogenous luminal proteins under biological stress conditions.
7. Optional: Applying this approach in stimulated conditions (high potassium, increased temperature) might reveal a greater activity-dependent role for Atlastin at synaptic terminals.

Minor Comments

1. Line 16: Atlastin should be italicized.
2. Figure 5A: Based on the relative intensities, it appears that control and mutant images are not contrast matched but this isn't stated.
3. Line 822: The number of static Atlastin mutant boutons used for analysis is missing.
4. Figure 9: The blue arrows are not annotated in the figure legend.

Significance

Atlastin is linked to Hereditary Spastic Paraplegia (HSP) and this study changes our understanding of the compartment-specific impacts of its loss. This study reveals the importance of using both membrane and luminal ER markers to accurately interpret phenotypes as well as the importance of considering compartment-specific effects on ER. These findings represent significant mechanistic and conceptual advances. The lack of genetic rescue is a limitation and adding an investigation of an endogenous luminal protein under basal and stress conditions would add significantly to our understanding of Atlastin dysfunction in HSP. Notably, the in vivo imaging approach introduced here can be adapted broadly for live imaging of Drosophila larvae. Thus, this work will be of interest to both neuronal cell biologists and the wider Drosophila community. This review is based on our expertise in neuronal cell biology.

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

Learn more at Review Commons

Referee #1

Evidence, reproducibility and clarity

In the present manuscript, the authors address an important question related to the ultrastructure and the dynamics of the ER in HSP. In contrast to previous studies, the authors here show (by using a membrane and luminal protein markers) that in the presynaptic terminals, the overexpressed BIP "mislocalizes" to the cytosol without affecting (or with minimal effect) the integrity of the ER membrane. Although they used an artificial system by overexpressing (overexpression) of BIP-sfGFP-HDEL (fused protein), the findings lack validation of the endogenous protein by biochemical and fluorescent tools.

Concerns:

I am worried about how the article is presented, mainly in the results section, as most of it refers to published data. The Results section is reserved for presenting new findings without external interpretation or comparison. The paper is written mainly as a comparison paper with other studies or relies on previous studies to strengthen their findings rather than coming up with novel findings. Up to figure 4, I missed the relevance of the new findings. The manuscript needs rewriting to emphasize its novelty and significance without comparing it to previous data. Moreover, the manuscript emphasizes the technology and the findings of the localization of the ER luminal proteins to the cytosol (which is not novel and was previously reported in other settings). Those two aspects were not given enough focus. Here are the main major and minor comments:

Major comments:

1. Lines 103-116 (first paragraph of the results section) describe mainly published data that is more suitable for the introduction section. It is annoying to refer to different published articles in the Results section to strengthen the results instead of showing them. The same goes for paragraphs two and three. Why mention those data in the Results section if they are already published and known?
2. Figure Legends-(in all Figures): The number of experimental repeats must be mentioned in the figure legends.
3. The way the figures are labeled is worrisome; supplementary figures are not ordered numerically.
4. The tubule extension in Figure 2D is not convincing. Is there a movie showing those changes? Better images are needed. It is essential to show which supplemental movie corresponds to which panel.
5. This is unnecessary in the results section: "To investigate the relationship between ER structure and function at synapses, we examined mutants of Atlastin, a GTPase that regulates ER tubule fusion. Drosophila has a single homolog while mammals have three Atlastin homologs, with Atlastin-1 enriched in the brain (Rismanchi et al., 2008)."
6. "This reduction in ER membrane marker intensity has also been observed in other HSP mutants, suggesting this is a common feature of ER shaping mutants and could indicate changes in ER membrane composition, integrity, or tubule thickness (P.rez-Moreno et al., 2023)." This comparison is important and should be shown in the same settings as for the Atlastin mutant rather than referring to published data.
7. Does the distribution of the luminal ER marker in Figure 6F diffuse due to mislocalization or reflux after being localized to the ER and then refluxed to the cytosol as was previously shown for the ER to Cytosol signaling (ERCYS) mechanism? Could you assess other ER-luminal protein localization biochemically? It is highly recommended to look at another soluble ER-protein localization in the Atlastin mutant without overexpression, which can be an artifact
8. "(data not shown)" in line 288. This affects the process of judging those data.
9. In comparison to Summerville et al. (2016) in Figure 7, the experiment was not done in the same way. It is important to keep the same settings for comparison
10. Does the Atlastin mutant induce the unfolded protein response and stress within the ER? It is necessary to look for UPR markers in those settings. It was shown previously that ER stress leads to protein reflux from the ER to the cytosol. Is there a difference in the ER stress markers in the presynaptic terminal?
11. It is important to add biochemical experiments to show that no fragmentation of the ER membrane occurred. It can be simply demonstrated by looking at the redox state of the ER, which would change if it were mixed with the reducing cytosol. Moreover, this can be shown by using an ER-targeted redox-sensitive fluorescent protein that is tethered to the ER membrane to follow changes in the redox state of the ER.

Minor comments:

1. It is important to call figures by order. Figure 2C is called before 2A-B. Figure 2B is called before Figure 2A.
2. Figure legends (Figure 2): "The same control dataset used in E-G was used in Figure 5 and Figure 5_Supplement." Why is this relevant?
3. Figure 4F is called before Figure-4D-E which are not called.
4. Figure 5B is called before the previous ones. Same for Figure 5A supplement.

Referees cross-commenting

I agree with the comments raised by reviewer2 and 3. Basically it is highly important to validate those data by genetic rescue. Moreover, it is essential to know the source of the displaced luminal marker to the cytosol. Is it mislocalization or it is a reflux of pre-existing protein to the cytosol after insertion to the ER. It is also recommended by me and the reviewers to test the endogenous protein rather than overexpression.

Significance

General assessment: This interesting paper shows that proteins can escape the ER under special conditions. However, the authors need more evidence to show that and rely less on the overexpression system, especially of BIP-GFP, which can cause proteostasis stress within the ER.

Advance: The results have been oversimplified in their explanations, and some points and complexities of the study need to be addressed further to make the most of them. These are often some of the more interesting concepts in the paper. I think many points can be addressed in the text by the authors being clear and concise with their reporting. At the same time, other experiments would turn this paper from an observational one into a very interesting mechanistic one. This paper is based on previously published articles from the group and other groups, and it is a nice progression. However, as mentioned, this paper depends primarily on published data, and the novelty is somehow lost between all the comparisons to other published data instead of emphasizing that. Without a substantial mechanistic improvement, the paper would remain observatory.

Audience: The microscopy tools can be great addition to researchers in the field to monitor protein trafficking especially Cell biologists (basic research)

My expertise: ER homeostasis, protein trafficking, cell biology

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

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Reply to the reviewers

Manuscript number: RC-2026-03460

Corresponding author(s): Louise, Walport

1. General Statements

We thank the reviewers for their critical reading and insightful comments on the manuscript and for highlighting the relevance of our data to developmental biology audiences.

Below we have included a detailed point-by-point response to each reviewer comment, divided into those that are linked with revisions in the manuscript, and those that are not. As well as this we have written two general statements regarding the recently published high-resolution structures of the CPLs and our findings linking the CPLs to other oocyte structures, both of which address multiple reviewer comments.

High resolution CPL structure papers

While this manuscript was under review, several papers were published in Nature or deposited on bioRxiv detailing high-resolution structures of the CPLs (DOIs: 10.1038/s41586-026-10360-7 ,10.1038/s41586-026-10513-8, 10.1038/s41586-026-10442-6, 10.64898/2026.03.22.713481). These structural studies validate the key scaffolding function of PADI6 in CPL formation, as well as the association of ubiquitination machinery (including the SCF complex) to the CPLs, which we also determined in this work through mass spectrometry. Our work is complementary to these studies. The published structures provide detailed insight into how the CPLs form and function. However, while the new papers identify the structure and composition of the core CPL fiber, due to the requirement for particle averaging, they cannot resolve the identity of proteins beyond this core that interact or are stored on the CPLs sub-stoichiometrically. This limitation is addressed by our sub-cellular single oocyte proteomic workflow which pools all CPLs within each oocyte, identifying proteins which become soluble upon CPL dissolution, whether due to presence in the core fibre or to association with the fibres. Our manuscript therefore provides a complementary atlas of the CPL-associated proteome as a resource for further studying the function of CPLs in early development. To place our work in the context of the new manuscripts we have added the following to the discussion:

• “During preparation of this manuscript, several high-resolution structures of the CPLs were reported80–83. Our proteomic workflow identified all CPL proteins resolved in these published structures as CPL-associated, including the newly identified SCF complex components and several F-box proteins. Notably, whilst highly informative, the structural studies cannot resolve the precise identity of individual proteins from families of structurally homologous proteins that form the CPL core, or of proteins which associate with the CPLs sub-stoichiometrically. One key example is the F-box proteins which offer substrate specificity to the SCF complex. Our proteomic analysis identified 10 different F-box proteins to have CPL-association. By contrast each published structure reports only a single or a few F-box proteins as part of the core complex. Notably different F-box proteins are reported in different structures. Our data provides an explanation for this variation, suggesting that even the core CPL fibres are non-homogeneous in the cell with different F-box proteins present in different locations (Fig 6B). Similarly, the close homology of a/b-tubulin proteins prevents identification of exact isoforms in the reported structures. Our data suggests that many different isoforms contribute to the CPLs (Fig 5E). Additionally, it is proposed that the CPLs act as storage hubs for a much wider range of proteins30. By allowing identification of proteins associated with the CPLs even at low occupancy our CPL-associated proteome provides a list of potential CPL-associated proteins for further structural and functional characterisation of CPL function.” CPLs and other oocyte structures

The presence of proteins from other large cellular structures in the CPL-enriched protein dataset was highlighted by reviewers 1 and 3, in particular reviewer 3: “the physical meshwork of CPLs may prevent loss of CPL-associated proteins as well as cytoplasmic protein complexes or organelles that are too large to escape the cytoplasm through the CPLs. This is particularly a concern for the authors' conclusions regarding high amounts of ELVA-associated and mitochondrial and mitochondria-associated proteins associated with the CPLs given the large size of these organelles/structures. Is there any evidence by an alternative method of direct association of ELVAs or mitochondria with CPLs? Others have not detected mitochondrial proteins associated with CPLs”.

Functional cross-talk with ELVA:

Regarding an association with the ELVA, we should clarify that we believe that the relation between CPLs and the ELVA is most likely not a direct association but a previously unknown functional interaction and we have revised the text to more clearly reflect this view. We identify proteins involved in protein degradation, most notably the SCF complex, in our CPL-enriched dataset. In support of their presence being likely due to direct CPL association, rather than indirect trapping of the large ELVA, the recently published CPL structures similarly identify numerous proteins involved in protein degradation as associated with the CPLs, suggesting these proteins are sequestered and inactivated on the CPLs. As we do, these other works also propose that the CPLs are critical hubs for proteostasis in the oocyte and early embryo, similar to the proposed function of the ELVAs. However, as discussed below in the context of the mitochondria, we acknowledge that it is possible that the high level of these proteins observed in our dataset could alternatively be due to reduced cytoplasmic escape and we have updated the limitations section of the manuscript to reflect this caveat in our interpretation.

• “Whilst we interpret proteome differences in Triton X-100 treated Padi6-KO oocytes to indicate an association with the CPLs, in the case of proteins associated with other large cellular structures such as mitochondria or the ELVA it is possible that this difference is instead due to physical entrapment of these structures by the CPLs during the precipitation step.” Interestingly, we identify RUFY1 in the CPL-enriched fraction. RUFY1 is a key marker of the ELVA where it functions as a scaffolding protein. In the manuscript we discussed the possibility that RUFY1 could therefore perform a similar function on the CPLs. In a recent work, it was reported that the number and size of RUFY1 compartments was increased in Padi6-null oocytes (DOI: 10.1038/s41594-026-01758-y). As RUFY1 is the key marker of the ELVAs this shows that their morphology is likely affected in the absence of Padi6. Together these data point towards a functional crosstalk between the two, potentially via the CPLs storing protein degradation machinery required by the ELVAs, as well as also storing/sequestering RUFY1, which could explain the increase in RUFY1 compartments in the absence of the CPLs.

Mitochondria:

Whilst it has been reported that there are defects in mitochondrial localisation in the absence of PADI6 and the CPLs (10.1016/j.ydbio.2010.11.033), we agree with the reviewers that it is possible these are not due to direct interactions between the CPLs and mitochondria, but rather from two separate roles of PADI6 and that our observation of mitochondrial proteins in the CPL-enriched set is due to increased physical entrapment of the large mitochondria by the CPLs rather than association. As additional links between the mitochondria and CPLs are not present in the literature unlike protein degradation machinery, we have removed the section entitled ‘The CPLs are associated with the oocyte mitochondria’, along with supplementary Figures 6E and 6F and added to the text the caveat that proteins associated with large cellular structures in our datasets could be due to physical entrapment. As we did not further discuss links between the CPLs and mitochondria in either the abstract or discussion, we do not believe the removal of this section significantly affects either the findings or novelty of this work.

PADI6 Catalytic Activity

Both reviewers 1 and 2 ask that we experimentally validate the loss of catalytic activity in the PADI6-C663A mutant. Along similar lines, reviewer 3 questions the rationale for the Padi6-C663A mouse line based on the lack of in vitro catalytic activity. We would like to reiterate that prior to this work there has been contradictory evidence regarding the catalytic activity of PADI6. Early work into PADI6 (10.1016/j.mce.2007.05.005) detected citrulline by IHC specifically in the oocytes of ovarian sections, which was absent in PADI6 knock-out ovaries. Later, it was shown by IF using anti-Citrulline antibodies that there is nuclear citrulline staining in 2-cell and 4-cell embryos that is ablated by a PADI inhibitor, in that study attributed to PADI1 (PADI1 presence detected by antibody-based techniques such as IF, 10.1038/srep38727). Together these manuscripts all posit that there is an active deiminase in oocytes and early embryos. We do not detect transcripts or protein for any PADI aside from PADI6 at the 2-cell stage and before suggesting any citrullination in the 2-cell embryo or before could only be a result of deimination by active PADI6 (Figure S4E).

However, we and others, have confirmed that wild-type PADI6 is not active in vitro under the same conditions as the other PADIs (DOIs: 10.1016/j.csbj.2024.08.019, 10.4236/abb.2011.24044). Whilst this may be interpreted as overall lack of catalytic activity, an alternative explanation is that incorrect assay conditions have been used. For in vitro assays, supra-physiologically high calcium concentrations are required to activate catalysis by PADIs 1 to 4. We have previously shown that these calcium binding residues are not conserved in PADI6 and PADI6 does not bind calcium. It is therefore possible that PADI6 has evolved to be activated by other as yet unknown activating signals so as to not have its function disrupted during the large calcium transient post-fertilization. In the absence of the correct activating signals, in vitro activity would not be expected, even if the enzyme is catalytically active in vivo.

We believe that this, together with the conservation of the catalytic tetrad residues, and the contradictory evidence regarding citrullination in vivo demonstrated that based on the current literature a catalytic function of PADI6 cannot be ruled out in vivo. This was our rationale for developing the Padi6-C663A mouse model in this work, to disentangle the dramatic phenotypes observed from full knockout of PADI6 from a possible catalytic function. Based on our previous structural characterization of human PADI6 (DOI: 10.1016/j.csbj.2024.08.019), if PADI6 were to have catalytic activity it would be through cysteine 663. Our data conclusively shows that catalytic activity of PADI6 through cysteine 663 is not required for murine female fertility, but that mice with this mutation are also not fully wildtype. Given the lack of large-scale structural damage loss of this cysteine imparts on the protein (Supplementary Figure 1), the observed phenotypes point towards either the disruption of a previously unidentified non-essential catalytic function or to more subtle changes to function from this mutation, for example through alterating the binding affinities of proteins that interact with PADI6 lacking this cysteine.

2. Point-by-point description of the revisions

Description of revisions incorporated into the manuscript along with discussion of reviewer comments

Reviewer 1:

• Major Comment 1: “1- The methods for differential gene expression analysis are insufficiently described. Were these calculated using Scanpy? If so, the rationale for this choice should be provided, as the number of replicates and the nature of the data appear more suited to standard bulk differential expression frameworks such as DESeq2 or edgeR.”

• Response and Incorporated Revision: We chose the Scanpy framework for analysis because it allows for quality control, PCA, normalization, and differential expression within a single Python environment. To calculate differential gene expression, we performed Student's t-test on log-normalized counts for each gene followed by correction for multiple testing using the Benjamini-Hochberg procedure. We have added this further clarification to the methods section:

“To identify dysregulated genes, for each stage, mean log2CPM ratios (test vs. wild-type) and q-values were calculated for each gene using a custom Python script (see Data and Code Availability), extracted and plotted using GraphPad Prism. In brief, an independent Student’s t-test was applied to the normalized expression values and p-values were corrected for multiple testing using the Benjamini-Hochberg procedure.”

• Major Comment 2:

*“2- In Figure 4C, it is unclear what correlation is being calculated. Additionally, the methods state that differential protein abundance was determined using the same approach as the scRNA-seq analysis. Given the lack of methodological clarity noted above, it is difficult to evaluate these results. The authors should justify whether the chosen method is compatible with the normalization approach used for the proteomics data.”

*

• Response and Incorporated Revision: We apologize for the lack of clarity on the calculated correlation and to improve this have amended the Figure legend for 4C to the following: “(C) Pearson correlation values for protein abundances in wild-type, Padi6-C663A and Padi6-KO GV oocyte and 2-cell embryo replicates when compared to all other replicates of the same condition. Samples of the same genotype and stage show high correlation in the abundance of individual proteins.”

Regarding the compatibility, dysregulated proteins and transcripts were determined using the same statistical method, independent Student’s t-tests corrected for multiple testing with the Benjamini-Hochberg procedure.

• Major Comment 4:

“4- A notable result is the complete lack of correspondence between differential RNA-seq and proteomics in 2-cell embryos. The authors state that "This is consistent with data showing that minimal translation occurs in the 2-cell embryo, with the first large translational wave only occurring in the morula," citing Israel et al. 2019. This statement is factually incorrect. The cited study did not measure translation directly. Recent work that specifically measured translation during preimplantation development has demonstrated that translation is highly dynamic throughout these stages (Ozadam et al. 2023, Nature). This claim should be corrected and the results discussed in the context of these more recent findings.”

• Response and Incorporated Revision: We have revised the claim, discussing our results in the context of the more recent Ozadam et al. 2023, Nature paper. The amended text reads: “This is consistent with data showing that protein abundance does not correlate with RNA level, but with ribosome occupancy and translation efficiency in the zygote58,59. Our results show that this lack of correlation in RNA and protein is maintained in the 2-cell embryo with RNA dysregulation and protein dysregulation uncoupled in Padi6-KO embryos, suggesting that transcriptomic and proteomic dysregulation need not be linked at early developmental stages.”

• Major Comment 6:

*“6- A large fraction of the manuscript interprets changes in the PADI6 knockout proteomics data as direct evidence that CPLs are associated with specific protein complexes (e.g., ribosomes) or cellular structures (e.g., mitochondria). However, these results are indirect and could alternatively be explained by roles of PADI6 that are independent of CPLs. These conclusions should be tempered, or this limitation should be explicitly acknowledged.”

*

• Response and Incorporated Revision:

We have addressed this comment in the General Statements section discussing links between the CPLs and the mitochondria. Given the previously identified links between protein degradation machinery and ribosomes with the CPLs, we believe the changes are due to the loss of CPLs. We have however included the following statement acknowledging that these defects could be due to alternate function of PADI6 in the Limitations of the study section: “…It is also possible that some differences are due to an alternate defect that alters protein solubility caused by the absence of PADI6 independent of CPL formation.”

• Major Comment 7:

“7- Relatedly, the authors conclude that CPLs are associated with mitochondria based on the CPL proteomics data. Several questions arise: Do the EM images show mitochondria in close proximity to CPLs? Is mitochondrial morphology affected in Padi6-null oocytes? Given that respiratory chain complexes are large, membrane-bound assemblies, how might they associate with CPLs? Could the Triton-insoluble CPL fraction be contaminated with other oocyte-specific superstructures, as the authors themselves allude to? Do the EM images show mitochondria in close proximity to CPLs? Is mitochondrial morphology affected in Padi6-null oocytes?

Reviewer 2:

• Major Comment 5: “5) The authors found that CPLs are associated with mitochondria. How do CPLs in the cytosol interact with the components of the electron transport chain in the mitochondria? Do CPLs directly interact with these proteins in the cytosol or attach to the outer mitochondrial membrane? Does the loss of PADI6 affect the morphology, membrane potential, and ROS production of mitochondria in oocytes?”

• Combined response to reviewer 1 major comment 7 and reviewer 2 major comment 5 and Incorporated Revision: As stated in the general statement, whilst it has been reported that there are defects in mitochondrial localisation in the absence of PADI6 and the CPLs (10.1016/j.ydbio.2010.11.033), it is possible these are not due to direct interactions. Presence of mitochondrial proteins in the CPL-enriched proteome could instead be caused by physical entrapment of the mitochondria by the CPLs. Whilst mitochondrial localization is known to be disrupted in PADI6 knockout oocytes (DOI: 10.1016/j.ydbio.2010.11.033), as additional links between the mitochondria and CPLs are not present in the literature unlike protein degradation machinery, we agree further work would be required to support this claim and have therefore removed the section entitled ‘The CPLs are associated with the oocyte mitochondria’, along with supplementary Figures 6E and 6F. As we did not further discuss links between the CPLs and Mitochondria in either the abstract or discussion, we do not believe the removal of this section significantly affects both the findings and novelty of this work.

• Major Comment 8:

“8-The authors should discuss their findings in the context of Liu et al. 2026 (Nature), which elucidates the structural basis of PADI6 in CPL formation. This comparison would be particularly informative given the overlapping scope of the two studies.”

• Response and Incorporated Revision: As discussed in the general statement, we have included a new discussion of how the published CPL structure papers compare to our manuscript in the general comments section above. We have incorporated the following in the Discussion section of our manuscript: “During preparation of this manuscript, several high-resolution structures of the CPLs were reported80–83. Our proteomic workflow identified all CPL proteins resolved in these published structures as CPL-associated, including the newly identified SCF complex components and several F-box proteins. Notably, whilst highly informative, the structural studies cannot resolve the precise identify of individual proteins from families of structurally homologous proteins that form the CPL core, or of proteins which associate with the CPLs sub-stoichiometrically. One key example is the F-box proteins which offer substrate specificity to the SCF complex. Our proteomic analysis identified 10 different F-box proteins to have CPL-association. By contrast each published structure reports only a single or a few F-box proteins as part of the core complex. Notably different F-box proteins are reported in different structures. Our data provides an explanation for this variation, suggesting that even the core CPL fibres are non-homogeneous in the cell with different F-box proteins present in different locations (Fig 6B). Similarly, the close homology of a/b-tubulin proteins prevents identification of exact isoforms in the reported structures. Our data suggests that many different isoforms contribute to the CPLs (Fig 5E). Additionally, it is proposed that the CPLs act as storage hubs for a much wider range of proteins30. By allowing identification of proteins associated with the CPLs even at low occupancy our CPL-associated proteome provides a list of potential CPL-associated proteins for further structural and functional characterisation of CPL function.”

• Minor Comment 1:

“1- For the scRNA-seq analysis, please expand the methodology for PCA. Specifically, how are read counts normalized prior to PCA? We assume some form of log-normalization was applied, but this is not described in the methods or figure legends.”

• Incorporated Revision: We apologize for this lack of clarity; log normalization was applied. The methods have been updated to the following to describe normalization prior to PCA: “PCA analysis of log normalized CPM values was performed using ScanPy on the full dataset, as well as oocyte, zygote, and 2-cell split data.”

• Minor Comment 2:

“2- Please clarify the z-score calculation for results shown in Figure 3. While the general approach can be inferred from context, the exact calculation is not provided.”

• Incorporated Revision: Z-scores were calculated with the ScanPy scale function, the following has been added into the methods to clarify this: “Transcript Z-scores were calculated using the pp.scale function in the Python package ScanPy…”

• Minor Comment 6:

“6- It is unclear why the authors conclude that PADI6 regulates UHRF1 at the protein level (Figure S5). The observation that UHRF1 levels are reduced in Padi6-null oocytes could simply reflect reduced maternal deposition. The evidence does not appear sufficient to support a specific claim of protein-level regulation by PADI6.”

• Incorporated Revision: We agree that it is possible that the reduced UHRF1 levels could be due to reduced maternal deposition, for example by reduced protein translation levels of UHRF1, and therefore we have amended our conclusion to the following: “…suggesting PADI6 regulates UHRF1 at the protein level or conceivably at the translational level during maternal deposition.”

Reviewer 2:

• Major Comment 4: “4) The authors also found that several proteasome subunits, as well as LAMP1 and RUFY1, were enriched in CPLs. These proteins are known to localize to ELVAs in GV and MII oocytes (Zaffagnini et al., 2024), suggesting functional crosstalk between CPLs and ELVAs. The authors should confirm that these components localize to the CPLs as well as ELVAs by immunostaining or using fluorescently labeled proteins. Are the morphology and localization of ELVAs affected by the loss of PADI6? Do CPLs colocalize or interact with ELVAs during oocyte maturation? It was reported that ELVAs were disassembled when RUFY1 was removed by Trim-Away in oocytes. Does the loss of RUFY1 affect CPL formation?”

• Response and Incorporated Revision: Unfortunately, the only way to directly validate protein localisation to the CPLs is by expansion microscopy, which we do not have the technical capacity to do and therefore cannot perform these experiments in an informative manner. Reviewer #3 agrees with this conclusion: “Although some of the suggestions by Reviewer #2 could provide interesting information, the immunofluorescence experiments suggested in my view are not likely to provide definitive information regarding association of specific proteins or structures with CPLs. Instead, higher resolution technologies such as proximity ligation or immuno-EM might be required. These experiments seem like good ways to extend the findings beyond the current manuscript, but I think are not essential for the major take home points.”

Regarding the morphology and localization of ELVAs in the absence of PADI6, it was recently reported that the number and size of RUFY1 compartments was increased in Padi6-null oocytes (DOI: 10.1038/s41594-026-01758-y). As RUFY1 is the key marker of the ELVAs this suggests that their morphology is likely affected, further pointing towards a functional crosstalk between the two. To highlight this we have added the following sentence in the discussion: “Additionally, recent work identified an increase in the number and size of RUFY1 and ProteoStat positive compartments in Padi6-null oocytes, further pointing towards a functional crosstalk between the ELVA and CPLs.” However, testing whether RUFY1 loss affects CPL formation is beyond the scope of this work investigating the functions of PADI6.

Reviewer 3:

• Major Comment 4: ‘4- Proteomics analysis: The authors carried out proteomics analysis on oocytes treated with Triton X-100 so that they would retain only cytoskeleton-associated proteins. As a control, Padi6-null oocytes (lacking CPLs) were used, and the authors interpret the proteins identified in the WT and not in the Padi6-null as CPL-associated proteins. It is not clear to me that this is a reasonable interpretation of the results. My concern is that the physical meshwork of CPLs may prevent loss of CPL-associated proteins as well as cytoplasmic protein complexes or organelles that are too large to escape the cytoplasm through the CPLs. This is particularly a concern for the authors' conclusions regarding high amounts of ELVA-associated and mitochondrial and mitochondria-associated proteins associated with the CPLs given the large size of these organelles/structures. Is there any evidence by an alternative method of direct association of ELVAs or mitochondria with CPLs? Others have not detected mitochondrial proteins associated with CPLs (see J. Li et al., doi 10.1038/s41594-026-01758-y).”

• Response and Incorporated Revision: We have addressed this comment in the General Statements section entitled “CPLs and other oocyte structures”. We believe links between the CPLs, and protein degradation machinery and the ELVA are well supported by both our data, and the recent and past literature covering the CPLs (DOIs: 10.1038/s41594-026-01758-y, 10.1038/s41586-026-10360-7 ,10.1038/s41586-026-10513-8, 10.1038/s41586-026-10442-6, 10.64898/2026.03.22.713481, 10.1016/j.cell.2024.01.031, 10.1016/j.cell.2023.10.003). As additional links between the mitochondria and CPLs are not present in the literature unlike protein degradation machinery, we have removed the section entitled ‘The CPLs are associated with the oocyte mitochondria’, along with supplementary Figures 6E and 6F. As we did not further discuss links between the CPLs and Mitochondria in either the abstract or discussion, we do not believe the removal of this section significantly affects both the findings and novelty of this work.

Responses to other reviewer comments including analyses that the authors prefer not to carry out

Reviewer 1:

• Major Comment 3: “3-The single-embryo proteomic measurements are an important aspect of the paper. However, additional quality control data are needed to assess data quality. In particular, a more systematic comparison to Ye et al. would strengthen confidence in these measurements.”

• Response: Unfortunately, the Ye et al. work has not released a list of the proteins identified in oocytes and early embryos, or their intensities, therefore we cannot compare in this manner. In terms of overall number of proteins identified the two approaches are comparable, however they differ in both their sample preparation and MS acquisition methods.

• Major Comment 5:

“5- The manuscript refers to the C663A mutation as a "catalytic mutant." While the structural and homology-based rationale is compelling, the entire paper's conclusions depend on this interpretation. Experimental validation of the inferred loss of catalytic activity would substantially strengthen the study.”

• Reviewer 2 Major Comment 1: “1) There is insufficient evidence to conclude that the C663A mutant is catalytically inactive. The authors should conduct an in vitro citrullination assay to show whether wild-type PADI6 has peptidyl arginine deiminase activity, but the C663A mutant loses it.”

• Combined response to reviewer 1 major comment 5 and reviewer 2 major comment 1: We are pleased the Reviewer 1 finds our structural and homology-based rationale for the design of the C663A mutation compelling. As discussed in the general statements, prior to this work no catalytic activity of PADI6 had been observed in vitro, despite contradictory in vivo data regarding its activity. It was this challenge in replicating in vivo conditions that might be required for protein activation in an in vitro assay that directly led us to develop our in vivo mouse model in this work. It is therefore not possible to experimentally validate any change in activity following the C663A mutation as wild-type PADI6 is also inactive under the in vitro assay conditions used for other PADI isozymes. Except when discussing the design of the mouse itself we have been careful to always describe the mouse based on its mutation rather than as a catalytic mutant and have used terms such as “putative” or “potential” in the manuscript to make clear that there is no direct evidence for any catalytic activity that could then be abolished.

• Minor Comment 3:

“3- MII oocytes are used for scRNA-seq experiments and GV oocytes for proteomics. Please provide a rationale for the use of two different developmental stages.”

• Response: The reasons for using MII oocytes over GV oocytes in the RNA-seq experiments was due to availability and sample number requirements. GV oocytes were used in place of MII oocytes for proteomic experiments as it was possible to gather many more GV oocytes per mouse than MII oocytes. Therefore, to increase the number of replicates in the single oocyte/embryo proteomics workflow developed in this work, we chose GV oocytes to increase confidence and show reproducibility.

• Minor Comment 4:

“4- While the data support the conclusion that maternal RNA and minor EGA mRNA degradation is defective, none of the experiments directly measure mRNA degradation. Direct experimental validation, even for a few select targets using standard decay assays, would strengthen this claim.”

• Response: Whilst our data does not directly measure mRNA degradation, we believe our data is sufficient evidence to state that mRNA degradation is defective in the absence of PADI6, in line with other work (DOI: 10.1101/gad.351238.123 and consequently that it would not be appropriate to use further mice for these experiments in line with the 3Rs.

• Minor Comment 5:

*“5- The statement "Together these results indicate that we have established a powerful sub-cellular proteomic workflow from single mouse oocytes capable of identifying proteins associated with the CPLs" overstates the findings. The results are consistent with this interpretation, but the approach described is not a sub-cellular proteomic workflow in the spatial proteomics sense. This language should be revised.”

*

• Response: We agree that our workflow is not a sub-cellular proteomic workflow in the spatial proteomics sense, but we believe our statement and discussion does not claim that our workflow is a spatial proteomic workflow at any point. We therefore do not believe any revision of language is necessary.

• Minor Comment 7:

“7- Many ribosomal, proteasomal, and mitochondrial proteins appear to associate with CPLs in a PADI6-dependent manner. Could an alternative explanation be that maternal deposition of these proteins is globally reduced in Padi6-null oocytes, rather than their association with CPLs being specifically affected?”

• Response: A global reduction in the maternal deposition of CPL-associated proteins would be reflected by a decrease in the levels of these proteins in intact oocytes. As the protein levels of the majority of CPL-associated proteins are not reduced in Padi6-KO oocytes (Figure 6A-B and Figure S6B), and for those that are reduced the effect is generally subtle, this discounts a global reduction in their maternal deposition.

  Reviewer 2:

• Major Comment 2: “2) The author found that the levels of key CPL scaffolding proteins from the SCMC (OOEP, TLE6, NALP5, and KHDC3) were not affected by the loss of PADI6. It should be examined whether the subcellular localization of these proteins is affected in Padi6-deficient and C663A mutant embryos using immunostaining.”

• Major Comment 3: “3) The authors found that CPLs contain components of the SKP1-CUL1-F-box protein (SCF) ubiquitin ligase complex. They also found that hPADI6 interacted with CUL1 when it was transiently transfected into HEK-293T cells. It is important to examine whether the stability or subcellular localization of these proteins is affected by the loss of PADI6 in oocytes.”

• Combined response to reviewer 2 major comment 2 and 3: From our intact GV oocyte proteomics experiments, we know that the stability of the SKP1-CUL-F-box proteins is not affected by the loss of PADI6, similar to the key CPL scaffolding proteins highlighted in major comment 2. Regarding localization, it was reported by Jentoft et al. in 2023 that due to the cytoplasmic abundance of CPL proteins, their true cellular distribution can only be measured by IF using a Halo-tag knock-in line to circumvent the use of secondary antibodies which aggregate at the subcortex. Alternatively, expansion microscopy could be used to determine differences in localization. Unfortunately, we do not have the capacity to generate these lines or perform expansion microscopy and therefore we are not able to conduct these experiments in an informative manner. Reviewer #3 agrees with this conclusion: “Although some of the suggestions by Reviewer #2 could provide interesting information, the immunofluorescence experiments suggested in my view are not likely to provide definitive information regarding association of specific proteins or structures with CPLs. Instead, higher resolution technologies such as proximity ligation or immuno-EM might be required. These experiments seem like good ways to extend the findings beyond the current manuscript, but I think are not essential for the major take home points.”

• Major Comment 6:

“6) Figure 6C, G, and I.

Statistical analysis should be done.”

• Response: We have performed statistical analysis of Figure 6G and demonstrate that the PADI6-N598S variant binding to UHRF1 is statistically significantly impaired (see below). However, the immunoprecipitation assay performed is a largely qualitative assay and we don’t believe that detailed quantification of it is appropriate. Similarly for Figures 6C and 6I we don’t think quantification is necessary as the assay represents presence or absence of a protein in a sample.

Reviewer 3:

• Major Comment 1: “Padi6 catalytic activity: Given that PADI6 was previously shown not to have catalytic activity in vitro, the rationale for doing the experiment mutating Padi6 function is weak. The authors claim that a homologous mutation in human PADI6 does not "significantly damage the folded state of PADI6", but this conclusion does not necessarily mean that a scaffolding or protein interaction function could not be affected by the mutation. The authors provide zero evidence of catalytic activity in the WT oocytes (which I agree would be technically quite challenging given the poor quality/specificity of antibodies that recognize citrullinated proteins and low amount of protein available for mass spec analysis) but still include a full paragraph in the Discussion regarding the potential catalytic activity and why it might be important. This focus implies that the underlying data support the concept, even though the authors do frame the paragraph carefully.”

• Response: We have primarily addressed this comment in the General Statements section of this document. Regarding scaffolding or interactional functions, as shown in our published X-Ray crystal structure of PADI6 (DOI: 10.1016/j.csbj.2024.08.019), the proposed catalytic cysteine is buried, not surface exposed, and doesn’t appear to be involved in structural interactions or disulphide bonds. We cannot however rule out subtle structural changes around the active caused by the C663A mutation resulting in altered protein-protein interaction binding affinities at proteins interacting near to the proposed PADI6 active site. To account for this possibility the following sentences have been added/amended in the discussion to read:

“Given the lack of large-scale structural damage the loss of C663 imparts on PADI6, the possibility of a non-essential catalytic function of PADI6 in oogenesis and early embryo development cannot be ruled out, potentially in the epigenetic regulation of transcription similar to PADI4. Alternatively, it is possible that the C663A substitution alters protein binding affinities for interactions on or near to the proposed PADI6 active site.”

• Major Comment 2:

*“2. Padi6 mutant embryo development: The Padi6 mutant embryo development findings are minimally different from WT controls. The embryos were all cultured in vitro and it is unclear if they would have developed fine in vivo, which is suggested from the lack of a difference in litter sizes, which if anything were slightly higher in the Padi6 mutant females. In the absence of additional useful information regarding why the development was slightly lower, this experiment does not seem to add to the conclusions of the paper but seems more like an incomplete side note that should be more deeply investigated.”

*

• Response: An explanation for the lack of difference in litter sizes but difference in developmental potential has been discussed in the text: “This phenomenon (significant decrease in early embryo numbers in one mouse line over another despite litter sizes remaining comparable) has been observed previously and is attributed to mice, and other species, producing greater numbers of eggs and pre-implantation embryos than the uterus can accommodate, with excess embryos lost during the pre-implantation stage50–52.” The difference in developmental potential is statistically significant for Padi6-C663A embryos. Without an impaired function of PADI6 we do not see how in vitro culture of the embryos would result in such a difference in developmental potential of the mutant compared to the wild type embryos as they were cultured under the same conditions. We agree with the reviewer that we haven’t yet determined the underlying cause for this difference but we think nonetheless that it is an important finding to highlight - that a single cysteine mutation in the active site of PADI6, which does not affect protein structure significantly impacts the development of early-stage embryos.

• Major Comment 3:

“3. Padi6 mutant 2C embryo EGA timing: The altered transcription in the Padi6 mutant 2C embryos appears to indicate that they are ahead in development relative to the WT based on the PCA plot and the relative downregulation of minor ZGA genes and upregulation of major ZGA genes. The 1-cell embryos were collected from spontaneously ovulating mice and the time of development was not controlled in any way. Mouse embryos are quite variable in their exact timing of development, even across different embryos in the same mouse. I find these changes in transcription likely to be explained by differences in developmental timing and I don't think the authors have robustly shown "dysregulation of EGA". Similarly, the delay in development of the Padi6-null embryos from zygote to 2C (Figure 1D) explains why the maternal mRNAs are upregulated in the Padi6-null mice - they are simply delayed in development.”

• Response: When harvesting 2-cell embryos, samples from all four mice were harvested on different days at the same time of day. If the differences between samples were only due to differences in developmental timing we would anticipate as significant differences between the embryos from mice with the same genotype as between those from different genotypes which is not what we observe. Given the significant developmental defects observed in these embryos (Figure 1), it is highly likely these are associated with defects on the transcriptional level. Furthermore, we observed a small but significant delay in Padi6-C663A embryos reaching the 2-cell stage (Figure 1D) which we believe makes it highly unlikely that the embryos from both C663A females were further along in development compared to those from both wild-type females.

The reviewer states that the upregulation of major EGA genes and downregulation of minor EGA genes further points toward an advancement in development. If this is the case, then it would be expected that there would also be increased degradation of maternal transcripts which decrease between the zygote and 2-cell stage in wild-type embryos. We do not see a further decrease of these transcripts in Padi6-C663A embryos. Finally, the reviewer notes the PCA plot as a reason for being advanced in development – PCA only measures differences between samples, not developmental time.

Taking into account the above, we do not agree with the reviewer’s interpretation of our data. Regarding Padi6-null mice, disrupted EGA has been reported in Padi6-null mice in other work (DOI: 10.1101/gad.351238.123.).

• Minor Comment 1:

“1. What was the point of splitting up the 2C embryo blastomeres rather than treating them as single embryos?”

• Response: 2C embryos were split up to investigate whether defects in Padi6-null 2-cell embryos were due to asymmetric inheritance of transcripts given the significant mis-localization of various oocyte structures in the absence of PADI6. As this was not clear in the text, we have added the following sentence clarifying the rationale and referencing Figure S4C-D where the transcriptomic correlation between blastomeres is shown: “The transcriptomes of separated blastomeres of the same 2-cell embryo showed high levels of correlation for embryos of each genotype suggesting asymmetric inheritance of transcripts is not a cause of PADI6 associated developmental defects (Figure S4C-D).”.

• Minor Comment 2:

“2. Proteomics - Because PADI6 makes up a significant fraction of total oocyte protein, and the Padi6-null oocytes don't have any PADI6, does this artificially increase the relative amount of the remaining proteins?”

• Response: Any such effect would have been corrected during data normalization.

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Referee #3

Evidence, reproducibility and clarity

Summary:

PADI6 is a highly abundant oocyte-specific protein and component of cytoplasmic lattices (CPLs). The current study attempts to better characterize mouse PADI6 function and CPL-associated proteins using a novel Padi6 mutant allele (predicted to be catalytically dead), RNA sequencing, and single oocyte proteomics approaches. Key findings reported are:

1. Validation of known Padi6-null female mouse phenotypes including infertility, disruption of CPL formation, impaired embryonic genome activation, and abnormal maternal mRNA degradation.
2. Mice homozygous for the Padi6-mutant allele, when mated to WT males, have a slight impairment in preimplantation embryo development in vitro but have normal fertility as indicated by average litter sizes.
3. CPLs are enriched in ribosomal proteins, proteins involved in protein degradation including ubiquitination proteins, and mitochondria. Several of the protein interactions with PADI6 were validated by showing co-immunoprecipitation of epitope-tagged proteins expressed in HEK-293 cells (UHRF1, UBE2D2, and CUL1).

Major comments:

• Are the key conclusions convincing?

• Padi6 catalytic activity: Given that PADI6 was previously shown not to have catalytic activity in vitro, the rationale for doing the experiment mutating Padi6 function is weak. The authors claim that a homologous mutation in human PADI6 does not "significantly damage the folded state of PADI6", but this conclusion does not necessarily mean that a scaffolding or protein interaction function could not be affected by the mutation. The authors provide zero evidence of catalytic activity in the WT oocytes (which I agree would be technically quite challenging given the poor quality/specificity of antibodies that recognize citrullinated proteins and low amount of protein available for mass spec analysis) but still include a full paragraph in the Discussion regarding the potential catalytic activity and why it might be important. This focus implies that the underlying data support the concept, even though the authors do frame the paragraph carefully.

• Padi6 mutant embryo development: The Padi6 mutant embryo development findings are minimally different from WT controls. The embryos were all cultured in vitro and it is unclear if they would have developed fine in vivo, which is suggested from the lack of a difference in litter sizes, which if anything were slightly higher in the Padi6 mutant females. In the absence of additional useful information regarding why the development was slightly lower, this experiment does not seem to add to the conclusions of the paper but seems more like an incomplete side note that should be more deeply investigated.
• Padi6 mutant 2C embryo EGA timing: The altered transcription in the Padi6 mutant 2C embryos appears to indicate that they are ahead in development relative to the WT based on the PCA plot and the relative downregulation of minor ZGA genes and upregulation of major ZGA genes. The 1-cell embryos were collected from spontaneously ovulating mice and the time of development was not controlled in any way. Mouse embryos are quite variable in their exact timing of development, even across different embryos in the same mouse. I find these changes in transcription likely to be explained by differences in developmental timing and I don't think the authors have robustly shown "dysregulation of EGA". Similarly, the delay in development of the Padi6-null embryos from zygote to 2C (Figure 1D) explains why the maternal mRNAs are upregulated in the Padi6-null mice - they are simply delayed in development.
• Proteomics analysis: The authors carried out proteomics analysis on oocytes treated with Triton X-100 so that they would retain only cytoskeleton-associated proteins. As a control, Padi6-null oocytes (lacking CPLs) were used, and the authors interpret the proteins identified in the WT and not in the Padi6-null as CPL-associated proteins. It is not clear to me that this is a reasonable interpretation of the results. My concern is that the physical meshwork of CPLs may prevent loss of CPL-associated proteins as well as cytoplasmic protein complexes or organelles that are too large to escape the cytoplasm through the CPLs. This is particularly a concern for the authors' conclusions regarding high amounts of ELVA-associated and mitochondrial and mitochondria-associated proteins associated with the CPLs given the large size of these organelles/structures. Is there any evidence by an alternative method of direct association of ELVAs or mitochondria with CPLs? Others have not detected mitochondrial proteins associated with CPLs (see J. Li et al., doi 10.1038/s41594-026-01758-y).
• Are the data and the methods presented in such a way that they can be reproduced?

The authors should be congratulated on the clarity and thoroughness of the Methods and Results descriptions in this manuscript. I have rarely seen this done so nicely. - Are the experiments adequately replicated and statistical analysis adequate?

The experiments were replicated and analyzed appropriately.

Minor comments:

Points for clarification:

1. What was the point of splitting up the 2C embryo blastomeres rather than treating them as single embryos?
2. Proteomics - Because PADI6 makes up a significant fraction of total oocyte protein, and the Padi6-null oocytes don't have any PADI6, does this artificially increase the relative amount of the remaining proteins?

Referees cross-commenting

It was interesting to read the additional reviews on this manuscript. Regarding Reviewer #1's points, we seem to be in agreement, in particular regarding major comment 7 regarding the possibility that the Triton-insoluble CPL fraction may be contaminated with other oocyte-specific superstructures. We all had concerns regarding the lack of evidence that PADI6 has catalytic activity and the point mutant does not, which impacts interpretation of many of the embryo development experiments.

Although some of the suggestions by Reviewer #2 could provide interesting information, the immunofluorescence experiments suggested in my view are not likely to provide definitive information regarding association of specific proteins or structures with CPLs. Instead, higher resolution technologies such as proximity ligation or immuno-EM might be required. These experiments seem like good ways to extend the findings beyond the current manuscript, but I think are not essential for the major take home points.

Significance

There are several very recent publications on CPLs, including two recently accepted papers (March 2026) reporting the structure of CPLs and associated proteins detected in situ or after CPL purification using cryo-EM and mass spec analysis (Chi et al., doi 10.1038/s41586-026-10442-6; Liu et al., doi 10.1038/s41586-026-10360-7). The associated proteins include UHRF1, tubulin proteins, and ubiquitin ligase components, similar to what was shown in the current manuscript. A third paper, also published in March 2026 (J. Li et al., doi 10.1038/s41594-026-01758-y), used cryo-EM and IP-mass spec combined with mutagenesis to draw similar conclusions. This manuscript specifically comments on the lack of associated mitochondrial proteins, conflicting with the current manuscript. Finally, a preprint (Y. Li et al, doi 10.64898/2026.03.30.715190) on the same topic was posted on bioRxiv April 1, 2026; similar methods were used and similar conclusions were drawn. The current manuscript stands out for using Padi6-null oocytes as a control, which in theory could improve the mass spec results to improve information regarding the extent and identity of associated proteins over what was done in these manuscripts (though see above for concerns related to this point). Further, if the authors were able to conclusively show that PADI6 catalytic activity played a role in preimplantation embryo development, it would be quite distinct from these papers that are focused on CPL structure and associated proteins.

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

The audience for this paper would be reproductive biologists or clinical infertility scientists, given the relevance to human Padi mutations. Should the Padi6 catalytic activity be defined and relevant to oocytes and early embryos, interest would be broadened to more general epigenetics of development and nuclear reprogramming. - 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.

Field of expertise: Reproductive biology, oocyte physiology, embryonic genome activation, epigenetics Lack of expertise: Proteomics

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Referee #2

Evidence, reproducibility and clarity

In this manuscript, the authors investigated the role of PADI6, which belongs to the peptidyl arginine deiminase (PADI) family and is involved in the formation of cytoplasmic lattices (CPLs) in oocytes, in mouse female fertility. The authors generated Padi6-deficient mice and C663A mutant mice, which are assumed to lose the catalytic activity of PADI6, and examined these mice in detail. The authors found that Padi6-/- mice were infertile, but the C663A mutant mice were not, although they showed a small reduction in their developmental potential. The authors also found that CPLs normally exist in GV oocytes of C663A mutant mice, whereas they disappear in PADI6-deficient GV oocytes. In addition, the authors conducted scRNA-seq analyses on MII oocytes, zygotes, and blastomeres from 2-cell embryos and found that Padi6-deficient and C663A mutant embryos resulted in different transcriptome defects, leading to defective EGA. They also performed single-cell proteomic analyses of wild-type and mutant oocytes and embryos and found that the loss of PADI6 caused drastic protein dysregulation. Finally, the authors conducted proteomic analysis of CPLs isolated from control, PADI6-deficeit and mutant oocytes and revealed that PADI6 mediates the association of some components of the ubiquitination machinery, ELVAs, and mitochondria with CPLs. These results suggest that PADI6 functions as a scaffold protein in CPL formation and regulates translation, respiration, and protein degradation in oocytes and early embryos. A detailed analysis of PADI6 functions in mouse oocytes and embryos and the establishment of a proteomic workflow for a single oocyte and embryo are appreciated, and the potential consequences of this work are interesting. However, since the role of PADI6 in CPL formation, early development, and female fertility has already been reported, further analysis is necessary to offer novelty and mechanistic insights that go beyond previous research.<br /> I have enlisted several major concerns that may help the authors address these issues.

Major comments

1) There is insufficient evidence to conclude that the C663A mutant is catalytically inactive. The authors should conduct an in vitro citrullination assay to show whether wild-type PADI6 has peptidyl arginine deiminase activity, but the C663A mutant loses it.

2) The author found that the levels of key CPL scaffolding proteins from the SCMC (OOEP, TLE6, NALP5, and KHDC3) were not affected by the loss of PADI6. It should be examined whether the subcellular localization of these proteins is affected in Padi6-deficient and C663A mutant embryos using immunostaining.

3) The authors found that CPLs contain components of the SKP1-CUL1-F-box protein (SCF) ubiquitin ligase complex. They also found that hPADI6 interacted with CUL1 when it was transiently transfected into HEK-293T cells. It is important to examine whether the stability or subcellular localization of these proteins is affected by the loss of PADI6 in oocytes.

4) The authors also found that several proteasome subunits, as well as LAMP1 and RUFY1, were enriched in CPLs. These proteins are known to localize to ELVAs in GV and MII oocytes (Zaffagnini et al., 2024), suggesting functional crosstalk between CPLs and ELVAs. The authors should confirm that these components localize to the CPLs as well as ELVAs by immunostaining or using fluorescently labeled proteins. Are the morphology and localization of ELVAs affected by the loss of PADI6? Do CPLs colocalize or interact with ELVAs during oocyte maturation? It was reported that ELVAs were disassembled when RUFY1 was removed by Trim-Away in oocytes. Does the loss of RUFY1 affect CPL formation?

5) The authors found that CPLs are associated with mitochondria. How do CPLs in the cytosol interact with the components of the electron transport chain in the mitochondria? Do CPLs directly interact with these proteins in the cytosol or attach to the outer mitochondrial membrane? Does the loss of PADI6 affect the morphology, membrane potential, and ROS production of mitochondria in oocytes?

6) Figure 6C, G, and I. Statistical analysis should be done.

Significance

This study provide the information of PADI6 function in CPL formation, early development, and female fertility.

The authors established single oocyte proteomic analysis and CPL isolation method, which are useful to examine the protein content in mouse oocytes and embryos.

This study is likely to be of interest to basic and clinical researchers.

My expertise is developmental and cell biology.

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Referee #1

Evidence, reproducibility and clarity

Summary:

This study characterizes two mouse models with mutations in Padi6, a protein central to maternal protein storage and cytoplasmic lattice formation. The authors perform proteomics and transcriptomics experiments using a knockout and a C663A point mutant, framing their results effectively within the substantial existing literature on PADI6. The most significant advance is the generation and characterization of the C663A mutation, which is interpreted as a catalytic-dead variant. While the structural and homology-based rationale for this interpretation is compelling, several conclusions would benefit from additional experimental validation or more cautious framing. The computational methods also require greater methodological detail.

Major comments:

1. TThe methods for differential gene expression analysis are insufficiently described. Were these calculated using Scanpy? If so, the rationale for this choice should be provided, as the number of replicates and the nature of the data appear more suited to standard bulk differential expression frameworks such as DESeq2 or edgeR.
2. In Figure 4C, it is unclear what correlation is being calculated. Additionally, the methods state that differential protein abundance was determined using the same approach as the scRNA-seq analysis. Given the lack of methodological clarity noted above, it is difficult to evaluate these results. The authors should justify whether the chosen method is compatible with the normalization approach used for the proteomics data.
3. The single-embryo proteomic measurements are an important aspect of the paper. However, additional quality control data are needed to assess data quality. In particular, a more systematic comparison to Ye et al. would strengthen confidence in these measurements.
4. A notable result is the complete lack of correspondence between differential RNA-seq and proteomics in 2-cell embryos. The authors state that "This is consistent with data showing that minimal translation occurs in the 2-cell embryo, with the first large translational wave only occurring in the morula," citing Israel et al. 2019. This statement is factually incorrect. The cited study did not measure translation directly. Recent work that specifically measured translation during preimplantation development has demonstrated that translation is highly dynamic throughout these stages (Ozadam et al. 2023, Nature). This claim should be corrected and the results discussed in the context of these more recent findings.
5. The manuscript refers to the C663A mutation as a "catalytic mutant." While the structural and homology-based rationale is compelling, the entire paper's conclusions depend on this interpretation. Experimental validation of the inferred loss of catalytic activity would substantially strengthen the study.
6. A large fraction of the manuscript interprets changes in the PADI6 knockout proteomics data as direct evidence that CPLs are associated with specific protein complexes (e.g., ribosomes) or cellular structures (e.g., mitochondria). However, these results are indirect and could alternatively be explained by roles of PADI6 that are independent of CPLs. These conclusions should be tempered, or this limitation should be explicitly acknowledged.
7. Relatedly, the authors conclude that CPLs are associated with mitochondria based on the CPL proteomics data. Several questions arise: Do the EM images show mitochondria in close proximity to CPLs? Is mitochondrial morphology affected in Padi6-null oocytes? Given that respiratory chain complexes are large, membrane-bound assemblies, how might they associate with CPLs? Could the Triton-insoluble CPL fraction be contaminated with other oocyte-specific superstructures, as the authors themselves allude to?
8. The authors should discuss their findings in the context of Liu et al. 2026 (Nature), which elucidates the structural basis of PADI6 in CPL formation. This comparison would be particularly informative given the overlapping scope of the two studies.

Minor comments:

1. For the scRNA-seq analysis, please expand the methodology for PCA. Specifically, how are read counts normalized prior to PCA? We assume some form of log-normalization was applied, but this is not described in the methods or figure legends.
2. Please clarify the z-score calculation for results shown in Figure 3. While the general approach can be inferred from context, the exact calculation is not provided.
3. MII oocytes are used for scRNA-seq experiments and GV oocytes for proteomics. Please provide a rationale for the use of two different developmental stages.
4. While the data support the conclusion that maternal RNA and minor EGA mRNA degradation is defective, none of the experiments directly measure mRNA degradation. Direct experimental validation, even for a few select targets using standard decay assays, would strengthen this claim.
5. The statement "Together these results indicate that we have established a powerful sub-cellular proteomic workflow from single mouse oocytes capable of identifying proteins associated with the CPLs" overstates the findings. The results are consistent with this interpretation, but the approach described is not a sub-cellular proteomic workflow in the spatial proteomics sense. This language should be revised.
6. It is unclear why the authors conclude that PADI6 regulates UHRF1 at the protein level (Figure S5). The observation that UHRF1 levels are reduced in Padi6-null oocytes could simply reflect reduced maternal deposition. The evidence does not appear sufficient to support a specific claim of protein-level regulation by PADI6.
7. Many ribosomal, proteasomal, and mitochondrial proteins appear to associate with CPLs in a PADI6-dependent manner. Could an alternative explanation be that maternal deposition of these proteins is globally reduced in Padi6-null oocytes, rather than their association with CPLs being specifically affected?
8. Although the authors discuss limitations of their study, more pertinent caveats, such as those raised above regarding indirect inference, would be appropriate for the limitations section.
9. We were unable to access the zenodo link. Please make sure this is available for the code to be reviewed.

Significance

General Assessment: The principal strength of this study is the generation and characterization of the PADI6 C663A point mutant. The authors contextualize their findings within the extensive existing literature on PADI6 and CPLs. The recent structural characterization of PADI6 in CPL formation by Liu et al. 2026 provides a complementary perspective that should be discussed alongside the current findings. Several key conclusions rest on indirect inference. The catalytic-dead interpretation of the C663A mutant, while structurally well-motivated, also lacks direct experimental validation. Additionally, the computational methods require better description to allow proper evaluation of the differential expression analyses.

Advance: The generation and characterization of a mouse model with a putative catalytic-dead PADI6 mutant represents a significant advance and will be an important contribution to the field.

Audience: This work will be of primary interest to a specialized audience studying oocyte biology, and preimplantation embryonic development. In our opinion, the study is unlikely to attract broad attention beyond these fields.

Reviewer Expertise: Computational biology, gene expression in early embryonic development

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Reply to the reviewers

1. General Statements

We thank the reviewers for their constructive criticisms and helpful suggestions.

2. Description of the planned revisions

Point-by-point reply explaining what revisions, additional experimentations and analyses are planned to address the points raised by the referees.

Reviewer #1

(Note: to see the Figures in our response we refer to the document Revision-plan_RC-2026-03552)

Summary: This study examines how simultaneous expression of high levels of alpha and beta tubulin impact microtubule organization, cell cycle progression and stress response. The main conclusions are that a/b tubulin overexpression 1) increases the density of microtubules in cells with mild effects on growth rate and catastrophe frequency; 2) causes mitotic spindle defects and cell cycle disruption; 3) alters the transcriptome and proteostasis; 4) causes mitochondrial stress by binding mitochondrial import proteins; 5) disrupts cellular stress response.

Major comments:

The results generally use an appropriate number of cells and technical replicates.

There are several instances in the manuscript where the data do not support the authors' conclusions. These include:

Page 6. "We detected a mild increase in MT growth rates in Dox-treated cells (Fig. 2b), which was observed in all of the growing MTs examined (Fig. 2c), consistent with an increase in soluble tubulin levels in all Dox-induced cells." The data do not support this statement. The histogram in Figure 2C shows that only a small portion of growth rate measurements are faster in the overexpression cells, and the statistical test in 2b suggests that the datasets are unlikely to be different. It is unclear from the presentation of the data why a small population of overexpression cells exhibit faster growth rates. The data in Figure 2b should be plotted as a superplot could show whether the faster data points are from specific cells or technical replicates. The same concern applies to the data in Figure 2D.

Answer:

We agree that an overlaid density plot as currently shown in Fig. 2c might visually suggest that only the non-overlapping tail differs between conditions, but this is not what the underlying data show. Comparison of individual comet measurements indicates that the entire Dox distribution is shifted toward faster speeds (as we state in the text), not a small subpopulation: a randomly selected Dox comet is faster than a randomly selected Ctrl comet in 62% of pairwise comparisons (50% expected if the groups were identical), and 69% of Dox comets exceed the Ctrl median speed. We have added a cumulative distribution plot (see Figure below) that makes this more explicit — the Dox curve runs to the right of Ctrl across essentially the entire range, rather than only in a discrete high-speed segment. We acknowledge that our previous Figure panel may not have represented the data properly and propose to replace current Fig. 2c with this new plot.

New Fig. 2c. Cumulative distribution plot of EB3-GFP comets (displacements in time).

Note: to see the Figures in our response we refer to the document Revision-plan_RC-2026-03552

Regarding the statistic in Fig. 2b: the reported P = 0.057 is from a test comparing group means. However, the Dox distribution is right-skewed and borderline non-normal (Shapiro-Wilk P = 0.054), and we realized that this is a condition under which a mean-comparison test is not well powered. A Mann-Whitney U test, which compares the full rank distribution and is more appropriate for data of this shape, gives P = 0.013 (Kolmogorov-Smirnov P = 0.0043). We will add these results and the effect-size measures mentioned above to a revised manuscript, and will report the rank-based test as the primary statistic for this comparison in the revised manuscript. All in all, we hope this clarifies that the effect is a genuine population-wide shift in comet speed. Note that we agree with the reviewer that the data should be plotted as a superplot in Fig. 2b, and we will do this in a revised manuscript.

For the data presented in Fig. 2d (duration of EB3-GFP displacements), we performed a similar analysis as described above. In contrast to Fig. 2c no significant changes are seen in duration, and here the concern of the reviewer is justified. We will indicate this clearly in the text. It does not change any of our conclusions.

Page 11. "Moreover, DNA content was highly aberrant after 48 hr, with large proportions of cells containing 4n chromosomes (Fig. 4d). Thus, persistent overexpression of tubulin affects the cell cycle and after 48 hr it results in severe DNA abnormalities, suggestive of CIN". The plot in Figure 4D shows increased propidium iodide signal below the 2N peak and above the 4N peak, but it is quite likely that this could represent signal from apoptotic cells. The authors should specifically stain for an apoptotic marker to test this possibility. This would suggest that prolonged overexpression of a/b tubulin leads to apoptosis, which could be important evidence for later conclusions in the study.

Answer:

We agree with the reviewer. We actually thought along the same lines and already performed the apoptosis experiment by staining tubulin overexpressing cells (dox) and control cells (ctrl) with Annexin, an apoptosis marker, and propidium iodide. We then quantified double-stained cells. The experiment was performed in triplicate. As shown in the Figure below (averages ± SEM), the data do not reveal differences in apoptosis. We therefore did not include these results in the original manuscript. However, based on the comment of the reviewer we will now include these data in a revised version of the manuscript. The conclusion is that tubulin overexpression does not lead to increased apoptosis.

Apoptosis Figure.

Note: to see the Figures in our response we refer to the document Revision-plan_RC-2026-03552

Page 11. "Combined, our data show that tubulin overexpression affects all three major cell cycle checkpoints, i.e. G1/S, G2/M, and the SAC in mitosis." The data do not fully support this conclusion. While the evidence for SAC-mediated delay in overexpression cells is strong, the evidence for other checkpoints is weak. The phosphor-RB experiment in Figure S3b lacks a positive control. The γH2A-X results in Figure 4f and g show that the difference is driven by a minor population of dim foci in control cells. Similar to the point above, these data should be plotted as a superplot to explore the possibility that this minor population arises from a small number of cells or a specific technical replicate.

Answer:

With respect to the “inclusion of a positive control”, we are not sure what is meant by the reviewer. Total RB is shown underneath the phosphor-RB lane, and underneath that lane we show a tubulin blot. Moreover, mass spectrometry data are included in Table 1, showing the levels of many other proteins. Note that both the western blot and proteomics data reveal similar RB1 levels in Ctrl and Dox cells.

New Fig. 4g. Cumulative distribution plot of 𝛾-H2AX foci intensity.

Note: to see the Figures in our response we refer to the document Revision-plan_RC-2026-03552

With respect to the γH2A-X results in Figure 4f and g, we re-analyzed and re-plotted the data as described above for Fig. 2c. A cumulative distribution plot, depicted above, clearly shows separation of the two populations. We ran several statistical tests, which all show highly siginificant values (Welch P = 1.5e-17, Mann-Whitney P = 3.2e-17, KS P = 1.1e-14). We propose to change the current Fig. 4g with the plot shown above, and we will indicate statistical tests.

We then tested the reviewer's proposal (driven by a minor population of dim foci in control cells) by fitting a 2-component Gaussian mixture to each condition separately. The table below shows close to the opposite of the reviewer's hypothesis. Both Ctrl and Dox contain the same two-population structure in similar proportions (roughly 75%/25%). The minor subpopulation is therefore not unique to Ctrl, but a feature of both conditions. Perhaps it is a cell-cycle-linked fraction. When we next compared the matched components directly we observed that the majority/lower-intensity component is shifted (102 → 112 AU, P = 1.5e-30), while the minor/higher-intensity component is statistically indistinguishable between conditions (143 vs. 146 AU, P = 0.11, ns). Thus, if anything, the effect is carried by the bulk population, and the minor subpopulation is the part that does not differ. All data are summarized in the table below.

2-component Gaussian mixture decomposition

Ctrl weight

Ctrl mean (AU)

Dox weight

Dox mean (AU)

Lower-intensity component

~78%

101.7

~71%

111.9

Higher-intensity component

~22%

143.3

~29%

146.3

Page 19. "This, in turn, lowers EEF1A1 causing attenuation of translation and dampened elongation rates. That other initiation and elongation factors are mildly down in Dox-induced cells, as are ribosomal proteins (Fig S6c, Table S1), indicates a mild ISR and general translation inhibition. We propose that tubulin overexpression results in mitochondrial dysfunction leading to stress and attenuated translation elongation. We observe the start of an ISR in these cells, which prevents a proper hypoxic response." This conclusion seems to be at odds with the earlier conclusion drawn from Figure 5e, where ISR genes are significantly decreased in overexpression cells. The authors should reconcile these results in the discussion.

Answer:

Our proteomics data suggest that attenuated translation elongation caused by lower EEF1A1 levels hampers the integrated stress response (ISR) in Dox-induced cells. One can intuitively understand this: translation is already lowered, it does not need to be lowered much further via the ISR. Thus, in Dox-induced cells the ISR is hampered compared to control cells, which do not suffer from mito-stress. In other words, the ISR is set in motion in Dox-induced cells but less compared to control cells. This is exactly what we see in the RNA-Sequencing experiments, where in Dox-induced cells mRNAs encoding proteins in volved in HIF-1 and PKR signaling (reflecting ISR) are down (Fig. 5e, right hand panel). Thus, ISR is hampered at the RNA level when tubulin is overexpressed. While we thought we had explained our view well enough on page 19, we realize that this may not have been the case and we will provide an improved explanation in the Discussion section of a revised manuscript.

Figure 7. This experiment lacks a key control - identifying peptides in a pull down from cells that do not overexpress the tagged tubulin. Without this control, it is impossible to discern which peptides bind to the beads, independent of tubulin. This concern is amplified by the results in Figure 7b where TIMM50 binding is tested in a follow-up experiment. Here the negative control is employed and it shows that TIMM50 pulls down in the absence of tagged tubulin. This indicates that TIMM50 may not bind to tubulin and calls into question any conclusions related to TIMM50 and mitochondrial proteostasis. Before making any conclusions from the pull down experiment, the authors must include the negative control and carefully assess which peptides are likely to be false positives.

Answer:

In contrast to what the reviewer states a negative control was included. As described on page 19: “Using beads coupled to ALFA-tag antibodies, we affinity-purified recombinant tubulin and tubulin-associated proteins (TAPs) from cell lysates of tubulin overexpressing cells, using non-induced cells as controls”. To make this more clear we propose to include a plot in Figure 7 showing the fold enrichment of TAPs in the dox-induced versus Ctrl cells.

The reason that TIMM50 enrichment in the recombinant tubulin pull down is not high is explained on page 21 of the manuscript: “We note that the relatively weak enrichment of TIMM50 on beads containing recombinant tubulins (Fig. 7b, lower blot, Table S1) as compared to the enrichment of the recombinant tubulins themselves (Fig. 7b, upper and middle blots, Table S1) is well explained, first by a low affinity of the tubulin-TIMM50 interaction itself, and second by competition for TIMM50 between recombinant tubulins, which are enriched after washing, and the much larger reservoir of endogenous tubulins, which are lost (together with TIMM50) after washing”.

While we believe that the weak enrichment of TIMM50 is well explained in the current set-up, we nevertheless feel that the tubulin-TIMM50 interaction should be further corroborated and we propose to perform a new experiment where we tag both TIMM50 (and AIFM) in addition to our dual tubulin constructs and show - via dual affinity purification - that the proteins do interact.

Figure 8. This figure and the associated text feel rather disconnected from the rest of the study. The authors do not make clear conclusions from these results. Perhaps these experiments should be further developed in a separate study?

Answer:

The physiological relevance of autoregulation is still largely unknown. Our analysis in Figure 8, where we show that autoregulation is activated upon stress (i.e. hypoxia and Gln deprivation), provides a clue. Moreover, we show that disruption of normal tubulin levels, which induces stress, dampens the hypoxic response. We believe these reciprocal effects fit nicely. However, since reviewer 2 is of the same opinion as this reviewer we are willing to remove the data in a revised version of the manuscript.

Page 25. "We found that tubulin overexpression induces mitochondrial dysfunction." The data do not strongly support this conclusion. The proteomic data in Figure 6 indicate that some mitochondrial proteins are less abundant in tubulin overexpressing cells, but the study does not include any experiments that actually test mitochondrial function. The authors could test this by including new experiments to measure mitochondrial membrane potential, or respiration activity, etc. These would be an important addition to the study.

Answer:

We agree with this criticism and will perform additional experiments in a revised version of the manuscript to describe mitochondrial dysfunction.

Page 26. "We provide evidence here that surplus tubulin slows general translation, increasing the time window for a TTC5-nascent tubulin interaction." The data do not demonstrate a decrease in translation rate. It is unclear what evidence the authors refer to with this statement. The proteomic analysis in Figure 6 measures protein abundance, and a decrease could be due to either decreased transcription, decreased translation, or increased protein degradation. The number of proteins that are shown to be downregulated in tubulin overexpressing cells is rather small (100s) which seems to argue against a general decrease in translation, despite the decrease in several translation regulators. To make this conclusion, the authors would need to add new experiments that measure translation rate.

Answer:

While we agree with the reviewer that “protein decrease could be due to either decreased transcription, decreased translation, or increased protein degradation”, we provide evidence below that, at least in our view, excludes transcription and degradation as mechanisms. We do agree that we should provide more compelling evidence that attenuated translation is at work in tubulin overexpressing cells. We will therefore perform an assay to measure translation rates in tubulin overexpressing and control cells.

Having stated which new experiment we will perform in a revised version of the manuscript, we now would like to extensively react to the above comment of the reviewer using our existing data. First, the reviewer argues that “the number of proteins that are shown to be downregulated in tubulin overexpressing cells is rather small (100s)”. However, this applies to the signficantly differentially expressed proteins (DEPs) and "only hundreds of proteins pass significance" is a power argument, not an effect-size argument. In Fig. 7c (heatmap) and Fig. S6b (probability distributions) we show that the whole population of 8224 proteins is down-regulated in Dox-induced cells.

We visualize probability distributions again in the Figure below, but this time we analyzed both proteomic data and matching transcriptomic data.

New Fig. S6. Probability distributions of proteomes and transcriptomes (a) and directionality of changes (b) comparing Dox-induced cells (Dox) to control cells.

Note: to see the Figures in our response we refer to the document Revision-plan_RC-2026-03552

At the protein level the median protein log2-fold change (L2FC) is -0.144. The mean L2FC is -0.149, which is highly similar to the median, indicating that the whole population shifts in a similar manner (panel a). Indeed, as shown in panel b the directionality of the change at the protein level is 91%. Thus, 91% of proteins is down in tubulin overexpressing cells. This effectively rules out protein degradation as a mechanism for decreased protein levels, as degradation is highly unlikely to be so aspecific.

Using our RNA-Seq dataset we analyzed the mRNA levels corresponding to the 8224 proteins in the proteomics analysis. In panel a of the Figure it can be seen that the median mRNA log2-fold change (L2FC) is 0.008, which is close to zero. Panel b shows that directionality of change is 45.7%, which is close to 50%, and is essentially what one would expect from distributions around zero. The Wilcoxon effect size (r) is 0.76 for protein, which is large, and 0.09 for mRNA, which is trivial. These data strongly suggest that transcription plays no role in the downregulation of the 8224 proteins in tubulin overexpressing cells. Thus, neither protein degradation nor transcription appear to play a role in the downregulation of proteins in tubulin overexpressing cells. We propose to add these new data to our revised manuscript and change current Fig. S6b for the new Fig. S6.

Minor comments:

Page 10." We also observed "extra-mitotic" centrioles at the onset of mitosis after Dox-treatment, indicative of mitotic arrest and aneuploidy, which eventually resolved into normal metaphase plates (Supplementary Videos 3, 4)." It is unclear whether these foci are centrioles. The SiR-tubulin reagent used in these experiment labels tubulin. It would be more accurate to describe these as "tubulin foci".

Answer:

We thank the reviewer for this comment. We will modify the text.

Page 13. "Analysis of TUBG1 reads revealed downregulation in tubulin overexpressing cells, albeit weakly (Fig. 5c)." These datapoints appear to be quite similar. Please provide a statistical analysis.

Answer:

The reviewer is correct, datapoints are quite similar. DESeq2 analysis reveals the difference in expression is minimal but significant (Dox vs Ctrl, log2fold change -0.111, p-value 0.016). These data are shown in Table S1 (sheet: DESeq2 24 hr).

Reviewer #2

Note: to see the Figures in our response we refer to the document Revision-plan_RC-2026-03552

Summary: This study develops an inducible HEK293F cell model that modestly overexpresses αβ-tubulin heterodimers. Using a dual expression system, the authors introduce exogenous TUBB3 and TUBA1A and combine cell biology, live-cell imaging, RNA-seq, proteomics, flow cytometry, and biochemistry to investigate the consequences of increased tubulin abundance. They suggest that, despite downregulation of endogenous tubulin transcripts, excess tubulin still accumulates in cells. This is accompanied by increased microtubule mass, changes in plus-end protein composition, defects in mitosis, and alterations in cell-cycle progression. The study further links tubulin overexpression to replication stress and broader changes in cellular physiology, including reduced abundance of mitochondrial respiratory proteins, altered translation-associated factors, and an attenuated response to hypoxic stress. In addition, the authors confirm previous observations that oxygen and nutrient deprivation reduce tubulin and microtubule abundance. Based on these findings, the authors propose that tubulin is not merely a structural component of microtubules but also contributes to the regulation of cellular homeostasis.

The possibility that tubulin abundance itself influences broader aspects of cellular physiology is conceptually interesting and warrants further investigation. At the same time, many of the mechanistic links proposed in the manuscript remain insufficiently resolved. A large number of cellular processes are associated with tubulin overexpression, but it is often unclear which phenotypes represent primary consequences of altered tubulin abundance and which are secondary responses. For instance, conclusions regarding mitochondrial dysfunction and translation attenuation are inferred from omic signatures rather than direct functional tests. Similarly, while the authors propose that altered tubulin abundance contributes to many of the observed phenotypes, the causal relationship between tubulin abundance and the downstream cellular defects is not fully established.

Despite being largely descriptive, the study has several strengths. The inducible dual-tubulin expression system is technically elegant and provides a useful platform to investigate the consequences of altered tubulin isotype composition and/or abundance. The work also indicates that relatively modest increases in tubulin levels can have measurable biological consequences, offering a possible explanation for why tubulin abundance is tightly regulated. Finally, the breadth of approaches-including transcriptomics, proteomics, imaging, and cell-cycle analyses-provides a valuable resource for the field. While many of the proposed connections remain to be mechanistically tested, the study raises a number of interesting hypotheses and highlights several promising directions for future work.

Answer:

We thank the reviewer for these positive comments.

Major comments:

Figure 1:

The dual expression system that the authors use to introduce exogenous tubulins is well described and characterized, representing an elegant strategy and useful tool for the field. The current version of the manuscript, however, is missing a quantitative assessment of the overall tubulin levels (endogenous + exogenous) upon doxycycline treatment (e.g., using western blot). Given that the article is centered on cellular roles of surplus soluble tubulin, the authors must quantify both the soluble and polymerized fractions of total cellular tubulin in control and doxycycline-treated samples.

Answer:

We will perform the assays requested by the reviewer and add them to a revised version of the manuscript.

Throughout the manuscript, the authors extrapolate the effects of TUBB3+TUBA1A overexpression to "tubulin overexpression". But how can they distinguish isotype-specific from general effects? If endogenous tubulins are massively downregulated upon the expression of exogenous TUBB3+TUBA1A, the tubulin isotype composition is presumably dramatically altered. If the authors wish to retain the claims later on in the manuscript that the observed phenotypes are associated with excess tubulin, they need to provide evidence by testing other isotype combinations. Alternatively, the authors should tone their claims to reflect the possibility that what they observe downstream of TUBB3+TUBA1A overexpression may be isotype-specific rather than general.

Answer:

Making new stable lines with other tubulin isotypes and analyzing the many downstream effects takes months and is beyond the scope of the present manuscript (see also below, Description of analyses that authors prefer not to carry out). Hence, we will tone down our claims by acknowledging that observations were made with one set of tubulin isotypes.

Figure 2:

While changes at the level of EB1, and to a lesser extent CLIP-170 upon TUBB3+TUBA1A overexpression are convincing, the claimed changes in microtubule dynamics are not supported by the data (small, but statistically insignificant trends are observed). The authors should tone down their claims and adapt the results subheadings and figure captions accordingly. Likewise, the authors state "our results convincingly show that soluble tubulin levels control +TIP composition at MT ends," which should be toned down, as the authors do not provide any experiments to probe this model (e.g., mild tubulin downregulation to restore normal protein levels and then characterize the +TIP composition).

Answer:

With respect to changes in microtubule dynamics we refer this reviewer to our answers to comments of reviewer #1 (pages 1,2). Briefly, by displaying a cumulative distribution plot in combination with appropriate tests we show that effects are statistically significant. We propose to include these data in a revised version.

We furthermore propose to perform dose-dependent doxycycline experiments (see also next comment) and test whether these cause dose-dependent +TIP composition shifts. If this is the case we maintain our current statement, if not, we will tone down this statement.

Figure 3.

Similar to Figure 2, the authors state that tubulin overexpression leads to mitotic defects. But this model is never challenged in rescue experiments, and the claims should therefore be toned down.

Answer:

We do not completely understand this comment. We simply turn on (or off) tubulin expression, and in our view the “rescue” experiment is the control situation, i.e. non-induced cells. To addres this criticism, we nevertheless propose to perform dose-dependent doxycycline experiments and test whether these cause dose-dependent mitotic effects.

The methodology that the authors chose to measure metaphase duration is inadequate, since it is difficult, if not impossible, to precisely measure metaphase duration with a tubulin label alone. A DNA label is required. Likewise, measurements of spindle length should be done in living, but not fixed cells. These parameters can be extracted from the same movies with a tubulin and a DNA stain.

Answer:

We will perform additional experiments where we add a DNA label (in addition to a tubulin label) to more accurately measure metaphase duration (and we take along spindle length).

We do not understand the claim of the reviewer that “measurements of spindle length should be done in living, but not fixed cells”. We and others have measured spindle length in fixed cells with immunostaining (PMID: 38117947, PMID: 40353778; PMID: 25568341), and it therefore appears to be an accepted method. Note that in these measurements we do include a DNA label.

The unaligned chromosomes in metaphase represent a striking phenotype associated with TUBB3+UBA1A overexpression. A close inspection of the mitotic spindle staining, however, doesn't seem to show a much denser microtubule network in dox-treated samples. This is surprising, and the authors should provide a quantification to support their model (e.g., tubulin fluorescence intensity normalized to an internal control), or at the very least discuss this paradox in the manuscript.

Answer:

We thank the reviewer for this observation and will analyze this in more detail.

Figure 4.

The authors convincingly demonstrate the alterations in cell cycle progression upon TUBB3+TUBA1A overexpression using flow cytometry. An orthogonal approach would strengthen this claim, while allowing the authors to mechanistically test the premature G1/S transition model that they propose. As is, the reduced G1 population could also be explained by increased G2/M population in these cells. Well-established time-resolved approaches exist for directly measuring G1/S transition timing, including FUCCI systems for live imaging and EdU pulse-chase methods for temporal cell cycle analysis. Without employing these validated methodologies, the inference of premature G1/S remains untested, leaving a key mechanistic link in the claim insufficiently supported.

Answer:

We thank the reviewer for this comment. We note that the flow cytometry data are supported both by RNA-Seq and proteomics results, as stated in the manuscript. Hence, orthogonal approaches were to some extent already performed. However, we do feel that additional evidence should be provided to support our premature G1/S transition model. Based on the suggestion of the reviewer we will perform an EdU pulse-chase experiment as orthogonal approach.

Figures 5-6.

The authors use next-generation sequencing to reveal transcriptional changes associated with TUBB3+TUBA1A overexpression. While these analyses appear comprehensive, it remains unclear how many of the alterations in gene expression are a direct consequence of TUBB3+TUBA1 overexpression and how many are a downstream consequence of the altered cell cycle profile. The authors should, at the very least, acknowledge this in the manuscript.

Answer:

This is actually acknowledged in the manuscript, on page 15: “These results are consistent with our FACS analysis and suggest that shifts in cell cycle fractions partly underlie gene expression differences”.

Similarly, the authors provide a careful proteomics profiling of cells overexpressing TUBB3+TUBA1 in both normoxia and hypoxia. But as with transcriptomics, it is unclear what the contribution of the altered cell cycle profile is in these analyses. This should, at the very least, be acknowledged in the manuscript.

Answer:

Again, this is actually stated in the manuscript, on page 18: “Metascape analysis revealed upregulation of terms associated with mitosis and G2/M transition, including the PLK1 pathway, in the Dox-induced cells, whereas G1/S-specific, and DNA repair terms were down (Fig. 6d, Table S1). These data are consistent with our FACS (Fig. 4a, b) and RNA-seq results (Fig. 5e)”.

The authors then leverage their omics data to propose a functional link between tubulin overexpression and translation and mitochondrial function. A limited number of targeted functional assays would substantially strengthen the manuscript and help distinguish between primary and secondary effects. For example, direct measurements of protein synthesis (e.g., puromycin incorporation or OPP labeling) would provide evidence for the proposed translation defects. Likewise, direct assessment of mitochondrial function (e.g., oxygen consumption, mitochondrial membrane potential, or ATP production) would strengthen claims regarding mitochondrial dysfunction. These experiments are standard in the field and could realistically be completed within several weeks to a few months, depending on local expertise and instrumentation. Moreover, they would test conclusions already central to the manuscript without opening entirely new directions.

Answer:

We thank the reviewer for these comments and helpful suggestions. We will perform experiments measuring translation and mitochondrial (dys)function (see also our rebuttal to reviewer #1 on pages 6 and 7), and include them in a revised version of the manuscript.

Figure 7.

The authors use proteomics-based approaches to characterize the partners of the overexpressed tubulins, revealing novel interactors. These data present an interesting but incomplete picture. For example, can the identified novel interactors bind any tubulin isotype, or are they specific to the TUBB3/TUBA1A used in this study? The enrichment of TIMM50 does not appear very strong. How reproducible are these data? The authors should provide quantifications from several independent biological replicates and perform statistical analyses.

Answer:

We thank the reviewer for these comments. As stated on page 22 of our manuscript: “Thus, AIFM1 and TIMM50 are consistently identified as TAPs using different purification strategies, tags, and cell lines”. For the revised version of the manuscript we will perform pull down experiments with other recombinant tubulins.

With respect to the relatively weak TIMM50 enrichment we refer to our answer to reviewer #1 on pages 5, 6 of this rebuttal. Briefly, we will perform additional pull down experiments (dual affinity purifications) to solidify our claims.

Figure 8.

While convincing, this figure largely confirms previous studies. In addition, it addresses a question that is different from the rest of the manuscript. The reviewer feels like this part could be taken out of the manuscript to reduce complexity and focus the scope of this work.

Answer:

Since reviewer #1 is of a similar opinion as this reviewer we are willing to remove the data presented in Fig. 8 in a revised version of the manuscript. We agree that this reduces complexity and focusses the scope of this work.

Minor comments:

There is a discrepancy between the manuscript and the methods that makes it unclear in which cells the transcriptomic analyses were done. The authors should clarify this.

Answer:

We are not sure what the reviewer means here, there is but one Dox-inducible cell line in which our own transcriptomic analyses was done. On page 37 we list the GEO numbers from which we retrieved expression data for Figure 8. Note that this part of the Methods section will be removed in a revised version, as we will not show Fig. 8 anymore.

The authors report "We also observed "extra-mitotic" centrioles...". However, they appear to refer to movies of SiR-tubulin-stained cells. This staining dows not allow visualization of centrioles, and the authors should revise their manuscript to either provide a clarification or correct this claim.

Answer:

We thank the reviewer for pointing out this mistake. We will correct this.

• *

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

NA.

4. Description of analyses that authors prefer not to carry out__ __

Reviewer #2

Throughout the manuscript, the authors extrapolate the effects of TUBB3+TUBA1A overexpression to "tubulin overexpression". But how can they distinguish isotype-specific from general effects? If endogenous tubulins are massively downregulated upon the expression of exogenous TUBB3+TUBA1A, the tubulin isotype composition is presumably dramatically altered. If the authors wish to retain the claims later on in the manuscript that the observed phenotypes are associated with excess tubulin, they need to provide evidence by testing other isotype combinations. Alternatively, the authors should tone their claims to reflect the possibility that what they observe downstream of TUBB3+TUBA1A overexpression may be isotype-specific rather than general.

Answer:

We thank the reviewer for this comment. Making new stable lines with other tubulin isotypes and analyzing the many downstream effects takes months and is beyond the scope of the present manuscript. Hence, we will tone down our claims by acknowledging that observations were made with one set of tubulin isotypes.

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

Learn more at Review Commons

Referee #2

Evidence, reproducibility and clarity

Summary:

This study develops an inducible HEK293F cell model that modestly overexpresses αβ-tubulin heterodimers. Using a dual expression system, the authors introduce exogenous TUBB3 and TUBA1A and combine cell biology, live-cell imaging, RNA-seq, proteomics, flow cytometry, and biochemistry to investigate the consequences of increased tubulin abundance. They suggest that, despite downregulation of endogenous tubulin transcripts, excess tubulin still accumulates in cells. This is accompanied by increased microtubule mass, changes in plus-end protein composition, defects in mitosis, and alterations in cell-cycle progression. The study further links tubulin overexpression to replication stress and broader changes in cellular physiology, including reduced abundance of mitochondrial respiratory proteins, altered translation-associated factors, and an attenuated response to hypoxic stress. In addition, the authors confirm previous observations that oxygen and nutrient deprivation reduce tubulin and microtubule abundance. Based on these findings, the authors propose that tubulin is not merely a structural component of microtubules but also contributes to the regulation of cellular homeostasis.

The possibility that tubulin abundance itself influences broader aspects of cellular physiology is conceptually interesting and warrants further investigation. At the same time, many of the mechanistic links proposed in the manuscript remain insufficiently resolved. A large number of cellular processes are associated with tubulin overexpression, but it is often unclear which phenotypes represent primary consequences of altered tubulin abundance and which are secondary responses. For instance, conclusions regarding mitochondrial dysfunction and translation attenuation are inferred from omic signatures rather than direct functional tests. Similarly, while the authors propose that altered tubulin abundance contributes to many of the observed phenotypes, the causal relationship between tubulin abundance and the downstream cellular defects is not fully established.

Despite being largely descriptive, the study has several strengths. The inducible dual-tubulin expression system is technically elegant and provides a useful platform to investigate the consequences of altered tubulin isotype composition and/or abundance. The work also indicates that relatively modest increases in tubulin levels can have measurable biological consequences, offering a possible explanation for why tubulin abundance is tightly regulated. Finally, the breadth of approaches-including transcriptomics, proteomics, imaging, and cell-cycle analyses-provides a valuable resource for the field. While many of the proposed connections remain to be mechanistically tested, the study raises a number of interesting hypotheses and highlights several promising directions for future work.

Major comments:

Figure 1:

1. The dual expression system that the authors use to introduce exogenous tubulins is well described and characterized, representing an elegant strategy and useful tool for the field. The current version of the manuscript, however, is missing a quantitative assessment of the overall tubulin levels (endogenous + exogenous) upon doxycycline treatment (e.g., using western blot). Given that the article is centered on cellular roles of surplus soluble tubulin, the authors must quantify both the soluble and polymerized fractions of total cellular tubulin in control and doxycycline-treated samples.
2. Throughout the manuscript, the authors extrapolate the effects of TUBB3+TUBA1A overexpression to "tubulin overexpression". But how can they distinguish isotype-specific from general effects? If endogenous tubulins are massively downregulated upon the expression of exogenous TUBB3+TUBA1A, the tubulin isotype composition is presumably dramatically altered. If the authors wish to retain the claims later on in the manuscript that the observed phenotypes are associated with excess tubulin, they need to provide evidence by testing other isotype combinations. Alternatively, the authors should tone their claims to reflect the possibility that what they observe downstream of TUBB3+TUBA1A overexpression may be isotype-specific rather than general.

Figure 2:

1. While changes at the level of EB1, and to a lesser extent CLIP-170 upon TUBB3+TUBA1A overexpression are convincing, the claimed changes in microtubule dynamics are not supported by the data (small, but statistically insignificant trends are observed). The authors should tone down their claims and adapt the results subheadings and figure captions accordingly. Likewise, the authors state "our results convincingly show that soluble tubulin levels control +TIP composition at MT ends," which should be toned down, as the authors do not provide any experiments to probe this model (e.g., mild tubulin downregulation to restore normal protein levels and then characterize the +TIP composition).

Figure 3.

1. Similar to Figure 2, the authors state that tubulin overexpression leads to mitotic defects. But this model is never challenged in rescue experiments, and the claims should therefore be toned down.
2. The methodology that the authors chose to measure metaphase duration is inadequate, since it is difficult, if not impossible, to precisely measure metaphase duration with a tubulin label alone. A DNA label is required. Likewise, measurements of spindle length should be done in living, but not fixed cells. These parameters can be extracted from the same movies with a tubulin and a DNA stain.
3. The unaligned chromosomes in metaphase represent a striking phenotype associated with TUBB3+UBA1A overexpression. A close inspection of the mitotic spindle staining, however, doesn't seem to show a much denser microtubule network in dox-treated samples. This is surprising, and the authors should provide a quantification to support their model (e.g., tubulin fluorescence intensity normalized to an internal control), or at the very least discuss this paradox in the manuscript.

Figure 4.

1. The authors convincingly demonstrate the alterations in cell cycle progression upon TUBB3+TUBA1A overexpression using flow cytometry. An orthogonal approach would strengthen this claim, while allowing the authors to mechanistically test the premature G1/S transition model that they propose. As is, the reduced G1 population could also be explained by increased G2/M population in these cells. Well-established time-resolved approaches exist for directly measuring G1/S transition timing, including FUCCI systems for live imaging and EdU pulse-chase methods for temporal cell cycle analysis. Without employing these validated methodologies, the inference of premature G1/S remains untested, leaving a key mechanistic link in the claim insufficiently supported.

Figures 5-6.

1. The authors use next-generation sequencing to reveal transcriptional changes associated with TUBB3+TUBA1A overexpression. While these analyses appear comprehensive, it remains unclear how many of the alterations in gene expression are a direct consequence of TUBB3+TUBA1 overexpression and how many are a downstream consequence of the altered cell cycle profile. The authors should, at the very least, acknowledge this in the manuscript.
2. Similarly, the authors provide a careful proteomics profiling of cells overexpressing TUBB3+TUBA1 in both normoxia and hypoxia. But as with transcriptomics, it is unclear what the contribution of the altered cell cycle profile is in these analyses. This should, at the very least, be acknowledged in the manuscript.
3. The authors then leverage their omics data to propose a functional link between tubulin overexpression and translation and mitochondrial function. A limited number of targeted functional assays would substantially strengthen the manuscript and help distinguish between primary and secondary effects. For example, direct measurements of protein synthesis (e.g., puromycin incorporation or OPP labeling) would provide evidence for the proposed translation defects. Likewise, direct assessment of mitochondrial function (e.g., oxygen consumption, mitochondrial membrane potential, or ATP production) would strengthen claims regarding mitochondrial dysfunction. These experiments are standard in the field and could realistically be completed within several weeks to a few months, depending on local expertise and instrumentation. Moreover, they would test conclusions already central to the manuscript without opening entirely new directions.

Figure 7.

1. The authors use proteomics-based approaches to characterize the partners of the overexpressed tubulins, revealing novel interactors. These data present an interesting but incomplete picture. For example, can the identified novel interactors bind any tubulin isotype, or are they specific to the TUBB3/TUBA1A used in this study? The enrichment of TIMM50 does not appear very strong. How reproducible are these data? The authors should provide quantifications from several independent biological replicates and perform statistical analyses.

Figure 8.

While convincing, this figure largely confirms previous studies. In addition, it addresses a question that is different from the rest of the manuscript. The reviewer feels like this part could be taken out of the manuscript to reduce complexity and focus the scope of this work.

Minor comments:

1. There is a discrepancy between the manuscript and the methods that makes it unclear in which cells the transcriptomic analyses were done. The authors should clarify this.
2. The authors report "We also observed "extra-mitotic" centrioles...". However, they appear to refer to movies of SiR-tubulin-stained cells. This staining dows not allow visualization of centrioles, and the authors should revise their manuscript to either provide a clarification or correct this claim.

Significance

This study addresses a long-standing question in cytoskeletal biology: what are the consequences of altering tubulin abundance independently of acute perturbations of the microtubule cytoskeleton? The work is primarily a conceptual and technical advance, providing an inducible system to investigate tubulin dosage and suggesting that tubulin abundance may influence cellular processes beyond microtubule assembly. The findings build on earlier work demonstrating that tubulin expression responds to physiological and environmental cues and raise the possibility that tubulin homeostasis interfaces with broader cellular stress-response pathways. While several of the proposed mechanistic links remain to be established, the study will be of interest to researchers working on the cytoskeleton, protein homeostasis, cell-cycle regulation, and cellular stress responses.

My expertise lies in cytoskeletal biology, mitosis, and quantitative cell biology. I am less qualified to evaluate in depth the aspects of the manuscript related to mitochondrial physiology and hypoxic signaling.

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

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Referee #1

Evidence, reproducibility and clarity

Summary: This study examines how simultaneous expression of high levels of alpha and beta tubulin impact microtubule organization, cell cycle progression and stress response. The main conclusions are that a/b tubulin overexpression 1) increases the density of microtubules in cells with mild effects on growth rate and catastrophe frequency; 2) causes mitotic spindle defects and cell cycle disruption; 3) alters the transcriptome and proteostasis; 4) causes mitochondrial stress by binding mitochondrial import proteins; 5) disrupts cellular stress response.

Major comments:

The results generally use an appropriate number of cells and technical replicates.

There are several instances in the manuscript where the data do not support the authors' conclusions. These include: Page 6. "We detected a mild increase in MT growth rates in Dox-treated cells (Fig. 2b), which was observed in all of the growing MTs examined (Fig. 2c), consistent with an increase in soluble tubulin levels in all Dox-induced cells." The data do not support this statement. The histogram in Figure 2C shows that only a small portion of growth rate measurements are faster in the overexpression cells, and the statistical test in 2b suggests that the datasets are unlikely to be different. It is unclear from the presentation of the data why a small population of overexpression cells exhibit faster growth rates. The data in Figure 2b should be plotted as a superplot could show whether the faster data points are from specific cells or technical replicates. The same concern applies to the data in Figure 2D.

Page 11. "Moreover, DNA content was highly aberrant after 48 hr, with large proportions of cells containing < 2n or > 4n chromosomes (Fig. 4d). Thus, persistent overexpression of tubulin affects the cell cycle and after 48 hr it results in severe DNA abnormalities, suggestive of CIN" The plot in Figure 4D shows increased propidium iodide signal below the 2N peak and above the 4N peak, but it is quite likely that this could represent signal from apoptotic cells. The authors should specifically stain for an apoptotic marker to test this possibility. This would suggest that prolonged overexpression of a/b tubulin leads to apoptosis, which could be important evidence for later conclusions in the study.

Page 11. "Combined, our data show that tubulin overexpression affects all three major cell cycle checkpoints, i.e. G1/S, G2/M, and the SAC in mitosis." The data do not fully support this conclusion. While the evidence for SAC-mediated delay in overexpression cells is strong, the evidence for other checkpoints is weak. The phosphor-RB experiment in Figure S3b lacks a positive control. The γH2A-X results in Figure 4f and g show that the difference is driven by a minor population of dim foci in control cells. Similar to the point above, these data should be plotted as a superplot to explore the possibility that this minor population arises from a small number of cells or a specific technical replicate.

Page 19. "This, in turn, lowers EEF1A1 causing attenuation of translation and dampened elongation rates. That other initiation and elongation factors are mildly down in Dox-induced cells, as are ribosomal proteins (Fig S6c, Table S1), indicates a mild ISR and general translation inhibition. We propose that tubulin overexpression results in mitochondrial dysfunction leading to stress and attenuated translation elongation. We observe the start of an ISR in these cells, which prevents a proper hypoxic response." This conclusion seems to be at odds with the earlier conclusion drawn from Figure 5e, where ISR genes are significantly decreased in overexpression cells. The authors should reconcile these results in the discussion.

Figure 7. This experiment lacks a key control - identifying peptides in a pull down from cells that do not overexpress the tagged tubulin. Without this control, it is impossible to discern which peptides bind to the beads, independent of tubulin. This concern is amplified by the results in Figure 7b where TIMM50 binding is tested in a follow-up experiment. Here the negative control is employed and it shows that TIMM50 pulls down in the absence of tagged tubulin. This indicates that TIMM50 may not bind to tubulin and calls into question any conclusions related to TIMM50 and mitochondrial proteostasis. Before making any conclusions from the pull down experiment, the authors must include the negative control and carefully assess which peptides are likely to be false positives.

Figure 8. This figure and the associated text feel rather disconnected from the rest of the study. The authors do not make clear conclusions from these results. Perhaps these experiments should be further developed in a separate study?

Page 25. "We found that tubulin overexpression induces mitochondrial dysfunction." The data do not strongly support this conclusion. The proteomic data in Figure 6 indicate that some mitochondrial proteins are less abundant in tubulin overexpressing cells, but the study does not include any experiments that actually test mitochondrial function. The authors could test this by including new experiments to measure mitochondrial membrane potential, or respiration activity, etc. These would be an important addition to the study.

Page 26. "We provide evidence here that surplus tubulin slows general translation, increasing the time window for a TTC5-nascent tubulin interaction." The data do not demonstrate a decrease in translation rate. It is unclear what evidence the authors refer to with this statement. The proteomic analysis in Figure 6 measures protein abundance, and a decrease could be due to either decreased transcription, decreased translation, or increased protein degradation. The number of proteins that are shown to be downregulated in tubulin overexpressing cells is rather small (100s) which seems to argue against a general decrease in translation, despite the decrease in several translation regulators. To make this conclusion, the authors would need to add new experiments that measure translation rate.

Minor comments:

Page 10." We also observed "extra-mitotic" centrioles at the onset of mitosis after Dox-treatment, indicative of mitotic arrest and aneuploidy, which eventually resolved into normal metaphase plates (Supplementary Videos 3, 4)." It is unclear whether these foci are centrioles. The SiR-tubulin reagent used in these experiment labels tubulin. It would be more accurate to describe these as "tubulin foci".

Page 13. "Analysis of TUBG1 reads revealed downregulation in tubulin overexpressing cells, albeit weakly (Fig. 5c)." These datapoints appear to be quite similar. Please provide a statistical analysis.

Significance

This study explores how increasing a/b tubulin expression impacts microtubule-dependent functions in cells and broadly explores other impacts on cell function. How tubulin expression changes impact cells is an important question because there are well-established developmental, cell cycle, and disease contexts where tubulin levels strongly increases. Furthermore, tubulin levels are known to be regulated in part by an 'autoregulation' mechanism that degrades tubulin mRNAs when soluble protein levels are high, but little is known about how this mechanism might impact other processes beyond tubulin.

This study seeks to add new knowledge on both points by using a system previously developed by the authors to conditionally and simultaneously overexpress alpha and beta tubulin. The use of this system is an advance for the field, which has previously relied on drugs that alter the soluble-polymer equilibrium of tubulin, rather than expression levels, to address these questions.

The study is also strengthened by combining experiments that validate the activity and assembly effects of overexpressed tubulin with exploratory experiments that measure impact across the transcriptome and proteome. This is an advance for the field. Previous studies have examined home tubulin-targeting drugs affect the transcriptome, but this study goes further by directly modulating tubulin levels and measuring both transcriptomic and proteomic impact. In addition, previous studies overexpressing a/b tubulin in budding yeast found similar effects on mitosis but did not examine broader impacts on the cell.

The major weakness of the study is that several of the main conclusions are not strongly supported by the current results. These are detailed above.

The audience for this study is a broad population of basic researchers, including the microtubule, mitosis, hypoxia, cell stress, translational regulation fields. The findings will open questions about how tubulin expression changes that occur in development and disease contexts might impact all of these processes, and what pathways might be used to harmonize them.

My expertise is in tubulin biology, including the tubulin gene family in development, tubulin proteostasis, and mitosis.

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

Reviewers' comments:

Reviewer #1

Evidence, reproducibility and clarity

The study entitled "Human bone marrow adipocytes drive prostate cancer bone metastasis progression via lipid-mediated induction of Angiopoietin-like 4" by Hernandez et al. investigates the role of the bone marrow adipocytes (BMAds) from red hematopoietic rich-areas in the progression of prostate cancer (PCa) bone metastases. To do so, the authors used an elegant three-dimensional culture of primary human rBMAds isolated from the femoral bone marrow of patients undergoing hip surgery then cultured with PCa cell lines. The authors claim that PCa cells take up FFAs released by rBMAds which enhance the epithelial-mesenchymal transition and motility through upregulation of ANGPTL4. The article is well written, the figures are very clear and the methodology is perfectly described. To further improve the understanding of this mechanism, the authors should address 1) how PCa cells take up the FFAs, 2) whether PCa cells enhance non-canonical FFAs release and 3) the specificity of the rBMAds in their ability to upregulate ANGPTL4 compared to other adipocytes.

We thank this reviewer for their positive and constructive feedbacks. Below, we provide detailed responses addressing each of their specific comments either with additional data and/or writing.

Major comments:

The paper's conclusions are overall convincing but the following supplementary experiments or discussion points could strengthen their claims.

1) Is ANGPTL4 upregulation in PCa cells specific to rBMAds or could it also be seen with other adipocytes, such as periprostatic adipocytes or SCAds (used in Fig 2)? Co-culture of PCa cells with SCAds should offer insights.

More precisely, the article does not state if ANGPTL4 upregulation could be induced prior to bone invasion, by the periprostatic adipose tissue FFA release for example, explaining why ANGPTL4-high cells could be found in bone metastasis. In that case, increased motility and migration could be BMAds independent and trigger the first metastatic events originating from the primary prostatic tumor.

To address this important question, we performed additional co-culture experiments using adipocytes isolated from human periprostatic adipose tissue (PPAT) and rBMAds. Although PPAT adipocytes also induced ANGPTL4 expression in PCa cells compared with non-cocultivated cells (NC), this induction was approximately 2.5-fold greater in PCa cells co-cultured with rBMAds (new Figure 6A). Consistent with these in vitro findings, analysis of publicly available PCa datasets revealed higher ANGPTL4 expression in bone metastases than in primary tumors (new Figure 6B). Together, these results suggest that although ANGPTL4 expression may be initiated within the primary tumor microenvironment, it is markedly amplified following colonization of the bone marrow niche.

In addition, as suggested by Reviewer 3, we assessed the clinical relevance of ANGPTL4 expression at different stages of disease progression. High ANGPTL4 expression in primary PCa tumors was not associated with either overall or disease-free survival (new Figure 6C). In contrast, elevated ANGPTL4 expression in bone metastases was significantly associated with poorer survival (new Figure 6D), indicating that the clinical relevance of ANGPTL4 is primarily linked to the metastatic bone microenvironment rather than the primary tumor. We therefore propose that, although ANGPTL4 expression may be initiated at the primary tumor site, it is markedly amplified within the bone marrow adipocyte-rich niche, where it promotes PCa cell migration and metastatic outgrowth. We have revised the manuscript accordingly (see lines 559-583).

2) The article hypothesizes an ANGPTL4-associated increase of motility and migration of PCa cells upon interaction with bone marrow adipocytes in the first metastatic bone, inducing enhanced invasion of said bone and secondary metastasis sites. However, the article lacks evidence that ANGPTL4 is also upregulated in cells from secondary metastasis sites in patients. It would be interesting to explore in the existing data set the expression of ANGPTL4 in secondary metastasis of patients who had previous bone metastasis. These points could be addressed in the concluding remarks.

We thank the reviewer for this interesting comment. Bone represents 80% of prostate cancer metastases (Gandaglia et al, Prostate, 2014, PMID: 24132735) and the bone metastases have been shown to act as a source of further metastatic dissemination (Gundem et al, Nature, 2015, PMID: 32728210; Hong et al, Nature commun, 2015, PMID: 25827447). Unfortunately, currently available public datasets only provide the anatomical site of metastatic lesions and do not distinguish between primary and secondary metastatic sites. Nevertheless, we examined ANGPTL4 expression in metastatic lesions. ANGPTL4 expression is maintained in liver, lung and lymph nodes (new Supplementary Figure 6A) suggesting that it might contribute to metastatic dissemination beyond bone. The manuscript has been revised accordingly (lines 575–580).

Additional experiments or qualifying the claims:

3) Fig 1 : It would be interesting to have an insight on the mechanism by which FFAs are uptaken by PCa.

Several evidences demonstrate that membrane-associated transport proteins facilitate and regulate this process, including CD36 (fatty acid translocase) and members of the fatty acid transport protein family (FATPs/SLC27A1–5). We evaluated the expression of these transporters implicated in the uptake of long-chain FFAs in our cellular models. CD36 expression was not detected at either the mRNA or protein level in all three prostate cancer cell lines (PC3, Du145, and LNCaP). The validity of our detection strategy was confirmed using a CD36-positive control (U937 leukemic cell line) and a corresponding negative control (U937 cells KO for CD36) (Supplementary Fig. F and G added). Among the FATP family members, FATP4 (SLC27A4 gene) was the most highly expressed transporter in all the three PCa cell lines (Supplementary Fig. 1H, added). We therefore investigated its potential contribution to FFA uptake by silencing SLC27A4 expression using siRNA in PC3 cells and knockdown efficiency was confirmed at both mRNA (Supplementary Fig. 1I added) and protein (Supplementary Fig. 1J added) level. Silencing of FATP4 reduced the uptake of exogenous fluorescent oleate (Supplementary Fig. 1K) but not palmitate (Supplementary Fig. 1L, added) showing a selectivity of FFA uptake depending on their nature. However, FATP4 knockdown did not affect lipid transfer in the co-culture model (Supplementary Fig. 1M, added), where several FFA species are present. Collectively, these findings indicate that the uptake rBMAd-derived FFAs is unlikely to be primarily mediated by FATP4 suggesting that alternative mechanisms, such as extracellular vesicle-mediated transfer or passive diffusion, may account for their uptake. These results have been included in Supplementary Figure 1F–M, and the manuscript has been revised accordingly (lines 396–411).

4) Fig 1D : It would be interesting to add an extra control of NC PCa treated with BODIPY to measure basal BODIPY uptake of PCa

To address this point, we performed an additional control experiment in which PC3 cells were directly exposed to 5 µM BODIPY FLC16, corresponding to the concentration used to preload rBMAds in the co-culture experiments (Fig. 1D). As expected, direct exposure resulted in higher BODIPY FL C16 uptake compared with co-culture with preloaded rBMAds.

This difference is expected since, during direct treatment, the fluorescent FFA is immediately available at 5 µM in the culture medium. In contrast, BODIPY FLC16 represents only a tracer when rBMAds are preloaded, and the released of FFAs during co-culture consist of a mixture of fluorescent and non-fluorescent species. The figure can be included in the manuscript upon referee’s request.

5) Fig 2 : The figure efficiently states that rBMAds undergo non-canonical lipolysis in comparison to SCAds, without PCa cells. Glycerol dosage and/or pan-lipase inhibitor treatment of rBMAds in co-culture with PCa would confirm rBMAds still show non-canonical lipolysis in bone metastasis environment.

To address this point, we quantified glycerol and FFAs released into the culture medium from PC3 cells alone or from rBMAds co-cultured with PC3 cells, in the presence or absence of the pan-lipase inhibitors paraoxon ethyl or orlistat. As shown in the new Supplementary Figure 2B, pan-lipase inhibition markedly reduced FFA release, whereas glycerol release remained unchanged. These results confirm that, even in the presence of PCa cells, FFA release from rBMAds occurs independently of canonical lipolysis.

6) Fig2 : Is ANGPTL4 upregulation in PCa cells specific to rBMAds or could it also be seen with other adipocytes, such as periprostatic adipocytes or SCAds ? Co-culture of PCa cells with SCAds should offer insights.

This comment was addressed in point 1.

7) Fig 2 : Could the authors specify if there is a possibility the lipolysis kinetics is slower in rBMAds instead of an actual incomplete lipolysis?

To determine whether the reduced glycerol release reflected delayed rather than incomplete lipolysis, we extended isoproterenol stimulation up to 24 h in rBMAds, using SCAds as a control. As shown in the new Supplementary Figure 2A (commented in the text, lines 425–430), glycerol release did not increase over time in rBMAds, whereas it progressively increased in SCAds. These results do not support delayed lipolysis in rBMAds but rather indicate that lipolysis remains incomplete despite prolonged stimulation.

7) Fig 3B/C : The author should provide tables to show : 1) all significantly up and down GO term 2) the top 20 genes DEG 3) any GO terms/genes related to EMT (table 1 should be associated with figure 3)

As proposed by the reviewer, we added a Table 1 in the revised manuscript with all significant upregulated and downregulated GO terms including gene names and the proportion of genes related to each GO term and p-value. We also added the top 20 of upregulated and downregulated genes.

8) Fig 5 : To complete experiences of KD of ANGPTL4 and PPARy inhibition, the author should also include the mRNA levels of EMT associated genes in these conditions.

We thank the reviewer for this suggestion. The EMT-associated genes originally included in the manuscript were selected based on the literature in pancreatic cancer as descriptive markers (Gordon et al, BMC Cancer, 2023, PMID: 37291514). In the revised manuscript, to further investigate the mechanisms underlying ANGPTL4-dependent cell migration, we reconstructed an ANGPTL4-associated gene network in Cytoscape using RNA-seq-derived differentially expressed genes enriched in cell migration GO terms and their interactions with ANGPTL4. Interestingly, the gene signature identified in our conditions do not clearly overlaps with canonical EMT-associated genes described in the literature. This analysis revealed a highly interconnected network rather than a linear signaling cascade (new Supplementary Figure 5L) suggesting that ANGPTL4 promotes cell migration by orchestrating a coordinated transcriptional program involving multiple complementary signaling pathways. While this systems-level analysis reveals a coherent migration-associated network, it does not aim to establish a direct functional role for each individual gene, but rather to define the global transcriptional context of ANGPTL4-dependent migration. In line with this, we added and discussed the Cytoscape network of ANGPTL4-associated migration genes in the revised manuscript (new Supplementary Figure 5L and commented in the text lines 538-545).

To better the clarity of the paper, the author should indicate in table S1 which patients are used in which figures. Also, what is the rationale for not using female patients in all the experiments?

We thank the reviewer for this helpful suggestion. We have revised Table S1 to improve its clarity by indicating, for each experiment, the corresponding patient information, including age, sex, and BMI. In this study, rBMAds from both male and female donors were used to establish and validate the 3D culture model and to characterize the mechanisms of FFA release. However, for the co-culture experiments investigating the crosstalk between rBMAds and PCa cells, only rBMAds from male donors were used. Since PCa is a male-specific disease, restricting these experiments to male donors minimizes the potential confounding effects of sex-dependent differences in BMAd biology and ensures that the model remains physiologically relevant.

The suggested additional experiment should be achievable in 6 months.

*9) Statistical analyses: The authors state in the Materiel and Methods that they used Student's t-test, one-way ANOVA or two-way ANOVA. These tests are applied to parametric data sets, validated for their normal distribution. Usually, n To determine the appropriate statistical test and post hoc analysis, data normality was first assessed using the Shapiro-Wilk test. Parametric tests were applied when data followed a normal distribution, whereas non-parametric tests were used when normality assumptions were not met. The specific statistical tests used for each analysis have now been indicated in the corresponding figure legends.

Minor Comments:

10) In Fig 1F, the author should discuss the discrepancy between the significant increase of TG uptake in PCa shown in 1B and the non-significant effect seen in 1F, given that TG represents 85% of the total FFAs shown in 1E and 1F.

Figures 1B and 1F correspond to two distinct experimental readouts and therefore should not be directly compared. Figure 1B measures the intracellular accumulation of TG in PCa cells following coculture with adipocytes. These TG are formed after the uptake of adipocyte-derived FFAs and their subsequent re-esterification into neutral lipids stored in lipid droplets. In contrast, Figure 1F quantifies the concentration of FFAs remaining in the culture medium at the end of the coculture period. Although extracellular FFA levels appear slightly higher in the presence of PCa cells than with rBMAds alone, this difference is not statistically significant. This is likely because FFAs released by rBMAds are continuously taken up by PCa cells during coculture, thereby limiting their accumulation in the medium. Therefore, the lack of a significant increase in extracellular FFAs does not contradict the marked intracellular accumulation of TG observed in Figure 1B.

*11) Fig 3 : In Fig 3G and 4E, staining quantification would be necessary. *

The quantification of the area of lipid droplets per nucleus depending on exogenous FFA treatment was done according to reviewer comments and added in a Figure 4E. Concerning Figure 3G, the images shown were intended as representative illustrations of the cytoskeletal and morphological changes observed following co-culture, rather than as a quantitative endpoint. The conclusions of this section are primarily supported by the quantitative functional assays measuring cell migration (Fig. 3D-E) and invasion (Fig. 3F), which directly assess the biological consequences of these morphological changes.

12) In Fig3/Sup Fig3, why is the invasion assay not shown for LNCaP cell line ?

According to reviewer comments, invasion assay was performed on LNCaP and added in the manuscript (new Supplementary Fig. 3D) on the revised manuscript. Coculture of rBMAds with LNCaP stimulate invasion as other PCa cell lines (PC3 and Du145).

*13) 5F: Is there a reason why the sum of FFA has a stronger effect than the individual ones ? *

We observed that the combination of palmitate, oleate, and linoleate induced a stronger increase in lipid accumulation (Figure 4E, only statistically significant when compared palmitate alone with the mix) and target gene expression (Figure 5F) than each FA alone. Although we did not investigate the underlying mechanism in the present study, we speculate that the combination is likely to better mimic the FA environment of rBMAds and may promote more efficient downstream signaling than individual FA. This aspect is also discussed in response to the point 4 of the referee 2.

14) 5E/F : Rationale for changing FFA treatment duration between 5E and 5F (72h then 24h) ?

While most FFA treatment and co-culture experiments with rBMAds were performed for 72 h, experiments involving ANGPTL4 siRNA or the PPARγ inverse agonist T0070907 were limited to 24 h. This shorter duration was chosen to preserve the efficacy of T0070907 and to capture the optimal window of siRNA-mediated knockdown. Importantly, we observed that FFA treatment was already sufficient to induce ANGPTL4 expression after 24 h, allowing us to investigate the contribution of ANGPTL4 and PPARγ signaling under conditions where the pharmacological inhibition and gene silencing remained effective. We have clarified this rationale in the revised manuscript (lines 255-256).

*15) For the discussion: the authors clearly describe the two different BMAds subtypes (cBMAds vs rBMAds), would it be interesting to question the role of cBMAds in PCa progression as well ? *

We thank the reviewer for this suggestion and agree that this is an important point to address. Because PCa bone metastases predominantly localize to red bone marrow areas, our study focused on the role of rBMAds in PCa progression. Nevertheless, we cannot exclude a potential contribution of constitutive bone marrow adipocytes, which reside primarily in yellow bone marrow, and whose effects on PCa cells may be similar to or distinct from those of rBMAds. We have now included this point in the concluding remarks of the Discussion (lines 599–601).

The studies are referenced appropriately.

*16) Please, could the authors indicate the co-culture duration with rBMAds in the legends of Figure 5. Excepted this point, the text and figures are clear and accurate. *

We added in the revised manuscript the duration time of coculture for the different experiments in Figure 5.

Significance

General assessment:

the authors used an elegant three-dimensional culture of primary human rBMAds isolated from the femoral bone marrow of patients undergoing hip surgery then co-cultured with PCa cell lines. The authors claim that PCa cells take up FFAs released by rBMAds which enhance the epithelial-mesenchymal transition and motility through upregulation of ANGPTL4. The most important aspects of this study are 1) the description of the non-canonical FFAs release from rBMAds, 2) the induction of EMT/motility of PCa cells induced by FFAs uptake. To further improve the understanding of this mechanism, the authors should address 1) how PCa cells take up the FFAs, 2) whether PCa cells enhance non-canonical FFAs release and 3) the specificity of the rBMAds in their ability to upregulate ANGPTL4 compared to other adipocytes.

This study extends the knowledge in the field of prostate cancer metastasis.

The authors have developed an elegant 3D culture model of primary human rBMAds, which is highly relevant for investigating the role of adipocytes in cancer cell behavior. Indeed, most models used in the literature rely on adipocytes differentiated from bone marrow mesenchemal stem cells. Although adipocytes differentiation models have recently been improved by incorporating 3D structure, the model developed by the authors is most physiological, as it is based on the direct use of primary bone marrow adipocytes. In this way, this model represents a valuable tool to advance our understanding of mechanisms involved in bone metastasis in breast/prostate cancers.

The type of audience that will be interested by this research include both basic and specialized researchers. Moreover, this study should improve 1) the understanding of the impact of rBMAds on prostate cancer behavior and 2) the robustness and physiological relevance of adipocyte-based studies.

Our expertise lies in the interaction between normal or pathological hematopoiesis with the components of bone marrow microenvironment.

We sincerely thank the reviewer for the constructive comments and suggestions, which have significantly contributed to improving the mechanistic depth and clarity of our manuscript. We believe that the additional data and revisions provided in this response address the main points raised and further strengthen the conclusions of our study.

Reviewer #2

Evidence, reproducibility and clarity

Summary: This manuscript focuses on evaluation of effects of bone adipocytes on prostate cancer and their potential role in prostate cancer bone metastases progression. Mechanistically, the results show that fatty acid (FFA) secreted by bone marrow adipocytes increased expression of ANGPTL4 in prostate cancer cell lines in vitro, and this increase was dependent on PPARgamma signaling, resulting in increased migration and invasiveness of the cells. Evaluation of data from SU2C data set, was also included to support the conclusions, showing that increased levels of ANGPTL4 expression in bone metastases are negatively correlated with patients' survival, suggesting that ANGPTL4 could be a therapeutic target for prostate cancer bone metastasis.

The authors previously investigated and published on crosstalk/interaction between periprostatic adipocytes and prostate cancer cells, where FFAs induced released by adipocytes elicited increased aggressiveness and dissemination of prostate cancer cells, with mechanisms involving increase in NOX5 expression. However, specifically bone marrow adipocytes effect on prostate cancer cell have not been investigated in details. The experiments are logically sequenced and data clearly presented, in general supporting the conclusions that FFAs secreted by bone marrow adipocytes affect prostate cancer cells migration and invasiveness in vitro.

Major comments:

1) The authors state: "These data collectively demonstrate that PCa cells can trigger the release of FFAs from rBMAds cultured in 3D (Fig 1), which are then rapidly taken up and re-esterified into TGs by cancer cells." There are no data presented to show that prostate cells trigger the FFAs release from adipocytes- the data only show that FFA from adipocytes are taken up by prostate cancer cells. Use of condition media in combination with the coculture experiments would address this point. It is not clear how the authors came to the following conclusions: " In co-culture, the levels of these FFAs tended to increase (Fig. 1E), a trend also observed in total FFA content (Fig. 1F). The data presented in this figure have no statistical significance to support this statement, and moreover, the relative abundance in the PC3 COC appears to be simply addition of the abundance of PC NC and rBMAds NC, no alterations of secretion.

We agree that our data do not directly demonstrate that prostate cancer (PCa) cells induce the release of FFAs from rBMAds. Rather, our results show that FFAs present in the co-culture system are efficiently taken up and re-esterified into triglycerides by PCa cells (Fig. 1B-D). Accordingly, we have revised the manuscript to attenuate our interpretation and avoid implying a causal effect of PCa cells on induction of FFA release by rBMAds. We have also modified the corresponding text describing Figures 1E and 1F to underline that there are no changes in FFA present in the culture medium between rBMAds alone or cocultivated with cancer cells (lines 392-395).

2) GO analysis presented in this manuscript indicates that prostate cancer cells grown in bone marrow adipocytes condition media exhibit increased expression of gene sets associated with cell migration, cell adhesion, etc. were significantly induced under these conditions (Fig 3C). However, it seems contradictory that while locomotion and invasion were increased so were the gene associated with adhesion, as one would speculate that with increased invasion and mobility you will not have increased adhesion. This analysis also show that downregulated gene sets were mainly associated with proliferation regulation. However, the data included in Fig 3 H and I and supp figure show no effects on proliferation of the prostate cancer cells. This discrepancy should be discussed.

We agree with the reviewer that the concomitant upregulation of the “cell adhesion” and the “cell migration” GO terms may appear contradictory. However, genes annotated within the “cell adhesion” category are not exclusively involved in stable cell–cell adhesion; many of them like integrins subunits (ITGA3, 5, 6, ITGB1, 5) or actin cytoskeleton genes (ACTB1, ACTG1, ACTN1, ACTN4) also participate in the dynamic remodeling of cell–matrix and cell–cell interactions that are required for efficient cell migration. In this context, increased expression of adhesion-related genes can be consistent with enhanced migratory capacity. Similarly, the “regulation of cell population proliferation” GO term includes both pro- (ID2, LRP5) and anti-proliferative genes such as cell cycle inhibitor genes (CDKN2A, CDKN2B, CDKN2C, CDKN3, TGFB3, TGFBR2) reflecting a complex and balanced transcriptional response. This may explain why no significant changes in prostate cancer cell proliferation were observed in functional assays under co-culture conditions (Fig. 3H–I). As requested by the Reviewer 1, the list of genes associated with each GO term has now been added in Table 1 and we modify the manuscript accordingly (line 456-460).

3) Some of the genes associated with effects of adipocytes condition media or treatment with FFAs were confirmed by PCR and western blot in PC3 cells, but not in DU145 or LNCaP. These experiments should be done, and results in the other two cell lines should be included to demonstrated the generality of the mechanism of the observed effects. This is important specifically, as LNCaP cells is the only cell line used that expresses androgen receptor that is the hallmark of prostate cancer, and majority of bone metastasis express androgen receptor (PC3 and DU145 do not). Similarly, no migration results under coculture of LNCaP and rBMAds were included.

We would like to clarify that several of the points raised are supported by data already included in the manuscript. Specifically, we showed that both coculture with rBMAds and treatment with exogenous FFAs increase ANGPTL4 expression in PC3 cells (Fig. 5B–F) as well as in Du145 cells (Supplementary Fig. 5A–E). In contrast, although LNCaP cells exhibited increased migration (Supplementary Fig. 3B) and invasion (new Supplementary Fig. 3D) following coculture with rBMAds, ANGPTL4 expression was undetectable in this cell line under both basal conditions and after coculture (data not shown). These findings indicate that the enhanced migratory and invasive properties of LNCaP cells are mediated through an ANGPTL4-independent mechanism, highlighting the biological heterogeneity of prostate cancer and indicating that not all cell lines recapitulate the same molecular pathway. The manuscript was revised accordingly (lines 514-518). Importantly, the relevance of ANGPTL4 is further supported by our analysis of clinical prostate cancer datasets, which showed increased ANGPTL4 expression in bone metastases in comparison to primary sites and its association with poor prognosis in metastatic disease (see response to Reviewer 1 points 1 and 2 and new Fig. 6).

4) An important question concerns the clinical relevance of the observed effects of FFAs. In the in vitro experiments mainly migration and invasion, FFAs were used at 10 µM, including conditions in which three different FFAs were combined, each at a concentration of 10 µM. Notably, the magnitude of the effects was similar when FFAs were applied individually or in combination, suggesting possible saturation of the signaling pathway. Therefore, lower FFA concentrations, such as those found in the bone marrow microenvironment should be used to better reflect physiological conditions. Moreover, the FFAs were measured in adiposities condition media but only relative abundance was included in figure 1E, not actual levels.

We agree that the clinical relevance of the FFA concentrations used should be carefully discussed. We would first like to clarify that all experiments with exogenous FFAs were performed using 100µM of each FFA (palmitate, oleate, or linoleate), including the mixture in which each FFA was added at 100µM. The 10 µM concentration mentioned in the review appears to result from a misunderstanding. As the reviewer points out, no additive effect was observed when the three FFAs were combined compared with individual treatments in the migration (Fig. 4F and Supplementary Fig. 4A–B) and invasion assays (Fig. 4H), suggesting that the signaling pathways involved may already be saturated under these experimental conditions.

To address the reviewer's concern regarding physiological relevance, we estimated the amount of FFAs released by rBMAds after 3 days of culture to be approximately 100µM total FFAs. Lipidomic analysis (Fig. 1E) further showed that palmitate, oleate, and linoleate account for approximately 20%, 30%, and 20% of the total FFAs, corresponding to physiological concentrations of approximately 20µM palmitate, 30µM oleate and 20µM linoleate, respectively__. __We therefore performed additional migration experiments using these physiological concentrations. Under these conditions, treatment with each individual FFA did not significantly affect PC3 cell migration. In contrast, the combination of the three FFAs at their physiological concentrations significantly increased migration, suggesting that although individual FFAs are insufficient at physiological levels, their combined presence reaches a threshold required to promote prostate cancer cell migration. We are ready to include theses results in the manuscript upon referee request.

*5) The authors used SU2C data sets to evaluate ANGPTL4 expression in bone metastases and associated increased expression worse better survival. However, in this data set, it is clear that ANGPTL4 exhibits significantly higher expression in liver metastases than in bone metastasis. Some discussion about this aspect would increase the potential translational indication. *

We thank the reviewer for this important comment (also raised by Reviewer 1, point 2). While approximately 80% of prostate cancer metastases are located in bone, these metastases can acquire the capacity to generate secondary metastatic sites and contribute to further metastatic dissemination (Gundem et al, Nature, 2015, PMID: 32728210; Hong et al, Nature Communications, 2015, PMID: 25827447). Analysis of prostate cancer metastatic datasets, in which ANGPTL4 expression is assessed across different metastatic sites, revealed that ANGPTL4 expression is maintained and even increased in metastases located at secondary sites, such as liver and lung, compared with bone metastases (new Supplementary Fig. 6A). These findings suggest that high ANGPTL4 expression is not restricted to the bone microenvironment but may persist or become amplified during metastatic progression and contribute to late-stage metastatic dissemination. These results have been added to the revised manuscript and discussed accordingly (lines 575-580).

Minor comments:

6) Preparation of the gel description stipulates "One hundred microliters of SCAds or rBMAds were added and homogenized quickly with 100µL of thrombin....." Number of cells added for normalization should be added to the methods.

We have now included in the method part (lines 137-138), the estimated number of adipocytes within the gel, based on cell counts performed in a subset of samples (Shin et al, Cell Reports, 2026, PMID: 42348417).

7) In this sentence- is it correct to assume that oleate is also uM and not uL? "One day after seeding, cells were treated with 100μM palmitate (Cayman #29558), 100μL oleate (Sigma Aldrich #O3008), 100μM linoleate (Sigma Aldrich #L9530), or with the mix of 3 FFAs (100μM palmitate/100μM oleate/100μM linoleate) during 3 days.

We agree with the reviewer, it is a mistake. It is a concentration of oleate and not a volume. It was corrected in the manuscript by 100µM oleate (line 215).

8) There is a description of an experiment: "PC3 and Du145 were transiently transfected with ANGPTL4 siRNA pool (final concentration 25nmol/L) using ON-TARGETplus SMARTpool (Thermo Scientific Dharmacon) or ON-TARGETplus nontargeting pool used as a control (Thermo Scientific Dharmacon). Transfection was done according to the manufacturer's instructions with Lipofectamine RNAiMAX (Invitrogen Life Technologies) followed by 24h of coculture with rBMAds. After coculture, a second transfection was done and gene extinction, migration and invasion were evaluated." The rationale for second transfection (assuming still with siRNA) has not been provided and it is not clear.

We agree with the reviewer that clarification is needed. A second siRNA transfection was performed 24 h after coculture with rBMAds to maintain ANGPTL4 knockdown during the subsequent 24 h migration and invasion assays. For more clarity, the section materials and methods was corrected accordingly (lines 255-256).

9) Figure 6. Survival: HR and number of patients at each time point should be added to the graph. Some English editing is needed

The number of patients in each section “low ANGPTL4 expression” (n=8) and “high ANGPTL4 expression” (n=8) was added in the legend of the figure 6D (line 705).

Significance

There are multiple studies focusing on adipocytes and FFAs effects on cancer, in general, as well as on prostate cancer specifically. Effects on migration and invasiveness are well documented in literature. The novel aspect of the current manuscript is specifically looking at red bone marrow adipocytes, but it is not clear that the effects of FFAs would be different than when other adipocytes are used.

We agree that adipocyte-derived fatty acids have been implicated in cancer progression in a large number of study as we recently reviewed (Attané and Muller Trends in Cancer, 2020, PMID: 32610069). However, the novelty of our study is that it demonstrates that the origin and metabolic identity of adipocytes determine the prostate cancer (PCa) response. Most previous studies have focused on adipocytes from primary tumor sites, while studies investigating bone metastasis have mainly relied on in vitro-differentiated bone marrow adipocytes (like OP9) or mesenchymal stem cell-derived models, which do not fully reproduce the properties of mature human bone marrow adipocytes (Shin et al, Cell Reports, 2026, PMID: 42348417).

Using primary human rBMAds, we show that bone marrow adipocytes display specific biological features, including a non-canonical lipolytic pathway, and induce a distinct molecular response in PCa cells compared with periprostatic adipocytes. Specifically, rBMAds induce stronger ANGPTL4 expression, whereas NOX5, previously identified by our team as a mediator of PPAT adipocyte-induced effects (Laurent et al, Mol Cancer Res, 2019, PMID: 30606769), is not increased following rBMAd coculture. This demonstrates that adipocytes from different anatomical niches are not functionally equivalent and activate distinct tumor signaling pathways. The relevance of ANGPTL4 is further supported by our analysis of clinical PCa datasets, which showed increased ANGPTL4 expression in bone metastases in comparison to primary sites and its association with poor prognosis in metastatic disease.

Reviewer #3

(Evidence, reproducibility and clarity (Required)):

The study identifies a role for free fatty acids released by bone marrow adipocytes from red hematopoietic rich-areas in promoting prostate cancer cell migration and viability by inducing the expression of ANGPTL4. To achieve this the authors use to cancer cell-lines (LNCaP, PC3 and DU145) and a coculture model for their phenotypic assays and perform RNA-seq on one line (n=5 per condition) subjected to co-culture activation or not. The selection of ANGPTL4 is supported by its significant association with shorter survival times in clinical RNA-seq data from a metastasis cohort (SU2C) when highly expressed.

*1) The paper is concise and clear. The authors also quantify free fatty acid release and neutral lipid accumulation. It would be interesting to have a more comprehensive analysis (pathway and coexpression) of the RNA-seq data with RT-PCR validation of a number of significant transcripts that are up and downregulated. *

In the revised manuscript, we further strengthened the analysis of the RNA-seq data by reconstructing an ANGPTL4-associated gene network in Cytoscape using RNA-seq-derived differentially expressed genes enriched in cell migration GO terms and their interactions with ANGPTL4. This analysis revealed a highly interconnected network rather than a linear signaling cascade (Supplementary Fig. 5L) suggesting that ANGPTL4 promotes cell migration by orchestrating a coordinated transcriptional program involving multiple complementary signaling pathways. While this systems-level analysis reveals a coherent migration-associated network, it does not aim to establish a direct functional role for each individual gene, but rather to define the global transcriptional context of ANGPTL4-dependent migration. In line with this, we added and discussed the Cytoscape network of ANGPTL4-associated migration genes in the revised manuscript (lines 538-545).

2) Also a survival analysis in a localised PCa cohort using publicly available RNA-seq data.

As suggested, we assessed the clinical relevance of ANGPTL4 expression at different stages of disease progression. High ANGPTL4 expression in primary PCa tumors was not associated with either overall or disease-free survival (new Figure 6C). In contrast, elevated ANGPTL4 expression in bone metastases was significantly associated with poorer survival (Figure 6D), indicating that the clinical relevance of ANGPTL4 is primarily linked to the metastatic bone microenvironment rather than the primary tumor. We have revised the Discussion accordingly (lines 569–575).

(Significance (Required)): Explores an interesting biological question but in a limited number of pre-clinical models. Interesting as a startpoint for further studies.

Prostate cancer research is inherently limited by the availability of representative experimental models, with only a limited number of well-characterized prostate cancer cell lines compared with other cancer types (Cunningham et al, J Biol Methods, 2015, PMID: 26146646). The major prostate cancer models used in the field, PC3, Du145, and LNCaP, were included in our study. Importantly, our study goes beyond classical cancer cell line models by incorporating ____primary human rBMAds____, which remain rarely used due to their limited accessibility and the technical challenges associated with their culture. Using this physiologically relevant model, we demonstrate that adipocyte origin and metabolic identity critically influence the tumor response. Indeed, rBMAds display specific biological properties, including a non-canonical lipolytic pathway, and induce a distinct molecular response in prostate cancer cells compared with periprostatic adipocytes. Specifically, rBMAds induce stronger ANGPTL4 expression and elevated ANGPTL4 expression in bone metastases was significantly associated with poorer survival (Figure 6D). In contrast, high ANGPTL4 expression in primary PCa tumors was not associated with either overall or disease-free survival (new Figure 6C) indicating that the clinical relevance of ANGPTL4 is primarily linked to the metastatic bone microenvironment rather than the primary tumor. Together, these results support the biological and translational relevance of our model and identify a bone marrow adipocyte-specific signaling axis involved in prostate cancer progression.

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Referee #3

Evidence, reproducibility and clarity

The study identifies a role for free fatty acids released by bone marrow adipocytes from red hematopoietic rich-areas in promoting prostate cancer cell migration and viability by inducing the expression of ANGPTL4. To achieve this the authors use to cancer cell-lines (LNCaP, PC3 and DU145) and a coculture model for their phenotypic assays and perform RNA-seq on one line (n=5 per condition) subjected to co-culture activation or not. The selection of ANGPTL4 is supported by its significant association with shorter survival times in clinical RNA-seq data from a metastasis cohort (SU2C) when highly expressed.

The paper is concise and clear. The authors also quantify free fatty acid release and neutral lipid accumulation. It would be interesting to have a more comprehensive analysis (pathway and coexpression) of the RNA-seq data with RT-PCR validation of a number of significant transcripts that are up and downregulated. Also a survival analysis in a localised PCa cohort using publicly available RNA-seq data.

Significance

Explores an interesting biological question but in a limited number of pre-clinical models. Interesting as a startpoint for further studies.

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Referee #2

Evidence, reproducibility and clarity

Summary: This manuscript focuses on evaluation of effects of bone adipocytes on prostate cancer and their potential role in prostate cancer bone metastases progression. Mechanistically, the results show that fatty acid (FFA) secreted by bone marrow adipocytes increased expression of ANGPTL4 in prostate cancer cell lines in vitro, and this increase was dependent on PPARgamma signaling, resulting in increased migration and invasiveness of the cells. Evaluation of data from SU2C data set, was also included to support the conclusions, showing that increased levels of ANGPTL4 expression in bone metastases are negatively correlated with patients' survival, suggesting that ANGPTL4 could be a therapeutic target for prostate cancer bone metastasis. The authors previously investigated and published on crosstalk/interaction between periprostatic adipocytes and prostate cancer cells, where FFAs induced released by adipocytes elicited increased aggressiveness and dissemination of prostate cancer cells, with mechanisms involving increase in NOX5 expression. However, specifically bone marrow adipocytes effect on prostate cancer cell have not been investigated in details. The experiments are logically sequenced and data clearly presented, in general supporting the conclusions that FFAs secreted by bone marrow adipocytes affect prostate cancer cells migration and invasiveness in vitro.

Major comments: The authors state: "These data collectively demonstrate that PCa cells can trigger the release of FFAs from rBMAds cultured in 3D (Fig 1), which are then rapidly taken up and re-esterified into TGs by cancer cells." There are no data presented to show that prostate cells trigger the FFAs release from adipocytes- the data only show that FFA from adipocytes are taken up by prostate cancer cells. Use of condition media in combination with the coculture experiments would address this point.

It is not clear how the authors came to the following conclusions: " In co-culture, the levels of these FFAs tended to increase (Fig. 1E), a trend also observed in total FFA content (Fig. 1F). The data presented in this figure have no statistical significance to support this statement, and moreover, the relative abundance in the PC3 COC appears to be simply addition of the abundance of PC NC and rBMAds NC, no alterations of secretion.

GO analysis presented in this manuscript indicates that prostate cancer cells grown in bone marrow adipocytes condition media exhibit increased expression of gene sets associated with cell migration, cell adhesion, etc. were significantly induced under these conditions (Fig 3C). However, it seems contradictory that while locomotion and invasion were increased so were the gene associated with adhesion, as one would speculate that with increased invasion and mobility you will not have increased adhesion. This analysis also show that downregulated gene sets were mainly associated with proliferation regulation. However, the data included in Fig 3 H and I and supp figure show no effects on proliferation of the prostate cancer cells. This discrepancy should be discussed.

Some of the genes associated with effects of adipocytes condition media or treatment with FFAs were confirmed by PCR and western blot in PC3 cells, but not in DU145 or LNCaP. These experiments should be done, and results in the other two cell lines should be included to demonstrated the generality of the mechanism of the observed effects. This is important specifically, as LNCaP cells is the only cell line used that expresses androgen receptor that is the hallmark of prostate cancer, and majority of bone metastasis express androgen receptor (PC3 and DU145 do not). Similarly, no migration results under coculture of LNCaP and rBMAds were included.

An important question concerns the clinical relevance of the observed effects of FFAs. In the in vitro experiments mainly migration and invasion, FFAs were used at 10 µM, including conditions in which three different FFAs were combined, each at a concentration of 10 µM. Notably, the magnitude of the effects was similar when FFAs were applied individually or in combination, suggesting possible saturation of the signaling pathway. Therefore, lower FFA concentrations, such as those found in the bone marrow microenvironment should be used to better reflect physiological conditions. Moreover, the FFAs were measured in adiposities condition media but only relative abundance was included in figure 1E, not actual levels. The authors used SU2C data sets to evaluate ANGPTL4 expression in bone metastases and associated increased expression worse better survival. However, in this data set, it is clear that ANGPTL4 exhibits significantly higher expression in liver metastases than in bone metastasis. Some discussion about this aspect would increase the potential translational indication.

Minor comments:

Preparation of the gel description stipulates "One hundred microliters of SCAds or rBMAds were added and homogenized quickly with 100µL of thrombin....." Number of cells added for normalization should eb added to the methods. In this sentence- is it correct to assume that oleate is also uM and not uL? "One day after seeding, cells were treated with 100μM palmitate (Cayman #29558), 100μL oleate (Sigma Aldrich #O3008), 100μM linoleate (Sigma Aldrich #L9530), or with the mix of 3 FFAs (100μM palmitate/100μM oleate/100μM linoleate) during 3 days.

There is a description of an experiment: "PC3 and Du145 were transiently transfected with ANGPTL4 siRNA pool (final concentration 25nmol/L) using ON-TARGETplus SMARTpool (Thermo Scientific Dharmacon) or ON-TARGETplus nontargeting pool used as a control (Thermo Scientific Dharmacon). Transfection was done according to the manufacturer's instructions with Lipofectamine RNAiMAX (Invitrogen Life Technologies) followed by 24h of coculture with rBMAds. After coculture, a second transfection was done and gene extinction, migration and invasion were evaluated." The rationale for second transfection (assuming still with siRNA) has not been provided and it is not clear.

Figure 6. Survival: HR and number of patients at each time point should be added to the graph. Some English editing is needed

Significance

There are multiple studies focusing on adipocytes and FFAs effects on cancer, in general, as well as on prostate cancer specifically. Effects on migration and invasiveness are well documented in literature. The novel aspect of the current manuscript is specifically looking at red bone marrow adipocytes, but it is not clear that the effects of FFAs would be different than when other adipocytes are used.

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Referee #1

Evidence, reproducibility and clarity

Summary:

The study entitled "Human bone marrow adipocytes drive prostate cancer bone metastasis progression via lipid-mediated induction of Angiopoietin-like 4" by Hernandez et al. investigates the role of the bone marrow adipocytes (BMAds) from red hematopoietic rich-areas in the progression of prostate cancer (PCa) bone metastases. To do so, the authors used an elegant three-dimensional culture of primary human rBMAds isolated from the femoral bone marrow of patients undergoing hip surgery then cultured with PCa cell lines. The authors claim that PCa cells take up FFAs released by rBMAds which enhance the epithelial-mesenchymal transition and motility through upregulation of ANGPTL4. The article is well written, the figures are very clear and the methodology is perfectly described. To further improve the understanding of this mechanism, the authors should address 1) how PCa cells take up the FFAs, 2) whether PCa cells enhance non-canonical FFAs release and 3) the specificity of the rBMAds in their ability to upregulate ANGPTL4 compared to other adipocytes.

Major comments:

The paper's conclusions are overall convincing but the following supplementary experiments or discussion points could strengthen their claims. Is ANGPTL4 upregulation in PCa cells specific to rBMAds or could it also be seen with other adipocytes, such as periprostatic adipocytes or SCAds (used in Fig 2) ? Co-culture of PCa cells with SCAds should offer insights. More precisely, the article does not state if ANGPTL4 upregulation could be induced prior to bone invasion, by the periprostatic adipose tissue FFA release for example, explaining why ANGPTL4-high cells could be found in bone metastasis. In that case, increased motility and migration could be BMAds independent and trigger the first metastatic events originating from the primary prostatic tumor. The article hypothesizes an ANGPTL4-associated increase of motility and migration of PCa cells upon interaction with bone marrow adipocytes in the first metastatic bone, inducing enhanced invasion of said bone and secondary metastasis sites. However the article lacks evidence that ANGPTL4 is also upregulated in cells from secondary metastasis sites in patients. It would be interesting to explore in the existing data set the expression of ANGPTL4 in secondary metastasis of patients who had previous bone metastasis. These points could be addressed in the concluding remarks.

Additional experiments or qualifying the claims:

Fig 1 : It would be interesting to have an insight on the mechanism by which FFAs are uptaken by PCa. Fig 1D : It would be interesting to add an extra control of NC PCa treated with BODIPY to measure basal BODIPY uptake of PCa <br /> Fig 2 : The figure efficiently states that rBMAds undergo non-canonical lipolysis in comparison to SCAds, without PCa cells. Glycerol dosage and/or pan-lipase inhibitor treatment of rBMAds in co-culture with PCa would confirm rBMAds still show non-canonical lipolysis in bone metastasis environment. Fig2 : Is ANGPTL4 upregulation in PCa cells specific to rBMAds or could it also be seen with other adipocytes, such as periprostatic adipocytes or SCAds ? Co-culture of PCa cells with SCAds should offer insights. Fig 2 : Could the authors specify if there is a possibility the lipolysis kinetics is slower in rBMAds instead of an actual incomplete lipolysis ? Fig 3B/C : The author should provide tables to show : 1) all significantly up and down GO term 2) the top 20 genes DEG 3) any GO terms/genes related to EMT (table 1 should be associated with figure 3) Fig 5 : To complete experiences of KD of ANGPTL4 and PPARy inhibition, the author should also include the mRNA levels of EMT associated genes in these conditions. To better the clarity of the paper, the author should indicate in table S1 which patients are used in which figures. Also, what is the rationale for not using female patients in all the experiments ?

the suggested additional experiment should be achievable in 6 months.

Satistical analyses: The authors state in the Materiel and Methods that they used Student's t-test, one-way ANOVA or two-way ANOVA. These tests are applied to parametric data sets, validated for their normal distribution. Usually, n < 30 implies the use of non-parametric tests. The authors should better justify the rationale for their choices. Also, the details of tests for each figure is not indicated in the legends as stated in the Mat&Med.

Minor Comments:

In Fig 1F, the author should discuss the discrepancy between the significant increase of TG uptake in PCa shown in 1B and the non-significant effect seen in 1F, given that TG represents 85% of the total FFAs shown in 1E and 1F. Fig 3 : In Fig 3G and 4E, staining quantification would be necessary. In Fig3/Sup Fig3, why is the invasion assay not shown for LNCaP cell line ? 5F: Is there a reason why the sum of FFA has a stronger effect than the individual ones ? 5E/F : Rationale for changing FFA treatment duration between 5E and 5F (72h then 24h) ? For the discussion : the authors clearly describe the two different BMAds subtypes (cBMAds vs rBMAds), would it be interesting to question the role of cBMAds in PCa progression as well ?

The studies are referenced appropriately.

Please, could the authors indicate the co-culture duration with rBMAds in the legends of Figure 5. Excepted this point, the text and figures are clear and accurate.

Significance

General assessment:

the authors used an elegant three-dimensional culture of primary human rBMAds isolated from the femoral bone marrow of patients undergoing hip surgery then co-cultured with PCa cell lines. The authors claim that PCa cells take up FFAs released by rBMAds which enhance the epithelial-mesenchymal transition and motility through upregulation of ANGPTL4. The most important aspects of this study are 1) the description of the non-canonical FFAs release from rBMAds, 2) the induction of EMT/motility of PCa cells induced by FFAs uptake. To further improve the understanding of this mechanism, the authors should address 1) how PCa cells take up the FFAs, 2) whether PCa cells enhance non-canonical FFAs release and 3) the specificity of the rBMAds in their ability to upregulate ANGPTL4 compared to other adipocytes.

This study extends the knwoledge in the field of protaste cancer metastasis. The authors have developed an elegant 3D culture model of primary human rBMAds, which is highly relevant for investigating the role of adipocytes in cancer cell behavior. Indeed, most models used in the literature rely on adipocytes differentiated from bone marrow mesenchemal stem cells. Although adipocytes differentiation models have recently been improved by incorporating 3D structure, the model developed by the authors is most physiological, as it is based on the direct use of primary bone marrow adipocytes. In this way, this model represents a valuable tool to advance our understanding of mechanisms involved in bone metastasis in breast/prostate cancers.

The type of audience that will be interested by this research include both basic and specialized researchers. Moreover, this study should improve 1) the understanding of the impact of rBMAds on prostate cancer behavior and 2) the robustness and physiological relevance of adipocyte-based studies.

Our expertise lies in the interaction between normal or pathological hematopoiesis with the components of bone marrow microenvironment.

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Reply to the reviewers

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

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Referee #3

Evidence, reproducibility and clarity

Summary

This manuscript presents a comprehensive experimental analysis of the calcineurin pathway in the fungal pathogen Cryptococcus neoformans, a pathway that is important for thermoregulation and virulence. Calcineurin is a calcium-dependent protein phosphatase complex that is conserved in eukaryotes and that is required for growth at high temperature in fungi, and thus for fungal pathogenesis in humans. The work uses a range of approaches including genetics, proteomics, and transcriptomics to establish important new insight into the pathway.

Genetic screens for growth of C. neoformans H99 / KN99 at high temperature in the absence of calcineurin discover suppressors including inactive alleles of the Yak1 kinase. Extensive mutagenesis and phosphoproteomics assays confirm Yak1 as the primary kinase that opposes calcineurin-dependent dephosphorylation, an important result in the field. This complements and extends the authors' recently published work in C. deneoformans (Yadav et al., 2025, https://doi/10.1073/pnas.2503751122), which identified but did not follow up Yak1 mutations as suppressing calcineurin deletion. The importance of that study, including Yak1, was highlighted in a news and views article (Mitchell, 2025, https://doi.org/10.1073/pnas.2511623122).

Proximity-labeling proteomics with TurboID discover interactors of calcineurin, a dataset complementary to phosphoproteomics (in wild-type, calcineurin deletion, yak1 deletion) in mapping the signaling pathway. Transcriptomics and translatomics assays aim to map gene expression regulation downstream of calcineurin. Furthermore, molecular functions of the Cna1 component of calcineurin are dissected with a series of mutants, including their impact on thermoregulation and Cryptococcus virulence in mice.

Major comments

The main result, that "Yak1 as the kinase that acts antagonistically to calcineurin at 37{degree sign}C", is thoroughly supported by multiple lines of evidence. The genetic suppressor screens identify 8 distinct alleles of Yak1 that allow cnb1∆ strains to grow at 37{degree sign}C. They confirm the suppressive effect of yak1∆ in two different strain backgrounds and in the presence of FK506 and CsA drugs. The phosphoproteomics experiments show 409 overlapping phosphorylation events that are down in yak1∆ compared to up in cna1∆, although a quantitative analysis e.g. enrichment of these shared targets is not presented.

The proximity-labeling proteomics is an important assay with appropriate controls, and generates several hypotheses that are then followed up on. The methods section on the proteomics results is detailed and comprehensive.

In my opinion, the results in the rest of the manuscript (validation of interactions witn microtubules etc, transcriptomics and translatomics, Cna1 mutant series) are not clearly integrated with the Yak1 kinase and proteomics results. Also, the discussion does little to critically synthesize the results presented within the context of wider knowledge including the authors' own recent work. The authors could choose to publish a more focused manuscript that concentrates on identifying Yak1 as the suppressor, or they could more clearly synthesise the wider set of results that they present.

Overall the figures are well presented both for the Cryptococcus microbiology (spot assays, mating, etc.) and omics experiments (e.g. consistent evidence from PCA that 3 biological replicates cluster together). Experimental design schematics help the reader,

Some claims are made superficially and need to be critically evaluated, notably the question of mitochondrial targets of the apparently cytosolic calcineurin complex.

Furthermore, the manuscript lacks critical details and data sharing for some experiments and analyses, notably the transcriptomics and translatomics assays that are not possible to evaluate as currently presented. No data sharing (e.g. reviewer tokens) was available for my review. DNA sequencing is listed as shared on NCBI project PRJNA1306639, and TurboID data listed as shared on PRIDE project PXD067478. There's no mention of data sharing for phosphoproteomics, nor for transcriptomics/translatomics. I consider it appropriate to share data along with preprints, and thorough data sharing is required for publication in any reputable journal.

Mitochondrial targets. The literature suggests that Calcineurin is located in the cytosol, however this manuscript reports differential calcineurin-dependent phosphorylation of mitochondrial proteins, including some that are encoded in the mitochondrial genome. I did not find the discussion of this in the paper convincing. It seems there are four possibilities (a) "calcineurin dephosphorylates [some mitochondrial proteins] prior to their import into the mitochondria"; (b) calcineurin dephosphorylates cytosolically exposed peptides of mitochondrial outer membrane proteins; (c) a subpopulation of Calcineurin is in mitochondria; or (d) calcineurin affects via a cascade or indirect effects mitochondrial kinases and/or phosphatases.

Dephosphorylation prior to import is inconsistent with current models of co-translational mitochondrial import, unless calcineurin were acting co-translationally? I do not think interactions with eIFs support this argument, because eIFs are release from the mRNA early in translation elongation.

Calcineurin acting on and interacting with cytosolically exposed peptides should be addressable by analysing current datasets to find differential phosphorylation and/or biotinylation specifically of cytosolic segments of mitochondrial proteins. I strongly recommend that the authors do this analysis and discuss the results.

The authors tried to assess Calcineurin localisation in mitochondria, briefly.

Otherwise, a cascade or indirect effects seem more likely.

Transcriptomics and translatomics: the data analysis descriptions, data presentation, and data sharing are not sufficient for publication. See e.g. MINSEQE guidlines https://doi.org/10.5281/zenodo.5706412, and https://doi.org/10.1093/bib/bbz124. Experimental descriptions are thorough. However, the Ribo-seq/ribosome profiling protocol described, with pre-incubation of cells with harringtonine and cycloheximide then slow lysis, is far from best practice established in the extensive literature on ribosome profiling methods (see papers by Gloria Brar, Nick Ingolia, Sebastian Leidel, and Vadim Gladyshev, etc.), a limitation that should be discussed. Sequencing preparation and execution should be described accurately, e.g. it does not make sense for Ribo-seq data with ~30nt inserts to use 150PE sequencing. Data analysis steps should be described sufficient to reproduce the analysis. Key QC should be reported: read depth for each dataset, read length and frame information critical for interpreting ribosome profiling data, scatter plots or comparisons of TPMs or other gene-level summaries beyond the "TE" . PCA plots must describe what the PCA is calculated on (TPMs, log2 fold-change, or all or some genes, etc.). Data should be shared including raw reads and summarised gene-level reads.

OPTIONAL: beyond reporting the data, there is scope for additional insights from analysing these data. For example, are Crz1-dependent genes differentially expressed or translated?

Discussion. The short 5-paragraph discussion mostly reiterates the results, with limited engagement with wider context. Even the authors' recent related work in C. deneoformans, where cytokinesis factors suppress calcineurin phenotypes, gets only 3 sentences. To increase its impact, the manuscript would benefit from a considerably expanded critical discussion, including some of:

• relating their C. neoformans and C. deneoformans results to each other.
• discussing evidence for and against the conservation of Yak1 being antagonistic to Cna1 amongst fungi or more broadly, e.g. was there any precedent for this result from work by other groups?
• discussing evidence for Cna1 and Yak1 having shared direct targets, including quantitatively from the new data and in reference to any other studies in other organisms.
• discussing localisation of Cna1, and how that might affect interpretation of TurboID data and of truncation mutants.
• expanding the discussion of mitochondrial targets with alternative hypotheses and wider literature engagement.
• evaluating transcriptomics and translatomics results in light of other studies in Cryptococcus and beyond.
• engaging with the role of calcineurin in translation: could it dephosphorylate translation initiation factors?

Minor comments

On novelty of TurboID in C. neoformans: it would be appropriate to cite Kalem, Panepinto, and co-authors' work which was to my knowledge the first TurboID work in this fungus (https://doi.org/10.1101/2022.01.13.475903).

On Cna1 interactors in the spliceosome: it would be appropriate to compare with the work by Madhani and colleagues that map the C. neoformans spliceosome and its function (https://doi.org/10.1016/j.cub.2021.09.004).

On Ribo-seq in C. neoformans: it would be appropriate to compare key results (e.g. TPMs, TE) and QC metrics to the only published Ribo-seq dataset in C. neoformans by Wallace, Maufrais, et al. (http://.doi.org/10.1093/nar/gkaa060). Disclosure: I am a lead author on that study. Likewise, for the arguments on splicing regulation it would be appropriate to compare with datasets from Wallace, Maufrais et al, and others from Guilhem Janbon lab, that conduct RNA-seq at different temperatures.

OPTIONAL: Do the truncation mutations of Cna1 affect its localisation or interactions?

Materials and Methods: Different parts are described in different levels of detail and this should be thoroughly checked so that a reasonable colleague could reproduce the experiments and analyses. The genetic screen and proteomics descriptions, for example, are thorough. All data analysis should be described for all assays, including methods used in software for sequence and image analysis beyond "Geneious prime" or "ImageJ", and software cited.

All strains should be thoroughly described, currently also in different levels of detail - e.g. what is the sequence of Cna1-TurboID tag (source of tag, linker, etc.).

Referee cross-commenting

All reviewers agree on the importance of Yak1-calcineurin interactions. All reviewers also agree on the need for synthesis of the data, and to address the current emphasis on the manuscript of associations/correlations/data magnitude over mechanism and synthesis.

Reviewer 1's point that "cna1∆ strain clustered apart from inactive mutants and even the epitope-tagged wild-type behaved differently from the true wild-type" is important. Reviewer 2's point about testing the functionality and localisation of Cna1-TurboID is also important, and aligns with the request to describe this strain in detail. These suggest additional experiments and/or recognizing limitations in the discussion, are needed.

Significance

Overall, the study represents an important advance in the field, that everyone working on calcium signaling in fungi, on Cryptococcus virulence mechanisms more generally, or on the calcineurin pathway more generally, will need to read and cite. Both the experimental results and the large-scale data presented are major contributions, notably the discovery of Yak1 kinase as the primary antagonist to calcineurin phosphatase at higher temperatures.

Thorough experimental and analysis descriptions and data sharing would make this study far more valuable. Synthesising the results, including with an upgraded critical discussion and literature engagement, would increase the impact of the study.

"Please define your field of expertise:" I'm a quantitative biologist working on gene expression regulation in fungi, using approaches including molecular microbiology and 'omics data, and have published on thermoregulation, translational control and its evolution, and C. neoformans.

Review signed by Edward Wallace, University of Edinburgh.

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Referee #2

Evidence, reproducibility and clarity

This study defines a comprehensive thermoregulatory network in Cryptococcus neoformans, revealing that calcineurin and its antagonistic kinase Yak1 regulate thermotolerance through shared substrates. The authors further show that calcineurin mediates thermal adaptation via novel interactions with translation initiation factors, spliceosome components, and mitochondrial proteins, and that distinct structural domains of calcineurin differentially regulate thermotolerance, meiosis, and virulence.

Overall, the study presents an extensive dataset integrating RNA-seq, TurboID proximity labeling, phosphoproteomics, and genetic screens. The experimental scope is impressive, but the analysis often emphasizes data magnitude rather than biological interpretation. The manuscript would benefit from deeper synthesis of what these datasets reveal about calcineurin function beyond its global impact.

Major Comments

1. The role of Yak1 mutations in spontaneous suppressors is not directly validated by allelic reconstruction or complementation in the original genetic backgrounds. Establishing causality is essential to link Yak1 loss with calcineurin-related thermotolerance phenotypes.
2. The interaction claims rely on the TurboID proximity map generated using a Cna1-TurboID fusion, which shows good replicate consistency and clear temperature-specific enrichments. However, the study does not show that the fusion protein is functional or correctly localized under heat stress. Calcineurin is known to relocalize during thermal stress at 37{degree sign}C, moving from diffuse cytoplasmic distribution to ER-associated puncta and the mother-bud neck. Without complementation of calcineurin-dependent phenotypes or independent localization data for the Cna1-TurboID fusion, the interactome identified in Fig. 2E-2G could reflect stress-induced relocalization or tag artifacts rather than calcineurin's native interaction landscape. The Western blots in Supplementary Fig. S2A-S2B confirm expression and biotinylation but not functional integrity or localization fidelity. Demonstrating that the fusion complements calcineurin loss is critical to attribute the 37{degree sign}C interactome to native calcineurin activity.

Minor Comments

Fig. S1C is missing a color legend.

Lines 106-108: The text does not match the referenced figure (Fig. S1D).

Fig. S1E: The authors clarify what distinguishes the two different knockout strains.

Fig. 2G: The authors state that "the most enriched biological processes included proteins from the translation initiation complex, the spliceosome, the proteasome machinery, and mitochondria." Please clarify what analysis supports these enrichments, as the GO term analysis in Fig. 2F does not include these processes.

Fig. 5F: Control wild-type crosses should be shown for comparison.

Panels in Fig. 5 should be reordered to match their sequence in the main text.

Significance

This study presents a comprehensive map of the thermoregulatory network in Cryptococcus neoformans, integrating genetic screens, proximity labeling, phosphoproteomics, and ribosome profiling to define a broad signaling framework controlling thermal stress adaptation. By combining these approaches, the authors provide a systems-level view of how calcineurin orchestrates thermotolerance, extending beyond individual pathways to reveal network-wide regulation. Through two independent genetic screens, the kinase Yak1 is identified as the principal antagonist of calcineurin, establishing a clear opposing relationship within the thermotolerance pathway and highlighting Yak1 as a key regulator of heat-stress signaling. Using TurboID proximity labeling, the study also uncovers previously unrecognized roles for calcineurin in microtubule organization, spliceosome function, and mitochondrial translation, substantially broadening the known functional scope of this conserved phosphatase.

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Referee #1

Evidence, reproducibility and clarity

This impressive manuscript combines several different "omic" technologies to broadly survey the functions of calcineurin in Cryptococcus neoformans. First, it utilizes genetic screens to identify YAK1 protein kinase as an antagonist of calcineurin signaling, mutations in which reverse the temperature-sensitive phenotypes of calcineurin deficiency. The phospho-proteomes of yak1∆, cna1∆, and wild-type strains were also determined at 25{degree sign} and 37{degree sign}, indicating potential instances of convergence of the regulatory enzymes on common substrates that could regulate thermotolerance. TurboID was optimized and implemented to further understand the proteins in close physical proximity to calcineurin, a number of which contain docking motifs for binding of calcineurin as well as phospho-sites that undergo calcineurin-sensitive changes. A new role for calcineurin in regulation of microtubule functions was deduced and validated to some degree using fluorescent probes of nuclear morphology and alterations to benomyl susceptibility. RNA-seq was utilized to establish roles of calcineurin in transcription and splicing of mRNAs. Ribo-seq was also utilized to establish roles of calcineurin in the efficiency of translation of subsets of mRNAs, particularly those encoding mitochondrial proteins. Then a series of strains expressing calcineurin proteins with epitope tags and C-terminal truncations were analyzed in great detail for variation in signaling outputs. C-terminal tags on Cna1 selectively abolished its role in virulence. Some truncation mutants had gained activity through loss of auto-inhibitory domains and other regulatory inputs. Others had lost activity almost completely. Phospho-proteomes of all these strains were analyzed at two temperatures and found to be consistent with some expectations. Curiously, the cna1∆ strain clustered apart from inactive mutants and even the epitope-tagged wild-type behaved differently from the true wild-type. Temperature caused a rather large shift in phospho-proteomes that was mostly independent of calcineurin. Wow, what an enormous resource for the field (and playbook to followed in other systems)!

Major concerns.

Despite the massive breadth of the multi-omics data, there was no real pinpointing of new substrates of calcineurin that could directly impact thermotolerance or the other phenotypes. Normally this achieved through site-directed mutagenesis of the phospho-sites within the substrate and careful analysis of the relevant phenotypes along with some directed analyses of calcineurin-dependent changes in phosphorylation of the substrate. The "validation" by enhanced benomyl sensitivity, for example, is not really a validation because the finding could be explained by calcineurin-mediated effects on drug import/export/metabolism as opposed to effects on the cytoskeleton. In the end, the manuscript produces a wealth of associations and correlations but falls short of advancing any specific molecular mechanism of regulation. This is the most prominent weakness of the manuscript.

Minor concerns.

1. Typos in fig 6F and 6G (hyperphosrylated?)
2. Why exactly do the inactive truncations of Cna1 look so different from cna1∆ mutants in terms of the phosphoproteomes at both temperatures (Fig. 6D)?
3. Why wasn't a Cna1-dead mutant (mutation in active site) also tested? What is the predicted behavior in phosphoproteomes and other methods?
4. Does the yak1∆ phosphoproteome resemble those of gain-of-function Cna1 alleles? Yak1∆ should be included in the principal components analysis of Fig. 6D.
5. Fig. 6E (clustering) seems to have missed the mark by failing to recapitulate some of the main associations in 6D. Can this be improved by tweaking the parameters? Or removed altogether?
6. Temperature seemed to cause a major shift of the phospho-proteome independent of calcineurin. Somehow that message was not obvious in the Discussion or Abstract.
7. More discussion of how C. deneoformans differs from C. neoformans is needed. How drastic is the "rewiring" of calcineurin, and what does this mean for the evolvability of calcineurin signaling across the tree of life?

Significance

The study takes on the difficult challenge of understanding how an environmental microbe has evolved to thrive at elevated temperatures of the human body, causing fungal disease. Calcineurin was previously shown to be necessary for proliferation of C. neoformans at such high temperature, but the mechanism was unclear. Though this study did not pinpoint an output of calcineurin signaling responsible for thermotolerance, it provided a vast survey of the numerous factors that could be involved and a resource for deeper studies in the future.

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Reply to the reviewers

Manuscript number: RC-2026-03566

Corresponding author(s): Mandë Holford

1. General Statements [optional]

The authors would like to thank the reviewers for their thorough analysis of our study and the critical perspective for improvements. We appreciate their time and effort, and expert feedback. Below we list all comments and suggestions of the reviewers, together with our detailed point-by-point reply (in blue).

2. Description of the planned revisions

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

Summary

The manuscript entitled « Neurons, Muscles, and Venom: Elucidating a Neural-to-Secretory Pathway in Cephalopod Predation » by Kirchhoff et al. investigates the anatomical and molecular basis of venom release in coleoid cephalopods. The authors used a combination of histology, immunohistochemistry, micro-computed tomography, comparative phylogenetics, and ex vivo calcium imaging to conclude that venom secretion from the posterior salivary gland (PSG) is under neuromuscular control through cholinergic and potentially dopaminergic regulation. They also show that this is a conserved structural feature across octopus, squid, and cuttlefish species.

Overall, this manuscript addresses an understudied topic, namely the mechanisms regulating venom secretion, which is poorly understood in most venomous systems despite their ecological and evolutionary significance. As such, this work provides an important anatomical and molecular characterization of cephalopod posterior salivary glands and generates valuable hypotheses regarding the neural regulation of venom secretion. I personally appreciate the quality of the histology work, a methodology largely neglected nowadays in a world thirsty for the use of high-tech, fancy instrumentations.

Although I command the authors for this elegant and visually pleasing study, I have some reservations about the major mechanistic conclusions (especially the cholinergic and dopaminergic regulation), which to me rely on indirect evidence, as no experiment directly demonstrates neural control of venom secretion. Therefore this manuscript would benefit from additional functional validation and certainly a more cautious interpretation of the findings.

Major Comments

• The principal conclusion of the manuscript is that venom release is under neuronal and neuromuscular regulation, which is highly likely given the authors convincingly demonstrate the presence of actin-positive muscular structures, neuronal markers within the PSG, cholinergic-associated markers, spontaneous calcium activity. Unfortunately, none of these experiments directly demonstrate control of venom secretion ! The presented evidence establishes anatomical proximity between neural and muscular elements but does not demonstrate causality. For instance, no experiments measure venom release following neuronal stimulation or receptor activation/inhibition.

Therefore I suggest that the authors substantially temper these conclusions or provide functional experiments demonstrating secretion following pharmacological or electrical stimulation.

Author’s response: We agree with the reviewer’s comments that our findings “convincingly demonstrate” that venom release is under neuronal control, but without experimental evidence cannot definitely make this claim. In vivo experimental verification of venom secretion after neuronal stimulation are complex studies with anatomical, analytical and animal welfare limitations. Even though we agree with the reviewer that these would be the ultimate verification for the neuronal control and neurotransmission systems involved in venom release, this is out of scope for the present study which is meant to be descriptive in providing a foundational overview of potential mechanisms for venom release. In this vein, we will revise the manuscript to “temper our conclusions” as the reviewer requested. Specifically, we will revise the contextualization of our data and make clear the level of insights that they allow versus their limitations.

• Furthermore, the conclusion that acetylcholine is a major neurotransmitter regulating the PSG is based on α-bungarotoxin labeling, ChAT expression and phylogenetic identification of nicotinic receptor homologs.

My concerns is that α-bungarotoxin binding specificity in cephalopods has not been demonstrated. Although I agree that α-bungarotoxin binding is generally associated with nAChRs binding (not only muscle-type, but also α-7 and α-9 containing neuronal receptors), there are also evidences (weaker, I admit) that it may also interact with GABAA receptors, as well as some VGICs (potassium, sodium). There are also confirmed non-canonical protein interactions, such as with Ly6-family proteins. So first, it must be determined what α-bungarotoxin is binding to in cephalopods. In addition, ChAT expression alone does not prove cholinergic neurotransmission, and to be fair, the receptor phylogeny does not establish receptor expression in the specific cells observed histologically (only that it is found in the venom gland transcriptome). Importantly, from what I could see, no co-localization is shown between, cholinergic neurons, receptor-positive cells, and muscle fibers.

The cholinergic circuit remains hypothetical, although it can be defended as a strong hypothesis. To reflect this, the authors should moderate their interpretation and explicitly distinguish between evidence for cholinergic potential and/or demonstrated cholinergic signaling.

Author’s response: While we agree with the reviewer that the target specificity of each marker needs to be verified in new species and taxa under study, we would like to point towards a study in the branchial heart in Sepia officinalis (Gebauer & Versen, 1998) showing strong inhibition of nicotinic signaling by alpha-bungarotoxin addition even in presence of high concentrations of the agonists. Additionally, alpha-bungarotoxin is widespread in use for muscle type nAChR identification and characterization across taxa, and the binding affinity has been proven to be exceptionally high for these receptors, with off-target affinities being significantly lower. Therefore, as the reviewer mentions, we have a “strong hypothesis” to suggest a cholinergic circuit is present in the venom gland. To highlight these target specificities and affinities for the markers used, we will add an additional supplementary section on their known molecular targets and their verification in cephalopods. Further, we will extend the discussion to point towards the limited knowledge on off-targets, receptor sequence/structural similarity ambiguities between vertebrates and invertebrates, and the resulting limitations on the data interpretation.

• The authors repeatedly suggest dopaminergic participation in venom release. Here, however, the evidence consists solely of transcriptomic identification of receptors clustering with dopamine-gated channels in phylogenetic analyses. Quid of dopamine synthesis enzymes, dopamine localization, dopaminergic neurons, dopamine-dependent physiological responses?

I believe the statements implying a role for dopamine in venom secretion are premature, so the authors should restrict discussion of dopamine to a candidate pathway requiring future validation.

Author’s response: We agree with the reviewer that this conclusion needs a more tempered tone aligning it with the indicators obtained from the phylogenetic analysis and will revise the text to indicate the need for future validation. However, we also would like to highlight that recently dopamine-gated channels have been verified and functionally characterized in the optic lobe of cephalopods [1], and these are clustering together with the PSG transcripts of the channels found in all three species of cephalopods included in this analysis, providing strong evidence for our hypothesis that there is dopaminergic participation in venom release.

[1] Courtney, A., Styfhals, R., Van Dijck, M., Boulanger, J., Geenen, L., Lanoizelet, M., ... & Schafer, W. R. (2025). Novel dopaminergic neurotransmission in the Octopus visual system. bioRxiv, 2025-04.

I also have some less important or minor comments:

• The distinction between secretory and smooth-striated tubules is a central component of the proposed secretion model. Yet, the functional interpretation of tubular subtypes remains uncertain, as the authors acknowledge that differentiation was clear in octopus, but incomplete or uncertain in squid, and micro-CT identification of secretory tubules in E. berryi was inconclusive.

Given this uncertainty, the proposed model of distal production and proximal transport remains speculative and additional histochemical characterization or molecular markers would strengthen these interpretations.

Author’s response: As highlighted by the reviewer, we stated that the functional organization within the gland in secretory and transportation regions is only one potential scenario and needs cross-species comparison and functional verification. In order to ensure that this differentiation is a proposed scenario of the functional architecture of the gland, we will rephrase the corresponding sections. We will revise the text to clarify that the findings in the octopus is a proposed model that needs to be confirmed in squids and cuttlefish.

• p6 The reference for the statement that « holocrine secretion is proposed for cone snail » is not convincing (Vonk et al. deals with scorpions, and only a schematic drawing is presented to illustrate the different secretion routes for various venomous animals) so the authors should provide a research article as reference, but I am not aware of any published study that explicitly tested this hypothesis and found positive evidence (need to show that whole-cell disintegration contributes substantially to venom release). « Insoluble granules » are seen inside secretory cells and sometimes also retrieved in milked venoms, but not always. If holocrine secretion occurs, they should always be there, if not, merocrine secretion might also be at work.

Author’s response: There seems to be some confusion about the cone snail holocrine secretion statement and we’d like to clarify. As written in the manuscript, “holocrine secretion is proposed for cone snails,” which means it is not definitive and is an ongoing topic of discussion in the field. A recent publication on cone snail venom release also suggests a holocrine release, and we will revise the text to mention this manuscript and update the references to include this citation [2].

[2] Rogalski, A., Himaya, S. W. A., & Lewis, R. J. (2023). Coordinated adaptations define the ontogenetic shift from worm-to fish-hunting in a venomous cone snail. Nature Communications, 14(1), 3287.

• A minor but possibly relevant comment on the fact that most antibodies were originally developed for vertebrate systems. Although some validation controls are shown, stronger evidence for specificity in cephalopod tissues would be desirable, particularly for NeuN, α-actin, and neurofilament (SMI-31).

Author’s response: As discussed for the bungarotoxin comment above, we agree on the importance of highlighting the target specificity of the histological markers in cephalopod tissue. Further, for monoclonal antibodies a single epitope is being targeted determining the high target specificity, thus target presence is assumed with signal recording. For polyclonal antibodies, such as the NeuN antibody, several epitopes are being targeted given better cross-taxa applicability and higher sensitivity, but increases the chance of off-target binding. Therefore, we will further establish a supplementary section on the molecular targets, tested control tissues for contextualization of PSG signal observations, and previous studies assessing the targets of these markers in cephalopods or molluscs.

Reviewer #1 (Significance (Required)):

Overall this manuscript provides an important anatomical and molecular characterization of cephalopod posterior salivary glands and generates valuable hypotheses regarding the neural regulation of venom secretion. The comparative dataset is extensive and likely to be of interest to researchers in cephalopod biology, neurobiology, and venom evolution. However, the major mechanistic conclusions currently exceed the strength of the evidence so that significant revision is therefore required to align the claims with the data.

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

The paper uses modern approaches to address a fascinating question that has been relatively unexplored since J.Z. Young's morphological work in the 1960s: how venom release is controlled in the posterior salivary gland (PSG) of coleoid cephalopods. The authors' work uses five species spanning the three major coleoid groups: octopus (Octopus bimaculoides), squid (Doryteuthis pealeii, Euprymna berryi), and cuttlefish (Ascarosepion bandense, Sepia officinalis), and employs a broad toolkit: synchrotron micro-CT, a panel of histological and immunohistochemical stains, multiplexed HCR, a comparative phylogeny of cys-loop ligand-gated ion channels, and an ex vivo calcium-imaging proof of concept.

Structurally, they identified a shared two-tubule architecture (proximal-striated and distal-secretory), a peri-tubular actin layer they interpret as a possible circular smooth-muscle layer, and dense innervation labeled by neurofilament and synapsin. They also show α-bungarotoxin-positive nicotinic receptor signal and ChAT expression near putative neuromuscular contacts in some of the species examined. In the PSG transcriptome datasets with confirmed LGIC recovery, acetylcholine- and dopamine-gated cation-channel groups are prominent. A live E. berryi PSG explant shows spontaneous calcium activity. From these findings, authors propose a working model in which cholinergic and dopaminergic input mediate secretory tubule activity and contraction of the surrounding muscle to move venom toward the beak.

The study is mainly descriptive and comparative. My major points address matching the strongest claims to the data presented. The minor points are figure, reference, and reproducibility fixes, several of which simply need a careful pass.

Major comments:

1. The calcium imaging is described inconsistently between the abstract and the rest of the paper. The abstract says "ex vivo stimulation of the PSG elicits calcium signaling throughout the gland" (L34-35), but no stimulation was applied. The methods describe only dissection, incubation in CAL-520, and epifluorescence imaging. The octomedia is physiological (not depolarizing), and the analysis step refers to "spontaneously active regions." Everywhere else the authors are more cautious. The section heading only "suggests" calcium signaling activation (L216), and the results call the activity spontaneous and the experiment a pilot study, noting that "further analyses are required to determine if this activity is neural or muscular" (L222-228). "Throughout the gland" also overstates a result localized near the gland edge.
2. Required either way: drop "stimulation" and "elicits" from the abstract, describe what was actually done, and soften "consistent with neural regulation" for a spontaneous signal of unknown cellular origin.
3. Optional (only if the authors want to keep the neural-regulation speculation) the explant preparation and the CAL-520 protocol already exist, so a depolarizing stim with a cholinergic agonist and antagonist control, recorded the same way, would show whether the signal is evokable and start to separate neural from muscular sources. This is an extension of the existing assay, not a new experimennt.
4. Reframing the section as spontaneous pilot activity resolves the point just as well. I am not asking for new data as a condition of publication, and either is fine.
5. The Results subheading "Live staining of squid venom gland explant" (L216) is imprecise. CAL-520 is a calcium indicator rather than a stain, and the experiment is live-tissue calcium imaging of an ex vivo explant, so the heading reads as histology on living tissue and underdescribes what was actually done.

Author’s response: The reviewer identified this analysis correctly as a pilot study and a bridging analysis between the histology based molecular indicators and the follow-up in vivo venom secretion stimulation study. We will rephrase the corresponding sections to ensure that it is consistently stated as a pilot study for spontaneous calcium activity in explants.

We would also like to point out that currently the molecular agonists of the nicotinic receptors in cephalopods, and even most of the other receptor types currently identified in these lineages, have not yet been determined. This functional characterization and ligand identification could be a stand-alone study and out of scope for the present study. In our current manuscript we provide preliminary evidence for potential calcium signaling in the gland. For our revised manuscript, we are attempting to include additional experiments to describe the variation of calcium activity in explanted venom glands upon addition of acetylcholine in comparison to the baseline spontaneous activity previously observed.

Replication and quantification are not reported. The descriptive observations are convincing overall, but the comparative language ("conserved," L36, L90; "stereotyped," L30) rests on single representative images, and I couldnt find n (animals, sections) for any stain or any quantification of the spatial and cross-species claims. For a claim about conservation across lineages, that support is necessary, and does not require new experiments.

• Give n (animals and sections) per stain per species.

• Where the claim is about spatial pattern (peripheral versus central, peri-tubular versus luminal), add basic quantification.

• Several claims are clearly meant to be qualitative. Say so, and be explicit about which conclusions are based on representative examples vs replicated or quantified observations.

• This should be achievable from the existing data.

Author’s response: We agree the replication of the experiments is crucial to ensure reproducibility and data interpretation and we will revise the corresponding sections to reflect quantification of experimental data, and where appropriate indicate if results are purely qualitative. While several tissue sections per animal have been stained, replication is most representative across specimens. This has been challenged by the accessibility of the study species, but also their maturity stage and related body sizes. We address these and other limitations in a dedicated supplementary section.

The actin antibody needs to be identified clearly. The main text calls Abcam ab119952 an "α-actin" marker, but the supplement consistently call it pan actin: the section is titled "Alpha-Pan Actin" and the body refers to the "alpha-pan actin antibody" and the "anti-pan actin antibody (ab119952)" (suppl. L140). The product documentation is ambiguous: ab119952 (clone 4A4) is described both as a pan-actin antibody and as an alpha smooth-muscle actin antibody, with an ACTA2 immunogen. As written, the methods describe a pan-actin antibody, which does not support "confirms a circular smooth muscle layer".

• Essential and non-experimental: state exactly which epitope was detected, and soften "confirms" to match the results text, which already says the staining "provides molecular evidence for the presence of [a] proposed circular smooth muscle layer"

• Optional: support the smooth-muscle claim with an independent smooth-muscle marker or a proper control.

Author’s response: We would like to thank the reviewer for this critical perspective on the marker used for smooth muscle actin. After a discussion with the scientific support of Abcam, advising that while smooth muscle actin is detected with higher affinity, skeletal muscle and gamma actin can also be detected. Therefore, we will repeat these experiments aiming for separate staining of smooth muscle actin and F-actin detecting across all isoforms and with higher species coverage. Accordingly, these sections will be revised to address the actin isoform differentiation, in addition to the previously mentioned marker target section in the supplements.

The title and abstract claim more than the present data show. The paper establishes molecular and structural underpinnings for neuromuscular control- tubule differentiation, peri-tubular actin, dense innervation, nicotinic receptor signal at putative junctions, ChAT expression in a subset of species, a cationic acetylcholine and dopamine channel repertoire, and spontaneous calcium activity. It does not show signal moving from neuron to muscle or secretory epithelium to secretion. "Elucidating a Neural-to-Secretory Pathway," may be too strong. The discussion is careful and uses the right tone ("working model," "potential"). Please bring the title and abstract in line with the hedging you already use. No new experiments are needed.

Author’s response: In agreement with the reviewer, we have revised the title to better reflect the nature of our results. Our new title is: Neurons, Muscles, and Venom: Molecular and Structural Insights into Venom Release in Cephalopods. Additionally, we have revised the abstract to be more tempered about our findings.

The phylogeny needs node support reported for the load-bearing nodes, and one label should be reconsidered. The interpretation rests on a few specific sister relationships, especially PSG unknown 3 sitting next to the cephalopod chemotactile receptors, which is what the chemotactile-trigger idea is built on. The absence of cephalopod sequences from the glycine, serotonin, and anionic ACh groups is also relevant, since it is used to rule signaling modes in or out. The methods report 1,000 ultrafast bootstraps (L536), so the values exist. They just don't appear on Figure 4 or in the text for the nodes that matter.

• Report bootstrap values for the nodes the interpretation depends on, and soften where support is weak. A small supplementary subtree of the PSG-unknown clades with their nearest neighbors would probably be easier to read than annotating Figure 4 directly.

• "PSG unknown 1" is described as a "cephalopod-specific subfamily," but its 11 sequences are all from A. bandense (L190-191). Is "A. bandense-specific in this dataset" not more accurate? PSG unknown 2 spans all three species and does support the cephalopod-wide label.

__Author’s response: __As proposed by the reviewer we will add bootstrap values to the phylogeny, and address the clade naming as needed. We would like to highlight that the PSG unknown 1 cluster includes only PSG sequences from A. bandense but further non-PSG sequences from E. berryi and Octopus sinensis cluster within this clade, and thus cephalopod-specific subfamily remains accurate. We will revise the result section to clarify this point.

Reproducibility:

Methods are strong. The supplement is detailed on staining protocols, the fixative comparison, the transcriptome pipeline, and the phylogenetics, with software versions throughout. The gaps that would stop someone reproducing the work are the replication numbers (above), acquisition and processing settings for any quantitative fluorescence comparison, and two deposition items. The data-availability statement says the paper reports no original code, but the calcium analysis used a custom Python script. Deposit the script or correct the statement. On the transcriptomes, two of four PSG datasets have public SRA accessions (D. pealeii SRX14223474, O. bimaculoides SRX1045409), but E. berryi and A. bandense are listed only as "unpublished." A. bandense in particular is included in the phylogeny, so accessions for those two would help.

Author’s response: __We thank the reviewer for pointing out the missing python script that has been used to normalize and visualize the calcium activity in the regions of interest, and we will add this information in the revised manuscript. For the transcriptome dataset, we will add the accession numbers in the revised manuscript as these datasets have been uploaded to NCBI SRA. __

Minor comments:

Figure legends and callouts need a careful consistency pass. Most are small and several are probably production or copy-editing artifacts..

By figure:

Figure 1.

• Panel b: legend lists "venom duct, salivary papilla and buccal mass," but the panel labels Buccal Mass, ASG, PSG, Digestive Gland, and Oesophagus. Reconcile.

• Panel c (L683-684): the color key is hard to follow. The legend gives "distal-secretory (pink)" and "digestive gland (purple)," but in the image the saturated magenta is the distal-secretory tubules and the digestive gland looks grey-lavender. The inset confirms distal in magenta, proximal in green. The "corresponding color code" does not carry across panels: in e the key uses green for proximal tubule lumen and purple for digestive gland (L690), while in c the magenta marks the distal tubules. Make the color assignments panel-specific.

• Panel d : "PSGPT" in the image, "PSGT" in the legend. The supplement text uses PSGT, while supplementary Fig. S1 labels it PSGPT. Pick one and use it throughout.

• Panel a: the tree is titled "venomous animal taxa" but includes non-venomous outgroups (sponges, echinoderms). "Major animal lineages, with venomous coleoids highlighted" would be more accurate.

__Author’s response: __We thank the reviewer for the critical view on the details of the figures. We will ensure that the small discrepancies in the figure labels and the color codes are being addressed in the revised manuscript.

Figure 2.

• The g-i legend has the wrong panel letters: it reads "E. berryi (e), O. bimaculoides (f), and Ascarosepion bandense (g)", but the TEM panels are g, h, and i (in-image labels EB, OB, AB confirm). The letters should be (g), (h), (i).

Author’s response: Will be corrected in the revised manuscript.

Figure 3.

• Panel r legend (L720): "regions 1-3 highlighted in p" should be "in q." The regions are marked on the CAL-520 projection (q), not the O. bimaculoides ChAT panel (p).

• Panel h is a chromogenic (DAB) Synorf-1 image with no DAPI, but the d-h legend describes synapsin "along with nuclear staining (DAPI: grey)." That holds for d-g. Note the exception for h.

__Author’s response: __Will be correct in the revised manuscript.

Text, references, and supplement.

• The species epithet is inconsistent: "Ascarosepion bandense" in the main text and Figs 2-3, "Ascarosepion bandensis" in supplementary Fig. S3a, and "Sepia bandensis (Ascarosepion bandense)" in Table S1. The genus is inconsistent in the literature, so just be consistent here

__Author’s response: __We thank the reviewer for catching these typos. As indicated the genus is inconsistent in the literature and was revised as we were writing the manuscript. We will correct the inconsistency in the revised manuscript.

• Small writing fixes: "predominancy" should be "predominance," "mucopolysaccharids" should be "mucopolysaccharides," "communication sides" should be "sites," and the supplementary Fig. S2 title "two differentiate tubule types" should likely read "two differentiated tubule types."

__Author’s response: __We will correct these typos in the revised manuscript.

Reviewer #2 (Significance (Required)):

General assessment and nature of the advance: This is mainly a descriptive and comparative study, and its strengths are breadth and integration. The advance is partly conceptual and substantially technical. I'm not aware of an existing cross-lineage molecular and structural survey of PSG neuromuscular organization across octopus, squid, and cuttlefish. The idea that venom release is under neuromuscular control has been proposed previously, but what is new here is putting it on a molecular and cross-lineage footing, with marker localization, receptor-like signal, and a channel repertoire across the three groups. Synchrotron micro-CT, multiplexed HCR and immunohistochemistry, a comparative cys-loop LGIC phylogeny, and a live ex vivo calcium recording together provide quite a versatile platform, and the paper will be a great resource and a methodological template. Its limitation is the gap between the structural and molecular evidence and the functional language used to describe it, which the major comments describe and can be straightforward to address.

Context. The relevant prior work includes Young, House, and the more recent histology and transcriptomics in S. officinalis and O. vulgaris, all of which the authors cite. The study also sits within a wider literature on venom-gland innervation in spiders, scorpions, snakes, and centipedes, which the authors use to argue that neuronal control of venom release is a recurring strategy implemented with different molecular components. The most novel proposal, a chemotactile route to PSG activation through the superior buccal lobe that could link the arms and oral sensory systems to venom release, connects to van Giesen et al. (2020) and the group's own micro-CT work. On the current data this remains speculative and should be framed as a hypothesis.

Audience. Comparative and evolutionary neurobiology, invertebrate zoology, venom biology, and cephalopod biology, with some reach into neurosecretion and neuromuscular-control work. The integrative approach and the resource value should extend its readership beyond the immediate field.

Reviewer expertise. Comparative and molecular neuroscience of cephalopods, the octopus peripheral nervous system, calcium imaging, multiplexed HCR, and transcriptomics. I am qualified to evaluate the molecular labeling, imaging, and comparative-neurobiology claims. I cannot independently assess the micro-CT reconstruction pipeline or the finer points of the ligand-gated ion channel phylogenetics, and I have weighted my comments on those sections accordingly.

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

This is a comprehensive study of the cephalopod venom gland by tissue staining , micro-CT imaging, calcium imaging and phylogenetics. The study detects markers of muscular and neuronal tissues in the venom gland along with excitatory acetylcholine- and dopamine-gated receptors suggesting neuro-muscular control of venom release.

I have only minor comments:

Table S1: It is unclear why not all the experiments where performed with all the species. Alternatively, why didn't the authors run all the experiments on one representative species?

Author’s response: We thank the author for this question and as we will highlight in the revised manuscript the experimental coverage across species was related to the availability of specimens for the corresponding analyses. When working with non-traditional model systems, it’s not possible to always have access to specimens of the adequate size and/or maturity stage. We aim to include coverage of techniques for all species used, but this is not achievable due to the complexity of the approaches and the mentioned accessibility of specimens.

We opted not to focus on a single species because cephalopods comprise approximately 800 coleoid species in the three major lineages of squid, octopus and cuttlefish. The posterior salivary gland(s) have been shown to produce toxic secretions and are to date assumed to be the primary venom producing organ. The community is still assessing the histological and functional diversification of these glands, but already recorded multiple differences in structural organization, paired or single glands, size and protein content across the species-tree but even across ontogenesis. Therefore, for a general understanding on the innervation pattern of the venom gland in cephalopods a cross-species and cross-coleoid comparison has higher potential to give a comprehensive picture of the functional organization within the gland and finally of the secretion process itself and brain-bite connection.

Line 52: "dating back 500 million years" - cnidarians are older than 500 million years, so it would be more precise to say "dating back at least 500 million years".

__Author’s response: __Will be corrected in the revised manuscript.

Figure 1a: even though some sponges are toxic, they don't have a toxin-injection apparatus, so they probably cannot be called venomous.

__Author’s response: __The species of the genus Haliclona have been shown to recruit nematocytes from cnidaria, employing them for prey capture. This recruitment mechanism is thought to be enough to categorize them as venomous is similar to other kleptocyte venomous species.

Line 120: a full stop or an "and" is missing after D. pealeii

__Author’s response: __Will be corrected in the revised manuscript.

Reviewer #3 (Significance (Required)):

This study will be mainly interesting to zoologists and venom researchers. The study advances our understanding of how the venom release is controlled in one of the important marine animals. While this work provides important insights into the anatomy as well as molecular and cellular basis of the cephalopod venom gland function, it could be strengthened by in vivo experiments showing correlation of the calcium signals with venom release and the role of the ion channels in this process (e.g. incubation of the venom gland in high concentrations of acetylcholine and dopamine).

__Author’s response: __We would like to thank the reviewer for his positive evaluation of our work, and agree that future studies are required to characterize the receptors found in the PSG with the neuronal control of the secretion process with verified venom secretion. We believe that the in vivo experiments that would be necessary to demonstrate this are out of scope for the present study, however an ex vivo experiment observing the activity induced by high neurotransmitter exposure could give additional insights. We are currently attempting these experiments and will revise the manuscript with our findings if the experiments are conclusive.

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

__Author’s response: __To ensure a timely revision of the manuscript we have addressed the minor typos and grammatical issues pointed out by the reviewers. Additionally, we’ve revised the title and abstract to tone down references to neuronal control and secretory release of cephalopod venom. Experimentally, we are currently working on additional histological tissue stainings for a more comprehensive comparative framework across the cephalopod lineages used in the study. As mentioned previously, this is based on availability of specimens and we will add any additional species coverage we can achieve. As stated in the replies above and addressing the concern regarding target specificity of the cellular markers used in our study, we revised the manuscript to include a section in the supplementary material section, and will further integrate these affinity vs limitations in the final revised discussion. Additionally, we are conducting additional ex vivo implant experiments of venom gland calcium imaging using acetylcholine and dopamine perturbations versus spontaneous signaling to characterize receptor activity. The revision of the discussion and figures will be finalized after completing the additional experiments.

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

__Author’s response: __The reviewers pointed out that a final verification of in vivo neuronal stimulation with subsequent venom secretion would be crucial to elucidate the mechanism of neuronal control of the venom gland. While we agree that this is the ultimate verification, the complexity of these analyses and the required additional functional receptor characterization and neurotransmitter system identification are out of scope of our study. However, we believe that the revision of our manuscript to highlight the molecular and structural foundations, and additional histological and ex vivo calcium activity experiments will provide a more comprehensive comparison of the venom gland functionality across cephalopod lineages. Together with tempering the conclusions about neuronal control and secretory venom release, these changes improve the strength of our study to be accepted for publication.

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Referee #3

Evidence, reproducibility and clarity

This is a comprehensive study of the cephalopod venom gland by tissue staining , micro-CT imaging, calcium imaging and phylogenetics. The study detects markers of muscular and neuronal tissues in the venom gland along with excitatory acetylcholine- and dopamine-gated receptors suggesting neuro-muscular control of venom release.

I have only minor comments:

Table S1: It is unclear why not all the experiments where performed with all the species. Alternatively, why didn't the authors run all the experiments on one representative species?

Line 52: "dating back 500 million years" - cnidarians are older than 500 million years, so it would be more precise to say "dating back at least 500 million years".

Figure 1a: even though some sponges are toxic, they don't have a toxin-injection apparatus, so they probably cannot be called venomous.

Line 120: a full stop or an "and" is missing after D. pealeii

Significance

This study will be mainly interesting to zoologists and venom researchers. The study advances our understanding of how the venom release is controlled in one of the important marine animals. While this work provides important insights into the anatomy as well as molecular and cellular basis of the cephalopod venom gland function, it could be strengthened by in vivo experiments showing correlation of the calcium signals with venom release and the role of the ion channels in this process (e.g. incubation of the venom gland in high concentrations of acetylcholine and dopamine).

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Referee #2

Evidence, reproducibility and clarity

The paper uses modern approaches to address a fascinating question that has been relatively unexplored since J.Z. Young's morphological work in the 1960s: how venom release is controlled in the posterior salivary gland (PSG) of coleoid cephalopods. The authors' work uses five species spanning the three major coleoid groups: octopus (Octopus bimaculoides), squid (Doryteuthis pealeii, Euprymna berryi), and cuttlefish (Ascarosepion bandense, Sepia officinalis), and employs a broad toolkit: synchrotron micro-CT, a panel of histological and immunohistochemical stains, multiplexed HCR, a comparative phylogeny of cys-loop ligand-gated ion channels, and an ex vivo calcium-imaging proof of concept. Structurally, they identified a shared two-tubule architecture (proximal-striated and distal-secretory), a peri-tubular actin layer they interpret as a possible circular smooth-muscle layer, and dense innervation labeled by neurofilament and synapsin. They also show α-bungarotoxin-positive nicotinic receptor signal and ChAT expression near putative neuromuscular contacts in some of the species examined. In the PSG transcriptome datasets with confirmed LGIC recovery, acetylcholine- and dopamine-gated cation-channel groups are prominent. A live E. berryi PSG explant shows spontaneous calcium activity. From these findings, authors propose a working model in which cholinergic and dopaminergic input mediate secretory tubule activity and contraction of the surrounding muscle to move venom toward the beak. The study is mainly descriptive and comparative. My major points address matching the strongest claims to the data presented. The minor points are figure, reference, and reproducibility fixes, several of which simply need a careful pass.

Major comments:

1. The calcium imaging is described inconsistently between the abstract and the rest of the paper. The abstract says "ex vivo stimulation of the PSG elicits calcium signaling throughout the gland" (L34-35), but no stimulation was applied. The methods describe only dissection, incubation in CAL-520, and epifluorescence imaging. The octomedia is physiological (not depolarizing), and the analysis step refers to "spontaneously active regions." Everywhere else the authors are more cautious. The section heading only "suggests" calcium signaling activation (L216), and the results call the activity spontaneous and the experiment a pilot study, noting that "further analyses are required to determine if this activity is neural or muscular" (L222-228). "Throughout the gland" also overstates a result localized near the gland edge.
   • Required either way: drop "stimulation" and "elicits" from the abstract, describe what was actually done, and soften "consistent with neural regulation" for a spontaneous signal of unknown cellular origin.
   • Optional (only if the authors want to keep the neural-regulation speculation) the explant preparation and the CAL-520 protocol already exist, so a depolarizing stim with a cholinergic agonist and antagonist control, recorded the same way, would show whether the signal is evokable and start to separate neural from muscular sources. This is an extension of the existing assay, not a new experimennt.
   • Reframing the section as spontaneous pilot activity resolves the point just as well. I am not asking for new data as a condition of publication, and either is fine.
   • The Results subheading "Live staining of squid venom gland explant" (L216) is imprecise. CAL-520 is a calcium indicator rather than a stain, and the experiment is live-tissue calcium imaging of an ex vivo explant, so the heading reads as histology on living tissue and underdescribes what was actually done.
2. Replication and quantification are not reported. The descriptive observations are convincing overall, but the comparative language ("conserved," L36, L90; "stereotyped," L30) rests on single representative images, and I couldnt find n (animals, sections) for any stain or any quantification of the spatial and cross-species claims. For a claim about conservation across lineages, that support is necessary, and does not require new experiments.
   • Give n (animals and sections) per stain per species.
   • Where the claim is about spatial pattern (peripheral versus central, peri-tubular versus luminal), add basic quantification.
   • Several claims are clearly meant to be qualitative. Say so, and be explicit about which conclusions are based on representative examples vs replicated or quantified observations.
   • This should be achievable from the existing data.
3. The actin antibody needs to be identified clearly. The main text calls Abcam ab119952 an "α-actin" marker, but the supplement consistently call it pan actin: the section is titled "Alpha-Pan Actin" and the body refers to the "alpha-pan actin antibody" and the "anti-pan actin antibody (ab119952)" (suppl. L140). The product documentation is ambiguous: ab119952 (clone 4A4) is described both as a pan-actin antibody and as an alpha smooth-muscle actin antibody, with an ACTA2 immunogen. As written, the methods describe a pan-actin antibody, which does not support "confirms a circular smooth muscle layer".
   • Essential and non-experimental: state exactly which epitope was detected, and soften "confirms" to match the results text, which already says the staining "provides molecular evidence for the presence of [a] proposed circular smooth muscle layer"
   • Optional: support the smooth-muscle claim with an independent smooth-muscle marker or a proper control.
4. The title and abstract claim more than the present data show. The paper establishes molecular and structural underpinnings for neuromuscular control- tubule differentiation, peri-tubular actin, dense innervation, nicotinic receptor signal at putative junctions, ChAT expression in a subset of species, a cationic acetylcholine and dopamine channel repertoire, and spontaneous calcium activity. It does not show signal moving from neuron to muscle or secretory epithelium to secretion. "Elucidating a Neural-to-Secretory Pathway," may be too strong. The discussion is careful and uses the right tone ("working model," "potential"). Please bring the title and abstract in line with the hedging you already use. No new experiments are needed.

5. The phylogeny needs node support reported for the load-bearing nodes, and one label should be reconsidered. The interpretation rests on a few specific sister relationships, especially PSG unknown 3 sitting next to the cephalopod chemotactile receptors, which is what the chemotactile-trigger idea is built on. The absence of cephalopod sequences from the glycine, serotonin, and anionic ACh groups is also relevant, since it is used to rule signaling modes in or out. The methods report 1,000 ultrafast bootstraps (L536), so the values exist. They just don't appear on Figure 4 or in the text for the nodes that matter.

6. Report bootstrap values for the nodes the interpretation depends on, and soften where support is weak. A small supplementary subtree of the PSG-unknown clades with their nearest neighbors would probably be easier to read than annotating Figure 4 directly.

7. "PSG unknown 1" is described as a "cephalopod-specific subfamily," but its 11 sequences are all from A. bandense (L190-191). Is "A. bandense-specific in this dataset" not more accurate? PSG unknown 2 spans all three species and does support the cephalopod-wide label.

Reproducibility:

Methods are strong. The supplement is detailed on staining protocols, the fixative comparison, the transcriptome pipeline, and the phylogenetics, with software versions throughout. The gaps that would stop someone reproducing the work are the replication numbers (above), acquisition and processing settings for any quantitative fluorescence comparison, and two deposition items. The data-availability statement says the paper reports no original code, but the calcium analysis used a custom Python script. Deposit the script or correct the statement. On the transcriptomes, two of four PSG datasets have public SRA accessions (D. pealeii SRX14223474, O. bimaculoides SRX1045409), but E. berryi and A. bandense are listed only as "unpublished." A. bandense in particular is included in the phylogeny, so accessions for those two would help.

Minor comments:

Figure legends and callouts need a careful consistency pass. Most are small and several are probably production or copy-editing artifacts.. By figure: Figure 1.

• Panel b: legend lists "venom duct, salivary papilla and buccal mass," but the panel labels Buccal Mass, ASG, PSG, Digestive Gland, and Oesophagus. Reconcile.
• Panel c (L683-684): the color key is hard to follow. The legend gives "distal-secretory (pink)" and "digestive gland (purple)," but in the image the saturated magenta is the distal-secretory tubules and the digestive gland looks grey-lavender. The inset confirms distal in magenta, proximal in green. The "corresponding color code" does not carry across panels: in e the key uses green for proximal tubule lumen and purple for digestive gland (L690), while in c the magenta marks the distal tubules. Make the color assignments panel-specific.
• Panel d : "PSGPT" in the image, "PSGT" in the legend. The supplement text uses PSGT, while supplementary Fig. S1 labels it PSGPT. Pick one and use it throughout.
• Panel a: the tree is titled "venomous animal taxa" but includes non-venomous outgroups (sponges, echinoderms). "Major animal lineages, with venomous coleoids highlighted" would be more accurate.

Figure 2.

• The g-i legend has the wrong panel letters: it reads "E. berryi (e), O. bimaculoides (f), and Ascarosepion bandense (g)", but the TEM panels are g, h, and i (in-image labels EB, OB, AB confirm). The letters should be (g), (h), (i).

Figure 3.

• Panel r legend (L720): "regions 1-3 highlighted in p" should be "in q." The regions are marked on the CAL-520 projection (q), not the O. bimaculoides ChAT panel (p).
• Panel h is a chromogenic (DAB) Synorf-1 image with no DAPI, but the d-h legend describes synapsin "along with nuclear staining (DAPI: grey)." That holds for d-g. Note the exception for h.

Text, references, and supplement.

• The species epithet is inconsistent: "Ascarosepion bandense" in the main text and Figs 2-3, "Ascarosepion bandensis" in supplementary Fig. S3a, and "Sepia bandensis (Ascarosepion bandense)" in Table S1. The genus is inconsistent in the literature, so just be consistent here
• Small writing fixes: "predominancy" should be "predominance," "mucopolysaccharids" should be "mucopolysaccharides," "communication sides" should be "sites," and the supplementary Fig. S2 title "two differentiate tubule types" should likely read "two differentiated tubule types."

Significance

General assessment and nature of the advance: This is mainly a descriptive and comparative study, and its strengths are breadth and integration. The advance is partly conceptual and substantially technical. I'm not aware of an existing cross-lineage molecular and structural survey of PSG neuromuscular organization across octopus, squid, and cuttlefish. The idea that venom release is under neuromuscular control has been proposed previously, but what is new here is putting it on a molecular and cross-lineage footing, with marker localization, receptor-like signal, and a channel repertoire across the three groups. Synchrotron micro-CT, multiplexed HCR and immunohistochemistry, a comparative cys-loop LGIC phylogeny, and a live ex vivo calcium recording together provide quite a versatile platform, and the paper will be a great resource and a methodological template. Its limitation is the gap between the structural and molecular evidence and the functional language used to describe it, which the major comments describe and can be straightforward to address.

Context. The relevant prior work includes Young, House, and the more recent histology and transcriptomics in S. officinalis and O. vulgaris, all of which the authors cite. The study also sits within a wider literature on venom-gland innervation in spiders, scorpions, snakes, and centipedes, which the authors use to argue that neuronal control of venom release is a recurring strategy implemented with different molecular components. The most novel proposal, a chemotactile route to PSG activation through the superior buccal lobe that could link the arms and oral sensory systems to venom release, connects to van Giesen et al. (2020) and the group's own micro-CT work. On the current data this remains speculative and should be framed as a hypothesis.

Audience. Comparative and evolutionary neurobiology, invertebrate zoology, venom biology, and cephalopod biology, with some reach into neurosecretion and neuromuscular-control work. The integrative approach and the resource value should extend its readership beyond the immediate field.

Reviewer expertise. Comparative and molecular neuroscience of cephalopods, the octopus peripheral nervous system, calcium imaging, multiplexed HCR, and transcriptomics. I am qualified to evaluate the molecular labeling, imaging, and comparative-neurobiology claims. I cannot independently assess the micro-CT reconstruction pipeline or the finer points of the ligand-gated ion channel phylogenetics, and I have weighted my comments on those sections accordingly.

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Referee #1

Evidence, reproducibility and clarity

Summary

The manuscript entitled « Neurons, Muscles, and Venom: Elucidating a Neural-to-Secretory Pathway in Cephalopod Predation » by Kirchhoff et al. investigates the anatomical and molecular basis of venom release in coleoid cephalopods. The authors used a combination of histology, immunohistochemistry, micro-computed tomography, comparative phylogenetics, and ex vivo calcium imaging to conclude that venom secretion from the posterior salivary gland (PSG) is under neuromuscular control through cholinergic and potentially dopaminergic regulation. They also show that this is a conserved structural feature across octopus, squid, and cuttlefish species. Overall, this manuscript addresses an understudied topic, namely the mechanisms regulating venom secretion, which is poorly understood in most venomous systems despite their ecological and evolutionary significance. As such, this work provides an important anatomical and molecular characterization of cephalopod posterior salivary glands and generates valuable hypotheses regarding the neural regulation of venom secretion. I personally appreciate the quality of the histology work, a methodology largely neglected nowadays in a world thirsty for the use of high-tech, fancy instrumentations. Although I command the authors for this elegant and visually pleasing study, I have some reservations about the major mechanistic conclusions (especially the cholinergic and dopaminergic regulation), which to me rely on indirect evidence, as no experiment directly demonstrates neural control of venom secretion. Therefore this manuscript would benefit from additional functional validation and certainly a more cautious interpretation of the findings.

Major Comments

• The principal conclusion of the manuscript is that venom release is under neuronal and neuromuscular regulation, which is highly likely given the authors convincingly demonstrate the presence of actin-positive muscular structures, neuronal markers within the PSG, cholinergic-associated markers, spontaneous calcium activity. Unfortunately, none of these experiments directly demonstrate control of venom secretion ! The presented evidence establishes anatomical proximity between neural and muscular elements but does not demonstrate causality. For instance, no experiments measure venom release following neuronal stimulation or receptor activation/inhibition. Therefore I suggest that the authors substantially temper these conclusions or provide functional experiments demonstrating secretion following pharmacological or electrical stimulation.
• Furthermore, the conclusion that acetylcholine is a major neurotransmitter regulating the PSG is based on α-bungarotoxin labeling, ChAT expression and phylogenetic identification of nicotinic receptor homologs. My concerns is that α-bungarotoxin binding specificity in cephalopods has not been demonstrated. Although I agree that α-bungarotoxin binding is generally associated with nAChRs binding (not only muscle-type, but also α-7 and α-9 containing neuronal receptors), there are also evidences (weaker, I admit) that it may also interact with GABAA receptors, as well as some VGICs (potassium, sodium). There are also confirmed non-canonical protein interactions, such as with Ly6-family proteins. So first, it must be determined what α-bungarotoxin is binding to in cephalopods. In addition, ChAT expression alone does not prove cholinergic neurotransmission, and to be fair, the receptor phylogeny does not establish receptor expression in the specific cells observed histologically (only that it is found in the venom gland transcriptome). Importantly, from what I could see, no co-localization is shown between, cholinergic neurons, receptor-positive cells, and muscle fibers. The cholinergic circuit remains hypothetical, although it can be defended as a strong hypothesis. To reflect this, the authors should moderate their interpretation and explicitly distinguish between evidence for cholinergic potential and/or demonstrated cholinergic signaling.
• The authors repeatedly suggest dopaminergic participation in venom release. Here, however, the evidence consists solely of transcriptomic identification of receptors clustering with dopamine-gated channels in phylogenetic analyses. Quid of dopamine synthesis enzymes, dopamine localization, dopaminergic neurons, dopamine-dependent physiological responses ? I believe the statements implying a role for dopamine in venom secretion are premature, so the authors should restrict discussion of dopamine to a candidate pathway requiring future validation.

I also have some less important or minor comments :

• The distinction between secretory and smooth-striated tubules is a central component of the proposed secretion model. Yet, the functional interpretation of tubular subtypes remains uncertain, as the authors acknowledge that differentiation was clear in octopus, but incomplete or uncertain in squid, and micro-CT identification of secretory tubules in E. berryi was inconclusive. Given this uncertainty, the proposed model of distal production and proximal transport remains speculative and additional histochemical characterization or molecular markers would strengthen these interpretations.
• p6 The reference for the statement that « holocrine secretion is proposed for cone snail » is not convincing (Vonk et al. deals with scorpions, and only a schematic drawing is presented to illustrate the different secretion routes for various venomous animals) so the authors should provide a research article as reference, but I am not aware of any published study that explicitly tested this hypothesis and found positive evidence (need to show that whole-cell disintegration contributes substantially to venom release). « Insoluble granules » are seen inside secretory cells and sometimes also retrieved in milked venoms, but not always. If holocrine secretion occurs, they should always be there, if not, merocrine secretion might also be at work.
• A minor but possibly relevant comment on the fact that most antibodies were originally developed for vertebrate systems. Although some validation controls are shown, stronger evidence for specificity in cephalopod tissues would be desirable, particularly for NeuN, α-actin, and neurofilament (SMI-31).

Significance

Overall this manuscript provides an important anatomical and molecular characterization of cephalopod posterior salivary glands and generates valuable hypotheses regarding the neural regulation of venom secretion. The comparative dataset is extensive and likely to be of interest to researchers in cephalopod biology, neurobiology, and venom evolution. However, the major mechanistic conclusions currently exceed the strength of the evidence so that significant revision is therefore required to align the claims with the data.

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Reply to the reviewers

1. Description of the planned revisions

Insert here a point-by-point reply that explains what revisions, additional experimentations and analyses are planned to address the points raised by the referees

1. Reviewer #2

2.

The main conclusion of this manuscript, stated in lines 549-554, claims that the difference in pathology between Δnsp2 mutant and WT virus infection cannot be explained by distinct viral replication since both viruses replicate similarly in vitro and in vivo. However, the data presented here is supportive that Δnsp2 mutant replicates to a lower extent when compared to WT virus. This is clearly seen in Figures 1C (at 24 hpi), and Figures 1D and 1E for in vitro experiments where there is a 2-log difference at multiple timepoints.

1. As described in the results section (line 281-287), the global growth kinetics were similar between viruses across various in vitro models. However, the magnitude of the viral loads differed from virus to virus and across models (Vero and A549-ALI higher loads for WT and A549-ACE2 higher load for ΔNsp2). We agree that this result is central in the understanding of the differences between WT and ∆NSP2 viruses. We have now planned an entire new set of viral replication experiment on A549-hACE2. For this, we will be using freshly titrated virus stocks of WT and two different ΔNsp2 clones. Quantitation of infectious particles will be performed.

4.

Authors do not provide a validation of the RNASeq analysis, i.e. authors must select a representative set of up- and down-regulated genes and perform RT-qPCR on the same samples to corroborate if the fold changes observed in RNASeq are also observed via an alternative method.

1. Using RT-qPCR, we will validate the expression of representative genes involved in immune checkpoint blockade, translation initiation, histone modification and DNA damage gene sets.

6.

Reviewer #3

7.

Virus localization - IHC/ISH needed (Lines 332-337) To determine whether the observed inflammatory differences relate to differences in viral antigen/RNA distribution which also reflect replication difference (rather than purely host immune modulation by Nsp2), viral IHC or in situ hybridization (ISH) should be performed on lung sections to localize virus within the tissue and correlate with inflammatory zones. Otherwise explain that replication differences may underlie differences in host response.

1. N protein staining (IHC) with hematoxylin counter staining will be performed to measure the viral antigen distribution and it colocalization within inflammatory zones.

2. 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.

1. Reviewer #1

2.

Early infection kinetics in ACE2-expressing cells. The authors report transiently reduced viral RNA levels in vivo during the early phase of infection, despite comparable viral loads at later time points. It would therefore be informative to determine whether a similar phenomenon occurs in ACE2-expressing cells. Time-course analyses of viral RNA and/or viral protein expression could help establish whether the mutant primarily affects early infection events rather than overall replicative capacity.

1. We have conducted a new set of experiments aimed at determining SARS-E RNA expression at 1, 24, 48 and 72HPI. These new results have been added to figure 1 (panels F and G) and the results were described and discussed in the line 288-293 and 577-585 :
2. “When comparing RNA replication of two different ΔNsp2 mutant clones and the WT virus in A549-hACE2, more expression of virus E gene was observed for clone 1 at low MOI, but no global differences were observed at higher MOI or with the clone 2 (Figure 1F and 1G). Differences between corresponding infection time-points were detected at 72HPI. More robust RNA E expression was observed for clone 1 at MOI of 0.05 and 0.5, when lower E expression was significatively reduced for clone 2 at MOI 0.05. These results indicate that deletion of Nsp2 has minimal impact on SARS-CoV-2 replication under the conditions tested.”
3. “An Nsp2 deletion mutant was successfully generated that shows similar in vitro replication kinetics relative to the wild type recombinant. Some differences in the magnitude of the viral loads were observed between mutant and WT virus, but this was inconsistent across cell culture systems used. In vitro RNA expression/replication data suggest that this difference may be caused by virus stock batch effects rather than a direct consequence of Nsp2 deletion. Although the WVPRA motif in Nsp2 sequence was reported to be required for efficient Nsp1 and Nsp3 self-cleavage [69], in the context of infection we did not observe any impairment of this process in the absence of Nsp2 under our experimental conditions. Of interest, a recent paper reported that a SARS-CoV-2 Nsp2 deletion mutant displays important viral RNA (Nsp12 and N) expression defects at very early times (3-4h) after infection [70]. We do not observe such defects at 24h, as assessed by E RNA expression measurements. Differences in the cell culture models and assessments of infectious viral progeny prevents a more detailed comparison with the study of Kim et al [70].”

*Given the reduced pathology and disease progression in the ∆NSP2-SARS-CoV-2 infected mice, have the authors considered assessing whether mice exposed to this mutant SARS-CoV-2 strain have enhanced responses to re-challenge with WT SARS-CoV-2? *

• We thank the reviewer for this interesting comment.Unfortunately, such experiment will not be doable as our BSL3 facility will soon close for renovation and an undetermined period of time. In an attempt to partially address the reviewer’s comment, we measured SARS-CoV2 neutralizing antibodies in mouse plasma at 7DPI. However, we could not detect any neutralizing activity for any of the groups analyzed at the lowest available plasma dilution.

Reviewer #2

1. The main conclusion of this manuscript, stated in lines 549-554, claims that the difference in pathology between Δnsp2 mutant and WT virus infection cannot be explained by distinct viral replication since both viruses replicate similarly in vitro and in vivo. However, the data presented here is supportive that Δnsp2 mutant replicates to a lower extent when compared to WT virus. This is clearly seen in Figures 1C (at 24 hpi), and Figures 1D and 1E for in vitro experiments where there is a 2-log difference at multiple timepoints.

2. As presented in figure 1, WT and ∆NSP2 mutant virus grow with overall similar kinetics. However, we do observe some variations in viral titers at some time points depending in the cell culture systems used. WT produces more virus in Vero and A549-ALI cells while ∆NSP2 is producing more virus in A549-ACE2 cells. We have conducted additional experiments using two independent ∆NSP2 clones and analyzed the kinetics of E RNA expression at low and high MOI in A549-ACE2 cells. These new data (Fig 1 F, G) show similar overall kinetics of E RNA expression with both clones behaving similar to WT at high MOI and one clone (clone 1) growing better at low MOI. These results suggest that the ∆Nsp2 mutant does not have a growth defect that could explain the difference in pathogenesis. This section of the discussion has been rephrased (line 575-585 and 599-598).

3. “An Nsp2 deletion mutant was successfully generated that shows similar in vitro replication kinetics relative to the wild type recombinant. Some differences in the magnitude of the viral loads were observed between mutant and WT virus, but this was inconsistent across cell culture systems used. In vitro RNA expression/replication data suggest that this difference may be caused by virus stock batch effects rather than a direct consequence of Nsp2 deletion. Although the WVPRA motif in Nsp2 sequence was reported to be required for efficient Nsp1 and Nsp3 self-cleavage [69], in the context of infection we did not observe any impairment of this process in the absence of Nsp2 under our experimental conditions. Of interest, a recent paper reported that a SARS-CoV-2 Nsp2 deletion mutant displays important viral RNA (Nsp12 and N) expression defects at very early times (3-4h) after infection [70]. We do not observe such defects at 24h, as assessed by E RNA expression measurements. Differences in the cell culture models and assessments of infectious viral progeny prevents a more detailed comparison with the study of Kim et al [70].”
4. “This difference could not be explained by reduction of viral load associated with the ∆Nsp2 mutation as no significant difference were observed in lung viral titer across the infection course.”

In Figure 1B, the expression of viral proteins Nsp1 and Nsp3 are normalized to N protein to conclude that they are not influenced by nsp2 deletion. N protein is known to have diminished expression when SARS-CoV-2 mutants replicate deficiently, which is the case of the Δnsp2 mutant under in vitro conditions. Why did the authors choose to normalize against N protein? Why was not a loading control such as beta-actin used?

• We apologize for the confusion.The wording of the original statement was misleading and have been modified to clarify our data. Nsp1 and Nsp3 have now been normalized to overall protein content (using stain-free blot). A new bar graph showing normalized protein expression was added to figure 1B. Expression of N and S is presented to demonstrate infection level and show that the Nsp1 and Nsp3 expression are not directly impacted by the Nsp2 deletion. Text modification Line 277-279:

• “Relative to N and S protein expression, comparable levels of Nsp1 and Nsp3 were detected in cells infected with either virus, indicating preserved polyprotein processing.”

• The infection time-point (48h) used for western blot analysis was added to the figure caption.

Authors analyze the expression of the envelope (E) gene to assess the viral replication in vivo. GAPDH gene is used as housekeeping gene. I wonder why authors chose these genes for this study, considering that E gene expression values range is small (101 to 10-2). N subgenomic RNA is more appropriate to measure active viral transcription since it is more abundant than E subgenomic RNAs. Also, GAPDH has been reported as not suitable housekeeping gene for SARS-CoV-2 infection (reported in PMID: 36377893).

• A broadly adopted E sarbeco primers-probe set was used to quantify viral RNA. Using RT-ddPCR, E gene expression was 3-5 log above the limit of detection at 7DPI allowing quantification of active viral transcription. Considering that quantification other viral transcripts is pertinent to a understanding of RNA replication dynamics, quantification of all viral transcripts by RNAseq have been add to the Supplementary figure 3 and described in line 331-339:

• “The global reduction in E transcript abundance was recapitulated in the RNAseq data (Supplementary Figure 3). In addition, reduced expression of several viral transcripts was observed in ΔNsp2-infected mice at all time points. This effect was particularly evident at 3 DPI (9/12 detected viral genes) and 7 DPI (5/12 detected viral genes), suggesting altered viral transcriptional dynamics despite comparable overall viral shedding. A trend toward improved clearance of the ΔNsp2 virus was also observed when comparing viral transcript abundance. As expected, following Nsp2 deletion, fewer transcripts mapping to the Orf1a region were detected in ΔNsp2-infected mice. This difference was not observed when transcripts aligned to the entire Orf1ab gene were analyzed, likely because Nsp2 constitutes only a small portion of the overall coding sequence.”

• GAPDH was used as housekeeping gene, because its RNA expression was abundant enough to directly normalize the E expression which requires high dilution for ddPCR quantification. In response to the reviewer’s comment that GAPDH is not suitable as a housekeeping, the cited study refers to clinical samples. In our hands, GAPDH expression in mice remains stable across infection time points.

There are several statements that are not correct in the Introduction: Lines 37-38: '... SARS-CoV-2 genome encodes a large replicase polyprotein that...' is not true, SARS-CoV-2 genome encodes for two large polyproteins (pp1a and pp1ab).

• Correction was made to this statement (line 37) :
• “The SARS-CoV-2 genome encodes two large replicase polyproteins…”

Line 41: '... leading to the activation of type I interferon...', IFNs as molecules are not activated, the correct phrasing for this sentence would be '... lead to the production / expression of type I interferon' or '... lead to activation of type I interferon signaling cascade...'.

• The sentence was modified (line 41) :
• “… leading to the activation of type I interferon, Nuclear Factor-kappa B (NF-κB), and inflammasome signaling pathways.”

Lines 52-54, this statement is a bit exaggerated. There has been a huge research effort during the past COVID-19 pandemic to understand the replication of coronavirus, especially SARS-CoV-2. Most mechanisms underlying SARS-CoV-2 infection including viral entry, formation or replication organelles, assembly, budding and exocytosis are already well characterize in the scientific literature.

• The line 52 to 55 have been revised to clarify the knowledge gap targeted by this study :
• “Although the SARS-CoV-2 replication cycle has been extensively characterized, the molecular determinants underlying the differences in disease severity and immune dysregulation observed between common cold coronaviruses and highly pathogenic SARS-related viruses remain incompletely understood. Several SARS-CoV-2 proteins have been proposed to contribute to viral pathogenesis [4, 23].”

*Line 295, there seems to be a number missing in '****P

The inclusion of uncropped Western blot data in the Supplementary Figures is appreciated. However, the approximate positions of the molecular weight markers should also be indicated in the corresponding main figure (Fig. 1B) to facilitate data interpretation.

• Molecular weight markers have been added to Figure 1B.

Figures 1C, 1D, 1E could be labelled with the corresponding tested cell line on top of each plot to improve interpretation of the figures.

• The Figures 1C to 1E were modified to improve the readability.

• 3A, the p-Value indicated with two asterisks on top of the figure might result confusing for readers. I would indicate it only in the figure caption.*

• We modified this p-value representation to clarify the figure and keep consistence with statistical test used for the comparison all over the other figure (two-way ANOVA = #).

• 7B, 7C, 7D additional arrows pointing to the main outlier transcripts could be added (in a similar fashion to ORF1a)*

• Labeling of Orf1a was removed as the expression of all viral transcripts were added in the Supplementary figure 3.
• For each volcano plots, label for the top 5 up and down regulated transcripts were added to the Figure 7.

Supplementary Figure 4A, there is a mistake in the left-panel western blot, authors indicate nsp1 protein to a band that corresponds to nsp2 in the main figure.

• This error has been corrected.

Reviewer 3

1. The absence of Nsp2 in the ΔNsp2 mutant is clear, but the claim that Nsp1 and Nsp3 levels are "comparable when normalized to N protein" is not supported by quantitative data and I suspect differences in replication both in vitro and in vivo explain the difference in host response. Of course, if there is less virus, then host response is different and typically reduced. The authors need to take a more honest approach to evaluation of the data.

2. We apologize for the confusion. N and S were used as viral load control and not used for normalization. Normalization was done using total cellular protein. The wording of the original statement was misleading and the wording of the statement has been modified to clarify our data analysis. Line 277-279 and 301-303 :

3. “Relative to N and S protein expression, comparable levels of Nsp1 and Nsp3 were detected in cells infected with either virus, indicating preserved polyprotein processing.”

4. “Protein expression was normalized relative to total protein content and shown aside the blot images. The experiment was performed twice, and a representative result is shown. Uncropped and Stain-Free blots are presented in Supplementary figure 2A and 2B”

5. We agree with the that differences in replication could influence the host response, but the objective of figure 1B was to show the direct influence of the Nsp2 deletion on Nsp1 and Nsp3 production.

6. *Figure 1B - ΔNsp2 and its impact on nsp1 and 3 expressions. Loading control and densitometry (Lines 269-271)à It is not clear whether the absence of nsp2 impacts the nsp1/3 expression. The blot appears to show enhanced Nsp1/Nsp3 in ΔNsp2, and the stain-free total protein signal in Supplementary Figure 4 appears stronger for ΔNsp2. Please provide (a) densitometric quantification of Nsp1/Nsp3 normalized to N, and (b) a standard housekeeping protein blot (eg actin/GAPDH) in the main figure to confirm equal loading. Please also indicate the time point of sample harvest for the WB, so the replication can be correlated figure 1C. *

7. We have now added a bar graph showing normalized expression of N, Nsp1, Nsp3 and S according to total protein content (figure 1B and supplementary figures 2A-B).Results show similar expression of Nsp1 and Nsp3 relative to N and S between WT and ∆NSP2 virus.

8. The infection time-point (48h) used for western blot analysis was added to the figure caption.

9. Figure 1C-E - Replication kinetics and infection dose (Lines 267-277) The claim of "comparable growth kinetics" is not fully supported - WT virus replicates faster and to higher titers in Vero and A549-ALI cultures at early/late time points, with statistically significant differences noted by the authors themselves. Additionally, infection doses were expressed as TCID50 and varied across cell models (Vero, A549-hACE2, A549-ALI), making cross-model comparison difficult and obscuring the actual MOI/copies-per-cell delivered. Please repeat key experiments using a standardized MOI or genome copies/cell across all models with the titer at 1-2h to reflect equal input virus, if different MOI or genome copies/cell dose is needed, please also provide explanation

. 10. Same MOI of 0.15 was used for Vero and A549-hACE2 growth kinetics. The MOI used was added to the materials and methods section and in the figure 1C and 1D graph titles. 11. For A549-ALI, the cells were differentiated for 3 weeks, during this time cells were growing in a complex 3-dimension structure where not all the cells were directly exposed to virus during infection. As so using MOI to compare the virus replication with other used models didn't seem appropriate to us. For full disclosure, we added the virus dose used in this experiment the figure 1E graph title. 12. To respond to the last point of the comment, we performed an additional growth kinetics experiment on A549-hACE2 using a low and high MOI, results were added in the figure 1F and 1G. The E gene copy number was measured at 1h post-infection and no significant differences were observed between the viruses. Measurement of infectious outputs from these experiments are ongoing and will be presented in the final version of the manuscript.

1. Cytokine/chemokine data presentation (Lines 332-337) The heatmap in Figure 3A uses a relative 0-10 scale that is difficult to interpret biologically. Please provide the raw concentration data (pg/mL or pg/mg protein) for key mediators, ideally as bar graphs/dot plots, so readers can assess whether the differences between WT and ΔNsp2 are of plausible biological/clinical magnitude. Figure 3A heatmap - visual clarity The color differences between WT and ΔNsp2 groups, and across timepoints, are subtle and difficult to distinguish visually. Consider an alternative visualization (e.g., separate scaling per mediator, or a dot plot) to improve readability

2. As the goal of the figure 3A was to present modulation of the whole mediator panel in one figure, we chose to conserve the heatmap representation while change the scaling for 0 to 60 to improve visualization.

3. To answer the reviewer’s comment, we added the raw concentration data for key mediators in the supplementary figures 4A to 4G.

4. Transcript-level validation of cytokine/chemokine changes (Lines 332-337) In addition to protein-level (ELISA/multiplex) data, qPCR for key cytokine/chemokine transcripts (e.g., Ccl2, Cxcl9, Ifng, Il6, Ccl5) in lung tissue would help determine whether Nsp2 acts at the level of transcription versus translation/secretion.

5. Gene expressions of key mediator measured by RT-qPCR were added to the supplementary figure 5. Those results were briefly described in line 364-365 :

6. “Higer levels of transcripts for those genes were also observed (Supplementary Figure 5).”

In vitro/in vivo correlation for CCL5/IL-6 findings (Lines 338-343) The supplementary A549-hACE2 data show that Nsp2 reduces CCL5 but not IL-6 in response to poly(I:C). Please clarify the rationale for using this specific readout to model the in vivo lung findings. Does Nsp2 expression also modulate CCL2, CXCL9, or IFN-γ in A549 cells? A more complete in vitro dissection - expressing Nsp2 vs. empty vector, stimulating with poly(I:C), and measuring IFN/ISG and chemokine/cytokine transcripts by qPCR alongside ELISA - would better support the proposed mechanism.

• We chose to use Nsp2/GFP control expression in A549-hACE2 with Poly I:C stimulation because SARS-CoV-2 infection by itself did not induce sufficient production of those mediators to be quantified at protein level in our setting.
• We chose to limit the number of mediators measured to CCL5 and IL6. Those specific mediators were chosen because CCL5 was the only one upregulated in vivo by the mutant and IL6 was part of those upregulated by the WT virus. In addition, IL6 have been chose as it could be easily quantified upon Poly I:C stimulation in A549.
• Unlike IFNγ, CCL2 and CXCL9 could be induced at RNA level in A549 upon Poly I:C or SARS-CoV-2 (data not shown), but we did not evaluate the ability of Nsp2 to modulate those mediators at a protein level.
• We did not observe modulation of IFN (RNA or protein level) or ISGs by Nsp2 in A549-hACE2 with Poly I:C stimulation, but we did not include the results as it was not a key change in mice infection.
• Quantification of CCL5 and IL6 gene expression by RT-qPCR was added to the supplementary figures 6D and 6E.

Discrepancy in differential expression results (Lines 475-484) The text states that ΔNsp2 infection shows a predominance of downregulated transcripts relative to WT (Figure 7B-D), yet the supplementary comparison (each condition vs. mock) reportedly shows similar proportions of up/down genes. Please clarify how these two comparisons relate, and whether they are actually measuring the same thing (ΔNsp2 vs WT directly, versus each vs mock separately).

• This section was edited to clarify the message to take in consideration the reviewer’s comment. Line 511-519 :
• “Across the course of infection, direct comparison of ΔNsp2- and wild-type-infected mice revealed a predominance of significantly lower transcript levels in the ΔNsp2 condition (Figure 7B–D). This effect was most pronounced at early time points, consistent with the separation observed in the UMAP analysis. Importantly, comparison of each infection condition with mock-infected controls showed that largely the same sets of genes were differentially expressed in both groups, with less than a 9% difference in the proportion of up- and downregulated genes (Supplementary Figure A–B). These findings indicate that deletion of Nsp2 does not substantially alter the transcriptional programs induced by infection but rather attenuates their magnitude. Thus, the differences observed between wild-type and ΔNsp2 infections primarily reflect weaker induction of infection-responsive genes rather than active repression in the absence of Nsp2.”

Mouse experiment design - tissue collection details (Line 300) Please clarify, for each timepoint (3, 5, 7 DPI), which tissues/samples were collected and which assays were performed on each. The Methods describe blood collection by cardiac puncture and multiple lung lobe allocations, but Figure 2A's schematic appears to show only lung collection for titer measurements - please reconcile the figure with the text.

• The figure 2A have been modified to improve clarity of the experimental design.

Figure 4C - terminology clarification (Line 367) The phrase "a distinct global leukocyte profile was already evident at 5 DPI" is not self-explanatory. Please define what is meant by "global leukocyte profile" and explain how Figure 4C/4B should be read/interpreted in the main text.

• Using “global leukocyte profile” we refer to changes in the proportion of each leucocyte populations and represented in a global manner in the stacked bar graph. Lines 399-401 were reworded for easier data interpretation by readers:
• “Distinct global leukocyte profiles, characterized by altered proportions of immune cell populations, were already evident at 3 DPI, indicating that the two viruses elicited divergent pulmonary immune responses.”

3. 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.

1. Reviewer #1

2.

Cell-intrinsic inflammatory responses. Given the marked reductions in CCL2 and IL-6 observed in ∆NSP2-SARS-CoV-2 infected mice, it would be valuable to determine whether infected ACE2-expressing cells intrinsically generate altered inflammatory signals. Measurement of inflammatory mediators following infection could help connect the cellular phenotype to the reduced pulmonary inflammation observed in vivo.

1. Secretion of IL-6 and some chemokines in response of SARS-CoV-2 infection in A549-A2 were attempted but since levels were near the detection limits, these could not be quantitated.

4.

Reviewer #2

5.

For in vivo experiments, there are some specific timepoints (Fig. 2F - 3 DPI; Fig. 2E - 7 DPI) were Δnsp2 mutant viral load is lower compared to the wild-type virus. The main conclusions in the Discussion must be modified according to this fact.

1. Figure 2E : The tendency for better viral clearance was highlighted in the result section (line 328-330). As no significant difference were observed and the trend at 7DPI is to the limit of detection, those results were not discussed further.

7.

• 3A depicts IFN alpha expression as upregulated in mock mice, shouldn't this be white considering it is baseline expression?*

1. We thank the reviewer for the remark. The color of the heatmap did not represent fold change but relative production. Therefore, mock condition with the high level of IFN⍺ were display in red. As we want to keep 1 color gradient and a visualization of all mediators in on graphic, we will keep this data representation style.

9.

Reviewer #3

10.

Histological staining choice - Carstairs vs H&E (Lines 332-337) The Carstairs-stained sections of WT and ΔNsp2 lungs appear visually similar, without obvious bronchointerstitial pneumonia. Carstairs staining is typically used to highlight fibrin/connective tissue, whereas H&E is the standard for assessing general tissue architecture and inflammatory cell infiltration. Please justify the choice of Carstairs staining for this analysis and describe how this choice may have limited the ability to detect or differentiate inflammatory changes between groups.

1. We thank the reviewer for this interrogation. In our past COVID study (PMID : 38365933, 40100623 and 40075368 ), we implement Carstairs staining to evaluate lung immunopathology. We chose this method instead of classic H&E staining because it offers more information to characterize the pathology with specific procedure to detect fibrosis, platelet accumulation and hemorrhagic (via red blood cell) in addition with the nucleus and global tissue’s structure. However, this choice of method did not have limited the ability to detect or differentiate inflammatory.

12.

Additionally: (a) what are the predominant differentially expressed transcripts, and do they correspond to the GSEA pathways highlighted in Figure 8 (e.g., DNA damage, epigenetic regulation)? (b) Given that fewer ORF1a-derived transcripts are detected in ΔNsp2-infected lungs, could differences in viral transcriptional/replication dynamics confound the host transcriptomic comparison? Please explain in the text. (c) Please specify how ORF1a-derived transcripts were quantified, given that ORF1a encodes Nsp1-11.

1. We thank the reviewer for the comment, here is the explanation regarding the transcriptomic analysis carried out in the study :
2. (A) We chose the GSEA approach instead of gene ontology (GO) on differential expressed gene (DEG), because this type of analysis takes into consideration how all genes of a pathways were regulated without using the significance threshold for each individual gene. As such, it reflects more how groups of genes were modulated then what are the top DEG. Taking this in consideration, highlighting predominant differentially expressed transcripts of discussed pathways does not seem relevant to us.
3. (B) Using our analysis pipeline (DEseq2), each gene expression was compared individually between the condition, thus change in one gene did not impact others. Moreover, only host genes were used for GSEA so viral genes expression could not impact this part of the transcriptomic analysis.
4. (C) Localization of viral gene/portion (Orf1a, Orf1ab, S, Orf3a, E, M, Orf6 Orf7a, Orf7b, Orf8, N and Orf10) was annotated on the viral genome then sequenced reads pseudo-maps (Kallisto quant). Kallisto uses an Expectation-Maximization (EM)algorithm to probabilistically assign multi-mapping reads to the correct transcripts (e.g. Nsp4 region with Orf1a and Orf1ab). In the end, Nsp2 deletion will have a higher impact on the number of reads (normalized sequencing deep) assigned to Orf1a as Nsp2 covers a greater proportion of this “gene” than in the whole Orf1ab gene.

17.

Figure 7 and 8 - figure consolidation (Lines 475-484) Consider combining Figures 7 and 8 into a single main figure, given their closely related content (differential expression and pathway enrichment from the same comparisons).

1. We thank the reviewer for the comment, but we chose to keep the figure 7 and 8 separated to keep a suitable font size and helping readers to analyze easily the figures.

19.

Figure 8 - presentation format (Lines 485-502)Figure 8 would benefit from a presentation similar to Figure 9B (dot plot with size = gene count, color = padj), allowing readers to assess both the magnitude (NES) and statistical confidence (padj) of each pathway - information not currently visible in the heatmap.

1. We thank the reviewer for the comment. As the padj value associated with all the pathways presented range between 10-9 and 10-8, we preferer to not overload the figure with noncrucial information.

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Referee #3

Evidence, reproducibility and clarity

Summary:

The authors investigated the role of SARS-CoV-2 Nsp2 by generating a recombinant virus lacking Nsp2 (ΔNsp2) and comparing it to wild-type (WT) recombinant virus. While ΔNsp2 replicated comparably to WT in vitro (Vero, A549-hACE2, ALI cultures) and in vivo (lung viral titers), ΔNsp2-infected K18-hACE2 mice showed markedly improved survival and reduced clinical disease severity. This was associated with reduced pulmonary and systemic inflammation, a shift from a myeloid-dominated, Th1-polarized response (WT) toward a more balanced antiviral response with enhanced lymphocyte/NK recruitment and altered antigen-presenting cell populations (ΔNsp2). RNA-seq revealed distinct early transcriptional programs, with ΔNsp2 infection showing reduced signatures related to epigenetic regulation/histone modification, RNA processing, and acute lung injury. CLIP-seq and proximity labeling further suggest that Nsp2 directly interacts with host RNA and components of the translational machinery, supporting a model where Nsp2 drives immunopathology by modulating host RNA processing and translation.

Major Comments

(1) The absence of Nsp2 in the ΔNsp2 mutant is clear, but the claim that Nsp1 and Nsp3 levels are "comparable when normalized to N protein" is not supported by quantitative data and I suspect differences in replication both in vitro and in vivo explain the difference in host response. Of course, if there is less virus, then host response is different and typically reduced. The authors need to take a more honest approach to evaluation of the data.

(2) Figure 1B - ΔNsp2 and its impact on nsp1 and 3 expression. Loading control and densitometry (Lines 269-271) It is not clear whether the absence of nsp2 impacts the nsp1/3 expression. The blot appears to show enhanced Nsp1/Nsp3 in ΔNsp2, and the stain-free total protein signal in Supplementary Figure 4 appears stronger for ΔNsp2. Please provide (a) densitometric quantification of Nsp1/Nsp3 normalized to N, and (b) a standard housekeeping protein blot (eg actin/GAPDH) in the main figure to confirm equal loading. Please also indicate the time point of sample harvest for the WB, so the replication can be correlated figure 1C.

(3) Figure 1C-E - Replication kinetics and infection dose (Lines 267-277) The claim of "comparable growth kinetics" is not fully supported - WT virus replicates faster and to higher titers in Vero and A549-ALI cultures at early/late time points, with statistically significant differences noted by the authors themselves. Additionally, infection doses were expressed as TCID50 and varied across cell models (Vero, A549-hACE2, A549-ALI), making cross-model comparison difficult and obscuring the actual MOI/copies-per-cell delivered. Please repeat key experiments using a standardized MOI or genome copies/cell across all models with the titer at 1-2h to reflect equal input virus, if different MOI or genome copies/cell dose is needed, please also provide explanation.

(4) Histological staining choice - Carstairs vs H&E (Lines 332-337) The Carstairs-stained sections of WT and ΔNsp2 lungs appear visually similar, without obvious bronchointerstitial pneumonia. Carstairs staining is typically used to highlight fibrin/connective tissue, whereas H&E is the standard for assessing general tissue architecture and inflammatory cell infiltration. Please justify the choice of Carstairs staining for this analysis, and describe how this choice may have limited the ability to detect or differentiate inflammatory changes between groups.

(5) Virus localization - IHC/ISH needed (Lines 332-337) To determine whether the observed inflammatory differences relate to differences in viral antigen/RNA distribution which also reflect replication difference (rather than purely host immune modulation by Nsp2), viral IHC or in situ hybridization (ISH) should be performed on lung sections to localize virus within the tissue and correlate with inflammatory zones. Otherwise explain that replication differences may underlie differences in host response.

(6)Cytokine/chemokine data presentation (Lines 332-337) The heatmap in Figure 3A uses a relative 0-10 scale that is difficult to interpret biologically. Please provide the raw concentration data (pg/mL or pg/mg protein) for key mediators, ideally as bar graphs/dot plots, so readers can assess whether the differences between WT and ΔNsp2 are of plausible biological/clinical magnitude.

(7) Transcript-level validation of cytokine/chemokine changes (Lines 332-337) In addition to protein-level (ELISA/multiplex) data, qPCR for key cytokine/chemokine transcripts (e.g., Ccl2, Cxcl9, Ifng, Il6, Ccl5) in lung tissue would help determine whether Nsp2 acts at the level of transcription versus translation/secretion.

(8) In vitro/in vivo correlation for CCL5/IL-6 findings (Lines 338-343) The supplementary A549-hACE2 data show that Nsp2 reduces CCL5 but not IL-6 in response to poly(I:C). Please clarify the rationale for using this specific readout to model the in vivo lung findings. Does Nsp2 expression also modulate CCL2, CXCL9, or IFN-γ in A549 cells? A more complete in vitro dissection - expressing Nsp2 vs. empty vector, stimulating with poly(I:C), and measuring IFN/ISG and chemokine/cytokine transcripts by qPCR alongside ELISA - would better support the proposed mechanism.

(9) Discrepancy in differential expression results (Lines 475-484) The text states that ΔNsp2 infection shows a predominance of downregulated transcripts relative to WT (Figure 7B-D), yet the supplementary comparison (each condition vs. mock) reportedly shows similar proportions of up/down genes. Please clarify how these two comparisons relate, and whether they are actually measuring the same thing (ΔNsp2 vs WT directly, versus each vs mock separately). Additionally: (a) what are the predominant differentially expressed transcripts, and do they correspond to the GSEA pathways highlighted in Figure 8 (e.g., DNA damage, epigenetic regulation)? (b) Given that fewer ORF1a-derived transcripts are detected in ΔNsp2-infected lungs, could differences in viral transcriptional/replication dynamics confound the host transcriptomic comparison? Please explain in the text. (c) Please specify how ORF1a-derived transcripts were quantified, given that ORF1a encodes Nsp1-11.

Minor Comments

(1) Figure 3A heatmap - visual clarity The color differences between WT and ΔNsp2 groups, and across timepoints, are subtle and difficult to distinguish visually. Consider an alternative visualization (e.g., separate scaling per mediator, or a dot plot) to improve readability.

(2) Mouse experiment design - tissue collection details (Line 300) Please clarify, for each timepoint (3, 5, 7 DPI), which tissues/samples were collected and which assays were performed on each. The Methods describe blood collection by cardiac puncture and multiple lung lobe allocations, but Figure 2A's schematic appears to show only lung collection for titer measurements - please reconcile the figure with the text.

(3) Figure 4C - terminology clarification (Line 367) The phrase "a distinct global leukocyte profile was already evident at 5 DPI" is not self-explanatory. Please define what is meant by "global leukocyte profile" and explain how Figure 4C/4B should be read/interpreted in the main text.

(4) Figure 7 and 8 - figure consolidation (Lines 475-484) Consider combining Figures 7 and 8 into a single main figure, given their closely related content (differential expression and pathway enrichment from the same comparisons).

(5) Figure 8 - presentation format (Lines 485-502) Figure 8 would benefit from a presentation similar to Figure 9B (dot plot with size = gene count, color = padj), allowing readers to assess both the magnitude (NES) and statistical confidence (padj) of each pathway - information not currently visible in the heatmap.

Significance

This is the first study to use both a mouse model and reverse genetics-derived viruses to investigate the role of Nsp2 in viral pathogenesis and host responses. The study integrates multiple levels of analysis, including in vitro and in vivo replication kinetics, comprehensive disease outcome measurements (survival, clinical scores, and weight loss), inflammatory mediator quantification by ELISA, immune cell phenotyping, and omics approaches (RNA-seq and CLIP-seq) to characterize global virus-host interactions. The preprint is accessible to researchers with a biological science background. The experimental design is logical, and the methodologies are easy to follow. However, while CLIP-seq/BioID data suggest Nsp2 interacts with translational machinery and host RNAs, the direct causal link isn't established in the study. The histopathology assessment methodology, inflammatory mediator heatmap analysis are visually confusing. RNA-seq interpretation is possibly confounded by differences in viral replication between wild type and mutant.

We are molecular virologists expert in studying host responses to infection with significant experience studying coronaviruses

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Referee #2

Evidence, reproducibility and clarity

In this manuscript, Lacasse et al. use reverse genetics to generate a SARS-CoV-2 Δnsp2 mutant virus to analyze the effect of non-structural protein 2 (nsp2) in viral replication and pathogenesis both in vitro and in vivo. This study presents a considerable amount of work to corroborate the role of nsp2 in viral replication, which has not been evaluated before. The manuscript is properly written and the language style is correct. However, the main weakness of this manuscript is an incorrect interpretation of the results. I expand on this issue and other relatively minor issues below.

Major

• The main conclusion of this manuscript, stated in lines 549-554, claims that the difference in pathology between Δnsp2 mutant and WT virus infection cannot be explained by distinct viral replication since both viruses replicate similarly in vitro and in vivo. However, the data presented here is supportive that Δnsp2 mutant replicates to a lower extent when compared to WT virus. This is clearly seen in Figures 1C (at 24 hpi), and Figures 1D and 1E for in vitro experiments where there is a 2-log difference at multiple timepoints. For in vivo experiments, there are some specific timepoints (Fig. 2F - 3 DPI; Fig. 2E - 7 DPI) were Δnsp2 mutant viral load is lower compared to the wild-type virus. The main conclusions in the Discussion must be modified according to this fact.
• In Figure 1B, the expression of viral proteins Nsp1 and Nsp3 are normalized to N protein to conclude that they are not influenced by nsp2 deletion. N protein is known to have diminished expression when SARS-CoV-2 mutants replicate deficiently, which is the case of the Δnsp2 mutant under in vitro conditions. Why did the authors choose to normalize against N protein? Why was not a loading control such as beta-actin used?
• Authors analyze the expression of the envelope (E) gene to assess the viral replication in vivo. GAPDH gene is used as housekeeping gene. I wonder why authors chose these genes for this study, considering that E gene expression values range is small (101 to 10-2). N subgenomic RNA is more appropriate to measure active viral transcription since it is more abundant than E subgenomic RNAs. Also, GAPDH has been reported as not suitable housekeeping gene for SARS-CoV-2 infection (reported in PMID: 36377893).
• Authors do not provide a validation of the RNASeq analysis, i.e. authors must select a representative set of up- and down-regulated genes and perform RT-qPCR on the same samples to corroborate if the fold changes observed in RNASeq are also observed via an alternative method.

Minor

• There are several statements that are not correct in the Introduction: Lines 37-38: '... SARS-CoV-2 genome encodes a large replicase polyprotein that...' is not true, SARS-CoV-2 genome encodes for two large polyproteins (pp1a and pp1ab). Line 41: '... leading to the activation of type I interferon...', IFNs as molecules are not activated, the correct phrasing for this sentence would be '... lead to the production / expression of type I interferon' or '... lead to activation of type I interferon signaling cascade...'. Lines 52-54, this statement is a bit exaggerated. There has been a huge research effort during the past COVID-19 pandemic to understand the replication of coronavirus, especially SARS-CoV-2. Most mechanisms underlying SARS-CoV-2 infection including viral entry, formation or replication organelles, assembly, budding and exocytosis are already well characterize in the scientific literature.
• Line 295, there seems to be a number missing in '****P < 0.000'
• Figures 1C, 1D, 1E could be labelled with the corresponding tested cell line on top of each plot to improve interpretation of the figures.
• The inclusion of uncropped Western blot data in the Supplementary Figures is appreciated. However, the approximate positions of the molecular weight markers should also be indicated in the corresponding main figure (Fig. 1B) to facilitate data interpretation.
• Fig. 3A depicts IFN alpha expression as upregulated in mock mice, shouldn't this be white considering it is baseline expression?
• Fig. 3A, the p-Value indicated with two asterisks on top of the figure might result confusing for readers. I would indicate it only in the figure caption.
• Figs. 7B, 7C, 7D additional arrows pointing to the main outlier transcripts could be added (in a similar fashion to ORF1a)
• Supplementary Figure 4A, there is a mistake in the left-panel western blot, authors indicate nsp1 protein to a band that corresponds to nsp2 in the main figure.

Significance

Strengths: the study is supported by a well-designed experimental framework, appropriate statistical analyses, and an adequate sample size. The manuscript is clearly written and employs a suitable scientific style and language. Furthermore, the breadth of experiments performed and the volume of data presented are substantial.

Limitations: the main limitations include drawing erroneous conclusions due to an incorrect interpretation of the data, the absence of appropriate controls in certain experiments, and the lack of independent validation of the RNA-seq findings.

Advance: this work addresses an important gap in our understanding of the role of nsp2 in coronavirus replication. To the best of my knowledge, this is the first study to investigate this question using a comprehensive reverse genetics approach combined with both in vitro and in vivo experimentation.

Audience: the manuscript will be of primary interest to specialized research groups working in the field of coronavirus virology.

Expertise: I am a researcher with over seven years of postdoctoral experience in molecular virology, with a particular focus on coronaviruses in two recognized international institutions. My expertise includes the development and application of coronavirus reverse genetics systems to generate deletion mutants for investigating gene function, as well as the design and generation of replicon systems for antiviral research.

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Referee #1

Evidence, reproducibility and clarity

Lacasse et al present a intriguing study assessing the role of NSP2 as a virulence factor in SARS-CoV-2, they present a well designed body of work showing the loss of this non-structural protein attenuates pathogenesis in a K-18-hAce2 mouse model. The in vivo data are compelling and support the conclusion that loss of NSP2 is associated with altered host inflammatory responses rather than major defects in viral replication. The observations of reduced CCL2, IL-6, CD45+ leukocyte infiltration, and disease severity in ∆NSP2 virus, despite comparable viral titers, are particularly interesting. Furthermore, the preservation of IFN-γ and CXCL9 responses suggests that antiviral immunity remains largely intact.

However, the mechanistic link between the in vitro phenotype and the in vivo immune phenotype remains incompletely defined. The manuscript would be strengthened by additional experiments addressing the following points:

1. Early infection kinetics in ACE2-expressing cells. The authors report transiently reduced viral RNA levels in vivo during the early phase of infection, despite comparable viral loads at later time points. It would therefore be informative to determine whether a similar phenomenon occurs in ACE2-expressing cells. Time-course analyses of viral RNA and/or viral protein expression could help establish whether the mutant primarily affects early infection events rather than overall replicative capacity.
2. Cell-intrinsic inflammatory responses. Given the marked reductions in CCL2 and IL-6 observed in ∆NSP2-SARS-CoV-2 infected mice, it would be valuable to determine whether infected ACE2-expressing cells intrinsically generate altered inflammatory signals. Measurement of inflammatory mediators following infection could help connect the cellular phenotype to the reduced pulmonary inflammation observed in vivo.
3. Given the reduced pathology and disease progression in the ∆NSP2-SARS-CoV-2 infected mice, have the authors considered assessing whether mice exposed to this mutant SARS-CoV-2 strain have enhanced responses to re-challenge with WT SARS-CoV-2?

Significance

This study provides critical insights into the role of NSP2 in modulating host inflammatory responses during SARS-CoV-2 infection. By demonstrating that attenuation of the ∆NSP2 virus is linked to altered inflammatory signalling rather than impaired viral replication, it highlights a distinct mechanism influencing disease severity. The preservation of key antiviral responses such as IFN-γ and CXCL9 further underscores the selective impact on host immunity. These findings advance understanding of viral-host interactions and suggest potential avenues for therapeutic intervention targeting inflammation without compromising antiviral defence.

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Reply to the reviewers

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

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Referee #3

Evidence, reproducibility and clarity

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

Establishing epithelial boundaries is a key aspect during development and tissue homeostasis. Epithelial tissues are characterized by an apico-basal axis that regulates tissue functions. While the functions of Ephrin signaling have previously been investigated in several in vitro models as well as in vivo, their biological requirements during morphogenesis remain elusive. Previous work from the same group established a proximity network of several Ephrin receptors. Highlighting the role of Ephrin signaling in epithelial homeostasis, their BioID screen identified PAR-3, a major component of the polarity machinery as a key target for Ephrin receptors, driving cell segregation. In this manuscript, Lavoie et al follow-up the potential role of Ephrin signaling specifically EPHA1 and EPHB4 during apico-basal establishment in a Caco-2 cell cyst model. Authors first demonstrate that a specific set of Ephrin receptors are expressed in 2D Caco-2 cells, independently of cell density. Loss of function experiment using shRNA mediated knock-down of EPHA1 and APHB4 leads to multi-lumen phenotype, an hallmark of epithelial disorganization. Authors described that this phenotype is driven by mitotic spindle misalignment. Rescue experiments showed that the phenotype was independent from the kinase activity but instead dependent on the ability to bind Ephrin ligands.. The last part of this manuscript focuses on the Ephrin ligand and their expression in Caco-2 cells. Using shRNA-mediated knockdown, they confirmed the requirement of Ephrin B2 that phenocopies the absence of Ephrin receptors.

Major comments:
- Are the key conclusions convincing? This manuscript describes in detail some aspects of Ephrin signaling during morphogenesis. The data are rigorous and overall adequate for the conclusion claimed by the authors. 
- Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether? All experiments were reproduced at least 3 times as stated by the authors.
- 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. To strengthen their conclusion, I would suggest the following:

1. Use a basoleteral marker to show colocalization with EPHR (fig. 1)
2. Do EPHA1/B4 knockdown line proliferate more? More nuclei are visible after knockdown. Proliferation was shown to affect mitotic spindle alignment in other epithelial models (Morrow et al, eLife 2019 https://doi.org/10.7554/eLife.48482). In the case where proliferation is increased, I wonder whether reducing cell proliferation by titrating down a cell cycle inhibitor would be sufficient to rescue the spindle misalignment and multi-lumen phenotype.
3. While experiments and controls are done properly, I am a bit puzzled by an important statement made by the author that do not fit some data. Authors wrote: "We used retroviral infection to express shRNA-resistant EPHA1-GFP and EPHB4-GFP at near endogenous levels". Looking at the data, I can only disagree with this statement, especially for EPHB4 where over expression seems 4-5x higher than endogenous level. While I recognize the difficulty of achieving endogenous level of expression, authors should clarify this point. Quantification of the over expression should be done for transparency and the result section should be modified to reflect the outcome.
4. Expression analysis of the Delta ICD mutant should be performed - If the antibody recognizes the missing intracellular part, finding an antibody recognizing a different antigen would help.
5. Would it be possible that the lack of rescue of the R104E mutant is linked to its much lower expression in both EPHA1/B4?
6. Does EPHA1/B4 over expression rescue the defect in mitotic spindle misalignment?
7. Would it be possible that the effects downstream of EPHA1 are mediated by recruitment of key cytoskeletal regulators (Ephexin regulating RhoA/RhoG and Vav2/3 regulating Rac1)? Is Rac1-GTP or RhoA-GTP level affected in their knockdown and/or rescue? Rac1 is a crucial regulator of lumen formation (Mack et al,doi.org/10.1038/ncb2608,Yagi et al, doi.org/10.1038/embor.2011.249, Fort et al doi.org/10.1038/s41556-018-0198-9). Would Rac1 signaling be important in this system?
8. It would be important to use a different cell line to confirm some of the important conclusions from this manuscript. I recognize the difficulty to obtain "normal" intestinal cell lines or their cost to acquire them. Would this mechanism be conserved across other healthy epithelial cell lines (breast, kidney or lung)?
   • 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. This proposed revision should not involve complicated new reagents/constructs. Kits are available for testing RhoGTPase signaling. Alternatively, constructs for bacterial expression and GST-Pull down activity assay can be obtained on Addgene. Estimated revision time ~3-4months.
- Are the data and the methods presented in such a way that they can be reproduced? Yes - Methods are clear and detailed. Catalog numbers for antibodies are clearly mentioned, as well as references for shRNA constructs.
- Are the experiments adequately replicated and statistical analysis adequate? Authors properly replicated their experiments and clearly stated in the figure legend. Partially - Given the number of pseudo-replications, it would be helpful and transparent to present the data as violin plots (Lord et al doi.org/10.1083/jcb.202001064). I would also strongly encourage to average pseudo replicates for each biological experiment and derive statistical analysis from biological repeats.



Minor comments:
Specific experimental issues that are easily addressable. 1. Quantify EPHA1/2/4 and EPHB4 expression. 2. Add a merge panel with EPHR/EZR
- Are prior studies referenced appropriately? Yes - Authors have done a great job of comparing their data with the current literature.
- Are the text and figures clear and accurate? Yes - While it is transparent to call WB for each figure, it can lead to some confusions for the reader.
- Do you have suggestions that would help the authors improve the presentation of their data and conclusions? See above.

Significance

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

Studying Ephrin signaling has been mostly done using brain/neuronal models. Building up on the author's previous work linking Ephrin signaling and epithelial biology, their conclusions add a layer of complexity to the field of luminogenesis. It also provides a nice model to further investigate the function of Ephrin signaling and I could see potential other studies digging into the mechanism by looking at early stages of polarity establishment (AMIS, trafficking,...). It would also provide interesting data to study signaling in healthy and disease-like models. - Place the work in the context of the existing literature (provide references, where appropriate).

I believe this work will add new knowledge on epithelial homeostasis regulation. Importantly, not much is known about the role of Ephrin A1/B4 in intestinal homeostasis/cancer so this manuscript would provide a framework for further studies. - State what audience might be interested in and influenced by the reported findings.

Anybody working on epithelial biology and cell signaling - 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.

Epithelial biology, Stem cell, Cytoskeleton. None.


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Referee #2

Evidence, reproducibility and clarity

The manuscript by Lavoie et al. investigates the role of EPHA1 and EPHB4 tyrosine kinase receptors in epithelial morphogenesis using shRNA-mediated knockdown in Caco-2 cells. The study finds that silencing these receptors results in disorganized spheroids with mitotic spindle orientation defects and multiple atrophic lumens. Importantly, these effects are dependent on the receptors' ligand-binding domains but not their kinase activities. The study also highlights the depletion of EFNB2, an EPHB4 ligand, causing similar defects in lumen formation. These findings suggest a novel non-catalytic role for EPHA1 and EPHB4 in epithelial morphogenesis.

Major Comments

1. Reproducibility of RNA Expression Levels:

Clarify whether the RNA levels shown in Figure 1A correspond to 2D (monolayer) or 3D (cysts) Caco-2 cells and include error bars (SD) for clarity. 2. Actin Blot Reproducibility:

Improve actin blots for EPHA1 and EPHB4 to ensure consistent actin signal intensity. Provide quantification with error bars (SD) and show RNA and protein levels in 3D Caco-2 cysts at different developmental stages. 3. Detailed Confocal Imaging:

Enhance confocal images of EPHA1 and EPHB4 localization in 3D Caco-2 spheroids with better image quality, magnification, and plot profile intensity to show exclusion from tight junctions. 4. Western Blot Consistency:

Simplify the presentation of western blots by removing unnecessary lanes and using consistent labeling. Ensure blots are performed on 3D Caco-2 depleted spheroids samples (day 6). 5. Figure Relevance:

Consider moving Figure 3 to the supplementary section as depletion of either EPHA1 or EPHB4 doesn't affect polarity markers localization. 6. Quantification and Statistical Analysis:

Include detailed quantification and statistical analysis for the mean angle of the mitotic spindle in dividing Caco-2 cells. Ensure statistical significance between constructs in Figure 5A and 5B. 7. Construct Expression Levels:

Show expression levels for all constructs in a single figure and consider generating stable cell lines expressing constructs at near endogenous levels for clearer results. 8. Protein Expression Validation:

Perform western blots for EFNB2, EFNA1, EFNA4, and EFNA2 and include magnified panels with plot profile intensity to demonstrate exclusion and localization. Consider proximity ligation assay (PLA) to demonstrate EPHB4/EFNB2 interaction. 9. Supplementary Figure Refinement:

Review and possibly exclude or refine supplementary figures to ensure they provide relevant and unique information.

Minor Comments

1. Increased Sample Size:

Increase the number of cells analyzed per experiment to ensure statistical robustness and provide clearer quantification of mitotic spindle orientation. 2. Clarification of Expression Levels:

Clarify the expression levels of shRNA-resistant constructs and consider using CRISPR/Cas9 for complete loss of gene function to improve the robustness of knockdown experiments. 3. Visualization Enhancements:

Enhance all figures with appropriate error bars, scale bars, and annotations to improve clarity and readability. 4. Proximity Ligation Assay:

A proximity ligation assay (PLA) could be done to demonstrate EPHB4/EFNB2 interaction at the basolateral membranes of 3D Caco-2 spheroids, providing stronger evidence of their interaction.

By addressing these major and minor comments, the authors can improve the clarity, reproducibility, and overall quality of their manuscript, making their findings more robust and impactful in the field of epithelial morphogenesis.

Significance

The study by Lavoie et al. provides significant contributions to the field of epithelial morphogenesis, particularly in understanding the roles of tyrosine kinase receptors EPHA1 and EPHB4. Here are the key aspects of its significance:

Novel Insights into EPHA1 and EPHB4 Functions

Non-Catalytic Role Discovery:

The study uncovers a novel non-catalytic role for EPHA1 and EPHB4 in epithelial morphogenesis. While these receptors are traditionally known for their kinase activities, this research shows that their role in spheroid morphology regulation is independent of their catalytic functions. This challenges the conventional understanding of kinase receptors and opens new avenues for research into their non-catalytic functions. Mitotic Spindle Orientation:

The findings demonstrate that EPHA1 and EPHB4 are crucial for proper mitotic spindle orientation in epithelial cells. Given that only a few membrane receptors have been previously implicated in spindle orientation, this discovery broadens the scope of cellular components involved in this process, potentially leading to more comprehensive models of cell division and tissue organization. Impact on Understanding Epithelial Morphogenesis Spheroid Formation and Morphology:

The study highlights the importance of EPHA1 and EPHB4 in the formation and organization of epithelial spheroids, which are vital for tissue architecture and function. By identifying defects in spheroid formation upon receptor depletion, the research underscores the role of these receptors in maintaining epithelial tissue integrity. Ligand-Binding Domain Importance:

The requirement of the ligand-binding domain for EPHA1 and EPHB4 to regulate spheroid morphology emphasizes the significance of receptor-ligand interactions in epithelial morphogenesis. This finding could lead to further investigations into other receptors and ligands involved in similar processes, enhancing our understanding of cellular communication and tissue development. Broader Implications for Cell Biology and Disease Research Potential Therapeutic Targets:

Understanding the non-catalytic roles of EPHA1 and EPHB4 could have implications for developing therapeutic strategies for diseases involving epithelial tissue, such as cancer. Targeting the non-catalytic functions of these receptors might offer novel approaches for intervention. Framework for Future Research:

The study provides a framework for future research into the non-catalytic roles of kinase receptors. It encourages the scientific community to look beyond the traditional catalytic activities of these receptors and explore their diverse functions in cellular processes.

Significance Summary

In summary, the study by Lavoie et al. significantly advances our knowledge of epithelial morphogenesis by revealing new functions for EPHA1 and EPHB4. It challenges existing paradigms, highlights the importance of non-catalytic roles of kinase receptors, and sets the stage for future research in cell biology and disease. These contributions are not only scientifically valuable but also have the potential to inform therapeutic developments and enhance our understanding of complex biological systems.

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Referee #1

Evidence, reproducibility and clarity

In this work, Lavoie et al addressed the roles of EPH family of tyrosine kinase receptors in epithelial morphogenesis, using the Caco-2 cell 3D culture system. Among the EPH receptors, the authors focused on EPHA1 and EPHB4, two receptors expressed basolaterally in the differentiated Caco-2 cells. Upon depletion of these proteins by shRNA knockdown, Caco-2 cell cysts exhibit multiple lumen phenotypes, similar to the one obtained by atypical PKC knockdown. The authors showed that deletion of EPHA1 or EPHB4 leads to spindle orientation defects instead of disrupting apical-basal polarity itself. Mechanistically, EPHA1 and EPHB4 requires ligand binding domain, not kinase domain for proper morphogenesis. Consistent with this, one of the EFN ligands, EFNB2 is required for spheroid morphogenesis, likely through an interaction between EPHB4 and EFNB2. Together, the authors proposed a ligand-receptor pair that controls Caco-2 spheroid morphogenesis.

Major comments:

1. In Figure 3, the authors claimed that EPHA and EPHB4 depletion does not affect apicobasal polarity based on marker localizations (ZO1, Par6, E-cad, Scrib). However, in the spheroid with multiple lumens, it would be hard to distinguish the localization issues. It seems that basolateral membrane became large or expand and mask the actual localization of some polarity and junctional markers.
2. Depletion of EPHA1 or EPHB4 lead to spindle misorientation phenotypes (Figure 4). If defects in spindle orientation is causative for abnormal morphogenesis of Caco-2 cells, morphogenesis defects observed in mutant form of EPHA1 or EPHB4 as well as EFNB2 depletion lead to similar spindle orientation defects. It would be critical to show specific pairs of EPH and EFN and their domains are required for the control of spindle orientation.
3. I did not get an understanding how EPHR and EFN controls mitotic spindle orientation. The authors cited many references for their potential mechanisms. However, as the authors already mentioned, EFN-EPHR is shown to control spindle orientation in the Drosophila neuroepithelium where some known regulators of spindle orientation (Mud etc. ) are seemingly associated. It would be important to show a mechanism of how vertebrate/mammalian EPHR and EFN regulate proper spindle orientation using their own Caco-2 system or others system.

Minor comments:

1. The authors focused on EPHA1 and EPHB4 based on the evidence that they are expressed in differentiated Caco-2 cells. Are they functional in both proliferative and differentiated Caco-2 cells? (I thought they are looking at proliferative Caco-2 cell cyst.) If so, what about EPHA2 and EPHA4? Do these two others expressed EPH contribute to spindle orientation?
2. The authors claimed that EPHA1 and EPHB4 act independently. They could test this by simply knocking down both proteins and to see whether additive effects exist or not.

Significance

EPH and EFN are already reported to control mitotic spindle orientation in invertebrates (Drosophila) through Dlg-1, Mud and similar ligand-receptor pair like semaphorins and plexins do control spindle orientation via negatively impacting CDC42 activity in mammals. Given that previous studies dig deeper into mechanism that can explain how these proteins affect spindle alignment, the current work should address a potential mechanism where EPHR and EFN controls mitotic spindle orientation.

This work is a typical cell biological study, and the audience who are interested in cell biology and epithelial morphogenesis would show an interest.

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Reply to the reviewers

Manuscript number: RC-2025-02932

Corresponding author(s): Amit Tzur

[Please use this template only if the submitted manuscript should be considered by the affiliate journal as a full revision in response to the points raised by the reviewers.

If you wish to submit a preliminary revision with a revision plan, please use our "Revision Plan" template. It is important to use the appropriate template to clearly inform the editors of your intentions.]

1. General Statements

We thank all Referees for their insightful comments and thoughtful review of our manuscript.

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. *

__! Original comments by Reviewers #1-3 are in gray. __

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

The study highlights a dephosphorylation switch mediated by PP2A as a critical mechanism for coupling E2F7/8 degradation to mitotic exit and G1 phase. The study is clear and experiments are well conducted with appropriate controls

I have some concerns highlighted below:

Point 1. In this sentence: This intricate network of feedback mechanisms ensures the orderly progression of the cell cycle. What feedback mechanism are the authors referring to?

Thank you for pointing this out. We aimed for a general comment. The original line was replaced with: “The intricate network of (de)phosphorylation and (de)ubiquitination events in cycling cells establishes feedback mechanisms that ensure orderly cell cycle progression.”

Point 2. Characterization of disorder in the N-terminal segments of E2F7 and E2F8

What does it mean disorder in this title?

“Disorder” is a structural biology term for describing an unstructured (floppy) region in a protein. We suggest the following title in hope to improve clarity: “The N-terminal segments of E2F7 and E2F8 are intrinsically unstructured”

Point 3. In the paragraph on the untimely degradation of E2F8 the authors keep referring to APC/C Cdc20, however the degradation is triggered by the Ken box which is specifically recognised by APC/C Cdh1. Can it be due to another ligase not APC/C?

In our anaphase-like system, Cdh1 cannot associate with the APC/C due to persistently high Cdk1 activity, maintained by the presence of non-degradable Cyclin B1. While the KEN-box is classically recognized as a Cdh1-specific motif, previous studies have also clearly demonstrated that APC/C-Cdc20 can mediate the degradation of KEN-box substrates. For example, BubR1 interacts with Cdc20 via two KEN-box motifs (PMIDs: 25383541, 27939943 and 17406666). Nek2A is targeted for degradation by the APC/C in mitotic egg extracts lacking Cdh1, in a manner that depends on both D-box and KEN-box motifs (PMID: 11742988). CENP-F degradation in Cdh1-null cells has been shown to be dependent on both Cdc20 and a KEN-motif (PMID: 20053638). Thus, the most simple explanation for our results is that degradation is KEN box dependent and controlled by Cdc20.

Regarding alternative E3 ligases, KEN-box mutant variants of non-phosphorylatable E2F8 remained stable in APC/CCdc20-active extracts, suggesting that this degradation is indeed APC/C-specific.

Please also see our response to Reviewer #3, Point 3.

Point 4. The assays to detect dephosphorylation are rather indirect so it is difficult to establish whether phosphorylation of CDK1 and dephosphorylation by PP2A on the fragments is direct.

First, the phosphorylation sites analyzed in this study conform to the full and most canonical Cdk1 consensus motif: S/TPxK/R. While recognizing that other kinases are proline directed as well, the cell cycle dependent manner of this control, and presence of a similar CDK-dependent mechanism for Cdc6, points us towards considering the role of CDKs.

Second, consistent with the direct role of CDK1 in this regulation, NMR experiments demonstrate conformational shifts of recombinant E2F8 following incubation with Cdk1–Cyclin B1 (not included in manuscript, but shown here for reviewer consideration); see Figure below. We have not yet established equivalent biochemical systems for PP2A.

Figure legend: NMR-based monitoring of E2F7 (a-c) and E2F8 (d-f) phosphorylation by Cdk1.

a(d). 15N,1H-HSQC spectrum of E2F7(E2F8) prior to addition of Cdk1. Threonine residues of interest, T45 (T20) conforming to the consensus sequence (followed by a proline), and T84 (T60) lacking the signature sequence are annotated. b(e). Strips from the 3D-HNCACB spectrum used for assigning E2F7(E2F8) residues. Black (green) peaks indicate a correlation with the 13Cα (13Cβ) of the same and previous residues. The chemical shifts assigned to T45 (T20) and T84 (T60) match the expected values for K44(K19) and P83(P59), thereby confirming the assignment. c(f). Top, overlay of subspectra before adding Cdk1 (black) and after 16 h of activity (red) at 298 K. Bottom, change in intensities of the T45/T84 in E2F7 and T20/T60 in E2F8 showing how NMR monitors phosphorylation and distinguishes between various threonine residues.

Third, PP2A is likely the principal phosphatase counteracting Cdk1-mediated phosphorylation during mitotic exit, targeting numerous APC/C substrates (PMID: 31494926). In light of our findings and the extensive literature, it is therefore reasonable to propose that E2F7 and E2F8 may also be direct PP2A targets.

Fourth, we cannot fully exclude the possibility that dephosphorylation of E2F7 and E2F8 by PP2A occurs indirectly. Nevertheless, indirect studies of PP2A substrate identification in the literature often rely on similar genetic perturbations, chemical inhibition, cell-free systems (coupled with immunodepletion, inhibitory peptides/proteins, and small-molecule inhibitors), and phosphoproteomics. Moreover, more direct assays are not without caveats, as they lack the cellular stoichiometric context, an important limitation for relatively promiscuous enzymes such as phosphatases.

Importantly, repeated attempts (conventional [Co-IP] and less conventional [affinity microfluidics]) to detect interactions between PP2A and E2F7 and E2F8 were unsuccessful. This result was unfortunate but not surprising, given that transient substrate–phosphatase interactions are often challenging to capture experimentally.

Given our evidence showing the regulation of E2F7 and E2F8 degradation in a manner that depends on Cdk1 and PP2A, the title of the manuscript remains appropriate: "Cdk1 and PP2A constitute a molecular switch controlling orderly degradation of atypical E2Fs.”

Please also see our response to Reviewer #3 Point 1.

Point 5. Although there seems to be a control by phosphorylation and dephosphorylation (which could be indirect), it is difficult to establish the functional consequences of this observation. The authors propose a feedback mechanism which regulates the temporal activation inactivation of E2F7/8 however, there are no evidence in support of this.

The components being studied here have been extensively characterized, as have the direct and indirect interactions that connect them and ensure orderly cell cycle progression. For example: i) The E2F1–E2F7/8 transcriptional circuitry functions as a negative feedback loop; ii) Cdk1 and PP2A counteract one another’s activity; iii) E2F1 promotes the disassembly of APC/CCdh1; iv) E2F7 and E2F8 are APC/C substrates with cell cycle-relevant degradation patterns; and v) Loss of Cdh1 leads to premature S-phase entry.

Our study brings these components together into a coherent regulatory module operating in cycling cells, revealed through cell-free biochemistry and newly developed methodologies with broad applicability to signaling research. We believe that advancing mechanistic understanding at this level of central regulators is impactful. And notably, this is a model, which we expect others in the field to test. We stand behind the result of each individual experiment and based on those findings are proposing a feedback circuit.

Point 6. Reviewer #1 (Significance (Required)):

The study is a good and well conducted work to understand the mechanisms regulating degradation of E2F7/8 by APC/C. This is crucial to establish coordinated cell cycle progression. While the hypothesis that disruption of this mechanism is likely responsible for altered cell cycle progression, there are no evidence this is just a back up pathway, whose functional significance could be limited to lack of APC/C Cdh1 activity. These experiments are rather difficult but the authors could comment on the limitation of the study and emphasise the hypothetical alterations which could result from the alterations of the described feedback loop

We thank Reviewer #1 for this comment. Accordingly, we have expanded the discussion to further elaborate on the potential molecular outcomes and limitations of our study.

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

Summary: The authors provide strong biochemical evidence that the regulation of E2F7 and E2F8 by APC is affected by CDK1 phosphorylation and potentially by PP2A dependent dephosphorylation. The authors use both full length and N-terminal fragments of E2F8 in cell-free systems to monitor protein stability during mitotic exit. The detailed investigation of the critical residues in the N-terminal domain of E2F8 (T20/T44) is well supported by the combination of biochemical and cell biology approaches.

We thank Reviewer #2 for their encouraging feedback.

Point 1. Major: It is unclear how critical the APC-dependent destruction of E2F7 and E2F8 is for cell cycle progression or other cellular processes. Prior studies have reported that Cyclin F regulation of E2F7 is critical for DNA repair and G2-phase progression. This study would be improved if the authors could provide a cellular phenotype caused by the lack of APC dependent regulation of E2F8 and/or E2F7.

We thank Reviewers #2 and #1 for this comment, which prompted substantial revisions. Below, we reiterate our response to Reviewer #1.

The molecular components examined in this study are well established in the literature. Key principles include: (i) the reciprocal regulation between E2F1 and its repressors, E2F7 and E2F8, which forms a transcriptional feedback loop; (ii) the opposing activities of Cdk1 and PP2A; (iii) the capacity of E2F1 to attenuate APC/CCdh1 activity; (iv) the fact that E2F7 and E2F8 are APC/C substrates with defined cell cycle–dependent degradation patterns; and (v) the requirement for Cdh1 to prevent premature S-phase entry.

Our study integrates these elements into a unified framework operating in proliferating cells. This framework is supported by biochemical reconstitution experiments and newly developed methodological tools, which we anticipate will be broadly applicable for dissecting signaling pathways. We view this type of mechanistic synthesis as valuable for the field. Importantly, we do not present this as a definitive model, but rather as a testable regulatory circuit constructed from robust individual findings.

Overall, our study is mechanistic and based on cell-free systems. The central aim of this manuscript is to define how the Cdk1–PP2A axis is integrated into the APC/C–E2F1 regulatory network controlling cell-cycle progression. Collectively, our findings support a model in which Cdk1/PP2A-dependent (de)phosphorylation modulates the stability of E2F7 and E2F8, thereby fine-tuning E2F1 activity and cell-cycle progression.

Point 2. Minor: All optional: It would have been interesting to see the T20A/T44A/KM in the live cell experiment (Figure 3F).

This is an excellent point. Following Reviewer #2’s request, we generated a stable cell line expressing a KEN-box mutant variant of E2F8-T20A/T44A (N80 fragment). The figure below demonstrates the impact of the KEN-box mutation on the dynamics of N80-E2F8-T20A/T44A in HeLa cells. Together, our data from both cellular and cell-free systems show that the temporal dynamics of both wild-type and non-phosphorylatable variants of E2F8 depends on the KEN degron. Please note that due to differences in the flow cytometer settings used for acquiring the original measurements and those newly generated at the Reviewer’s request, the numeric data for N80-E2F8-T20A/T44A-KEN mutant will not be integrated into the original plots shown in the original Figure 3c–e in the manuscript.

Figure legend: Dynamics of mutant variants of N80-E2F8-EGFP in HeLa cells.

Top: Bivariate plots showing DNA content (DAPI) vs. EGFP fluorescence, with G1/G1-S phases and G2/M phases highlighted (black and gray frames, respectively). Bottom: Histograms showing EGFP signal distributions within these cell cycle phases. Blue arrows highlight subpopulations of G2/M cells with relatively low EGFP levels. The data was generated by flow cytometry.

Point 3. Figure 4C-D - include the corresponding blots for the WT E2F7.

This is a good point, which we previously overlooked. The requested data will be integrated in the revised manuscript.

Point 4. It is unclear how selective or potent the PP2A inhibitors are that are used in Figure 5. Is it possible to include known targets of PP2A (positive controls for PP2A inhibition) in the analysis performed in Figure 5?

Thank you for this helpful suggestion. Following Reviewer #2’s comment, we performed gel-shift assays of Cdc20 and C-terminal fragment of KIF4 (Residues: 732-1232), both known targets of PP2A (PMIDs: 26811472; 27453045). See data below.

__Figure legend: PP2A inhibitor LB-100 block protein dephosphorylation in G1-like extracts. __

Time-dependent gel shifts of mitotically phosphorylated Cdc20 and the C-terminal fragment of KIF4 (residues 732–1232) following incubation in G1 extracts supplemented with LB-100 or okadaic acid (OA; positive control). Substrates (IVT, 35S-labeled) were resolved by PhosTag SDS–PAGE and autoradiography.

Point 5. Is the APC still active in LB-100 or OA treated conditions? Is it possible to demonstrate the APC is active using known substrates in this assay (e.g., Securin (Cdc20) and Geminin (Cdh1) or similar).

This is an excellent point and we should have clarified this previously. Importantly, treatment with 250 µM LB-100 does not abolish APC/C-mediated degradation (otherwise, the assay would not be viable), but it does attenuate degradation kinetics. This is reflected by the prolonged half-lives of Securin and Geminin relative to mock-treated extracts (see below). Consistently, we noted in the manuscript: “Although APC/C-mediated degradation is also affected, it remains efficient, allowing us to measure relative half-lives of APC/C targets that cannot undergo PP2A-mediated dephosphorylation.” Following this comment, and one by Reviewer #3, these data are included in the revised manuscript.

__Figure legend: APC/C-specific activity in cell extracts treated with LB-100. __

Time-dependent degradation of EGFP–Geminin (N-terminal fragment of 110 amino acids) and Securin in extracts supplemented with LB-100 and/or UbcH10 (recombinant). A control reaction contained dominant-negative (DN) UbcH10. Proteins (IVT, 35S-labeled) were resolved by SDS-PAGE and autoradiography.

Reviewer #2 (Significance (Required)): Advance: A detailed analysis is provided for the critical N-terminal residues in E2F7 and E2F8 that when phosphorylated are capable of restricting APC destruction. The work builds on prior work that had identified the APC regulation of E2F7 and E2F8.

Point 6. Audience: The manuscript would certainly appeal to a broad basic research audience that is interested in the regulation of APC substrates and/or E2F axis control via E2F7 & E2F8. The study could have a broader interest if the destruction of E2F7 or E2F8 could be shown to be biologically relevant (e.g., critical for cell fate decision G1 vs G0, G1 length, timely S-phase onset, or expression of E2F1 target genes in the subsequent cell cycle).

To clarify, we subdivided Reviewers’ comments into separate points. Reviewer #2’s Points 1 and 6 address essentially the same issue; our detailed response is therefore provided under Point 1. We again thank Reviewer #2 for raising this concern, which led to substantial revisions to both the manuscript text and the supporting data.

We thank Reviewer #2 for their constructive comments and criticism.

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

This manuscript presents a well-structured study on the regulatory interplay between Cdk and Phosphatase in controlling the degradation of atypical E2Fs, E2F7 and E2F8. The work is relevant in the field of cell cycle regulation and provides new mechanistic insights into how phosphorylation and dephosphorylation govern APC/C-mediated degradation. The use of complementary cell-based and in vitro approaches strengthens the study, and the findings have significant implications for understanding the timing of transcriptional regulation in cell cycle progression.

Point 1. However, several points in this paper require further clarification for it to have a meaningful impact on the research community. The characterization of the phosphatase is unclear to me. The use of OA is necessary to guide the research, but it is not precise enough to rule out PP1 and then identify which PP2A is involved - PP2A-B55 or PP2A-B56. To clarify this, the regulatory subunits should either be eliminated or inhibited using the inhibitors developed by Jakob Nilsson's team.

We are grateful for this comment, which prompted an extensive series of experiments that have undoubtedly strengthened our manuscript.

First, we wish to clarify that LB-100, unlike okadaic acid (OA), is not considered a PP1 inhibitor.

Second, we have conducted a large set of experiments to address this important question of the strict identity of the phosphatase involved in the dephosphorylation of atypical E2Fs.

I. We initially attempted to immunodeplete the catalytic subunit of PP2A (α) from G1 extracts as a means to validate PP2A-dependent dephosphorylation. In retrospect, this was a naïve approach given the protein’s high abundance; although immunoprecipitation was successful, immunodepletion was inefficient, preventing us from using this strategy (see Panel a in the figure below). As an alternative, we incubated immunopurified PP2A-Cα with mitotic phosphorylated E2F7 and E2F8 fragments (illustrated in Panel b). A time-dependent gel-shift assay demonstrated enhanced dephosphorylation in the presence of immunopurified PP2A-Cα (Panel c) compared to immunopurified Plk1 (control reaction), suggesting that mitotically phosphorylated E2F7 and E2F8 are targeted by PP2A. This new data is now integrated in Figure 5.

Figure legend: Immunopurified PP2A-Cα facilitates dephosphorylation of E2F7 and E2F8 in cell extracts. a) Inefficient immunodepletion (ID) of the catalytic subunit α of PP2A (PP2A-Cα) from cell extracts despite three rounds of immunopurification, as detected by immunoblotting (IB) with anti-PP2A-Cα and anti-BIP (loading control; LC) antibodies (BD bioscience, Cat#: 610555; Cell Signaling Technology, Cat#: 3177). Briefly, G1 cell extracts were diluted to ~10 mg/mL in a final volume of 65 μL. Anti-PP2A-Cα antibodies (3 μg) were coupled to protein G magnetic DynabeadsTM (15 μL; Novex, Cat#: 10004D) for 20 min at 20 °C. For each depletion round, antibody-coupled beads were incubated with cell extracts for 15 min at 20 °C. Cell extracts and beads were sampled after each step to assess immunodepletion and immunopurification (IP) efficiency. Equivalent immunopurification steps are shown for Plk1 (bottom). b) Schematic of the dephosphorylation assay using mitotically phosphorylated in vitro translated (IVT) targets and immuno-purified PP2A-Cα/Plk1. c) Dephosphorylation of mitotically phosphorylated E2F7 and E2F8 fragments, detected by electrophoretic mobility shifts in Phos-Tag SDS-PAGE. Immunopurified Plk1 was used for control reactions (antibodies: Santa Cruz Biotechnology: Cat#: SC-17783). *Image was altered to improve visualization of mobility shifts.

II. Next, we used pan-B55-specific antibodies for immunodepletion of all B55-type subunits. This approach was unsuccessful despite five rounds of immunopurification (see Panel a in the figure below). Both suboptimal binding and the high abundance of endogenous B55 subunits likely contributed to this outcome. Thus, dephosphorylation in B55-depleted extracts could not be tested.

Figure legend: PP2A-B55 facilitates dephosphorylation of E2F7 and E2F8 fragments.

a) __Immunodepletion (ID) of B55 subunits in G1 extracts is inefficient despite five rounds of immunopurification; assessed by immunoblotting (IB) using anti-pan-B55 and anti-Cdk1 (loading control; LC) antibodies (see previous figure for more details). Cell extracts and beads were sampled after each round to monitor immunodepletion and immunopurification efficiency. b) Schematic of a dephospho-rylation assay using immuno-purified B55 subunits. __c) __Dephosphorylation of mitotically phosphorylated E2F7 and E2F8 fragments by immuno-purified B55. Control reactions performed with immuno-purified Plk1. d) __Schematic of a dephosphorylation assay performed in G1 cell extracts supplemented with B55-interacting (B55i) or control peptides (see peptide sequence on next page). RO-3306 was added to limit Cdk1 activity. __e) __Dephosphorylation of E2F7 and E2F8 fragments (mitotically phosphorylated) in G1 extracts supplemented with B55-interacting/control peptides. __f) __Schematic of the dephosphorylation assay using in vitro–translated B55/B56 subunits (unlabeled). __g) __Dephosphorylation of mitotically phosphorylated E2F7 (top) and E2F8 (bottom) fragments in reticulocyte lysate containing B55/B56 subunits. Dephosphorylation was assessed by electrophoretic mobility shifts in Phos-Tag SDS-PAGE. Panels marked with an asterisk were adjusted to improve visualization of gel-shifts. Arrowheads denote distinct, time-dependent mobility-shifted forms of E2F7 and E2F8 fragments. Antibodies used: anti-pan-B55 (ProteinTech, Cat#: 13123-1-AP); anti-Plk1 (Santa Cruz Biotechnology, Cat#: SC-17783); anti-Cdk1 (Santa Cruz Biotechnology, Cat#: SC-53217). Dynabeads™ (Novex, Cat#: 10004D) were used for immunopurification.

As with PP2A-Cα, we incubated immunoprecipitated B55 subunits with mitotically phosphorylated E2F7 and E2F8 fragments (illustrated in Panel b). The results were less definitive compared to PP2A-Cα; nevertheless, they demonstrated accelerated dephosphorylation in the presence of immunopurified B55 subunits (Panel c) relative to Plk1 (control). These results hint at B55-mediated dephosphorylation of E2F7 and E2F8.

III. Given that PP2A-B55 could be immunodepleted satisfactorily, despite successful immunoprecipitation, we ordered the B55-specific peptide and corresponding control peptide reported recently by Jakob Nilsson’s team as PP2A-B55 inhibitors (see below).

Figure legend: Adapted from Kruse, T., et al., 2024; ____Science Advances. Figure 3, Panel B. ____PMID: 39356758.

Despite our long-anticipated wait for these peptides to arrive, this line of experimentation proved disappointing. We wish to elaborate:

The study by Kruse et al. (PMID: 39356758) is an elegant integration of classical enzymology, performed at the highest level, with structural insight into the conserved PP2A-B55 binding pocket that governs substrate specificity. Their work identified a consensus peptide that binds PP2A-B55 specifically with nanomolar affinity.

Kruse et al. provide compelling evidence for a direct and specific interaction between their reported B55 inhibitor (B55i) and PP2A-B55. Their data show that the engineered inhibitor disrupts the binding of helical elements that underlie substrate recognition by PP2A-B55.

However, we could not find direct evidence of PP2A-B55 enzymatic inhibition by the B55i peptide; for example, a B55-specific in vitro dephosphorylation assay demonstrating sensitivity to B55i in a dose-dependent manner. To the best of our understanding, the sole functional consequence described by Kruse et al. was the delay in mitotic exit observed upon expression of YFP-tagged B55i peptides in cells. However, this approach is indirect, given the long interval between cell manipulation and analysis and the complexity of mitotic exit. Furthermore, we assumed that the requested reagents had been validated in cell-free extracts; however, Kruse et al. do not report any experiments performed in these systems. We, in fact, became uncertain whether we had correctly understood Reviewer #3’s request to use these reagents and therefore sought clarification from the Editor.

In vitro, Kruse et al. reported nanomolar binding affinities for B55i (Figure S14). In our cell extracts, however, we required concentrations of approximately 250 μM to detect an effect on dephosphorylation, evident as altered electrophoretic mobility of both E2F7 and E2F8 (Panel e). At this concentration, the peptide also caused nonspecific effects, rendering the extracts highly viscous (‘gooey’), at times preventing part of the reaction mixture from passing through a 10 μL pipette tip.

The gel-shift assays shown in Panel e (Page 16) do demonstrate delayed dephosphorylation in extracts treated with the B55i peptide relative to the control peptide. Nevertheless, we prefer to exclude these data because the peptide concentrations required for the assay compromised extract integrity. Moreover, we believe that the PP2A-B55–specific peptide described by Nilsson et al. requires additional validation before it can be considered a reliable functional inhibitor in cell-free systems or in vivo. Accordingly, we are unable to directly address the experiments as suggested.

IV. In the final set of experiments (Page 16, Panels f and g), we supplemented dephosphorylation reactions with in vitro–translated B55/B56 subunits (illustrated in Panel f). Although the expected concentration of in vitro–translated proteins in reticulocyte lysate is relatively low (100–400 nM), we reasoned that supplementing the reactions with excess of regulatory B subunits (non-radioactive) could still promote dephosphorylation in a differential manner that reflects the B55/B56 preference of E2F7 and E2F8.

We cloned and in vitro expressed all nine B55/B56 regulatory subunits. While the exact amount of each subunit introduced into the reaction cannot be precisely determined, their expression levels were reasonably uniform (see figure below).

__Figure legend: Expression of B55/B56 subunits in reticulocyte lysate. __B55/B56 subunits were cloned into the pCS2 vector and expressed in reticulocyte lysate supplemented with ³⁵S-Methionin. Proteins were resolved by SDS–PAGE and autoradiography.

Returning to Panel g (Page 16), B55 subunits facilitated the accumulation of lower–electrophoretic mobility forms of both E2F7 and E2F8 fragments to the greatest extent. This is evident from the distinct lower–mobility species that emerge over time (marked by arrowheads) and the smear intensity corresponding to the buildup of dephosphorylated forms. Among the tested subunits, B55β exerted the strongest effect on both substrates, suggesting that mitotically phosphorylated E2F7 and E2F8 display a heightened preference for the PP2A-B55β holoenzyme. Control reactions with reticulocyte lysate are also shown.

Taken together, our original and newly added data indicate that PP2A, specifically PP2A-B55, counteracts Cdk1-dependent phosphorylation during mitotic exit. Importantly, cell cycle regulators such as Cdc20 can be targeted by both PP2A-B55 and PP2A-B56 holoenzymes. Thus, while we are confident in concluding that mitotically phosphorylated E2F7 and E2F8 are targeted by PP2A-B55, we cannot rule out the possibility of functional interactions between E2F7/E2F8 and PP2A-B56.

Point 2. It would also be valuable for this study to investigate the mechanisms underlying this regulation. In particular, is it exclusive to E2F7-8 or could other substrates contribute to the generalisation of this regulatory process?

Assuming Reviewer #3 is referring to the cell cycle mechanism regulating E2F7 and E2F8 half-life via conditional degrons, we wish to clarify that the temporal dynamics of APC/C targets regulated by dephosphorylation has been demonstrated previously. Examples include KIFC1, CDC6, and Aurora A (PMIDs: 24510915; 16153703; 12208850, respectively).

Point 3. The observation that Cdc20 may target E2F8 is interesting but needs to be further clarified to ensure that weak Cdh1 activity does not contribute to this degradation. Elimination of Cdc20 would be necessary to support the authors' conclusion.

We gratefully acknowledge this input. The newly implemented experiment and corresponding findings are presented on the next page. The immunodepletion (ID) procedure (Panel a) achieved >60% reduction of Cdc20 and Plk1 in mitotic extracts (Panel b), as confirmed by immunoblotting (IB). Plk1-depleted extracts were used to validate extract-specific activity after successive rounds of immunodepletion at 20°C. Bead-bound Cdc20 and Plk1 were also analyzed by IB for validation (Panel b, right).

As expected, the phospho-mimetic E2F8 fragment (T20D/T44D) remained stable in Plk1- and Cdc20-depleted mitotic extracts, serving as negative control (Panel c). In contrast, degradation of the non-phosphorylatable variant (T20A/T44A), as well as the APC/CCdc20 substrate Securin (positive control), was strongly hampered in Cdc20-depleted extracts compared to Plk1-depleted extracts. These results confirm that the untimely degradation of the non-phosphorylatable E2F8 in mitotic extracts is Cdc20-dependent. These new data are presented in Figure S3 of the revised manuscript.

Figure legend: Untimely degradation of the non-phosphorylatable E2F8 in mitotic extracts is Cdc20-dependent.____a) Schematic of the immunodepletion (ID) protocol; additional technical details are provided below. b) Plk1 (top) and Cdc20 (bottom) levels in NDB mitotic extracts before and after three rounds of immunodepletion, as detected by immunoblotting (IB). Plk1 and Cdc20 levels were normalized to Tubulin and Cdk1, respectively. Both normalized and raw values are presented as percentages. Immunoprecipitation (IP) efficiency is shown on the right. c) Degradation profiles of phospho-mutant E2F8 variants and Securin (positive control) in NDB mitotic extracts depleted of Plk1 (control) or Cdc20.

__ ---__

Point 4. This study focuses on two proteins of the E2F family. These two proteins share similar domains, phosphorylation sites and a KEN box. However, their sensitivity to APC is different. What might explain this difference? Are there any inhibitory sequences for E2F7? Or why is the KEN box functional in E2F8 but not in E2F7?

This is an excellent question. Here are our thoughts: The processivity of polyubiquitination by the APC/C varies between substrates in ways that influence degradation rate and timing (PMID: 16413484). Although E2F7 and E2F8 are related, their sequence identity is below

50%, and their C-terminal domains differ substantially (see below) [FIGURE]. These structural differences likely contribute to differences in APC/C-mediated processivity and, consequently, to variations in protein half-lives. Additionally, E2F8 contains two functional KEN-boxes involved in its degradation, whereas E2F7 has only one. This may increase the kon rate of E2F8 for the APC/C, further enhancing its recognition and ubiquitination. Furthermore, re-examining the study by de Bruin and Westendorp (PMID: 26882548, Figure 2f; copied below), we note that the dynamic of inducibly expressed EGFP-tagged E2F7 in cells exiting mitosis is milder compared to E2F8 (see the black lines in both charts). This, as well as the oversensitivity of E2F7 degradation to Cdh1 downregulation accord with E2F7 being less potent substrate of APC/CCdh1.

Figure legend: Adapted from Boekhout et al., 2016; ____EMBO Reports. Figure 2, Panel F. ____PMID: 26882548.

The stability of the E2F7 fragment in cells and extracts was unexpected. We initially hypothesized that the unique N-terminal tail of E2F7 masks the KEN-box, functioning as an inhibitory sequence. However, removal of this region did not restore degradation (original manuscript; Figure 1e). Furthermore, extending the fragment by 20 additional residues failed to confer degradation (original manuscript; Figure S2). These observations suggest that E2F7 may require a distal or modular docking site for APC/C recognition. We did not pursue this question further.

Point 5. An additional element that could strengthen this work would be referencing the study by Catherine Lindon: J Cell Biol, 2004 Jan 19;164(2):233-241. doi: 10.1083/jcb.200309035. In Figure 1 of this article, there is a degradation kinetics analysis of APC/C complex substrates such as Aurora-A/B, Plk1, cyclin B1, and Cdc20. This could help position the degradation of E2F7/8 relative to known APC/C targets. This can be achieved by synchronizing cells with nocodazole and then removing the drug to allow cells to progress and complete mitosis.

This is an interesting point and one we should have clarified better previously. The temporal dynamics of E2F8 in synchronized HeLa S3 cells, relative to three known APC/C substrates, were reported in our previous study (PMID: 31995441; Figure 1a, copied on the right). Specifically, protein levels were measured for Cyclin B1, Securin, and Kifc1. Unlike Cyclin B1 and Securin, which are targeted by both APC/CCdc20 and APC/CCdh1, Kifc1 is degraded exclusively by APC/CCdh1. Cells were released from a thymidine–nocodazole block.

Following Reviewer #3’s comment, we re-blotted the original HeLa S3 synchronous extracts. The new data [FIGURE] can be incorporated into the revised manuscript if requested.

Point 6. Minor points: Does phosphorylation of E2F7-8 proteins alter their NMR profile? This could help understand how phosphorylation/dephosphorylation affects their sensitivity to the APC/C complex.

Excellent suggestion. Indeed, we had originally aimed to include a more extensive set of NMR data in this manuscript. Our goal was to monitor E2F7 and E2F8 fragments in cell extracts and assess structural changes induced by phosphorylation and dephosphorylation during mitosis and mitotic exit. However, purifying the E2F7 fragment proved more challenging than anticipated. In addition, the extract-to-substrate ratio requires further optimization: Substrate concentrations must be high enough for reliable NMR detection, but below levels that would saturate the enzymatic activity in the extracts.

That said, the short answer to the reviewer’s question is Yes: NMR profiles of E2F7 and E2F8 fragment do change following incubation with recombinant Cdk1–Cyclin B1 (see next page). If possible, we wish to exclude these NMR data from the manuscript.

Figure legend: NMR-based monitoring of E2F7 (a-c) and E2F8 (d-f) phosphorylation by Cdk1.

a(d). 15N,1H-HSQC spectrum of E2F7(E2F8) prior to addition of Cdk1. Threonine residues of interest, T45 (T20) conforming to the consensus sequence (followed by a proline), and T84 (T60) lacking the signature sequence are annotated. b(e). Strips from the 3D-HNCACB spectrum used for assigning E2F7(E2F8) residues. Black (green) peaks indicate a correlation with the 13Cα (13Cβ) of the same and previous residues. The chemical shifts assigned to T45 (T20) and T84 (T60) match the expected values for K44(K19) and P83(P59), thereby confirming the assignment. c(f). Top, overlay of subspectra before adding Cdk1 (black) and after 16 h of activity (red) at 298 K. Bottom, change in intensities of the T45/T84 in E2F7 and T20/T60 in E2F8 showing how NMR monitors phosphorylation and distinguishes between various threonine residues.

Point 7. Do these substrates bind to the APC/C complex before degradation? Does E2F7 bind better than E2F8?

We were unable to detect interactions between endogenous E2F7 and E2F8 and the APC/C complex. In general, detecting endogenous E2F8, and especially E2F7, by immunoblotting proved challenging, making co-immunoprecipitation (Co-IP) even more difficult.

However, interactions between EGFP-tagged E2F7 snd E2F8 and Cdh1 have been demonstrated previously (PMID: 26882548, Figure 2e). In contrast, only the N-terminal fragment of E2F8, but not the corresponding fragment of E2F7, was found to bind Cdh1 (see figure on the right). This observation is consistent with the stability of the E2F7 fragment in APC/C-active extracts. These new data are presented in Figure S2 of the revised manuscript.

__Figure legend: N-terminal fragment of E2F8 but not E2F7 binds Cdh1. __

Co-Immunoprecipitation (IP) was performed in HEK293 cells transfected with EGFP-tagged E2F7/E2F8 fragments, using GFP-Trap® (Chromotek, Cat#: GTMA-20). Antibodies used for immunoblotting: ant-GFP (Santa Cruz Biotechnology: Cat#: SC-9996); anti-Cdh1 (Sigma-Aldrich, Cat#: MABT1323).

Point 8. Why do the authors state that 250 µM of LB-100 has little effect on APC/C activity?

We thank Reviewers #2 and 3 for raising this point. As shown in the manuscript, treatment with 250 µM LB-100 does not abolish APC/C-mediated degradation (otherwise, the assay would not be viable). However, it does attenuate degradation kinetics, as reflected by the prolonged half-lives of Securin and Geminin (see figure below and Figure S7 of the revised manuscript).

__Figure legend: APC/C-specific activity in cell extracts treated with LB-100. __

Time-dependent degradation of EGFP–Geminin (N-terminal fragment of 110 amino acids) and Securin in extracts supplemented with LB-100 and/or UbcH10 (recombinant). A control reaction contained dominant-negative (DN) UbcH10. Proteins (IVT, 35S-labeled) were resolved by SDS-PAGE and autoradiography.

Point 9. How can E2F8 be a substrate for both the SCF and APC/C complexes? (If I understood correctly.)

This can happen because they are degraded by different E3 at different times during the cell cycle. To clarify further, certain proteins can be targeted by both the APC/C and SCF complexes, reflecting distinct regulatory needs. A classic example is CDC25A, as shown by M. Pagano and A. Hershko in 2002 (PMID: 12234927). Additional examples include the APC/C inhibitor EMI1 (PMIDs: 12791267 [SCF] and 29875408 [APC/C]).

Reviewer #3 (Significance (Required)): This manuscript presents a well-structured study on the regulatory interplay between Cdk and Phosphatase in controlling the degradation of atypical E2Fs, E2F7 and E2F8. The work is relevant in the field of cell cycle regulation and provides new mechanistic insights into how phosphorylation and dephosphorylation govern APC/C-mediated degradation. The use of complementary cell-based and in vitro approaches strengthens the study, and the findings have significant implications for understanding the timing of transcriptional regulation in cell cycle progression.

We wish to thank Reviewer #3 for their positive and encouraging view of our work.

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

This manuscript presents a well-structured study on the regulatory interplay between Cdk and Phosphatase in controlling the degradation of atypical E2Fs, E2F7 and E2F8. The work is relevant in the field of cell cycle regulation and provides new mechanistic insights into how phosphorylation and dephosphorylation govern APC/C-mediated degradation. The use of complementary cell-based and in vitro approaches strengthens the study, and the findings have significant implications for understanding the timing of transcriptional regulation in cell cycle progression.

• However, several points in this paper require further clarification for it to have a meaningful impact on the research community. The characterization of the phosphatase is unclear to me. The use of OA is necessary to guide the research, but it is not precise enough to rule out PP1 and then identify which PP2A is involved - PP2A-B55 or PP2A-B56. To clarify this, the regulatory subunits should either be eliminated or inhibited using the inhibitors developed by Jakob Nilsson's team. It would also be valuable for this study to investigate the mechanisms underlying this regulation. In particular, is it exclusive to E2F7-8 or could other substrates contribute to the generalisation of this regulatory process?

• The observation that Cdc20 may target E2F8 is interesting, but needs to be further clarified to ensure that weak Cdh1 activity does not contribute to this degradation. Elimination of Cdc20 would be necessary to support the authors' conclusion.

• This study focuses on two proteins of the E2F family. These two proteins share similar domains, phosphorylation sites and a KEN box. However, their sensitivity to APC is different. What might explain this difference? Are there any inhibitory sequences for E2F7? Or why is the KEN box functional in E2F8 but not in E2F7?

• An additional element that could strengthen this work would be referencing the study by Catherine Lindon: J Cell Biol, 2004 Jan 19;164(2):233-241. doi: 10.1083/jcb.200309035. In Figure 1 of this article, there is a degradation kinetics analysis of APC/C complex substrates such as Aurora-A/B, Plk1, cyclin B1, and Cdc20. This could help position the degradation of E2F7/8 relative to known APC/C targets. This can be achieved by synchronizing cells with nocodazole and then removing the drug to allow cells to progress and complete mitosis.

Minor points:

• Does phosphorylation of E2F7-8 proteins alter their NMR profile? This could help understand how phosphorylation/dephosphorylation affects their sensitivity to the APC/C complex.

• Do these substrates bind to the APC/C complex before degradation? Does E2F7 bind better than E2F8?

• Why do the authors state that 250 µM of LB-100 has little effect on APC/C activity?

• How can E2F8 be a substrate for both the SCF and APC/C complexes? (If I understood correctly.)

Significance

This manuscript presents a well-structured study on the regulatory interplay between Cdk and Phosphatase in controlling the degradation of atypical E2Fs, E2F7 and E2F8. The work is relevant in the field of cell cycle regulation and provides new mechanistic insights into how phosphorylation and dephosphorylation govern APC/C-mediated degradation. The use of complementary cell-based and in vitro approaches strengthens the study, and the findings have significant implications for understanding the timing of transcriptional regulation in cell cycle progression.

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

Learn more at Review Commons

Referee #2

Evidence, reproducibility and clarity

Summary:

The authors provide strong biochemical evidence that the regulation of E2F7 and E2F8 by APC is affected by CDK1 phosphorylation and potentially by PP2A dependent dephosphorylation. The authors use both full length and N-terminal fragments of E2F8 in cell-free systems to monitor protein stability during mitotic exit. The detailed investigation of the critical residues in the N-terminal domain of E2F8 (T20/T44) is well supported by the combination of biochemical and cell biology approaches.

Major:

It is unclear how critical the APC-dependent destruction of E2F7 and E2F8 is for cell cycle progression or other cellular processes. Prior studies have reported that Cyclin F regulation of E2F7 is critical for DNA repair and G2-phase progression. This study would be improved if the authors could provide a cellular phenotype caused by the lack of APC dependent regulation of E2F8 and/or E2F7.

Minor:

All optional: It would have been interesting to see the T20A/T44A/KM in the live cell experiment (Figure 3F). Figure 4C-D - include the corresponding blots for the WT E2F7. It is unclear how selective or potent the PP2A inhibitors are that are used in Figure 5. Is it possible to include known targets of PP2A (positive controls for PP2A inhibition) in the analysis performed in Figure 5? Is the APC still active in LB-100 or OA treated conditions? Is it possible to demonstrate the APC is active using known substrates in this assay (e.g., Securin (Cdc20) and Geminin (Cdh1) or similar).

Significance

Advance: A detailed analysis is provided for the critical N-terminal residues in E2F7 and E2F8 that when phosphorylated are capable of restricting APC destruction. The work builds on prior work that had identified the APC regulation of E2F7 and E2F8.

Audience: The manuscript would certainly appeal to a broad basic research audience that is interested in the regulation of APC substrates and/or E2F axis control via E2F7 & E2F8. The study could have a broader interest if the destruction of E2F7 or E2F8 could be shown to be biologically relevant (e.g., critical for cell fate decision G1 vs G0, G1 length, timely S-phase onset, or expression of E2F1 target genes in the subsequent cell cycle).

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Referee #1

Evidence, reproducibility and clarity

The study highlights a dephosphorylation switch mediated by PP2A as a critical mechanism for coupling E2F7/8 degradation to mitotic exit and G1 phase. The study is clear and experiments are well conducted with appropriate controls

I have some concerns highlighted below :

1. In this sentence : This intricate network of feedback mechanisms ensures the orderly progression of the cell cycle. What feedback mechanism are the authors referring to?

2. Characterization of disorder in the N-terminal segments of E2F7 and E2F8

What does it mean disorder in this title?

1. In the paragraph on the untimely degradation of E2F8 the authors keep referring to APC/C Cdc20, however the degradation is triggered by the Ken box which is specifically recognised by APC/C Cdh1. Can it be due to another ligase not APC/C?

2. The assays to detect dephosphorylation are rather indirect so it is difficult to establish whether phosphorylation of CDK1 and dephosphorylation by PP2A on the fragments is direct.

3. Although there seems to be a control by phosphorylation and dephosphorylation (which could be indirect), it is difficult to establish the functional consequences of this observation. The authors propose a feedback mechanism which regulates the temporal activation inactivation of E2F7/8 however, there are no evidence in support of this.

Significance

The study is a good and well conducted work to understand the mechanisms regulating degradation of E2F7/8 by APC/C. This is crucial to establish coordinated celll cycle progression. While the hypothesis that disruption of this mechanism is likely responsible for altered cell cycle progression, there are no evidence this is just a back up pathway, whose functional significance could be limited to lack of APC/C Cdh1 activity. These experiments are rather difficult but the authors could comment on the limitation of the study and emphasise the hypothetical alterations which could result from the alterations of the described feedback loop

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

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Referee #3

Evidence, reproducibility and clarity

Summary

The authors observe that proteasomal protein and activity is increased in skeletal muscle of mice fed a high fat diet. Concordant with this, they find increased expression of Nfe2l1 (NRF1), an ER localized protein that can be cleaved to produce a transcription factor that activates a set of genes that includes most proteasome subunits. To test the role of Nfe2l1 in the response to high fat feeding, the authors generated muscle specific KO of Nfe2l1 and characterized the muscles using fiber typing, proteomic, ubiquitinomic, RNAseq and metabolomic analysis on the muscle of these mice. Gastrocnemius muscle fast twitch fibers appeared most affected and modulated towards slow twitch phenotype, whilst soleus muscle appeared unaffected. Mitochondrial function was decreased as were levels of complex III. Ubiquitinome analysis showed differential ubiquitination of proteins involved in muscle structure and function and increased K48 ubiquitin chain linkages. Metabolomic studies showed altered amino acid metabolism, glucose metabolism and induction of a Warburg effect. Finally, upon high fat feeding, the Nfe2l1 mKO mice gained less weight, had higher energy expenditure, and were more insulin sensitive.

Major comments

1. The authors have conducted a multi-omics analysis of the skeletal muscle of mice bearing a muscle specific KO of Nfe2l1 and have attempted to integrate the findings. However, despite reading the manuscript several times, I have trouble trying to identify the key message of the paper and so feel that a lot of data was presented, but without a clear sense of how all the data (or some of it) really ties together. I suggest that the authors identify the main message, select the relevant data for the main body of the text and assign the remaining data to supplementary figures. The discussion should emphasize the main message.
2. Metabolically, the most impressive result was the minimal weight gain on high fat feeding. The authors vaguely suggest that Nfe2l1 might be a therapeutic target 'to preserve muscle mass and healthy metabolism in obesity and beyond'. Since the main effect of Nfe2l1 seemed to be downregulation of the proteasome, should the authors have tested the effects of low dose proteasome inhibitors in WT mice to mimic the partial loss of proteasome activity seen in the Nfe2l1 mKO on the response to high fat feeding? This could confirm or support the idea that the main effect is due to Nfe2l1 modulation of the proteasome.
3. The authors claim that there is rewiring of the UPS in obesity through the induction of Nfe2l1. What do the authors mean by rewiring? If the main effect of Nfe2l1 is to modulate proteasome activity, presumably all upstream processes (ubiquitination by various E3s) are affected. Indeed, in the ubiquitinomic analysis in figure 4F, there do not appear any pathways that are downregulated. Regardless, there is no data presented to show that specific pathways of ubiquitination are altered and therefore 'rewired'. The 'rewiring' strikes me as a fancy term used inappropriately here.
4. I was surprised that the authors did not use the tamoxifen inducible Cre to inactivate Nfe2l1 in adult muscle. As such, the interpretation of the results of their study is limited by the effects of loss of Nfe2l1 during development and so inhibit to some degree potential links to translation. The authors should note this limitation in their discussion.
5. Relevant to the above point about KO from development, in the first characterization of the mKO of Nfe2l1, (Figures 2G, 2I) the muscles actually look dystrophic. There appear to be central nuclei in the muscle of the mKO in Fig 2G and sarcomeric dysorganization in Fig 2I and the authors mention the presence of inflammatory cytokines and regenerative isoforms (Fig 2H) in the muscle. Are the mKO dystrophic, undergoing damage and regeneration? This is an important point to address with quantification of central nuclei, inflammatory cytokine expression, infiltration by mononuclear cells, fibrosis, blood levels of creatine kinase.

Minor comments

1. Abstract - the authors used the fancy term 'hormetic'. My understanding is that this refers to a phenomenon where effects at low dose (usually positive) are different or opposite from effects at high dose (usually negative). I didn't see such a biphasic phenomenon in the Nfe2li mKO mice. Also the authors should specify that it is a muscle specific KO.
2. Text on page 3 'In human muscle, we noted that NFE2L1 is highly expressed, at much higher levels compared to other established muscle regulators, such as NFE2L2 or PPARGC1A (Fig. 1K)'. Discerning the importance of a transcription factor by comparing its expression at the mRNA level is dubious. It is the protein that acts and the extent of gene transcriptional activity that is important.
3. Figure 2A-C - The mKO mice are smaller and have less lean mass and fat mass. Were the mKO mice born with smaller muscles and therefore had trouble feeding or competing for breast milk prior to weaning? This again relates to the issue of not having used a tamoxifen inducible KO. Are the muscle sizes proportionate to body weight or more importantly body length or tibial length?
4. Figure 2G - As mentioned in general comment 5, the mKO muscle looks dystrophic. Also the % fibers of each type should be quantified to demonstrate the fiber type shifting. This should ideally be done in the complex zone of the gastrocnemius where all the fiber types are present. Also, the fibers look bigger in the mKO. It is standard to do an analysis of the distribution of cross-sectional areas of the muscle fibers and this can be done in a fiber specific manner from the stained images in the middle panels (with laminin staining added to delineate the fibers).
5. Figure 2J - remarkably complex III (cytochrome C reductase) levels are significantly decreased. Any explanation for this? Does Nf2el1 bind to the promoter or regulate its transcription?
6. Figure 2H - state in legend whether the 'relative expression levels' are for protein or for mRNA.
7. Figure 3C, 3G - why does the trypsin-like activity of the proteasome go up when the other 2 activities of the proteasome go down?
8. Figure 4E - Why is there a set of proteasome genes that are upregulated in the mKO? Most of these (except Psmd9/Rnp4) encode subunits of the PA28 activator. Is this a compensatory response or a response to inflammation in the dystrophic muscle? This needs some comment in the paper.
9. Figure 5D, text page 8 - 'we found several genes to be oppositely regulated between soleus and GC'. What genes were these and are they enriched in a particular pathway e.g. one that modulates fiber type phenotype?
10. Figure 6D, 6E - The increased energy expenditure and increased food intake may simply be due to increased heat loss from the smaller mKO mice (they have a relatively larger body surface area).
11. Figures 7A, 7B - Was the body composition different in the mKO mice fed a high fat diet vis WT HFD mice?
12. Figure 7E - What is the insulin tolerance like when normalized to starting glucose?
13. Discussion - Please insert figure numbers in the discussion so reader can refer back to the data on which the conclusions in the discussion are being made.
14. Figure 1G and Discussion first paragraph - It would be more quantitatively precise to measure the ubiquitinated proteins by western blot (as done in Fig 3I) than to sum up the ubiquitin linkages.
15. Discussion para 2, ref 26. This reference is to a paper on effects of lipid peroxidation on muscle atrophy in aging or disuse and not to obesity. Revise to be more precise.
16. Discussion page 12 last para - 'some components of the proteasome'. As mentioned earlier, these appear to be mostly subunits of the PA28 proteasome activator. Should state this and discuss.
17. Discussion page 13, para 3 and extended data Fig 2A-2D. What is the significance of the higher FGF21 and GDF15 expression in mKO muscle? Could they be involved in the improved glucose tolerance or the decreased fat mass respectively?
18. Methods section 2.8 - many abbreviations for reagents that are not defined e.g. SDC, CAA, TCEP, etc
19. Methods 2.11 - the authors did whole muscle proteomics and ubiquitinomics which they recognized would be limited by the overwhelming representation by myofibrillar proteins. Did they try any manoeuvres to enhance detection of non-myofibrillar proteins?
20. Methods, section 2.13 - the mitochondria were quantified by protein assay. Since the 8000g pellet used to isolate the mitochondria may contain other proteins, should the mitochondria be quantified in a more specific way e.g. assaying several mitochondrial proteins or measuring mitochondria DNA content? This is important vis a vis figure 2L which showed decreased mitochondrial respiration in the mKO.
21. Extended data Fig 1D. Were these measures of markers of atrophy done at the protein level or mRNA level? They should be done at the mRNA level as this is a more sensitive and precise marker of atrophy than the protein levels (which don't change as much and for which many antibodies are not specific).
22. There is a lot of useful omics data here. Where will they be shared for use by the research community?

Referees cross-commenting

The overall tenor of the three reviews is similar. Comments are both overlapping and complementary. I realize that I forgot two other specific comments:

• (a) In extended fig 1C, the authors quantify the slower migrating LC3B-I band, but it is the faster migrating lipidated LC3B-II band that is a marker of autophagasomes that should have been quantified.
• (b) Some references e.g. 37, 40 are missing information.

Significance

The authors have carried out what appears to be a thorough multi-level omics study of a muscle specific KO of Nfe2l1. It appears to have been technically well done, but I do not have expertise in such analyses and so cannot be rigorously critical in this aspect. (My expertise is in UPS function in skeletal muscle.) The major limitations of the present manuscript are highlighted in my major comments.

In view of the important role of Nfe2l1 in regulation of expression of the proteasome, the muscle specific KO provided a partial inhibition of proteasome activity and therefore a unique view into the role of the proteasome in muscle particularly under the condition of high fat feeding. Therefore, the potential audience could be quite broad including researchers in muscle biology, UPS and obesity. However, Nfe2l1 has other effects besides induction of expression of proteasome genes, thereby limiting the confidence that all effects observed are related to the modulation of the proteasome and the consequences of such modulation on levels of UPS substrates

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Referee #2

Evidence, reproducibility and clarity

In this paper, Lemmer and colleagues explore the role of the endoplasmic reticulum (ER)-resident transcription factor Nfe2l1 in muscle metabolism in mice following high-fat diet (HFD). Here, the authors made the interesting observation that HFD is associated with increased proteasome activity in skeletal muscles (Fig.1), a process known to rely on Nfe2l1 and confirmed by Figs. 2 and 3. By using a tissue-specific Nfe2l1 knockout (KO) mouse model, the authors show that Nfe2l1 is also critical in preserving mitochondria and oxidative phosphorylation in muscles during HFD (Figs. 4, 5 and 6). Finally, the authors show that fast/glycolytic muscle fiber growth in Nfe2l1 KO mice is accompanied by reduced body weight and improved glucose tolerance (Fig. 7).

This paper is potentially interesting and addresses the important issue of energy metabolism regulation in diet-induced obesity (DIO) using an original mouse model. However, the argument presented in this paper has sometimes logical gaps, making it difficult for the reader to connect all the dots. For instance, what is the relationship between proteasome function and energy metabolism in DIO? Is there any relationship at all? Ultimately, Nfe2l1 has other target genes than the proteasome ones, particularly those related to mitophagy process (PMID: 30135079, this paper should be cited and discussed) which could easily explain the observations made by the authors regarding respiration and metabolism...

1. The authors failed to explain why muscle cells upregulate their proteasomes during HFD. My prediction is that this happening because of increased protein synthesis which itself occurs as a consequence of sustained mTOR signaling. Increased translation would then result in increased supply of defective ribosomal products (DRiPs) which need to be timely cleared by the ubiquitin-proteasome system (UPS). I leave to the authors the possibility to address this hypothesis experimentally.
2. The authors consistently show a correlation between HFD and increased Nfe2l1 expression. These observations, however, do not imply that Nfe2l1 is activated in DIO. The authors should assess Nfe2l1 processing - or at least nuclear translocation - in muscles over time
3. If Nfe2l1 is indeed activated by HFD, what would be the stimulus? Compromised proteasome function? Oxidative stress? Cholesterol changes? This point needs to be clarified.
4. Fig. 1C: the increased proteasome subunit expression in DIO seems minuscule... How about Western-blotting the native gel for proteasome subunits to check whether the observed proteasome activity matches the proteasomes amounts under these conditions?
5. Fig. 2J: a densitometry quantification of the WB would be welcome.
6. Fig. 2K. captions are incomplete. What is PMG, SUC or FCCP?
7. Discussion:" Furthermore, we found that some components of proteasome activity are higher in cells or tissues lacking Nfe2l1, indicating a potential compensatory posttranslational modification of proteasome function." What components?? Is it shown in the manuscript? Unclear.
8. Discussion: Next to changes in total amount and activity, we also found that proteasome subunits accumulated in a hyperubiquitylated state (Extended Data Fig. 1A), but the relevance of this observation will need further investigation. These proteasome subunits are not assembled ones, but likely derive from DRiPs, as a consequence of increased translation (see point 1).
9. Discussion: "Clearly, disturbances in UPS and ERAD cause ER stress and inflammation (10), which we also observe in our model." Where are the data in this regard? Do the authors mean Fig. 5B? I do not see any convincing data on inflammation here (BTW, what is Gm11517?).

Significance

General assessment:

As previously discussed, this work from Bartel's lab is interesting but not suitable for publication in its present form. It should be revised to clarify the role of Nfe2l1-induced proteasomes in DIO.

Advance

Although the role of Nfe2l in mitochondrial function is known (PMID: 30135079, this paper should be cited and discussed), the consequences on energy metabolism in skeletal muscles described in this paper are novel.

Audience

If appropriately revised, this manuscript should be of interest to a wide readership.

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Referee #1

Evidence, reproducibility and clarity

Summary:

In the manuscript entitled "Nfe2l1-mediated proteasome function controls muscle energy metabolism in obesity", Lemmer and colleagues observe elevated 20S proteasome activity along with increased expression of the transcription factor Nfe2l1, a known stimulator of proteasome subunit biogenesis, in muscle tissue of diet-induced obese mice. To understand the role of Nfe2l1 in regulating skeletal muscle proteostasis, they use siRNA to knockdown Nfe2l1 in cultured C2C12 muscle cells and cross Nfe2l1 floxed mice with and Acta1-Cre line to KO Nfe2l1 specifically in muscle fibers. Nfe2l1mKO mice show reduced body and muscle size, impaired enzymatic activity of some proteasome subunits, an accumulation of ubiquitylated proteins, a fast-to-slow shift in muscle fiber phenotype and metabolic abnormalities, including impaired mitochondrial function and mild increases in relative energy expenditure. Multi-omics analysis at transcript, protein, ubiquitinated protein and metabolite levels indicate a strong influence of Nfe2l1 loss on muscle homeostasis. These affects appear to predominately affect fast-type (i.e. Gastrocnemius) rather than slow-type (i.e. soleus) muscles. Finally, Nfe2l1mKO mice fail to gain weight on a high fat diet and are therefore spared the typical metabolic alterations associated with obesity.

Major comments:

1. The authors push the idea that the UPS, via Nfe2l1, plays an 'adaptive' role in regulating muscle proteostasis, however, all signaling experiments investigating the effect of muscle fiber Nfe2l1 KO are performed under basal conditions.
2. Due to the use of ACTA1-Cre to conditionally KO Nfe2l1 in muscle fibers, Nfe2l1 is also absent during development. It is therefore difficult to distinguish the acute effects of Nfe2l1 on muscle proteostasis from those that may result from developmental impairment. It is conceivable that remodeling of muscle architecture would be more active during development than in mature muscle and therefore perhaps more sensitive to impairments in proteasome biogenesis. Use of an inducible Cre system (e.g. the tamoxifen inducible HSA-MerCreMer model) and/or the addition of acute Nfe2l1 overexpression experiments would be needed to dissociate acute, primary effects of Nfe2l1 from the secondary features of long term Nfe2l1 KO and disruption of proteostasis.
3. It is unclear what the HFD experiments reported in Figure 7 add to our understanding of the role of Nfe2l1 in skeletal muscle. I could understand if an inducible Nfe2l1mKO system was used to test the role of Nfe2l1 in already obese mice... but a failure of a mouse displaying myopathic features to put on weight is not the same as an alteration that improves metabolic health. As Nfe2l1mKO mice do not become obese, the authors are unable to directly test what role the upregulation of muscle Nfe2l1 plays in maintaining proteostasis in obesity. On the other hand, I find it hard to conclude that the absence of muscle Nfe2l1 is beneficial for metabolic health if fed a HFD, especially given the reported increase in p62 and LC3B (indicative of autophagy impairment) and the impaired muscle mitochondrial function. Further investigations in older mice would be required to determine the long-term impact of muscle Nfe2l1 KO on whole-body health under both normal and high-fat diet feeding conditions.
4. The authors note several interesting muscle phenotypes, including a fast-to-slow fiber type transition and an increased expression of neonatal myosin heavy chain isoforms (Myh3 & 8). The representative images seem to indicate that IIA (green) fibers are larger in Nfe2l1mKO mice. I would recommend quantifying fiber type-specific cross sectional area in Gastrocnemius muscle sections from these mice, as well as confirming the increased 'regeneration' phenotype by quantifying the prevalence of centralized nuclei.
5. Figure 3D: Why would Nfe2l1 KD lead to a larger increase in ubiquitylated proteins after proteasome inhibition? If Nfe2l1 KD reduces proteasome subunit gene expression (presumably also protein content) and proteasome activity (although this effect is rather mild), then blocking a proteasome with lower activity should lead to a lower accumulation of ubiquitylated proteins, despite an accumulation of ubiquitylated proteins under basal conditions.
6. Fig3C&G: The finding that Nfe2l1 KD/KO mildly reduces chymotrypsin-like and caspase-like (in mice) activity, but strongly increases trypsin-like activity is surprising. As these activities are mediated by different Beta subunits within the 20S core particle, it would be important to also test whether protein levels of PSMB5 (Chymotrypsin), PSMB6 (Caspase) and PSMB7 (trypsin) are altered by Nfe2l1 in accordance with differences in their measured activity.
7. The authors have a tendency to use vague terms to describe changes in proteostasis resulting from Nfe2l1 KO, for example: 'recalibration', 'adaptive', 'fine-tuning', 'remolding', 'remodeling', 'rewiring'. While it is understandable that Nfe2l1 and the UPS will have different roles under different conditions, the use of vague language makes it difficult to understand whether they are referring to reduced or increased proteasome activity. Please be clear and precise as the direction of the changes observed. The same goes for the extension of conclusions made on measures of proteasome activity to mean activity of the UPS / protein breakdown. Specific examples are described within the minor comments section.

Minor comments:

Introduction: Nfe2l1 does not restore proteasome activity per se, but stimulates proteasome subunit biogenesis and thereby increases proteasome content. This would not necessarily influence activity, which also relies on the presence of substrate/ubiquitination.

Introduction: 'we investigate remodeling of the muscle UPS in obesity and define the role of Nfe2l1 as a new regulator of muscle biology'. This statement is an overreach, particularly seeing as a role for Nfe2l1 has already been described in skeletal muscle, albeit under a different context (ref. 29).

Results: "Of note, leptin levels in chow-fed animals were indifferent". I guess this is a typo? Should be 'different' not 'indifferent'.

Results: "These global changes are in line with the notion that UPS is activity is rewired and metabolism impacted by HFD feeding." Please use specific language to describe the changes you see.

Results: "The data supported the hypothesis that Nfe2l1 stimulates protein degradation via the proteasome, as the dominant lysine-linkage was the proteasome-targeting linkage K48, accounting for more than 86 % and being significantly higher in muscle of mKO mice compared to tissue of WT controls (Fig. 4G)." While it is clear that depleting a protein contributing to proteasome biogenesis would impair proteasome function, this would not be sufficient to say that Nfe2l1 promotes protein degradation via the proteasome. So far, there is no evidence that increasing Nfe2l1 increases protein degradation.

Figure 1L: What is the unit of measurement for gene expression?

Figure 2G: There appears to be significant freeze damage in H&E and SDH sections from Nfe2l1mKO mice. Perhaps you can find better representative images.

Results: "In summary, these results establish Nfe2l1 as an adaptive regulator of proteasomal activity and ubiquitylation in cultured myocytes". Why do these results establish Nfe2l1 as an 'adaptive' regulator? These are steady state conditions. Results so far would only indicate that Nfe2l1 controls proteasome subunit biogenesis in myocytes, which is well known in other cell types and has also been shown in skeletal muscle tissue.

Results: "The proteome showed many significantly regulated proteins and in general a higher protein load in the mKO condition (Fig. 4A), potentially caused by impaired proteasomal protein degradation." What is meant by a 'higher protein load'

Discussion: "Here, we show that proteasomal activity and management of ubiquitin levels in muscle is a regulated and critical process in obesity, as proteasome levels and function are increased in obesity." This is actually not shown. As Nfe2l1 KO mice do not become obese, it is unclear what role this increase plays under the conditions of obesity.

Discussion: "Interestingly, at the same time, total ubiquitin levels are largely unchanged, which suggests a dynamic recalibration of the rates of protein synthesis and degradation, including the processes necessary for ubiquitylation and its targets". The authors seem to be interpreting ex vivo proteasome activity assays as a readout of protein breakdown rates in vivo. These Proteasome activity assays are only a readout of proteasome content, not activity, since substrate entry into the 26S proteasome is tightly controlled by its cap structure. Ex vivo, substrates able to independently access the inside of the 20S proteasome (and hence the active protease sites) are provided in abundance.

Discussion: "However, overall proteasomal activity was lower and ubiquitin levels higher, indicating the predominant role of Nfe2l1 determining rates of UPS in myocytes." The reduction in activity was not so strong that it could be considered predominant. Furthermore, proof is only provided for Nfe2l1 regulating proteasome content... not rates of UPS breakdown, which also relies on the ubiquitination part of the system.

Discussion: "There seems to be profound crosstalk between proteostatic mechanisms in muscle, as we found in the proteome of Nfe2l1 mKO muscle that autophagy pathways are markedly upregulated, including p62 and LC3B levels (Extended Data Fig. 1B-C)". This should be first introduced into the results section.

Discussion: "Uncoupling of mitochondria and loss of mitochondrial membrane potential in myocytes are associated with the induction of FGF21 (33), a myokine that is implicated in regulating energy metabolism. We find that FGF21 and GDF15 expression were higher in muscle of mKO mice compared to WT controls, and for GDF15 also plasma levels were elevated (Extended Data Fig. 2A-D)." This should be included in results section.

Significance

General assessment: after identifying increased proteasome activity and an associated increase in Nfe2l1 expression in the muscle of obese mice, this work provides strong evidence that muscle fiber Nfe2l1 expression is necessary for muscle fiber development / homeostasis, with wide ranging effects of muscle fiber Nfe2l1 KO, including on body and muscle size, fiber type composition and mitochondrial content and function. On the other hand, muscle fiber Nfe2l1 KO mice fail to become obese, making it hard to draw conclusions on the role of increased Nfe2l1 in the muscle of obese mice.

Advance: This study complements recent work showing a role for increased Nfe2l1 expression in maintaining proteostasis under a different proteostatic challenge, and suggests a role for muscle Nfe2l1 in response to obesity.

Audience: This study is likely to be of interest to readers interested in proteostasis, the UPS and muscle biology.

Expertise: Muscle proteostasis and aging.

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Reply to the reviewers

We thank the reviewers for their careful and constructive evaluation. We believe the requested revisions are feasible will substantially strengthen the manuscript.

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Referee #3

Evidence, reproducibility and clarity

In this manuscript, Halter and colleagues propose a novel approach to sample level analysis of single cell disease atlas by only considering cellular proportion. They perform an evaluation with several SOTA approaches including ones using both pseudo-bulk or combination of compositional and transcriptional changes. While bench-marking results are positive, the design of the study including selected data and evaluated statistics differs from previous studies possibly indicating some bias selections. The paper has also strong statements on the fact their method is not affected by batches, while this is only shown in a single data set and some of the evaluated data has batched samples removed. These results are very likely misleading and authors need to either remove such strong claims or show strong evidence supporting it.

Main points

Authors indicate only samples with 500 cells are included. How would the method work without such a filter? Evaluation should also be done on sparse data, as this might be frequent in single cell studies. Otherwise, tgus should be also discussed as a limitation of the study. Authors should discuss the potential risk of this variance-based thresholding inadvertently filtering out rare, low-variance cell populations that carry critical biological significance. Also, could it be that this filter simply selects condition specific cells (cancer cells in cancer samples?). Regarding the previous concern, it is unclear if this performance retention is unique to ECODA's log-ratio approach. For a fair comparison, the authors should benchmark the competing compositional methods using the exact same HVC subset to determine if the performance advantage stems from the algorithm itself or simply the feature selection. In this case, some methods, such as PILOT, need cell types. To comprehensively demonstrate ECODA's performance, the authors should compare their approach against recently introduced sample-level representation methods. QOT: https://academic.oup.com/bib/article/26/1/bbae713/7953914. Joodaki, M. (n.d.). PILOT-GM-VAE: patient-level analysis of single-cell disease atlas with optimal transport of Gaussian mixture variational autoencoders. Pang, K. (n.d.). PULSAR: a Foundation Model for Multi-scale and Multi-cellular Biology. Regarding the data selection, authors should include all the previous data as in previous studies. See PILOT, PILOT-GM-VEA or QOT for a larger selection of data sets. The current approach uses k-means but some of the evaluated methods are shown to work better with other clustering methods (Leiden) or similarity metrics (Cosine). Authors should improve the benchmarking to also include richer strategies on how to perform clustering and include metrics evaluating the distances directly (silhouette index). Data has very strong filters that remove confounding factors. For example, the authors handle demographic confounders (such as age) in the Gong & Sharma dataset by severely restricting the cohort (males <= 40 years), which limits real-world clinical applicability where cohorts have complex, overlapping covariates. Can ECODA deal with the data sets without any kind of filter on confounding factors?

In the Stephenson dataset, the authors manually restricted the data to a single clinical location ("Ncl site"). If ECODA is as robust to batch effects as claimed, manual exclusion of multi-center data should be unnecessary. The authors should explain why this pre-filtering was required and evaluate if ECODA can accurately stratify patients when all multi-center data is included. Another example of a batch rich data is the KPMP Kidney data, which include multicenter and multi protocols single nuc vs. single cell data. The claim that ECODA is robust to batch effects is currently supported only by ANOSIM scores on two datasets, which is insufficient by current single-cell benchmarking standards. To rigorously demonstrate that ECODA effectively resists batch effects while conserving biological variance, the authors should evaluate their sample-level embeddings by using more data and also utilizing metrics such as Silhouette batch, LISI, and so on (take a look at scvi-tools, https://docs.scvi-tools.org/en/1.3.3/tutorials/notebooks/scrna/harmonization.html). Besides, they need to drop all filters based on clinical variables and include additional data sets as previously discussed.

Referees cross-commenting

Reviewers do focus on distinct but non conflicting aspects, while some similar points regarding benchmarking are quite similar between us and reviewer 2. I would like however to stress the batch correction aspect, which is currently a big statement on the manuscript, but we could capture several design issues with this aspect.

Significance

The discussion on how to analyze single cell data of patients cohorts is of strong significance. Authors make an interesting point that cell frequencies can work well, but the results are clearly biased by data selection and experimental design. The study will have a greater value if authors can tune down most of their claims and instead have a more balanced analysis on when compositional analysis is best and when transcriptional signatures are best. This is likelly to be very study/data dependent.

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Referee #2

Evidence, reproducibility and clarity

This manuscript benchmarks scRNA-seq sample representation methods for unsupervised patient stratification. The authors demonstrate that centered log-ratio (CLR)-transformed cell-type proportions (ECODA) match or outperform more complex state-of-the-art methods while requiring orders of magnitude fewer computational resources. The accompanying scECODA R package facilitates practical adoption.

Software availability. scECODA, integrated into Bioconductor and Seurat workflows as an open-source R package, substantially increases the practical impact of this work. scECODA comes with proper documentation and meaningful tutorials.

Major Concerns

1. The benchmark conflates methods with fundamentally different objectives. Several benchmarked methods were not designed primarily for unsupervised patient stratification by clustering. MrVI, for instance, explicitly targets the identification of local gene expression shifts that would be missed by a composition-based approach (scPoli likely behaves similarly though this manuscript lacks analysis). These methods are likely complementary to ECODA rather than competing with it. This is already partly visible in the benchmark: MrVI performs superior to ECODA on the Adams and Stephenson datasets while underperforming elsewhere. The authors should investigate and discuss why ECODA underperforms in these specific cases for example, whether transcriptional reprogramming rather than compositional shifts dominates the biological signal in those datasets. Such an analysis would provide practical guidance for method selection and reframe the benchmark as a characterization of complementary use cases rather than a simple ranking.
2. The Leiden clustering benchmark requires clarification and extension. This concern has several distinct components that should each be addressed:
   • Batch correction dependency: ECODA's robustness to batch effects may derive partly from cell types being called in batch-corrected embedding spaces (e.g., Harmony or scVI), rather than from ECODA itself. The authors should clarify whether cell-typing in batch-corrected embeddings are a prerequisite for ECODA's batch robustness, and if so, make this explicit in the workflow recommendations.
   • Performance in challenging compositional scenarios: The Gong Sharma dataset, which requires fine-grained immune cell-type resolution to separate CMV-positive from CMV-negative individuals, is arguably the most demanding test case for Leiden-based annotation. Would unsupervised Leiden clustering achieve comparable performance to expert labels in this scenario? This is not addressed in the current analysis.
   • Resolution parameter guidance: The manuscript implies that higher Leiden resolutions are generally better for ECODA, but there must be practical limits to this - overclustering introduces noisy, sparsely populated clusters that destabilize CLR estimates. The authors should provide clearer guidance on how to select the resolution parameter in the absence of expert labels.
   • Stability of the identified marker cell types: Figure 3B shows that the top contributing cell types identified by ECODA differ substantially between HiTME and authors_HR annotations for the Adams dataset. How stable are these "marker" cell types across annotation strategies, and what are the implications for biological interpretation?
3. The range of zero-handling values tested is too narrow. The benchmarked pseudocount values are in a relatively small range, and performance differences among them are minimal. To establish that the recommended default (pseudocount of 0.5) is genuinely optimal rather than arbitrarily chosen, the authors should extend the analysis to much smaller values (e.g., 1×10⁻³) and much larger values (e.g., 100). This would demonstrate that performance degrades at the extremes and that the current default sits in a robust optimum.
4. The HVC analysis would benefit from a more rigorous feature selection framework. The current approach selects highly variable cell types based on unsupervised variance ranking. Since the goal is patient stratification, it would be informative to compare this approach against supervised feature selection methods (e.g., LASSO-penalized classification). This comparison would clarify whether the variance-based approach approximates supervised selection, or whether meaningful discriminative signal is being left on the table. Separately, the claim that HVC-based ratios are directly translatable to clinical platforms such as flow cytometry should be made more carefully: several of the identified marker cell types (e.g., KLRF1⁻ GZMB⁺ CD27⁻ memory CD4 T cells) require multi-parameter panels that are not routinely employed in clinical practice.
5. Cell-type annotation subjectivity introduces a potential source of bias not discussed. The authors evaluate annotation robustness across strategies but do not discuss a related concern: future studies may define cell types in a manner that, intentionally or not, introduces a desired sample stratification, while cell populations associated with unwanted variation (e.g., technical confounders) may be merged or excluded. This subjectivity could inflate ECODA's apparent performance in practice and should be acknowledged explicitly in the Discussion as a caveat of annotation-dependent methods.
6. The title and framing overstate a causal claim. "Cell type composition drives patient stratification" implies that compositional differences causally determine clinical phenotypes. The benchmark establishes that compositional representations perform well for stratification, not that composition causes the underlying biology. The title and several passages in the manuscript should be revised to reflect this distinction for example, replacing "drives" with "predicts" or "reflects."
7. Foundation model-based methods should be discussed and ideally benchmarked. PULSAR, which uses the Universal Cell Embeddings (UCE) foundation model as a basis for sample-level representations, was recently introduced and represents an emerging class of methods not covered in this benchmark. Including PULSAR would future-proof the comparison. If the computational burden of full benchmarking is prohibitive, it would be a valuable addition to the Discussion.
8. The benchmark should address large-scale and multi-study scenarios. Studies with thousands of samples (e.g., OneK1K) and multi-study atlases (e.g., the Human Lung Cell Atlas) represent the trajectory of the field. Including at least one such dataset would substantially strengthen the claim that ECODA is scalable and robust to batch effects. This is especially critical as deep-learning based methods might scale favorably with the number of samples.

Minor Points

• The number of nearest neighbors used for modularity computation is three, which is small and may introduce instability. A sensitivity analysis across a range of neighbor values is warranted.
• A comparison to the cLISI (cell-type Local Inverse Simpson's Index) metric, widely used in single-cell integration benchmarks, would be appreciated, though cLISI operates at the cell level rather than the sample level and adaptation for this setting might be necessary.

Significance

Given rapidly increasing scRNA-seq cohort sizes, rigorous evaluation of sample-level representation strategies is pressing. The field has invested heavily in complex methods, making this comparative analysis valuable.

This is a well-executed benchmarking study that delivers a clear and practically useful message: properly handled cell-type compositional data is a powerful and underappreciated representation for scRNA-seq cohort analysis.

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Referee #1

Evidence, reproducibility and clarity

This paper presents the ECODA method and scECODA package, which uses simple sample-level representations based on transformed cell-type abundances to recover biological stratification of the samples. This compares favourably to more complex embedding-based methods across 11 datasets.

I would like to congratulate the authors on a well written and interesting manuscript. My most important concern is that there is potentially some circularity in the labels and disease classifications used for evaluation. Some of this is mitigated by the cluster-derived cell labels, but not all of it, since part of the concern relates to how the sample-level disease labels were defined. A negative-control benchmark using labels not expected to be composition-driven would help clarify this.

The manuscript appears to motivate ECODA partly as a tool for de novo exploratory patient stratification, but the benchmark mainly evaluates recovery of known biological labels. This is a reasonable validation strategy, but it does not directly assess whether the method can discover previously unknown patient subgroups, or determine the number and clinical relevance of such groups without label guidance. This distinction should be made clearer early in the paper.

p3:

'across 11 patient cohorts' - are there common aspects to these? It would be good to indicate why these were chosen and what the strategy is.

p7, Fig 2 A:

The runtime for ECODA and GloProp seem to be significantly less than the shuffled baseline, but the implication is that they do more calculations, which seems surprising. Is this an artifact?

p8/9:

A possible limitation is that the benchmark may be enriched for studies where compositional shifts are already expected to be strong.

In a similar sense, for disease states that are conventionally defined in a specific cell type, the analysis could be recovering label-associated annotation structure rather than independent disease biology. This is especially relevant for high-resolution manual annotations, where disease-associated cell states may already encode part of the biological contrast being evaluated.

A negative-control or stratified benchmark on labels not expected a priori to be composition-driven, or on composition-matched sample groups, would be a useful cross-check here.

p10:

It would also be interesting to see the robustness to small sample sizes, as this isn't mentioned elsewhere, but potentially could be a confounder in many patient derived samples.

p11:

The distinction between ECODA and scECODA could be a little clearer here. As far as I understand scECODA is the R tool and ECODA is the general method?

p13:

The claim that inter-sample biological variation is largely explained by cell-type abundance may need some qualification, because some of the disease or disease-state labels may themselves be partly compositionally defined. If disease state was assigned or refined using histopathology, cellular composition, or the presence of particular cell populations, then a composition-based method is partly being evaluated against labels that already contain composition-like information. This might weaken the interpretation that composition is an independent driver of disease biology, rather than a correlate of how the disease category was operationally defined.

It would therefore be useful to give more detail on how these disease labels were derived. This concern is not removed by using cluster-derived cell labels, because the possible circularity is in the disease-state definition rather than the cell annotation procedure.

'For example, ratios...immunotherapy response.' - A citation here would be good.

'Cost effective diagnostic assays...' - Perhaps a bit of an overstatement. This would likely require validation across larger cohorts, clinical sample-processing conditions, sequencing depth/cell recovery difference, etc. This claim could be softened or framed as a future direction.

p14:

'Expert author annotations...' - this could be clarified. Were these all manually curated annotations from the original studies, or did some original studies use automated/reference-based annotation followed by curation?

p15:

'We further controlled...' - was the analysis also evaluated over these separate subsets (other than just males <= 40) as a cross check?

p19:

HVCs: Could you comment on this procedure, versus something more akin to highly variable gene selection?

Significance

This paper presents a fast and interpretable method for sample-level stratification of single-cell RNA-seq cohorts, based primarily on compositional differences in cell-type abundance. This makes it of broad interest to researchers performing cohort-level scRNA-seq analysis, since its speed and simplicity make it an attractive baseline even when more involved downstream analyses are planned. However, as presented, its performance is less well established for datasets without reliable high-resolution annotations, for settings where the relevant structure is not primarily compositional, and for genuine de novo discovery of patient subgroups rather than recovery of known labels.

My background is in computational biology and biophysics.

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

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Referee #3

Evidence, reproducibility and clarity

Summary

During mitosis transcription is silenced (except at centromeres) and the majority of chromatin-bound RNA is removed from chromosomes. Previous work has shown that retention of elongating RNAPII on mitotic chromosomes through a WAPL degron leads to transcription-dependent chromosome segregation errors. Additionally, retention of chromatin bound RNAs through mutation of HNRNPU/SAF-A also leads to chromosome segregation errors. However, the field lacks a complete understanding of the mechanisms that remove RNA from chromatin in mitosis. Previous work from the Oliveira lab (and others) demonstrated that depletion of Lds/TTF2 also leads to chromosome segregation errors, but it was not possible to directly link chromosome segregation defects to persistent mitotic transcription. In this current work the authors examine the role of TTF2 in mitosis in human cells. They nicely show that TTF2 is required to release transcripts from chromatin during mitosis and that retention of transcripts on chromatin leads to chromosome segregation errors. Interestingly the authors find that depletion of TTF2 leads to an increase in the number of R-loops present on mitotic chromosomes and that R-loop-containing DNA is a major component of anaphase bridges. The results presented in the manuscript are high quality and the data support the conclusions. This work is important because it provides further evidence that the removal of RNA and transcription complexes from mitotic chromosomes is important for accurate chromosome segregation. There are a couple of points that the authors should consider prior to publication listed below and some minor issues with data presentation that should be corrected.

Major points

1. The authors use RNAi to deplete TTF2 and examine mitosis following depletion. The authors state that TTF2 depletion requires 48 hours, or approximately 2 cell cycles. Since TTF2 is depleted for the entire cell cycle it is possible that transcription termination defects caused by TTF2 depletion during interphase causes defects in mitosis and that the observed phenotypes are not a result of mitotic function of TTF2. This concern is somewhat addressed by the observation where the authors inhibit transcription using triptolide and show that this treatment rescues chromosome segregation defects observed following TTF2 depletion. However, the TRP treatment is for 4 hours, which includes a substantial portion of interphase. The length of TTF2 depletion is a significant concern and I think there are two ways that this could be addressed:

a. Create a TTF2-AID (or dTAG) cell line and analyze chromosome segregation defects following TTF2 depletion only in mitosis. This is a difficult and time-consuming experiment but is also the most direct test of the role of TTF2 in mitosis. This experimental system would be required for publication in a high-impact journal.

b. Include a section in their discussion acknowledging that indirect effects could be a cause of the chromosome segregation errors observed following TTF2 depletion. 2. The authors nicely show that TTF2 depletion leads to a significant retention of EU-labeled RNA on mitotic chromosomes but do not address the nature of these transcripts. Additionally, the authors do not show that TTF2 depletion leads to changes in transcription in interphase cells. This work could be improved by the addition of EU-RNA sequencing data showing that TTF2 depletion leads to transcriptional changes in interphase (e.g. transcription past the normal termination site) and EU-RNA sequencing to identify that transcripts that are retained on mitotic chromosomes. Neither of these experiments are absolutely necessary for publication but would significantly improve the general interest of this work. 3. The authors show that TTF2 depletion leads to an increase of R-loops on anaphase bridges. Previous work has shown that R-loops are present at mitotic centromeres (29170278) and that activation of ATR through these R-loops is necessary for accurate chromosome segregation. This work is clearly relevant to the authors results and has not been cited or discussed. This previous work should be included in the discussion and interpretation of the authors' work.

Minor points

1. In Figure 1 the authors show a comparison of the levels of EU-labeled RNA in control and TTF2-depleted cells at each stage of mitosis. The graphs in B and D would be much easier to compare if these were combined into a single graph.
2. There are a number of quantitative plots that are lacking statistical comparisons between key groups. These are: Figure 1B and D, Figure 1F, S2B, Figure 4DE, S6C,

Significance

This advance is incremental but adds to accumulating evidence that transcription termination is important for normal chromosome segregation.

The strengths of this work are high quality data, careful analysis, and the fact that conclusions follow directly from the data presented.

The weaknesses are that the model system in not optimal to address the question being posed and that the authors have not completely characterized their model system.

This work will primarily be of interest to groups working on mitotic chromatin:RNA and transcriptional regulation.

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Referee #2

Evidence, reproducibility and clarity

Summary:

In this original article, authors attempt to define the molecular and cellular consequences of retaining spurious transcriptional activity in mitotic chromosomes. The study uses the depletion of TTF2 (transcription termination factor 4) in tissue culture of HeLa cells as a model. Results show the accumulation of nascent RNAs and R-loops as a product of such aberrant transcription which, strikingly, increases the incidence of chromosome segregation errors. Importantly, authors elegantly show that these errors are corrected by inhibition of RNA Polymerase2 activity with previously reported drugs. This reviewer finds the study very interesting and compelling, very well written and structured. However, I consider that the adjustment of several aspects might improve the manuscript:

Major comments.

1. The main limitation of the study relies on the approach followed to deplete TTF2. Authors used siRNAs in order to decrease the levels of this factor, which implies an incubation time of 48h. This might represent a limitation. Regarding this aspect, this referee request to show the proof of TTF2 depletion in the main figure with accurate quantification when possible.
2. Most of the main conclusions are very well supported by quantification of imaging data. However, this referee suggests the generation of superplots (ref) where values and average for each replicate can be clearly visualized. Statistical analyses comparing the median from each different conditions by t-student (unpaired test) will better support the outcome.
3. Authors show a beautiful correlation between the presence of R-loops and chromosome segregation errors (Figure 6). I request the authors to replicate the experiment with cn or TTF2 siRNAs in combination with the triptolide treatment. Additionally, and to provide further evidence about the functional consequences of retaining R-loops, I wonder if authors can drive specific R-loop depletion by using RNase H activity. This will definitely reveal whether transcription activity or/and its product underlies the chromosome segregation defect.

Minor comments.

1. I highly recommend to include the value of all the statistic tests in each plot.
2. I would suggest the incorporation of a final paragraph at the end of the introduction summarizing the most important results of the study.
3. In the introduction, and based on wide evidences showing transcriptional activity at centromere regions (Chan 2012, Liu 2016, Perea-Resa 2024), and to a much lower extend, at the chromosome arms of mitotic chromosomes (Palozola, 2017), I would rephrase to make clear that transcription is generally repressed rather than globally silenced in mitosis.

Referees cross-commenting

After reading the comments from the other two referees, I maintain my view about the quality/interest of the manuscript. I endorse the potential publication of this work, after addressing the recommendations, in a reasonable period of time.

Significance

Authors provide a compelling study addressing the functional relevance of repressing transcription early in mitosis to properly segregate chromatids to daughter cells. In addition, the study also pursuits to illuminate the molecular and cellular consequences of inactivating TTF2 function and to provide insight into the chromosome segregation defects found under TTF2 misfunction. The study considers and discusses the most important aspects of the literature relevant for the proposed questions. The results are very encouraging and mostly confirmed by several orthogonal approaches.

The major strength is the direct correlation found between R-loop retention and chromosome segregation defects. The major limitation is, however, the usage of slow siRNA-based strategies to deplete TTF2. The use of degron-protac alternatives would be very beneficial although I do not consider this an essential aspect.

The study is sound and address very interesting still open questions. The publication of the results will influence and benefit a wide audience specially researches working on the mitosis and transcription fields. Research on R-loops, a field full of open questions, would also acknowledge the insights from this study.

Overall, I consider the study very interesting and compelling. I support the evaluation and envision that its publication, once addressed the above described comments, will be feasible within roughly 3-6 months of revision.

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Referee #1

Evidence, reproducibility and clarity

In this manuscript, Tovini and colleagues investigate the role of transcriptional silencing during mitosis using depletion of TTF2, a factor implicated in mitotic transcription termination. The authors show that TTF2 depletion leads to retention of elongating transcripts on mitotic chromatin, defects in chromosome organization and compaction, delayed mitotic progression, and increased chromosome segregation errors, particularly DNA bridges and UFBs. They further report accumulation of R-loops and demonstrate that transcription inhibition largely suppresses the observed segregation defects.

Overall, this manuscript is interesting and potentially important, and the study is technically sound. In particular, I liked the experiments showing continued transcript elongation during mitosis in TTF2-depleted cells. The rescue experiments with triptolide also support the conclusion that transcription contributes significantly to the observed phenotypes. The methods and statistical analyses appear generally appropriate and sufficient for reproducibility.

At the same time, I think that several aspects of the mechanistic interpretation are somewhat overstated, and some important alternative explanations remain insufficiently addressed. For these reasons, I believe the manuscript would benefit from substantial revision before publication.

Major comments

1. The authors favor a model where persistent transcription and R-loop accumulation interfere with Top2A-mediated sister chromatid resolution. While this is certainly possible, I do not think the presented data fully support such a specific interpretation. The authors demonstrate a pronounced chromosome organization phenotype. TTF2 depletion causes broadened metaphase plates and approximately 1.5-fold increased chromosome volume. These observations suggest a substantial defect in mitotic chromosome compaction. An important alternative possibility should be considered, namely that persistent mitotic transcription interferes with Condensin I and/or Condensin II loading and/or retention. Given the current understanding that chromosome condensation and loop organization are highly dynamic processes, it is conceivable that ongoing transcription could impair Condensin-mediated chromosome assembly. At minimum, the authors should assess chromosomal localization of Condensin I and II in mitotic cells after TTF2 depletion (for example CAP-H/CAP-D2 and CAP-H2/CAP-D3). Such analysis, ideally also including triptolide rescue, would substantially strengthen the mechanistic interpretation and help distinguish between a primarily transcription/R-loop-mediated defect and a more global chromosome assembly defect.
2. The authors conclude that kinetochore-microtubule attachments are largely normal, based on Mad2 localization, inter-centromere distance, and the absence of strongly uncongressed chromosomes. In my opinion, these measurements are indirect and do not sufficiently demonstrate robust mature end-on attachments. Given the observed metaphase spreading, mild congression defects, and SAC-dependent delay, it remains possible that TTF2 depletion causes more subtle defects in k-fiber stability or attachment robustness. I think a cold-stability assay of spindle microtubules would be important here. Such experiment would directly address whether cold-stable k-fibers are normally formed and maintained in TTF2-depleted cells. Ideally, this should be combined with kinetochore markers and quantification of k-fiber intensity. Without such analysis, the statement that KT-MT attachments are unaffected should be toned down.
3. The manuscript generally frames mitotic transcription as detrimental to chromosome segregation. However, several previous studies, including work from Hongtao Yu's lab, reported that localized centromeric/kinetochore transcription during mitosis contributes positively to chromosome segregation, including correct Sgo1 localization and centromeric function (this literature is not discussed, despite appearing conceptually relevant to the present study). This is not necessarily a contradiction; it seems possible that a limited and spatially restricted mitotic transcription program at centromeres may be beneficial, whereas persistent chromosome-wide elongation caused by TTF2 depletion becomes pathological. However, this distinction should be discussed explicitly. As currently written, the manuscript risks giving the impression that mitotic transcription is generally deleterious, which would not be fully consistent with the literature. The authors should check whether Sgo1 is localized correctly after TTF2 depletion in both Noc-arrested and metaphase (MG132- or ProTAME-arrested) cells.
4. I was somewhat confused by the interpretation of RPA70-positive fibers. The authors state that they "did not detect a major increase" in RPA70-coated UFBs, arguing against an important contribution of replication-associated intermediates. However, in the next sentence, they report that approximately 20% of TTF2-depleted anaphases display an RPA70-positive fiber and, importantly, this phenotype is largely reverted by triptolide. In my opinion, this is not a trivial observation and appears difficult to fully reconcile with the conclusion that replication-associated events contribute minimally to the phenotype. In principle, RPA70 positivity should not necessarily be interpreted exclusively as evidence of replication stress. Persistent transcription, R-loops, or transcription-associated topological stress could generate ssDNA intermediates that can recruit RPA. Do RPA-positive fibers co-localize with R-loops? Therefore, the Discussion would benefit from a more balanced interpretation of these findings.
5. The rescue experiments with triptolide are convincing and support a transcription-dependent contribution to the phenotype. However, because triptolide treatment was performed over several hours, these experiments do not formally distinguish between ongoing transcription elongation during mitosis and perturbations arising earlier in the cell cycle, including possible transcription-replication conflicts during late S/G2. This limitation should be acknowledged more clearly in the Discussion, especially given the recently described role of TTF2 in replisome eviction. It would be informative to perform a time-course analysis of triptolide rescue. Demonstration that the phenotype can be substantially reverted within ~30 minutes of treatment would strongly support the interpretation that persistent transcription during mitosis, as opposed to earlier cell-cycle perturbations, is the major contributor to the observed defects.

Minor comment:

It would be useful to check whether RHINO-positive/R-loop-associated structures preferentially localize to centromeric versus chromosome arm regions. Such information may help distinguish physiological mitotic transcription from pathological transcript retention.

Referees cross-commenting

I have carefully read the other reviews and they do not change my overall assessment of the manuscript or my recommendations.

Significance

General assessment:

This is an interesting and potentially important study addressing how transcriptional silencing contributes to mitotic fidelity. The strongest aspect of the work is the convincing demonstration that transcription elongation persists during mitosis after TTF2 depletion and contributes to chromosome segregation defects. The main limitation is that the mechanistic interpretation currently appears somewhat narrower than supported by the data.

Advance:

The study extends previous work on TTF2 by linking defective mitotic transcriptional silencing to chromosome organization and chromosome segregation defects. The demonstration of transcription elongation during mitosis after TTF2 depletion is particularly interesting.

Audience

The work will likely be of interest to researchers studying mitosis, chromosome biology, transcription, genome stability, and chromosome organization.

Expertise:

mitosis, chromosome organization, nuclear organization, cell biology, biochemistry. I do not consider myself an expert in R-loop biology or transcription-coupled repair.

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Reply to the reviewers

Reviewer #1:

Major comments:

1. Lines 103-116 (first paragraph of the results section) describe mainly published data that is more suitable for the introduction section. It is annoying to refer to different published articles in the Results section to strengthen the results instead of showing them. The same goes for paragraphs two and three. Why mention those data in the Results section if they are already published and known?

We have reorganized this material by moving some background information to the Introduction. Our intention was not to incorporate published data to strengthen our results, but rather to provide essential context for interpreting our findings. We have therefore left some of this foundational information in the results section to create a clear narrative flow, enabling readers to understand the basis for our experimental design and interpretations without needing to recall details from earlier paragraphs in the Introduction. For example, we considered it crucial to restate the earlier report of the BiP:sfGFP:HDEL phenotype in Atlastin mutants, since our results supporting luminal ER protein displacement contradict the previous fragmentation model.

The following concept was in line 103 in the Results section, and is now in the introduction in lines 82-92: "Conventional light microscopy, commonly used in studies of neuronal ER structure, lacks the resolution necessary to visualize individual ER tubules in small structures, such as presynaptic terminals. The ER is highly sensitive to fixation, and live imaging experiments in neurons in vivo have been conducted on upright microscopes using water dipping objectives with a typical axial resolution limit of >300 nm, which cannot distinguish the densely packed ER tubules at presynaptic terminals (3,8,21,28,39-42). Electron microscopy offers higher resolution, but cannot be used in live samples and has typically been limited to thin 2D sampling (in which it is difficult to distinguish ER cross-sections from synaptic vesicles) (8,20,22)."

Figure Legends-(in all Figures): The number of experimental repeats must be mentioned in the figure legends.

This information is provided in Supplementary Table 1, which contains detailed information about the genotype, statistical analysis, and number of larvae and NMJs analyzed. If the journal requires this information in figure legends, we can move it.

The way the figures are labeled is worrisome; supplementary figures are not ordered numerically.

We will be happy to rename supplementary figures according to journal guidelines.

The tubule extension in Figure 2D is not convincing. Is there a movie showing those changes? Better images are needed. It is essential to show which supplemental movie corresponds to which panel.

We have now included a corresponding video of the same neuron used as an example of tubule extension. We also added another frame to the figure to provide further information on the tubule event we captured. (Figure 2D, Movie S10)

This is unnecessary in the results section: "To investigate the relationship between ER structure and function at synapses, we examined mutants of Atlastin, a GTPase that regulates ER tubule fusion. Drosophila has a single homolog while mammals have three Atlastin homologs, with Atlastin-1 enriched in the brain (Rismanchi et al., 2008)."

This information was moved to the introduction.

"This reduction in ER membrane marker intensity has also been observed in other HSP mutants, suggesting this is a common feature of ER shaping mutants and could indicate changes in ER membrane composition, integrity, or tubule thickness (Perez-Moreno et al., 2023)." This comparison is important and should be shown in the same settings as for the Atlastin mutant rather than referring to published data.

We agree with the reviewer that it is important to determine whether other ER-shaping proteins, besides Atlastin, also show a decrease in tdTomato:Sec61b to support our claim that this could be a common feature among ER-shaping mutants. To do this, we examined mutants of another ER-shaping protein, Reticulon 1, which regulates membrane bending and stabilization in ER tubules. These loss-of-function mutants were a gift from Dr. Cahir O'Kane at the University of Cambridge and were used in his lab's Pérez-Moreno et al., 2023 publication. We found that in our hands tdTomato:Sec61b levels were reduced in Reticulon 1 mutants, consistent with the results reported by Pérez-Moreno et al. (2023). These results are in Figure 3E-F. We also examined the synaptic distribution of the luminal ER marker, BiP:sfGFP:HDEL, in Reticulon 1 mutants to see if it is displaced to the cytosol. Notably, it remained ER-associated, unlike in Atlastin mutants. These results are in Figure 6F-G, results lines 267-270, and discussion lines 542-545.

Does the distribution of the luminal ER marker in Figure 6F diffuse due to mislocalization or reflux after being localized to the ER and then refluxed to the cytosol as was previously shown for the ER to Cytosol signaling (ERCYS) mechanism? Could you assess other ER-luminal protein localization biochemically? It is highly recommended to look at another soluble ER-protein localization in the Atlastin mutant without overexpression, which can be an artifact.

ER stressors can induce ERCYS, in which some luminal proteins, including PDIA3, DNAJB11, ERp29, and an eroGFP reporter, reflux by 30-70% to the cytoplasm without subsequent degradation (unlike ERAD (ER-associated degradation). This phenomenon has only previously been observed in yeast and glioblastoma tumor cells from mice and human . We believe that our work provide the first suggestion that this may occur in neurons, and particularly in a neurological disease model.

We do not believe that the reflux phenotype for BiP:sfGFP:HDEL is due to its overexpression for two reasons: (1) we observe reflux in our neuronal Atlastin knockdown experiments, even when the levels of BiP:sfGFP:HDEL are significantly reduced artificially because of titration of the GAL4 between the RNAi and the reporter (Figure 7A), and (2) BiP:sfGFP:HDEL overexpression somewhat suppresses endogenous BiP upregulation ((Figure 10 and see Reviewer 1.10), arguing that the transgene does not induce ER stress). We included a new "limitations of the study" section to be transparent about the caveats of the BiP:sfGFP:HDEL reporter (lines 639-664).

Identifying potential endogenous neuronal ERCYS substrates in our in vivo preparation poses several challenges. First, biochemical approaches, such as fractionation, are not possible in our complex in vivo sample because neuronal ER proteins would mix with ER from other tissues upon homogenization. Second, detecting endogenous proteins with antibodies requires fixation and permeabilization, which notoriously disrupts ER structure and even causes our reporter BiP:sfGFP:HDEL to collapse from a smooth distribution, as visualized by live imaging and FRAP, to a punctate distribution. Third, using antibodies rather than neuronally restricted transgenes makes it challenging to determine whether the signal originates from the neuron or from dense ER structures in the surrounding muscle. Fourth, some ER luminal proteins can displace as little as 30% in the ERCYS examples cited above, and the sensitivity of our imaging assays may limit our ability to detect these small changes. Finally, the limited availability of tagged transgenes and antibodies specific to Drosophila luminal ER proteins (see next paragraph) poses additional challenges. These limitations highlight the need for future studies to develop novel tools and techniques to more definitively test whether we are indeed observing ERCYS. We have included a paragraph on these future challenges in our discussion in lines 639-664. Identifying endogenous targets of ERCYS in fly neurons is a worthwhile goal, but beyond the scope of the current study. These next steps will particularly benefit from identifying the machinery involved in the reflux of our BiP:sfGFP:HDEL reporter.

Tools we tested: We investigated several options: (1) a tagged PDI transgene (a gift from Karen Hibbard), which was not detectable at presynaptic terminals, (2) a tagged BiP (FlyORF; F000956) that did not localize to the ER, and (3) full-length endogenous BiP detected by antibody staining. We did not detect obvious reflux of endogenous BiP to the cytoplasm (Figure 9), with the caveat that in fixed samples, the BiP signal was not tightly co-localized with the ER marker even under control conditions. However, we did use this antibody to detect an increase in BiP in Atlastin mutant presynaptic terminals, indicating ER stress (see Reviewer 1.10).

Though we have not identified endogenous targets, we believe that our studies with the exogenous reporter will be of great interest to the field, as they clarify the previously reported Atlastin phenotype and provide the first report of a new defect in a human disease animal model.

In comparison to Summerville et al. (2016) in Figure 7, the experiment was not done in the same way. It is important to keep the same settings for comparison

In Figure 7D-E, we compare the distribution of BiP:sfGFP:HDEL in cell bodies, axons, and muscles between controls and Atlastin mutants. To clarify the experimental approach relative to Summerville et al. (2016): while both our studies examined the same cellular compartments (cell bodies, axons and nerve terminals) using the BiP:sfGFP:HDEL reporter, we employed super-resolution Airyscan microscopy. This enhanced resolution was critical for definitively demonstrating that this is a functional rather than a structural phenotype and that ER displacement is progressive, and repeating this experiment at lower resolution as previously reported does not provide any new information. We identified two distinct distribution phenotypes in Atlastin mutants expressing BiP:sfGFP:HDEL, which were not described in the Summerville et al., 2016 paper. From our manuscript (lines 249-251): "We identified two distinct ER network phenotypes in Atlastin mutants expressing BiP:sfGFP:HDEL: "Partial loss" NMJs retained both diffuse signal and identifiable ER network structures, while "Complete loss" NMJs showed no visible ER network structures. Note that the "Complete loss" phenotype in Atlastin mutants reflects the absence of detectable luminal marker signal in organized ER structures, but not the complete absence of ER membranes, as demonstrated by our ER membrane marker tdTomato:Sec61β results."

Does the Atlastin mutant induce the unfolded protein response and stress within the ER? It is necessary to look for UPR markers in those settings. It was shown previously that ER stress leads to protein reflux from the ER to the cytosol. Is there a difference in the ER stress markers in the presynaptic terminal?

The reviewer suggested that Atlastin mutant synapses may exhibit ER stress. To address this, we examined levels of the ER chaperone BiP, a well-established ER stress marker whose expression increases during UPR activation. We first validated that our BiP antibody can detect changes in ER stress by feeding control larvae with 50mM DTT for 24 hours. These results are in the new Figure 10A. Note that we were unable to test sensitivity to ER stress in this way in Atlastin mutant larvae because they did not consume the DTT-treated food, as assessed by blue food coloring in the larvae's guts.

Using this antibody, we measured baseline BiP levels at NMJs of Atlastin mutants on normal food, and found they were slightly increased compared to controls. We conclude from these experiments that Atlastin mutant synapses have mild ER stress. Notably however, Atlastin mutants co-expressing UAS-BiP:sfGFP:HDEL or UAS-tdTomato:Sec61b did not show significantly increased endogenous BiP levels, suggesting that transgene expression at least partly suppresses the mild ER stress response, even though there is extensive cytosolic displacement. These results argue (1) that the mild ER stress in Atl mutants does not strictly correlate with the reflux phenotype, and (2) that the reflux phenotype is not an artifact of overexpression-induced stress. These results are described on lines 430-436 in the results section and shown in Figure 10B-E, and their implications discussed on lines 585-598.

We also explored another strategy to detect ER stress by assessing eIF2α phosphorylation, a key event in the Unfolded Protein Response (UPR) pathway. We obtained a phospho-eIF2α antibody (Cell Signaling; #3597) that was reported to work in Drosophila. However, when we tested this antibody by Western blot, we were unable to detect a band at the expected molecular weight for phosphorylated eIF2α, even in positive-control samples treated with DTT to induce ER stress. We therefore concluded that this antibody is not suitable for reliably detecting ER stress in our experimental system. The failure of this antibody highlights the challenges of finding robust tools to measure ER stress in Drosophila.

It is important to add biochemical experiments to show that no fragmentation of the ER membrane occurred. It can be simply demonstrated by looking at the redox state of the ER, which would change if it were mixed with the reducing cytosol. Moreover, this can be shown by using an ER-targeted redox-sensitive fluorescent protein that is tethered to the ER membrane to follow changes in the redox state of the ER.

The reviewer asked us to test whether the redox state of the ER is disrupted, which could indicate exchange between the cytosol and ER due to membrane rupture. As noted above, biochemical approaches such as fractionation are not possible in this in vivo sample. We attempted to address this concern by creating a UAS-Sec61β:roGFP construct, using the roGFP sequence from Igbaria et al. (2019) to monitor the ER lumen redox environment in Atlastin mutants. Since Sec61β is membrane-tethered, it should remain in the ER and not undergo reflux, making it an ideal sensor for detecting any mixing between the reducing cytosolic environment and the oxidizing ER lumen that would occur if membrane fragmentation and/or ruptures were present. We tested this approach in wild-type Drosophila S2 cells and used the Gal4-UAS binary expression system to co-express Actin-Gal4 (to drive expression of UAS constructs), UAS-Sec61β:roGFP (redox sensor), and UAS-BiP:Halo:HDEL (as a control reporter insensitive to DTT treatment).

Our experiments showed no detectable changes in the fluorescent properties of UAS-Sec61β:roGFP following 30 min 10mM DTT treatment compared to DMSO vehicle control, including no increase in 405-nm excitation fluorescence or changes in 488nm/405nm excitation ratios. These results suggest that either the roGFP sensor requires further optimization for sensitivity in this cellular system or that additional controls and calibration steps are needed to establish the dynamic range of the assay. We believe this experiment falls beyond the scope of the current study, given the extensive optimization required. However, it represents an important future direction for testing membrane fragmentation as a mechanism underlying the phenotypes observed in Atlastin mutants. The possibility of ER integrity defects is mentioned in the discussion on lines 547-559.

Minor comments:

1. It is important to call figures by order. Figure 2C is called before 2A-B. Figure 2B is called before Figure 2A.

The revised manuscript has all figures in order of appearance in the text.

Figure legends (Figure 2): "The same control dataset used in E-G was used in Figure 5 and Figure 5_Supplement." Why is this relevant?

We wanted to be transparent about reusing the same control dataset across multiple figures to avoid any appearance of data duplication. This notation clarifies that, although the data appear in different contexts (Figures 2 and 5. This version does not contain a Figure 5_Supplement), it represents the same biological samples analyzed for different parameters, ensuring readers understand that these are not independent datasets.

Figure 4F is called before Figure-4D-E which are not called.

We revised our manuscript and reorganized Figure 4 to ensure that all figure panels are referenced in sequential order and that panels 4D-E, which were previously not cited in the text, are now properly referenced when discussing their corresponding results.

Figure 5B is called before the previous ones. Same for Figure 5A supplement.

We referenced Figure 5A in lines 211-212, which precedes our discussion of Figure 5B. To clarify the figure order, we removed the early references to Figures 2D-G and Movies 7-14, which were mentioned only to indicate that we were analyzing the same dataset in different ways.

The revised manuscript has all figures in order of appearance in the text.

Referees cross-commenting

I agree with the comments raised by reviewer2 and 3. Basically it is highly important to validate those data by genetic rescue. Moreover, it is essential to know the source of the displaced luminal marker to the cytosol. Is it mislocalization or it is a reflux of pre-existing protein to the cytosol after insertion to the ER. It is also recommended by me and the reviewers and me to test the endogenous protein rather than overexpression.

We have addressed these points in our responses to the following reviewer questions:

• Genetic rescue: Please see our responses to Reviewer 1/Question #10 and Reviewer 2/Question #1.
• Source of displaced luminal marker: We provide some evidence addressing this in our response to Reviewer 3/Question #1.
• Endogenous protein localization: We have examined this and detailed our findings in our responses to Reviewer 1/Question #7 and Reviewer 2/Question #6.

  Reviewer #1 (Significance (Required)):

General assessment: This interesting paper shows that proteins can escape the ER under special conditions. However, the authors need more evidence to show that and rely less on the overexpression system, especially of BIP-GFP, which can cause proteostasis stress within the ER. Advance: The results have been oversimplified in their explanations, and some points and complexities of the study need to be addressed further to make the most of them. These are often some of the more interesting concepts in the paper. I think many points can be addressed in the text by the authors being clear and concise with their reporting. At the same time, other experiments would turn this paper from an observational one into a very interesting mechanistic one. This paper is based on previously published articles from the group and other groups, and it is a nice progression. However, as mentioned, this paper depends primarily on published data, and the novelty is somehow lost between all the comparisons to other published data instead of emphasizing that. Without a substantial mechanistic improvement, the paper would remain observatory.

Audience: The microscopy tools can be great addition to researchers in the field to monitor protein trafficking especially Cell biologists (basic research)

My expertise: ER homeostasis, protein trafficking, cell biology

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

Summary The endoplasmic reticulum (ER) is a continuous organelle that extends throughout neurons to regulate fundamental processes. The analysis of ER dynamics at synaptic terminals is limited by the challenge of imaging these structures at high resolution. In this manuscript, the authors use super-resolution (~170 nm) live imaging and a combination of membrane and luminal ER markers at the Drosophila larval NMJ, an important model synapse, to investigate dynamic ER architecture in vivo. They report a detailed characterization of the presynaptic ER organization and dynamics at wild-type and GTPase Atlastin mutant NMJs. Their analysis using the ER membrane marker tdTomato:Sec61b reveals the presence of an intact ER network in Atlastin mutants. This contrasts with the apparent ER fragmentation phenotype previously reported and replicated here when using a luminal marker. Their findings instead point to the progressive displacement of luminal proteins to the cytosol in Atlastin mutants specifically at synapses. The authors propose that the disruption of ER protein dynamics at synapses is a compartment-specific ER stress response. The manuscript is well written, results are clearly presented, and experiments are technically rigorous.

Major comments

1. The baseline ER phenotypes in Atlastin mutants are mild with complete loss of ER network only observed in terminal boutons. This interesting and unexpected result should be further confirmed by genetic rescue. The authors can use a UAS rescue line previously reported in PMID: 19341724.

We tested the UAS-Atl-myc rescue line and unfortunately found that even in wild-type neurons, overexpression of Atlastin produced strong ER organization defects that precluded the rescue experiment. Instead, to confirm the cell autonomy of the phenotype and to test it wth an independent tool, we performed a presynaptic knockdown of Atlastin by RNAi and found that BiP:sfGFP:HDEL is displaced, as observed in the Atlastin null mutant. These results are in now shown in Figure 7A-C.

Lines 204-7: It's not clear how a greater coefficient of variation indicates that the marker is more concentrated in subsynaptic structures or what is meant by 'subsynaptic structures.'

We added the following text to explain, in lines 181-183: "A higher CoV indicates an uneven distribution of tdTomato:Sec61β within the presynaptic terminal, with some areas showing higher concentrations than others (in contrast to the uniform, diffuse signal expected from fragmentation)." To avoid confusion with postsynaptic structures called the subsynaptic reticulum, we have removed the term "subsynaptic". The intended meaning is distinct structures found within the presynaptic terminal.

There's a mistake in Figure 6C and the associated text. The summed percentage of the three phenotypic categories adds up to 110% for Atlastin mutants. *

The reviewer noted that the summed percentage of the three phenotypic categories in Figure 6C adds up to 110% for Atlastin mutants, which appears to be a mathematical error. However, this is not an error, but rather a reflection of our quantification methodology, in which a single bouton can exhibit more than one type of ER dynamics per movie recorded. Our quantification counts each phenotype independently, so boutons displaying multiple phenotypes contribute to more than one category. This approach provides a more comprehensive view of the range of ER dynamics present in Atlastin mutants, as restricting the analysis to mutually exclusive categories would underrepresent the complexity of the phenotypes observed. To make this point clear, we made the following change to the text in lines 257-259: "We note that the sum of these percentages exceeds 100% because one NMJ exhibited multiple phenotypes: one branch had a complete loss, while the other branch had no phenotype. These phenotypes were counted separately."

Figure 8: the ER looks fragmented in 1st instar controls and mutants. The authors should address this difference from more mature NMJs.

We would like to clarify that the bulk of experiments in this manuscript (including all ER dynamics, luminal marker redistribution, and membrane marker analyses discussed throughout the Results) were performed in 3rd instar larvae, which are more mature larval NMJ preparations standard in the field. Figure 8 was included specifically to test whether the Atlastin mutant phenotype we describe throughout the paper is also detectable at an earlier developmental stage, not to replace or reinterpret our primary findings.

Regarding the specific observation that the ER appears more fragmented in Figure 7F-H relative to the more mature NMJs shown elsewhere: this fragmentation, observed similarly in both control and Atlastin mutant 1st instar larvae, likely reflects technical challenges associated with dissecting these smaller, more delicate early-stage specimens rather than a genotype-specific effect. Because fragmentation occurred similarly in both genotypes, we could still reliably assess the redistribution of BiP:sfGFP:HDEL as our primary phenotypic readout in this experiment. We have added the following text (lines 306-309) to clarify this point: "Note that in 1st instar larvae, both normal networks in controls and residual networks in Atlastin mutants appeared more fragmented than in 3rd instar preparations, likely due to the technical challenges of dissecting these smaller, more delicate specimens. Since ER fragmentation occurred similarly in both genotypes, we could still reliably assess the redistribution of BiP:sfGFP:HDEL as our primary phenotypic readout.

The images in figure 9B do not seem representative of the quantification in Figure 9D. Specifically, the partial loss Atlastin NMJ appears to have recovered as fully as the complete loss Atlastin NMJ.

The images showed FRAP recovery across the entire bouton, but we photobleached only a small region within each bouton and quantified only this region. We have now added outlines to clearly delineate the specific FRAP regions that were analyzed in each image, which clarify that the partial loss Atlastin showed less recovery than the overall bouton. We have also reordered the figures to more clearly convey our message (Figure 9 is now Figure 8).

We also made a few changes to the paragraph on lines 347-350 to clarify our experimental reasoning: "We photobleached en passant boutons using a defined region of 6.8 x 7.8 microns (dashed box in Figure 8D) to ensure that BiP:sfGFP:HDEL could recover from the ER networks surrounding the FRAP region (Movies S20-S23)."

We also added this sentence to the figure legends of Figure 8: "The dashed boxes in (D) indicate areas that were photobleached and analyzed for recovery quantification in (E-F)."

Optional: An overexpressed luminal marker is displaced to the cytoplasm in Atlastin mutants. It would be interesting to know and increase the significance of the findings if the same is true of endogenous luminal proteins under biological stress conditions.

As noted in our response to Reviewer #1 suggested that Atlastin mutant synapses may exhibit ER stress. To address this, we examined levels of the ER chaperone BiP, a well-established ER stress marker whose expression increases during UPR activation. We first validated that our BiP antibody can detect changes in ER stress by feeding control larvae with 50mM DTT for 24 hours. We were unable to perform this experiment in Atlastin mutant larvae because they did not consume the DTT-treated food, as assessed by blue food coloring in the larvae's guts. These results are in Figure 10A. In the future, it will be of interest to establish a protocol to examine Atlastin mutants by feeding or treating larval fillets with DTT.

We measured BiP levels at NMJs of Atlastin mutants and found they were slightly increased compared to controls. Atlastin mutants co-expressing UAS-BiP:sfGFP:HDEL or UAS-tdTomato:Sec61b did not show significantly increased endogenous BiP levels, suggesting that transgene expression suppresses the mild ER stress response. We conclude from these experiments that Atlastin mutant synapses have mild ER stress. These results are in Figure 10B-E).

Optional: Applying this approach in stimulated conditions (high potassium, increased temperature) might reveal a greater activity-dependent role for Atlastin at synaptic terminals.

This is a very interesting idea, as we have only examined synapses at rest. However, this is beyond the scope of this paper.

Minor Comments

1. Line 16: Atlastin should be italicized.

Thank you for catching this typo. We have fixed it.

Figure 5A: Based on the relative intensities, it appears that control and mutant images are not contrast matched but this isn't stated.

Thank you for catching this omission. We added to the figure legend: "Control and Atlastin mutant images are not contrast matched."

Line 822: The number of static Atlastin mutant boutons used for analysis is missing.

Thank you for catching this omission. We have fixed this supplementary table.

Figure 9: The blue arrows are not annotated in the figure legend.

Thank you for catching this omission. We have fixed this figure legend.

Reviewer #2 (Significance (Required)):

Atlastin is linked to Hereditary Spastic Paraplegia (HSP) and this study changes our understanding of the compartment-specific impacts of its loss. This study reveals the importance of using both membrane and luminal ER markers to accurately interpret phenotypes as well as the importance of considering compartment-specific effects on ER. These findings represent significant mechanistic and conceptual advances. The lack of genetic rescue is a limitation and adding an investigation of an endogenous luminal protein under basal and stress conditions would add significantly to our understanding of Atlastin dysfunction in HSP. Notably, the in vivo imaging approach introduced here can be adapted broadly for live imaging of Drosophila larvae. Thus, this work will be of interest to both neuronal cell biologists and the wider Drosophila community. This review is based on our expertise in neuronal cell biology.

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

In this manuscript, the authors investigate the structural dynamics of the endoplasmic reticulum (ER) in Drosophila neurons and examine the role of the ER-shaping protein Atlastin in ER morphology. Their discovery on the neuromuscular junction (NMJ)-specific contribution of Atlastin to ER integrity is intriguing and may provide valuable insights into the pathological mechanisms underlying Atlastin mutations associated with hereditary spastic paraplegia (HSP) and hereditary sensory neuropathy. The key observation on ER protein showing an aberrant cytoplasmic localisation in mutant cells appears convincing. Though this phenomenon's characterisation stays at the point of primary observation with its mechanics unclarified, establishing this new and unexpected functional rather than structural Atl effect is important and useful for the field. The observation that ER is structurally preserved in this mutant with absolute lack of Atl are also extremely useful.

It is unclear if the cytoplasmic localisation affects an exogenous overexpressed ER marker or endogenous protein would also appear in cytoplams, the authors should consider adding an immunostaining data to test that.

Authors offer speculations on potential reasons for the cyto localisation of the ER marker suggesting that relocation at the cell periphery specifically combined with slow clearance there is the most likely explanation (still unclear what stops the marker from spreading through the entire cell). They suggest that decrease in cotranslational translocation is unlikely as this would result in somatic accumulation of the marker. However, if the clearance in the periphery is less efficient than in soma, the accumulation there might reflect a compromised translocation. Any clarifying experiments, if practical, to directly demonstrate how ER proteins in relocates to the cytoplasm in atl mutant would help understanding better the phenomenon. For example, would proteasomal inhibition make the marker accumulate more across the cell? Authors also suggest links to ER stress. Would stress induction phenocopy the mutant?

Reviewer #3 asked whether defective proteasomal clearance underlies the cytosolic accumulation of BiP:sfGFP:HDEL in Atlastin mutants. We addressed this directly. First, proteasome function appears intact in the mutants: baseline ubiquitinated protein levels (FK1 antibody) were comparable between control and Atlastin mutants, and MG132 treatment produced a similar increase in ubiquitination in both genotypes, confirming both antibody specificity and normal proteasome activity. We then examined BiP:sfGFP:HDEL directly. In controls, MG132 caused the marker to accumulate at axons and presynaptic terminals, showing that it is normally cleared from these compartments by the proteasome. Critically, this accumulated marker remained associated with intact ER networks: MG132 did not induce diffuse cytosolic BiP:sfGFP:HDEL in any compartment (cell bodies, axons, or presynaptic terminals), even where levels rose substantially. Thus, blocking proteasomal clearance raises ER-localized marker but does not generate the cytosolic pool seen in Atlastin mutants, indicating that impaired clearance is not sufficient to cause the displacement phenotype. We separately noted that BiP:sfGFP:HDEL was already elevated in Atlastin mutant axons without MG132, paralleling the axonal tdTomato:Sec61β accumulation in Figure 4, consistent with reduced baseline clearance specifically in mutant axons, but this does not lead to cytosolic displacement. This experiment is now shown in Figure 11, described in Results (lines 445-475), and discussed in lines 576-581.

Minor comments:

Line 146:

"fast dynamics (Thank you for catching this mistake. We have corrected it.

Fig. 2D: The data representation of "Tubule displacement" image is unclear. The ER tubule indicated by the red arrow does not seem to show any changes over time (like static). time 0 in stamp appears behind the image.

Thank you for catching the typo. We have fixed it. Additionally, we added black arrows to highlight a tubule that is not moving, allowing the reader to compare it with the moving tubule. We also included a video of all types of ER tubule dynamics to ensure the reader can also look at the raw data (Movies S9-11).

• • Line 157-158 (and relevant method sections):

The definition of static and dynamic boutons is ambiguous. The author should describe in more detail this point including how long they observed the structure to define the changes in ER tubule dynamics.

We provide in the methods (lines 779-791) a detailed explanation of how we categorized boutons as dynamic or static. In addition, we added the following to explain in the results section how we defined static vs dynamic:

Old sentence: We qualitatively categorized boutons as "static" if we observed no change in ER network structure or "dynamic" if we observed at least one change.

New sentence in lines 143-147: "We imaged boutons for 40 sec at 0.92 sec intervals to capture ER dynamics over this observation period. Boutons were qualitatively categorized as "static" if we observed no detectable changes in ER network structure throughout the entire 40 sec imaging session, or "dynamic" if we observed at least one of the three defined dynamic events during this time window."

Fig. 2E: What n=75 and n=29 represent is unclear, are these the number of boutons in en passant and terminal subjected for qualitative analysis?

We removed these n values from the figure and added this information to the Supplementary Table 1, which contains detailed information about the genotype, statistical analysis, and number of larvae and NMJs analyzed.

Fig. 2: What the qualitative analysis represents is unclear, are the points pulled from different experiments?

The data in Fig. 2 E-F comes from movies acquired in the same experiment. The number of independent animals and NMJs imaged is described in Table 1.

* *Line 231: Regarding "...we found a small but significant reduction in dynamic boutons in Atlastin mutants (76%), ...", how do the authors assess significance. If proportion of static/dynamic ER in boutons was obtained from multiple experiments, it should be presented e.g. as in average {plus minus} standard deviation, or clarify that the proportion is representative of x independent experiments.

The videos used for this figure were acquired from a single experiment. We use a chi-square test to determine significance relative to the "expected" distribution of dynamics types from controls, as these are categorical rather than continuous data (see PMID 31145670). Information regarding genotype, statistical analysis and number of larvae and NMJs can also be found in Supplementary Table 1.

Line 267-269 and Fig. 6B: The author's conclusion that "Complete loss of ER network structure in NMJ of BiP:sfGFP:HDEL overexpressing Atl mutant" seem to be based on the lack of signal from luminal marker, which may be undetectable due to changes to tubular volume or marker loss to the cytoplasm, as suggested by the authors, while the membranous ER structure is intact. It would be useful to discuss this point and potentially add ER membrane-stained control.

We agree with the reviewer that Atlastin mutants categorized as 'complete loss mutants' do not actually lack ER at synapses. We think this is an important point so we added the following to the results in lines 251-254: "Note that the "Complete loss" phenotype in Atlastin mutants reflects the absence of detectable luminal marker signal in organized ER structures, not the complete absence of ER membranes, as demonstrated by our ER membrane marker tdTomato:Sec61β results."

We attempted to co-label the ER membrane and ER lumen, but these crosses yielded very few live larvae (in either controls or Atlastin mutants, and those that survived had severely deformed NMJs. We added Figure 6-Supplement showing the results of this experiment, and described them on lines 270-273.

Fig. 6C: In Atl mutant, why does the total of the proportion exceed 100% (10 + 45 + 55)?

The reviewer noted that the summed percentage of the three phenotypic categories in Figure 6C adds up to 110% for Atlastin mutants. This is not an error, but rather a reflection of our quantification methodology because a single bouton can exhibit more than one type of ER dynamics per movie recorded. Our quantification counts each phenotype independently, so boutons displaying multiple phenotypes contribute to more than one category. This approach provides a more comprehensive view of the range of ER dynamics present in Atlastin mutants, as restricting the analysis to mutually exclusive categories would underrepresent the complexity of the phenotypes observed. To make this point clear, we made the following change to the text in lines 257-259: "We note that the sum of these percentages exceeds 100% because one NMJ exhibited multiple phenotypes: one branch had a complete loss, while the other branch had no phenotype. These phenotypes were counted separately."

Fig. 9C, line 342-344: In FRAP experiment using CD8, it seems that the Partial loss Atl mutant shows slower recovery that control. There seems to be a mismatch in triangle symbols of Partial loss Atl mutant between legend and plot (one is filled and the other is empty). This should be clarified.

Thank you for catching this mistake. We have fixed the figure.

fig. 10 is a clever way to verify the cytoplasmic localization of the ER marker; however, its description and annotation can be improved, and it would be stronger if 4 curves in F for mutant and controls with the trap and normal were shown.

The reviewer suggested merging our graphs but we believe that keeping them separate is clearer.

Line 495: Drosophila have ReepA and ReepB, but not Reep1-4. If the authors discuss their speculation based on their observation (using Drosophila), the gene names should be unified in the same species, and explain the corresponding genes to mammalian cells.

We made the following changes to address the reviewer's concern about gene nomenclature consistency (lines 502-506): "These ER-derived vesicles are likely to involve ReepA and ReepB, the Drosophila orthologs of mammalian REEP1-4, which regulate ER vesicle formation in mammalian cells (67). Notably, while overexpression of Atlastin can regulate REEP vesicle fusion in mammalian systems (67), it is not essential for vesicle formation, suggesting similar regulatory relationships may exist between Atlastin and Reep genes in Drosophila."

Line 548; should UPR be Unfolded Protein Response?

Thank you for catching the typo. We have fixed it.

Reviewer #3 (Significance (Required)):

This study advances the understanding of how ER morphogens affect neuronal cells specifically, the lack of which limits researchers ability to comprehend the neuronal pathologies associated with ER structure-function. The observation on ER content aberrant localisation caused by the lack of key structural protein should be of a great interest for cell and neuronal biologists and researchers of the associated diseases and shows the field a new direction. Though, mechanistic details remain to be unraveled, it constitutes a fundamental, conceptual advance.

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

Learn more at Review Commons

Referee #3

Evidence, reproducibility and clarity

In this manuscript, the authors investigate the structural dynamics of the endoplasmic reticulum (ER) in Drosophila neurons and examine the role of the ER-shaping protein Atlastin in ER morphology. Their discovery on the neuromuscular junction (NMJ)-specific contribution of Atlastin to ER integrity is intriguing and may provide valuable insights into the pathological mechanisms underlying Atlastin mutations associated with hereditary spastic paraplegia (HSP) and hereditary sensory neuropathy. The key observation on ER protein showing an aberrant cytoplasmic localisation in mutant cells appears convincing. Though this phenomenon's characterisation stays at the point of primary observation with its mechanics unclarified, establishing this new and unexpected functional rather than structural Atl effect is important and useful for the field. The observation that ER is structurally preserved in this mutant with absolute lack of Atl are also extremely useful.

It is unclear if the cytoplasmic localisation affects an exogenous overexpressed ER marker or endogenous protein would also appear in cytoplams, the authors should consider adding an immunostaining data to test that.

Authors offer speculations on potential reasons for the cyto localisation of the ER marker suggesting that relocation at the cell periphery specifically combined with slow clearance there is the most likely explanation (still unclear what stops the marker from spreading through the entire cell). They suggest that decrease in cotranslational translocation is unlikely as this would result in somatic accumulation of the marker. However, if the clearance in the periphery is less efficient than in soma, the accumulation there might reflect a compromised translocation. Any clarifying experiments, if practical, to directly demonstrate how ER proteins in relocates to the cytoplasm in atl mutant would help understanding better the phenomenon. For example, would proteasomal inhibition make the marker accumulate more across the cell? Authors also suggest links to ER stress. Would stress induction phenocopy the mutant?

Minor comments:

Line 146: "fast dynamics (<1 sec)" a velocity should be presented as distance/time

Fig. 2D: The data representation of "Tubule displacement" image is unclear. The ER tubule indicated by the red arrow does not seem to show any changes over time (like static). time 0 in stamp appears behind the image.

Line 157-158 (and relevant method sections): The definition of static and dynamic boutons is ambiguous. The author should describe in more detail this point including how long they observed the structure to define the changes in ER tubule dynamics.

Fig. 2E: What n=75 and n=29 represent is unclear, are these the number of boutons in en passant and terminal subjected for qualitative analysis?

Fig. 2: What the qualitative analysis represents is unclear, are the points pulled from different experiments?

Line 231: Regarding "...we found a small but significant reduction in dynamic boutons in Atlastin mutants (76%), ...", how do the authors assess significance. If proportion of static/dynamic ER in boutons was obtained from multiple experiments, it should be presented e.g. as in average {plus minus} standard deviation, or clarify that the proportion is representative of x independent experiments.

Line 267-269 and Fig. 6B: The author's conclusion that "Complete loss of ER network structure in NMJ of BiP:sfGFP:HDEL overexpressing Atl mutant" seem to be based on the lack of signal from luminal marker, which may be undetectable due to changes to tubular volume or marker loss to the cytoplasm, as suggested by the authors, while the membranous ER structure is intact. It would be useful to discuss this point and potentially add ER membrane-stained control.

Fig. 6C: In Atl mutant, why does the total of the proportion exceed 100% (10 + 45 + 55)?

Fig. 9C, line 342-344: In FRAP experiment using CD8, it seems that the Partial loss Atl mutant shows slower recovery that control. There seems to be a mismatch in triangle symbols of Partial loss Atl mutant between legend and plot (one is filled and the other is empty). This should be clarified

fig. 10 is a clever way to verify the cytoplasmic localisatoin of the ER marker, however its description and annotation can be improved, and it would be stronger if 4 curves in F for mutant and controls with the trap and normal were shown.

Line 495: Drosophila have ReepA and ReepB, but not Reep1-4. If the authors discuss their speculation based on their observation (using Drosophila), the gene names should be unified in the same species, and explain the corresponding genes to mammalian cells.

Line 548; should UPR be Unfolded Protein Response?

Significance

This study advances the understanding of how ER morphogens affect neuronal cells specifically, the lack of which limits researchers ability to comprehend the neuronal pathologies associated with ER structure-function. The observation on ER content aberrant localisation caused by the lack of key structural protein should be of a great interest for cell and neuronal biologists and researchers of the associated diseases and shows the field a new direction. Though, mechanistic details remain to be unraveled, it constitutes a fundamental, conceptual advance.

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

Learn more at Review Commons

Referee #2

Evidence, reproducibility and clarity

Summary

The endoplasmic reticulum (ER) is a continuous organelle that extends throughout neurons to regulate fundamental processes. The analysis of ER dynamics at synaptic terminals is limited by the challenge of imaging these structures at high resolution. In this manuscript, the authors use super-resolution (~170 nm) live imaging and a combination of membrane and luminal ER markers at the Drosophila larval NMJ, an important model synapse, to investigate dynamic ER architecture in vivo. They report a detailed characterization of the presynaptic ER organization and dynamics at wild-type and GTPase Atlastin mutant NMJs. Their analysis using the ER membrane marker tdTomato:Sec61b reveals the presence of an intact ER network in Atlastin mutants. This contrasts with the apparent ER fragmentation phenotype previously reported and replicated here when using a luminal marker. Their findings instead point to the progressive displacement of luminal proteins to the cytosol in Atlastin mutants specifically at synapses. The authors propose that the disruption of ER protein dynamics at synapses is a compartment-specific ER stress response. The manuscript is well written, results are clearly presented, and experiments are technically rigorous.

Major comments

1. The baseline ER phenotypes in Atlastin mutants are mild with complete loss of ER network only observed in terminal boutons. This interesting and unexpected result should be further confirmed by genetic rescue. The authors can use a UAS rescue line previously reported in PMID: 19341724.
2. Lines 204-7: It's not clear how a greater coefficient of variation indicates that the marker is more concentrated in subsynaptic structures or what is meant by 'subsynaptic structures.'
3. There's a mistake in Figure 6C and the associated text. The summed percentage of the three phenotypic categories adds up to 110% for Atlastin mutants.
4. Figure 8: the ER looks fragmented in 1st instar controls and mutants. The authors should address this difference from more mature NMJs.
5. The images in figure 9B do not seem representative of the quantification in Figure 9D. Specifically, the partial loss Atlastin NMJ appears to have recovered as fully as the complete loss Atlastin NMJ.
6. Optional: An overexpressed luminal marker is displaced to the cytoplasm in Atlastin mutants. It would be interesting to know and increase the significance of the findings if the same is true of endogenous luminal proteins under biological stress conditions.
7. Optional: Applying this approach in stimulated conditions (high potassium, increased temperature) might reveal a greater activity-dependent role for Atlastin at synaptic terminals.

Minor Comments

1. Line 16: Atlastin should be italicized.
2. Figure 5A: Based on the relative intensities, it appears that control and mutant images are not contrast matched but this isn't stated.
3. Line 822: The number of static Atlastin mutant boutons used for analysis is missing.
4. Figure 9: The blue arrows are not annotated in the figure legend.

Significance

Atlastin is linked to Hereditary Spastic Paraplegia (HSP) and this study changes our understanding of the compartment-specific impacts of its loss. This study reveals the importance of using both membrane and luminal ER markers to accurately interpret phenotypes as well as the importance of considering compartment-specific effects on ER. These findings represent significant mechanistic and conceptual advances. The lack of genetic rescue is a limitation and adding an investigation of an endogenous luminal protein under basal and stress conditions would add significantly to our understanding of Atlastin dysfunction in HSP. Notably, the in vivo imaging approach introduced here can be adapted broadly for live imaging of Drosophila larvae. Thus, this work will be of interest to both neuronal cell biologists and the wider Drosophila community. This review is based on our expertise in neuronal cell biology.

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Referee #1

Evidence, reproducibility and clarity

In the present manuscript, the authors address an important question related to the ultrastructure and the dynamics of the ER in HSP. In contrast to previous studies, the authors here show (by using a membrane and luminal protein markers) that in the presynaptic terminals, the overexpressed BIP "mislocalizes" to the cytosol without affecting (or with minimal effect) the integrity of the ER membrane. Although they used an artificial system by overexpressing (overexpression) of BIP-sfGFP-HDEL (fused protein), the findings lack validation of the endogenous protein by biochemical and fluorescent tools.

Concerns:

I am worried about how the article is presented, mainly in the results section, as most of it refers to published data. The Results section is reserved for presenting new findings without external interpretation or comparison. The paper is written mainly as a comparison paper with other studies or relies on previous studies to strengthen their findings rather than coming up with novel findings. Up to figure 4, I missed the relevance of the new findings. The manuscript needs rewriting to emphasize its novelty and significance without comparing it to previous data. Moreover, the manuscript emphasizes the technology and the findings of the localization of the ER luminal proteins to the cytosol (which is not novel and was previously reported in other settings). Those two aspects were not given enough focus. Here are the main major and minor comments:

Major comments:

1. Lines 103-116 (first paragraph of the results section) describe mainly published data that is more suitable for the introduction section. It is annoying to refer to different published articles in the Results section to strengthen the results instead of showing them. The same goes for paragraphs two and three. Why mention those data in the Results section if they are already published and known?
2. Figure Legends-(in all Figures): The number of experimental repeats must be mentioned in the figure legends.
3. The way the figures are labeled is worrisome; supplementary figures are not ordered numerically.
4. The tubule extension in Figure 2D is not convincing. Is there a movie showing those changes? Better images are needed. It is essential to show which supplemental movie corresponds to which panel.
5. This is unnecessary in the results section: "To investigate the relationship between ER structure and function at synapses, we examined mutants of Atlastin, a GTPase that regulates ER tubule fusion. Drosophila has a single homolog while mammals have three Atlastin homologs, with Atlastin-1 enriched in the brain (Rismanchi et al., 2008)."
6. "This reduction in ER membrane marker intensity has also been observed in other HSP mutants, suggesting this is a common feature of ER shaping mutants and could indicate changes in ER membrane composition, integrity, or tubule thickness (P.rez-Moreno et al., 2023)." This comparison is important and should be shown in the same settings as for the Atlastin mutant rather than referring to published data.
7. Does the distribution of the luminal ER marker in Figure 6F diffuse due to mislocalization or reflux after being localized to the ER and then refluxed to the cytosol as was previously shown for the ER to Cytosol signaling (ERCYS) mechanism? Could you assess other ER-luminal protein localization biochemically? It is highly recommended to look at another soluble ER-protein localization in the Atlastin mutant without overexpression, which can be an artifact
8. "(data not shown)" in line 288. This affects the process of judging those data.
9. In comparison to Summerville et al. (2016) in Figure 7, the experiment was not done in the same way. It is important to keep the same settings for comparison
10. Does the Atlastin mutant induce the unfolded protein response and stress within the ER? It is necessary to look for UPR markers in those settings. It was shown previously that ER stress leads to protein reflux from the ER to the cytosol. Is there a difference in the ER stress markers in the presynaptic terminal?
11. It is important to add biochemical experiments to show that no fragmentation of the ER membrane occurred. It can be simply demonstrated by looking at the redox state of the ER, which would change if it were mixed with the reducing cytosol. Moreover, this can be shown by using an ER-targeted redox-sensitive fluorescent protein that is tethered to the ER membrane to follow changes in the redox state of the ER.

Minor comments:

1. It is important to call figures by order. Figure 2C is called before 2A-B. Figure 2B is called before Figure 2A.
2. Figure legends (Figure 2): "The same control dataset used in E-G was used in Figure 5 and Figure 5_Supplement." Why is this relevant?
3. Figure 4F is called before Figure-4D-E which are not called.
4. Figure 5B is called before the previous ones. Same for Figure 5A supplement.

Referees cross-commenting

I agree with the comments raised by reviewer2 and 3. Basically it is highly important to validate those data by genetic rescue. Moreover, it is essential to know the source of the displaced luminal marker to the cytosol. Is it mislocalization or it is a reflux of pre-existing protein to the cytosol after insertion to the ER. It is also recommended by me and the reviewers to test the endogenous protein rather than overexpression.

Significance

General assessment: This interesting paper shows that proteins can escape the ER under special conditions. However, the authors need more evidence to show that and rely less on the overexpression system, especially of BIP-GFP, which can cause proteostasis stress within the ER.

Advance: The results have been oversimplified in their explanations, and some points and complexities of the study need to be addressed further to make the most of them. These are often some of the more interesting concepts in the paper. I think many points can be addressed in the text by the authors being clear and concise with their reporting. At the same time, other experiments would turn this paper from an observational one into a very interesting mechanistic one. This paper is based on previously published articles from the group and other groups, and it is a nice progression. However, as mentioned, this paper depends primarily on published data, and the novelty is somehow lost between all the comparisons to other published data instead of emphasizing that. Without a substantial mechanistic improvement, the paper would remain observatory.

Audience: The microscopy tools can be great addition to researchers in the field to monitor protein trafficking especially Cell biologists (basic research)

My expertise: ER homeostasis, protein trafficking, cell biology

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Reply to the reviewers

1. __ General Statements__ We thank the reviewers for their thoughtful and constructive evaluations of our work. We are particularly encouraged that both recognize the value of this study as a scalable and systematic framework for the functional exploration of the human KZFP family and agree that the resource generated here will be of broad interest to the KZFP, transposable element, and genome regulation communities. Reviewer 1 explicitly notes that "the screening framework itself represents a potentially useful resource for prioritizing candidate KZFPs for downstream study" and that "the study may nonetheless serve as a useful starting point for future investigations into KZFP biology and transcriptional regulation." Reviewer 2 similarly emphasizes that "the authors provide an efficient and valuable screening platform that can identify promising candidates for further investigation" and that "the methodological advance represents the primary contribution of the work."

We can only concur with these assessments. The principal goal of this study was not to elucidate the physiological roles of all or even a subset of individual KZFPs, but rather to provide a scalable framework that enables their systematic prioritization and generates experimentally testable hypotheses regarding their functions. To support our argument, we ventured into some mechanistic analyses, but these could not pretend to be complete and definitive. In that respect, we hear the reviewers when they note that the original manuscript does not always sufficiently distinguish candidate discovery from mechanistic validation. In its revised version, we will therefore more clearly frame the inducible K562 overexpression assay as a standardized and sensitive readout of regulatory potency rather than as a direct surrogate of physiological function. Within this framework, K562 fitness defects are interpreted as a quantitative measure of the extent to which ectopic KZFP expression perturbs transcriptional homeostasis in a controlled cellular context, while the direct targets and transcriptional networks identified through our integrative analyses are presented as hypotheses to be tested in more physiologically relevant systems. Accordingly, the revised manuscript preserves the broad scope and resource aspect of the study while incorporating additional experimental validation, expanded methodological descriptions, and a more cautious interpretation of the proposed biological functions of the selected KZFPs.

__Although this document is submitted as a Revision Plan, we have already incorporated a substantial number of revisions into the transferred manuscript. In particular, we have implemented most of the presentation, methodological, and conceptual modifications requested by the reviewers, including clarification of the scope of the study, extensive revisions of the Results and Discussion, expanded Materials and Methods, and numerous figure and text corrections. These revisions are detailed in Section 3 ("Description of the revisions that have already been incorporated into the transferred manuscript"). __

The remaining points requiring additional experimentation or more extensive analyses are described in Section 2 ("Description of the planned revisions").

__ Description of the planned revisions__

Reviewer 1 Major comment 1

“Finally, several aspects of the data presentation are currently difficult to reconcile. In Fig. 1D, the meaning of the purple category is unclear, and the percentage scaling on the x-axis is difficult to reconcile with the cumulative values displayed. For instance, the sum of all the bars would not reach 100%, as the values of the bars span percentages up to 4% at most (for 105 MYO KZFPs) according to this plot. Similarly, the reported numbers of TE-binding KZFPs in Fig. 1E-F and Fig. S1D appear internally inconsistent and should be clarified. Specifically, 53+14=67 KZFPs are reported to bind TEs in total, yet a larger number of KZFPs appears associated with individual TE families (e.g., 86 for LTR.ERV1). If the values shown correspond to percentages rather than absolute counts, this should be explicitly clarified in both the figure and legend. In addition, Fig. S1D appears inconsistent with the counts reported in Fig. 1E-F, as only 5 out of the 53 toxic KZFPs displayed in the plot show no enrichment for any of the highlighted TE families.”

We thank the reviewer for this insightful comment, which has helped us identify areas where the presentation of our data can be substantially improved. We agree that the current presentation of the TE-binding analyses could be clearer and that revising these figures will improve both their readability and the overall consistency of the manuscript. In the revised manuscript, we will clarify the apparent inconsistencies in the presentation of the TE-binding KZFP analyses and revise the corresponding figures and legends accordingly. Importantly, these inconsistencies do not arise from errors in the underlying data but rather from an insufficient explanation of the statistical enrichment analyses and the way the results are represented. We will therefore redesign the relevant figures and expand their legends to more clearly describe the analytical approach, the enrichment criteria, and the interpretation of the results. We believe that these revisions will improve the clarity, transparency, and internal consistency of the manuscript, allowing readers to more readily interpret the TE-binding analyses. Minor comments of the reviewer 1 were extremely useful to detect mistakes and we are grateful for that. All the modifications that were asked see below were included in the manuscript.

Reviewer 1 Major comment 2

“Finally, while the proteomics results aimed at identifying SCAN-dependent interactors are of interest, several aspects of the experimental design and data analysis remain unclear. In particular, it is not specified whether the experiment was performed in biological replicates or as a single measurement. This is important, as it directly affects how the data can be interpreted and how stringent downstream filtering can be. In the Results section, the authors state that "we identified a set of SCAN-dependent interactors, i.e., proteins that co-immunoprecipitated with the full-length construct but were absent in controls and lost upon deletion of the SCAN domain," which suggests a relatively binary, "presence/absence" filtering strategy. However, this description does not specify whether any quantitative threshold (e.g., enrichment ratio) was applied when comparing full-length constructs to deletion mutants. In contrast, the Methods section states that "proteins lacking signal above background were excluded and proteins were additionally required to show stronger signal in at least one bait condition than in GFP controls based on heatmap clustering (see script)," which instead suggests that a threshold-based criterion was used to define enrichment relative to controls and deletion mutants. If this is the case, the exact criteria and thresholds used for filtering should be clearly stated and consistently reported between the Results and Methods sections. If replicate measurements were not performed, this should be explicitly acknowledged, as peptide-level variability may substantially influence the identification of high-confidence interactors, particularly if the applied cutoffs are not highly stringent.”

We agree that a more detailed description of the experimental design and analysis strategy, together with additional validation, will strengthen the interpretation of the proteomic data. In the revised manuscript, we expanded the Results and Materials and Methods sections to provide a clearer and more quantitative description of the filtering strategy, including the enrichment criteria and thresholds used to define SCAN-dependent interactors. To further strengthen these findings, we propose to perform an independent biological replicate of the co-immunoprecipitation mass spectrometry experiment. This additional experiment will increase confidence in the identified SCAN-dependent interactors and further support the conclusions drawn from the proteomic analysis.

Reviewer 1 Minor comments

• In Fig. 2A, readability could be improved by adjusting the layering of points, as the darker dots (in particular the red ones) are currently obscured by lighter ones. Alternatively, removing the outline of the points (which is not transparent) may also improve visibility, but in that case the legend for point size would need to be updated accordingly.

Thank you for this helpful suggestion. We will revise Figure 2A to improve its readability by reworking the layering of the points in accordance with the reviewer's recommendation. We will also evaluate the point outlines and, if appropriate, remove them and update the point-size legend accordingly to ensure the figure is clear and easy to interpret.

Reviewer 2 – Major comment

“- The authors looked at available chromatin data in either K562 cells or HEK293 cells, which I think is a very good way of utilizing publicly available data. Since the authors showed that different KZFPs might be functionally relevant in different cell types/tissues, I was wondering if they checked if there is available ChIP Seq or CUT&RUN data in those specific cell types/tissues. If yes, that data should be included in the manuscript.”

We agree that integrating KZFP binding data generated in biologically relevant cell types or tissues would further strengthen the proposed regulatory models. As described in the revised manuscript, we have already adopted this approach for ZNF43 by integrating chromatin landscape data from thymus and liver, where suitable datasets were available.

To further address this point, we propose to systematically explore publicly available ChIP-seq, CUT&RUN, CUT&Tag, and related chromatin profiling datasets for the other KZFPs investigated in this study. Where suitable datasets are available, these analyses will be incorporated into the revised manuscript to further support the proposed tissue-specific regulatory models and provide additional biological context for the identified target genes.

__ Description of the revisions that have already been incorporated in the transferred manuscript__

Reviewer 1 Major comment 1

“The large-scale overexpression screen represents the foundation of the manuscript and provides a potentially valuable resource for prioritizing candidate KZFPs for downstream study. However, several aspects of the experimental setup and data presentation currently limit the interpretation of the reported proliferation defects. First, key details regarding the screening workflow remain unclear. While the Methods section describes the overall procedure, it is difficult to determine when cells were seeded relative to doxycycline induction, in which plate format the cells were maintained throughout the experiment, and whether medium exchange was performed during the 9-day assay. These points are particularly relevant given the use of suspension K562 cells (which can complicate medium exchange in a 96-well plate format and make long-term culture more difficult to control) and a metabolic viability readout (PrestoBlue), as differences in nutrient depletion or overgrowth could also influence the signal independently of reduced proliferation or toxicity. Additional clarification regarding seeding density, timing of induction, plate format, culture handling throughout the assay, and whether cell morphology/density was visually monitored would substantially improve interpretability and reproducibility. Second, it is unclear whether the observed proliferation phenotypes may be influenced by differences in transgene expression levels or integration effects. Were all constructs validated for comparable expression following induction? In the absence of such controls, it remains difficult to determine whether the reported phenotypes reflect specific KZFP activities or differences in overexpression efficiency. While it may not be possible to conclusively distinguish KZFP-specific effects from toxicity associated with high transgene expression levels, this limitation should at least be acknowledged. In addition, the possibility that some phenotypes may be influenced by transgene integration effects should also be considered. Unless independent transductions were validated for the KZFPs classified as toxic, it remains difficult to exclude integration-site-specific contributions to the observed proliferation defects. Third, the normalization strategy would benefit from additional clarification. In Fig. S1A, the LacZ control appears variably affected by doxycycline treatment across plates, whereas the GFP control appears more stable. Since normalization relies on the mean behavior of both controls within each batch and condition, the authors should clarify whether this variability could influence hit calling.”

We agree that additional methodological details improve the clarity and reproducibility of the screening assay. Accordingly, we substantially expanded the Materials and Methods section to describe the experimental workflow, quality controls, data normalization, and hit-calling criteria. The revised paragraph is reproduced below.

Arrayed overexpression screen

To systematically assess the effect of human KZFP overexpression on cellular fitness, K562 cells were individually transduced with doxycycline-inducible lentiviral vectors encoding 366 human KZFPs. Lentiviral particles were produced as described above and used to transduce cells without MOI calculation. __Instead, a fixed volume of viral supernatant (200µL per × 104 cells in 48 well plate filled with 200ul of RPMI) was used for all transductions to ensure comparable experimental conditions. Transduced cells were selected with puromycin before doxycycline induction. Following puromycin selection (1µg/mL for 3 days), cells were seeded at 20 000 cells per well in 24-well plates filled with 1ml of medium in technical triplicate for each KZFP. Following puromycin selection and prior to doxycycline induction, cell survival was visually assessed as a quality control metric for each KZFP construct (Supp __Table 2____). Doxycycline (1µg/mL) was added immediately after cell seeding to induce expression of the HA-tagged KZFPs. At each time point, metabolic activity was measured using PrestoBlue™ reagent according to the manufacturer's instructions (10µL reagent added to 100µL culture medium, incubated for 3h in a 96 plates). Absorbance was recorded at 570 nm and 600 nm using a plate reader (Hidex Sense Microplate Reader), GFP- and LacZ-expressing control wells were included on every plate to account for plate-to-plate and batch-to-batch variability. Peripheral wells were filled with culture medium to minimize evaporation-induced edge effects. Cells were maintained in RPMI supplemented with 10% fetal bovine serum (FBS) and 1× penicillin–streptomycin, and splited (1/10) with aspiration of the surface medium every three days throughout the assay while maintaining doxycycline at 1µg/mL. Cell proliferation was assessed after 4, 7, and 9 days of induction. and the A570/A600 ratio was used as a surrogate measure of viable cell number and proliferative capacity. For computational normalization, raw A570/A600 values were first background-corrected by subtracting the signal from medium-only controls and then normalized in two steps. First, each value was divided by the mean signal obtained from the GFP and LacZ control wells from the corresponding batch and induction condition to correct for inter-batch variability. Second, the resulting value was normalized to the corresponding −Dox condition for the same KZFP and time point to correct for seeding variability, yielding a relative proliferation score that reflects the effect of KZFP induction. KZFPs with a normalized proliferation score ≤ 0.85 at day 9 were arbitrarily classified as proliferation-impairing hits in this screening framework.

After doxycycline induction, dot blot analysis using anti-HA and anti-actin antibodies was systematically performed to assess KZFP expression and sample loading, respectively (Supplementary DotBlot.pdf). The HA signal following doxycycline induction (HA_Dox) and actin signal following doxycycline induction (Actin_Dox) were visually scored from the dot blot signals (__Supp __Table 2).

In addition, to strengthen the methodological description and address these concerns more directly, we will:

1/ Include a supplementary table summarizing our experimental observations for each individual KZFP throughout the screening process (See preliminary Supp Table 2). -> See header here:

2/ Perform and include Dot Blot analyses, to assess and compare transgene expression levels across KZFP constructs. (Supplementary File DotBlot.pdf____). Generation of these files is in progress, with a few missing dot blots still being completed (we have done 303 over 366 already). However, preliminary versions have already been submitted. -> See header of the .pdf here:

In addition, we agree that a more explicit discussion of the limitations of our screening approach improves the interpretation of our findings. Accordingly, we expanded the Discussion to address the limitations associated with variable transgene integration, heterogeneous transgene expression, potential toxicity due to ectopic KZFP overexpression, and the use of K562 cells as a standardized rather than physiological cellular model.

“Several methodological considerations should be taken into account when interpreting these results. As with any lentiviral overexpression screen, three potential sources of technical variability may influence the observed phenotypes: differences in transgene integration sites, heterogeneity in transgene expression levels, and non-specific toxicity resulting from ectopic overexpression. Variable integration sites are unlikely to represent a major source of bias in the present study because all analyses were performed on polyclonal populations of transduced cells rather than individual clones, thereby averaging integration-site effects across many independent events. In contrast, heterogeneity in transgene expression levels is expected, as the abundance of each KZFP depends not only on transduction efficiency but also on intrinsic differences in mRNA stability, translational efficiency, and protein stability. To minimize these sources of variability, all constructs underwent systematic quality control, including assessment of cell survival following puromycin selection and evaluation of transgene expression by HA dot blot after doxycycline induction. Although transgene expression levels varied across KZFPs (Supplementary File DotBlot.pdf), this variability showed no systematic relationship with the proliferation phenotypes, suggesting that differences in overexpression efficiency are unlikely to be the primary determinant of toxicity. Nevertheless, ectopic expression exposes cells to supraphysiological concentrations of KZFPs capable of generating non-physiological interactions or regulatory effects. Therefore, while the screening strategy is well suited for identifying candidate functional regulators, independent validation under endogenous expression conditions remains essential to confirm KZFP-specific functions.”

Reviewer 1 Major comment 2:

“A central conceptual issue throughout the manuscript is that the downstream functional analyses of the selected KZFPs remain largely disconnected from the original screening phenotype. The four candidates were prioritized based on proliferation defects observed upon overexpression in K562 cells; however, the subsequent analyses (with the only exception being a more in-depth experimental analysis of ZNF498 in ciliogenesis, which stands out as comparatively more directly supported by experimental evidence) primarily rely on correlative expression patterns and KZFP ChIP-seq datasets to infer potential biological functions in unrelated cellular contexts. As a result, it remains unclear whether the proposed transcriptional programs are mechanistically linked to the proliferation phenotypes that motivated candidate selection in the first place. This issue is evident across multiple sections of the manuscript. For example, the proposed role of ZNF43 in regulating fatty acid metabolism and detoxification pathways is primarily inferred from tissue-level expression correlations. While these analyses focus on genes identified as potential ZNF43 targets, the underlying ChIP-seq datasets were themselves generated under ZNF43 overexpression conditions. Therefore, the current analyses do not establish whether ZNF43 regulates these pathways under physiological expression levels or within a relevant cellular context, nor how such regulation relates to the proliferation defect observed in K562 cells. Moreover, several proposed target genes remain substantially expressed in tissues where ZNF43 expression is not particularly low (e.g., kidney and heart muscle), suggesting that additional regulators are likely involved. Similarly, the proposed model of ZNF257-mediated regulation of MAGEA genes during spermatogenesis is intriguing but does not fully account for the expression behavior of all MAGEA family members, particularly MAGEA2B, which displays strong expression in spermatocytes despite high ZNF257 expression. This expression pattern should be acknowledged in the main text and reflected in Fig. 3K. In addition, the labels for MAGEA6 and MAGEA2B in Fig. 3C appear to be inverted. More broadly, the proposed regulatory model is difficult to reconcile with the generally restricted expression pattern of MAGEA genes across adult tissues, as their expression does not appear to consistently correlate with ZNF257 levels outside the germline context. Related concerns also apply to the analyses of ZNF498 and ZNF18, where the proposed functions in cilium formation and sperm maturation remain disconnected from the proliferation defects identified in the initial screen.”

We agree that this comment raises an important conceptual point and has helped us clarify the scope of the study and the interpretation of our findings. In the revised manuscript, we explicitly distinguish hypothesis generation from mechanistic validation by clarifying that the proliferation phenotype observed in K562 cells reflects the regulatory potential of ectopically expressed KZFPs rather than their physiological functions. We also adopted a more cautious interpretation of the functional analyses, emphasizing that the proposed regulatory networks are hypothesis-generating and that individual KZFPs are unlikely to act as sole regulators. More broadly, we emphasize that the primary objective of this study is to establish a scalable screening platform for prioritizing KZFPs and identifying biologically relevant contexts for future investigation, rather than to provide a comprehensive functional characterization of individual KZFPs. We agree that this comment highlights an important limitation of our proposed regulatory model. In the revised manuscript, we adopted a more nuanced interpretation by presenting ZNF257 as a contributor to, rather than the sole regulator of, the MAGEA transcriptional program, and by explicitly discussing the exceptions identified by the reviewer.

Modification in the revised manuscript:

1/

“Integrative transcriptomic, chromatin and proteomic analyses reveal diverse mechanisms, including transposable element–linked repression (ZNF43), promoter-proximal regulation (ZNF257), and SCAN domain–dependent transcriptional activation (ZNF498/ZSCAN25 and ZNF18).”

Is now:

“Integrative transcriptomic, chromatin and proteomic analyses identify distinct regulatory properties and generate testable hypotheses regarding diverse mechanisms, including transposable element-associated repression (ZNF43), promoter-proximal regulation (ZNF257), and SCAN domain-dependent transcriptional activation (ZNF498/ZSCAN25 and ZNF18).”

2/

“Detailed follow-up of four such candidates, ZNF43, ZNF257, ZNF498 and ZNF18, revealed as hypothesized distinct modes of action, ranging from TE-linked transcriptional repression to promoter-proximal gene silencing and SCAN domain-mediated transcriptional activation. These findings reinforce the view that KZFPs, while often viewed as a homogeneous family of TE-repressive TFs, are rather functionally diverse regulators with wide-ranging impacts on human biology.”

Is now:

“Detailed follow-up of four such candidates, ZNF43, ZNF257, ZNF498 and ZNF18, identified distinct regulatory properties and generated hypotheses regarding their physiological functions. By integrating overexpression-induced transcriptional responses, chromatin occupancy, proteomic analyses and tissue-specific expression data, we propose candidate biological contexts in which these KZFPs may operate. These hypotheses now provide a framework for future mechanistic studies performed under physiological conditions. Together, these findings reinforce the view that KZFPs, while often viewed as a homogeneous family of TE-repressive transcription factors, comprise functionally diverse regulators with broad potential roles in human biology.”

3/

“We conclude from these data that ZNF43 regulates a transcriptional program related to fatty acid metabolism and detoxification, allowing for the preferential expression of its effectors in the liver (Fig. 2G). Interestingly, neither expression nor chromatin state followed the same pattern at the functionally unrelated DNAI4 locus, indicating that this gene is subjected to other dominant regulators.”

Is now:

“Together, these observations identify a small set of candidates ZNF43 target genes involved in fatty acid metabolism and detoxification and suggest that ZNF43 may contribute to the regulation of these transcriptional programmes in appropriate physiological contexts (Fig. 2G). However, these conclusions are derived from overexpression-based datasets and tissue-level expression analyses and should therefore be considered hypothesis-generating. Interestingly, neither expression nor chromatin state followed the same pattern at the functionally unrelated DNAI4 locus, indicating that additional regulatory mechanisms contribute to the control of these genes.”

4/

“It strongly suggests that ZNF257 contributes to initiating the transcriptional repression of these two MAGEA genes during early spermiogenesis, after which their silencing may be stabilized through stable epigenetic mechanisms such as DNA methylation.”

Is now:

“These observations suggest that ZNF257 may contribute to the initiation of transcriptional repression of a subset of MAGEA genes during the spermatogonia-to-spermatocyte transition, after which their silencing may be stabilized through epigenetic mechanisms such as DNA methylation.”

5/

“Together, these results identify ZNF498 as a transcriptional activator of gene modules controlling cytoskeleton-dependent processes and suggest that this TF may act as a regulator of neuronal cytoskeletal architecture, warranting investigation in relevant neural models.”

Is now:

“Together, these results indicate that ZNF498 functions as a transcriptional activator in our overexpression system and support the hypothesis that it contributes to transcriptional programmes controlling cytoskeleton-dependent processes in physiologically relevant neural contexts, warranting further investigation in dedicated neural models.”

6/

“The co-expression of ZNF18 and its target genes at the spermatid stage suggests that ZNF18 activates a transcriptional program supporting these processes.”

Is now:

“The co-expression of ZNF18 and its candidate target genes at the spermatid stage is consistent with the hypothesis that ZNF18 contributes to transcriptional programmes supporting these processes.”

7/

“The four KZFPs characterised here illustrate this diversity. ZNF43 represses a coherent set of genes involved in fatty acid metabolism and detoxification through binding to nearby LTR/ERV1 integrants, with its expression anticorrelating that of its targets: i.e., highly expressed in thymus and bone marrow, where these metabolic genes are silent, and lowly expressed in liver, where they are most active. This represents a clear example of host genomes coopting TE-derived sequences and shaping their regulatory activities in a cell-type specific manner by the differential expression of KZFPs. ZNF257, by contrast, acts as a promoter-proximal repressor whose targets show accelerated sequence evolution at their promoters, consistent with integration into a KZFP-orchestrated GRN through rapid promoter diversification, a feature previously described for KZFPs (Farmiloe et al., 2023). Its regulation of the MAGEA gene cluster exemplifies a distinct evolutionary mechanism: an ancestral intronic binding site, present in MAGEA6 gene body, before ZNF257 emerged, was propagated across the cluster through tandem duplication, enabling coordinated regulation of multiple paralogs. Temporal expression analysis during spermatogenesis further suggests that ZNF257 initiates MAGEA repression at the spermatogonia-to-spermatocyte transition, after which silencing may be maintained through epigenetic mechanisms such as DNA methylation. ZNF498 and ZNF18, both SCAN-containing KZFPs with variant KRAB domains, on the other hand acted as transcriptional activators. ZNF498 activates a programme centred on microtubule cytoskeleton organisation, as demonstrated by the disruption of ciliogenesis upon its overexpression, and both ZNF498 and its targets are broadly expressed in the central nervous system, particularly in excitatory neurons where microtubule dynamics are essential for axonal architecture. ZNF18 similarly activates genes involved in chromatin remodelling and cytoskeletal reorganisation at the spermatid stage, processes that are hallmarks of spermiogenesis. Together, these case studies demonstrate that even within a single screen, KZFPs with fundamentally different regulatory logics can be identified through a single unifying phenotype and then mechanistically dissected to uncover their unique properties.”

Is now:

“The four KZFPs characterized here illustrate the functional diversity that can be uncovered using this screening strategy. For ZNF43, integration of overexpression transcriptomics with ChIP-exo binding data identified a small set of candidate direct target genes located near LTR/ERV1 elements. Their tissue-specific expression patterns are consistent with the hypothesis that ZNF43 contributes to transcriptional programmes associated with fatty acid metabolism and detoxification, although these analyses, which rely on overexpression-derived datasets and tissue-wide correlations, do not establish physiological regulation or causality. Rather, they identify a candidate regulatory network whose functional relevance will require investigation in appropriate biological models. More generally, these observations support the concept that host genomes may exploit TE-derived regulatory sequences in a tissue-specific manner through differential KZFP expression, while recognizing that additional transcription factors almost certainly participate in controlling these gene expression programmes. Similarly, ZNF257 emerged as a promoter-associated transcriptional repressor in our overexpression system. Evolutionary analyses suggest that tandem duplication propagated an ancestral ZNF257-binding sequence across the MAGEA locus, generating the hypothesis that ZNF257 may contribute to coordinated regulation of this gene cluster during spermatogenesis. The temporal expression profiles of ZNF257 and the MAGEA genes are compatible with such a model but remain correlative and therefore require direct functional validation. ZNF498 and ZNF18, two SCAN-containing KZFPs with variant KRAB domains, displayed transcriptional activation rather than repression following overexpression. For ZNF498, the integration of transcriptomic analyses with expression profiling pointed to microtubule cytoskeleton organization as a candidate biological process, a prediction that was further supported experimentally by the marked impairment of ciliogenesis following ZNF498 overexpression in hTERT-RPE1 cells. This represents the strongest functional validation presented in this study and supports the biological relevance of the analytical framework developed here. For ZNF18, the co-expression of the KZFP and its candidate target genes during spermatogenesis is consistent with the hypothesis that it contributes to transcriptional programmes involved in chromatin remodelling and cytoskeletal reorganization during spermatid differentiation. Together, these case studies illustrate how a standardized overexpression screen can identify KZFPs with distinct regulatory properties and generate biologically coherent hypotheses regarding their physiological functions. Rather than establishing definitive functions for individual KZFPs, this framework prioritizes candidates, proposes relevant cellular contexts, and provides a foundation for future mechanistic studies performed under physiological conditions.”

“In addition, interpretation of the SCAN-deletion experiments is complicated by the reduced expression levels of the deletion constructs relative to the corresponding full-length proteins, making it difficult to determine whether the observed proliferation phenotypes are pathway-specific or partially driven by differential expression.”

We thank the reviewer for this important observation and agree that differences in expression levels between the full-length and ΔSCAN constructs could complicate the interpretation of the observed phenotypes. To address this concern, we performed a quantitative comparison of the expression levels of full-length and ΔSCAN proteins using both western blotting and transgene expression using RNAseq, while accounting for differences in transgene length. This result are now added in (Fig S6C, D).

With modification of the legend:

• HA signal after OE of HA-tagged ZNF18, ZNF18∆SCAN, ZNF498, ZNF498∆SCAN or GFP in K562 cells. Actin as control.
• Quantification of ZNF18, ZNF18∆SCAN, ZNF498, ZNF498∆SCAN It appears that the difference is small (Minor comments of the reviewer 1

“- In the Abstract and in the "Limitations of the study" section, the term "annotation" is used. It would be preferable to specify "functional characterization" instead of "annotation".

Done as suggested by the reviewer.

• In the Introduction, there may be a minor citation confusion. Following the sentence: "Characterized by an N-terminal KRAB domain and a C-terminal tandem array of C2H2 zinc fingers, KZFPs primarily target transposable element (TE)-embedded sequences," the cited references are predominantly experimental studies supporting this statement. However, the inclusion of the review "Bruno, Mahgoub and Macfarlan, 2019" appears less appropriate in this context, as it does not directly present ChIP-seq data supporting this claim. More relevant primary studies from the same research area include "Wolf et al. 2020" and "Bruno et al. 2025.".

Done as suggested by the reviewer.

• In Fig. 1A, "D10" appears inconsistent with the text and other figures (Fig. 1B, 1G, 1H), which refer to 9 days post-induction.

Done as suggested by the reviewer.

• In Fig. S1, there may be a mismatch in the highlighted plate: the zoomed image appears to correspond to the first plate from the top. The correct plate should be highlighted for consistency.

Done as suggested by the reviewer.

• In Fig. 1B, there is a typographical error ("K ZFPs" instead of "KZFPs").

Done as suggested by the reviewer.

• In Fig. S1E, it is unclear what "other" refers to. Please clarify whether this represents the mean of all remaining KZFPs or a defined subset, ideally in the figure description.

Done as suggested by the reviewer.

• In Fig. S2E, "SetDB1" should be corrected to "SETDB1".

Done as suggested by the reviewer.

• In Fig. 3B, it is unclear what distinguishes the upper and lower "Diverse REs". A brief clarification in the figure legend would improve interpretability, particularly regarding the transposable element families included.

Done as suggested by the reviewer.

• In Fig. S3C, the x-axis labels appear slightly misaligned and shifted to the right.

Done as suggested by the reviewer.

• In Fig. 3C, the labels for MAGEA6 and MAGEA2B appear to be inverted.

Done as suggested by the reviewer.

• In Fig. 3K, "MAGE3" should be corrected to "MAGEA3".

Done as suggested by the reviewer.

• In the ZNF498 section, line 4, the punctuation should be corrected so that the period appears after the figure reference ("promoters (Fig. S1E).").

Done as suggested by the reviewer.

• In the final sentence of the ZNF498 section, a noun appears to be missing after "cytoskeleton-dependent," possibly "processes".

Done as suggested by the reviewer.

• In the last section of the Results and corresponding figures and their descriptions, "SCAN dependant" should be corrected to "SCAN-dependent".”

Done as suggested by the reviewer.

Major comments of the reviewer 2

“- The authors chose four KZFPs to study in detail, but why they chose these 4 candidates is unlcear to me. It would be nice to add a more detailed description of the process by which they chose the four candidates.”

We agree that the rationale for selecting the four KZFPs should be presented more explicitly. Accordingly, we revised the manuscript to clarify the selection criteria.

“However, a modest correlation was noted between the number of transcription start sites (TSS) bound by KZFPs and the drop in PrestoBlue signal induced by their overexpression (Fig. 1G), and SCAN-containing KZFPs (SKZFPs) tended to induce proliferation defects more frequently than family members lacking this domain (Fig. 1H).”

Is now:

“However, a modest correlation was noted between the number of transcription start sites (TSS) bound by KZFPs and the drop in PrestoBlue signal induced by their overexpression (Fig. 1G), and SCAN-containing KZFPs (SKZFPs) tended to induce proliferation defects more frequently than family members lacking this domain (Fig. 1H). These observations indicated that KZFPs affecting proliferation do not constitute a homogeneous functional group, prompting us to select representative candidates spanning the evolutionary, structural, and genomic diversity of the KZFP family for mechanistic characterization.____”

“- The materials and methods part of the manuscript is not detailed enough for other researchers to reproduce the study. They should add more details to both experiments and data analysis part of this section. Below I highlight some examples for sake of clarity, but the authors should revise the whole materials and methods section and add more details keeping these examples in mind:

• The authors do not state the titer of lentiviral vectors they generate nor the MOI or amount of virus they use to transduce the cells

• In many cases, the specific softwares and the software version is not stated e.g., the analysis of the Gene Ontology Biological Processes

• It would be beneficial for the readers to get more details about the construct they used, for example a map of the plasmid.

• It is unclear how many cells were used for RNA extraction

• It is unclear which microscopes were used for imaging.

• The concentration of antibodies used for staining and the product number, and provider of the antibody is not always depicted.”

We agree that the additional methodological details requested by the reviewer will improve the reproducibility and transparency of the study. Accordingly, we have expanded the Methods section to provide a more detailed description of the experimental procedures and data analysis workflow.

“Lentiviral particles were produced in HEK293T cells by transient co-transfection of transfer, packaging and envelope plasmids. Cells were transfected at approximately 70–80% confluence using a standard lipid-based transfection reagent. Viral supernatants were collected 48 h after transfection, cleared by centrifugation, filtered through 0.22-µm membranes, and used fresh or stored appropriately until use. Recipient K562 or hTERT-RPE1 cells were transduced under conditions optimized for efficient gene delivery.”

Is now:

“Lentiviral particles were produced in HEK293T cells. 105 cells were seeded in 24 well plates filled with 1ml DMEM the day before transfection. Cells were co-transfected individually with 0.15ug of each plasmids encoding KZFPs tagged with HA (pTRE-KZFPX-HA-PGK-puro), 0.1ug of the packaging plasmid (pR8.74) and 0.07ug of the envelope plasmid (pMD2G) using TransIT®-LT1 Transfection Reagent (MIR 2306), according to the manufacturer's instructions. Viral supernatants were harvested 24h after transfection, clarified by centrifugation, filtered through 0.45-µm filters and used immediately.”

“Coding sequences were cloned into doxycycline-inducible lentiviral transfer vectors designed to express N-terminally HA-tagged proteins.”

Is now:

“Coding sequences corresponding to 366 human KZFP open reading frames were codon-optimized for human expression and cloned into doxycycline-inducible lentiviral transfer vectors expressing C-terminal HA-tagged proteins under the control of a tetracycline-responsive promoter pTRE-KZFPX-HA-PGK-puro. All expression constructs used in the primary overexpression screen have been deposited and are publicly available (De Tribolet et al., 2023). A schematic representation of the lentiviral expression cassette, including the promoter, HA tag, cloning site, antibiotic resistance cassette, and regulatory elements, is provided in Supplementary file. Selected constructs encoding ZNF43, ZNF257, ZNF498 and ZNF18 were used for follow-up mechanistic studies. For SCAN-domain functional analyses, deletion constructs lacking the SCAN domain (ΔSCAN) were generated for ZNF18 and ZNF498 in the same lentiviral backbone. Deletion were done using In-Fusion cloning with specific primers. PCR was performed with high-fidelity polymerase, followed by gel purification and recombination with the linearized plasmid using the In-Fusion HD Cloning Kit (Takara Bio©) according to the manufacturer’s protocol. The product was transformed into HB101 Escherichia coli cells, and colonies were screened by PCR. Positive clones were verified by Sanger sequencing, and confirmed plasmids were propagated and purified for further use.”

“Total RNA was extracted...”

Is now:

“For each biological replicate, approximately 1 × 10⁶ K562 cells were harvested 72 h after doxycycline induction. Total RNA was extracted…”

“Images were acquired by fluorescence microscopy under identical conditions across samples.”

Is now:

“Images were acquired using a confocal microscope Leica-SP8 (Leica Biosystems) with an objective HC PL APO 63x/1.40 and a pinhole size of 1 AU, using identical acquisition settings for all conditions. Images were processed using Fiji/ImageJ (version 2.9.0) without nonlinear intensity adjustments.”

“Cells were fixed and stained with antibodies against ciliary markers (ARL13B)”

Is now:

“Cells were fixed in 4% paraformaldehyde, permeabilized with 0.1% Triton X-100, blocked with 2% BSA, and incubated with rabbit anti-ARL13B (Proteintech, Cat. No. 17711-1-AP, 1:200) followed by Alexa Fluor 568-conjugated donkey anti-rabbit IgG (Thermo Fisher Scientific, Cat. No. A-10042, 1:1000). Nuclei were stained with Hoechst (1 µg/mL).”

“- The authors mention that KZFPs are usually expressed at a low level in the K562 cell line they use, but there is no figure showing the expression level of KZFPs in this cell type. It would be important to see the baseline KZFP expression in these cells, the level of overexpression and compare it to the endogenous expression levels they show in different cell types/tissues, at least for the four candidates studied more in depth. This would help to understand whether this level of activity is something that could occur naturally in a physiologically relevant context.”

We thank the reviewer for this insightful suggestion and fully agree that providing additional context regarding endogenous and ectopic KZFP expression levels will help readers better assess the physiological relevance of our findings. As suggested, we included data showing the baseline expression levels of the four selected KZFPs in K562 cells together with the expression levels achieved following doxycycline-induced overexpression. We also compared these values with publicly available transcriptomic data from cell lines. Importantly, only cell lines are assessed as we need ground through (K562) to estimate transgene expression. We modified Fig. S2, Fig. S3, Fig. S4 and Fig. S5 to add the results of these analysis. Here is ZNF43 as an example:

With the following legend:

“(C) Distribution of endogenous expression levels, (using GFP control cells), of all expressed genes (light grey) and all KZFPs (dark grey) in K562 cells. The solid red line indicates endogenous ZNF43 expression in GFP control cells, whereas the dashed red line indicates the corrected transgene expression following doxycycline induction.

(D) Endogenous ZNF43 expression across Human Protein Atlas cell lines, (https://www.proteinatlas.org/about/download#cell_line), following normalization to the local RNA-seq dataset. K562 cells are highlighted in red. The dashed red line indicates the corrected transgene level measured following doxycycline-induced overexpression in K562 cells overexpressing ZNF43.”

Modified the result section:

“ZNF43 is a ~43-million-year-old KZFP with a canonical TRIM28-recruiting KRAB domain and 19 zinc fingers that preferentially recognize an LTR/ERV1-embedded sequence (Fig. S1F). We first verified that ZNF43 overexpression impaired the growth of K562 cells (Fig. S2A, B). Endogenous ZNF43 expression was readily detectable in K562 cells and across human cell lines (Fig. S2C, D). Following doxycycline induction, transcript abundance markedly increased and exceeded the highest endogenous expression level observed among the analyzed cell lines (Fig. S2C, D).”

We also updated the Methods section:

“Quantification of endogenous and transgene expression levels

Endogenous KZFP expression in K562 cells was estimated from GFP control RNA-seq samples using normalized mean expression values obtained from the differential expression analyses. For ZNF18, whose transgene sequence is identical to the endogenous coding sequence (i.e., not codon-optimized), transgene-derived expression was estimated directly by subtracting the endogenous transcript abundance measured in GFP controls from the total transcript abundance measured following doxycycline induction (OE − GFP). For ZNF43, ZNF257 and ZNF498, the overexpression constructs were synthesized using codon-optimized coding sequences. RNA-seq reads were therefore additionally aligned against the codon-optimized transgene reference sequences to specifically quantify exogenous transcripts without interference from endogenous reads. Because these codon-specific counts are generated through an independent alignment strategy, they are not directly comparable to the endogenous RNA-seq expression values. To calibrate these measurements, a scaling factor was derived from the ZNF18 dataset by comparing the codon-specific read counts with the transgene abundance estimated from the differential expression analysis (OE − GFP). This empirically determined correction factor was subsequently applied to all codon-optimized constructs, thereby expressing transgene abundance on the same scale as the endogenous RNA-seq measurements. Corrected transgene expression values were then used for all downstream comparisons. To compare endogenous expression across physiological contexts, publicly available RNA-seq datasets from the Human Protein Atlas (cell lines) were downloaded and normalized to the local RNA-seq scale. A normalization factor was calculated from the median expression ratio of KZFPs detected in both the Human Protein Atlas K562 dataset and the local K562 GFP control RNA-seq dataset, and subsequently applied uniformly to all Human Protein Atlas datasets. This normalization enabled direct comparison of endogenous expression across biological contexts with the corrected transgene expression values. Global KZFP expression was calculated as the median normalized expression of all annotated KZFPs within each biological context. For the four KZFPs selected for detailed characterization, endogenous expression across Human Protein Atlas cell lines was compared with corrected transgene expression following doxycycline induction. Expression distributions of all genes and KZFPs were visualized using ranked expression plots and density histograms. All analyses were performed in R using the tidyverse package.”

We fully acknowledge that the overexpression system used in this study was primarily designed as a discovery platform to identify candidate functions, targets, and interaction partners of KZFPs that are otherwise expressed at lower levels in K562 cells. As the reviewer correctly points out, determining whether these regulatory effects occur at endogenous expression levels in physiologically relevant cellular contexts represents an important next step. We Thereby also clarified this in the “Limitations to this study” paragraph:

“To better place our experimental system into a physiological context, we compared endogenous KZFP expression in K562 cells with publicly available transcriptomic datasets from the Human Protein Atlas. These analyses showed that K562 cells do not exhibit unusually low global KZFP expression compared with other human cell lines. However, consistent with the restricted expression patterns of this protein family, KZFPs as a whole are expressed at substantially lower levels than the average human gene. For the four KZFPs characterized in detail, doxycycline induction produced transcript levels that exceeded the highest endogenous expression observed across the analyzed human cell lines. Accordingly, the overexpression system used in this study was not designed to recapitulate physiological expression levels but rather to maximize the identification of candidate target genes, interacting partners, and regulatory pathways for KZFPs that are otherwise expressed at low endogenous levels. Consequently, the molecular interactions identified here should be considered as hypotheses requiring validation under endogenous expression conditions in physiologically relevant cellular models.”

“- RNA seq analysis: It is unclear how many cells were used in the RNA seq analysis, I would like to ask the authors to clarify that. Moreover, from my understanding the RNA seq analysis was done on day 3, while the Presto Blue analysis was done on days 4, 7 and 9. I would like to kindly ask the authors to motivate their choice for the day of the RNA sequencing analysis.”

We agree that this information required clarification. The Methods section has been revised to specify the number of cells used for RNA-seq library preparation and to explain the rationale for performing RNA-seq after 3 days of doxycycline induction, before measurable proliferation defects emerge, in order to capture primary transcriptional responses to KZFP overexpression. The corresponding modification has also been added to the Results section when introducing the RNA-seq analyses.

“For transcriptome profiling, K562 cells expressing the indicated inducible constructs were treated with doxycycline for 72 h before harvest. Total RNA was extracted using the NucleoSpin RNA plus kit (Macherey-Nagel) according to the manufacturer’s recommendations. RNA quantity and purity were assessed by spectrophotometry, and RNA integrity was evaluated before library preparation.”

Is now:

“For transcriptome profiling, 1 × 10⁶ K562 cells expressing the indicated inducible constructs were treated with doxycycline for 72 h before harvest. RNA was collected after 3 days of induction to capture the primary transcriptional responses to KZFP overexpression before substantial differences in proliferation became apparent. This early time point was chosen to minimize secondary transcriptional changes resulting from altered cell growth, cell-cycle distribution, or cellular stress, which become detectable in the proliferation assays performed after 4, 7, and 9 days of induction. Total RNA was extracted using the NucleoSpin RNA plus kit (Macherey-Nagel) according to the manufacturer’s recommendations. RNA quantity and purity were assessed by spectrophotometry, and RNA integrity was evaluated before library preparation.”

“We then profiled the transcriptome of K562 cells overexpressing ZNF43 by deep RNA sequencing (RNA-seq)”

Is now:

“We then profiled the transcriptome of K562 cells overexpressing ZNF43 by deep RNA sequencing (RNA-seq) after 3 days of doxycycline induction, a time point selected to capture primary transcriptional responses before the onset of measurable proliferation defects.”

Minor comments of the reviewer 2

“- Figure S1D is not mentioned in the text before figure S1E. The order of the panels should be changed in the figure.

Done as suggested by the reviewer.

• "We selected genes that were downregulated upon ZNF43 overexpression and harboured a ZNF43 binding site within 10kb of their TSS (Fig. 1A) - don't the authors mean Fig. 2A?

Done as suggested by the reviewer.

• In Figure 4D, the GO terms cannot be read, as the sentences seem to be cut.

Done as suggested by the reviewer.

• All figures and figure legends need to be revised. In some cases, the letter size is too small, or the legend and explanation of colours is missing. Please see some examples below: Fig. S6C, Fig 6C, Fig S4C, Fig S5C (letter size too small) Fig S6G, Fig 4E (label/scale is missing)”

Homogenized to Arial 6 by default as requested by most of journal guidelines

__ Description of analyses that authors prefer not to carry out__

We think that by proceeding as described above we will have addressed all major conceptual issues raised by the reviewers.

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Referee #2

Evidence, reproducibility and clarity

Summary

Foley et al establishes a scalable framework to probe KZFP function. They performed an array of inducible overexpression screen of 366 human KZFPs in K562 cells. This screen, together with the analysis of transcriptomic and available chromatin and proteomic datasets revealed that KZFPs regulate many different mechanisms, highlighting the functional diversity of KZFPs. Understanding this functional diversity is a very interesting, timely and relevant question, but it is also challenging to study. Therefore, the approach the authors develop is promising. While the quality of the experiments and data analysis is high, the weakness I see in the manuscript is the lack of major biological insights in relevant model systems. Please see my detailed comment in the significance part.

Major comments

• The authors chose four KZFPs to study in detail, but why they chose these 4 candidates is unlcear to me. It would be nice to add a more detailed description of the process by which they chose the four candidates.
• The materials and methods part of the manuscript is not detailed enough for other researchers to reproduce the study. They should add more details to both experiments and data analysis part of this section. Below I highlight some examples for sake of clarity, but the authors should revise the whole materials and methods section and add more details keeping these examples in mind:
  • The authors do not state the titer of lentiviral vectors they generate nor the MOI or amount of virus they use to transduce the cells
  • In many cases, the specific softwares and the software version is not stated e.g. the analysis of the Gene Ontology Biological Processes
  • It would be beneficial for the readers to get more details about the construct they used, for example a map of the plasmid.
  • It is unclear how many cells were used for RNA extraction
  • It is unclear which microscopes were used for imaging.
  • The concentration of antibodies used for staining and the product number, and provider of the antibody is not always depicted.
• The authors looked at available chromatin data in either K562 cells or HEK293 cells, which I think is a very good way of utilizing publicly available data. Since the authors showed that different KZFPs might be functionally relevant in different cell types/tissues, I was wondering if they checked if there is available ChIP Seq or CUT&RUN data in those specific cell types/tissues. If yes, that data should be included in the manuscript.
• The authors mention that KZFPs are usually expressed at a low level in the K562 cell line they use, but there is no figure showing the expression level of KZFPs in this cell type. It would be important to see the baseline KZFP expression in these cells, the level of overexpression and compare it to the endogenous expression levels they show in different cell types/tissues, at least for the four candidates studied more in depth. This would help to understand whether this level of activity is something that could occur naturally in a physiologically relevant context.
• RNA seq analysis: It is unclear how many cells were used in the RNA seq analysis, I would like to ask the authors to clarify that. Moreover, from my understanding the RNA seq analysis was done on day 3, while the Presto Blue analysis was done on days 4, 7 and 10. I would like to kindly ask the authors to motivate their choice for the day of the RNA sequencing analysis.

Minor comments

• Figure S1D is not mentioned in the text before figure S1E. The order of the panels should be changed in the figure.
• "We selected genes that were downregulated upon ZNF43 overexpression and harboured a ZNF43 binding site within 10kb of their TSS (Fig. 1A) - don't the authors mean Fig. 2A?
• In Figure 4D, the GO terms cannot be read, as the sentences seem to be cut.
• All figures and figure legends need to be revised. In some cases, the letter size is too small, or the legend and explanation of colours is missing. Please see some examples below: Fig. S6C, Fig 6C, Fig S4C, Fig S5C (letter size too small) Fig S6G, Fig 4E (label/scale is missing)

Significance

Understanding the diverse roles of KZFPs is an important and interesting research question. However, studying KZFPs is challenging, as many KZFP-mediated effects appear to be highly cell type- and tissue-specific. This complexity is also highlighted by the findings of the current manuscript.

A major strength of this study is the development of a scalable system that enables the simultaneous investigation of the entire KZFP family. Performing such analyses on an individual basis would be extremely time-consuming. Therefore, the authors provide an efficient and valuable screening platform that can identify promising candidates for further investigation. In this regard, the methodological advance represents the primary contribution of the work.

At the same time, the study lacks a clear biological conclusion. While the screen identifies KZFPs with potential functional effects, it would substantially increase the impact of the manuscript if the authors selected at least one candidate for in-depth characterization in a biologically relevant cellular context. The current study is still of high quality and importance without these experiments, but such follow-up analyses would greatly strengthen the biological significance of the findings.

Another limitation is that the experiments were performed in a cell type in which many of the investigated KZFPs are not normally expressed. As a result, the forced overexpression strategy may not accurately reflect physiological conditions and could potentially generate false-positive results. This concern is particularly relevant in light of the authors' statement that "KZFPs with sufficient regulatory potency to perturb cellular fitness outside of their normal setting are strong candidates for playing important roles within it." While this may indeed be true for some KZFPs, it is also possible that certain observed phenotypes simply arise from ectopic expression in an inappropriate cellular environment.

More generally, the observation that KZFPs can have functions beyond TE repression is already established in the literature. Therefore, the manuscript provides limited new biological insight into this concept. The authors could potentially strengthen the novelty of the study by placing greater emphasis on specific KZFP subfamilies, such as SCAN-containing zinc finger proteins, which are a novel direction and have been implicated in non-canonical regulatory roles.

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Referee #1

Evidence, reproducibility and clarity

Summary

In the manuscript "An overexpression platform reveals the functional diversity of human KRAB-Zinc Finger Proteins in maintaining cellular homeostasis", the authors describe a scalable framework aimed at prioritizing individual KZFPs for functional characterization. The study is centered on a large-scale screening approach in which human erythroleukemia K562 cells were transduced with inducible constructs enabling the overexpression of 366 individual KZFPs. The effects of KZFP overexpression on cellular proliferation were then assessed using a cell viability assay comparing induced and non-induced conditions.

Based on the results of this primary screen, the authors selected four KZFPs for further investigation among those whose overexpression was associated with proliferation defects. Follow-up analyses integrated tissue- and cell type-specific expression patterns of these KZFPs with expression analyses of putative target genes identified from previously published ChIP-seq datasets, with the aim of inferring potential biological functions. On the basis of these analyses, the authors propose that the selected KZFPs may regulate distinct gene networks involved in processes including fatty acid metabolism, spermatogenesis, and other aspects of cellular homeostasis.

The study spans multiple biological contexts, but the evidence supporting several of the individual conclusions remains relatively preliminary, and the breadth of the manuscript often comes at the expense of mechanistic depth.

Major comments

1. Interpretation and robustness of the initial overexpression screen

The large-scale overexpression screen represents the foundation of the manuscript and provides a potentially valuable resource for prioritizing candidate KZFPs for downstream study. However, several aspects of the experimental setup and data presentation currently limit the interpretation of the reported proliferation defects. First, key details regarding the screening workflow remain unclear. While the Methods section describes the overall procedure, it is difficult to determine when cells were seeded relative to doxycycline induction, in which plate format the cells were maintained throughout the experiment, and whether medium exchange was performed during the 9-day assay. These points are particularly relevant given the use of suspension K562 cells (which can complicate medium exchange in a 96-well plate format and make long-term culture more difficult to control) and a metabolic viability readout (PrestoBlue), as differences in nutrient depletion or overgrowth could also influence the signal independently of reduced proliferation or toxicity. Additional clarification regarding seeding density, timing of induction, plate format, culture handling throughout the assay, and whether cell morphology/density was visually monitored would substantially improve interpretability and reproducibility. Second, it is unclear whether the observed proliferation phenotypes may be influenced by differences in transgene expression levels or integration effects. Were all constructs validated for comparable expression following induction? In the absence of such controls, it remains difficult to determine whether the reported phenotypes reflect specific KZFP activities or differences in overexpression efficiency. While it may not be possible to conclusively distinguish KZFP-specific effects from toxicity associated with high transgene expression levels, this limitation should at least be acknowledged. In addition, the possibility that some phenotypes may be influenced by transgene integration effects should also be considered. Unless independent transductions were validated for the KZFPs classified as toxic, it remains difficult to exclude integration-site-specific contributions to the observed proliferation defects. Third, the normalization strategy would benefit from additional clarification. In Fig. S1A, the LacZ control appears variably affected by doxycycline treatment across plates, whereas the GFP control appears more stable. Since normalization relies on the mean behavior of both controls within each batch and condition, the authors should clarify whether this variability could influence hit calling. Finally, several aspects of the data presentation are currently difficult to reconcile. In Fig. 1D, the meaning of the purple category is unclear, and the percentage scaling on the x-axis is difficult to reconcile with the cumulative values displayed. For instance, the sum of all the bars would not reach 100%, as the values of the bars span percentages up to 4% at most (for 105 MYO KZFPs) according to this plot. Similarly, the reported numbers of TE-binding KZFPs in Fig. 1E-F and Fig. S1D appear internally inconsistent and should be clarified. Specifically, 53+14=67 KZFPs are reported to bind TEs in total, yet a larger number of KZFPs appears associated with individual TE families (e.g. 86 for LTR.ERV1). If the values shown correspond to percentages rather than absolute counts, this should be explicitly clarified in both the figure and legend. In addition, Fig. S1D appears inconsistent with the counts reported in Fig. 1E-F, as only 5 out of the 53 toxic KZFPs displayed in the plot show no enrichment for any of the highlighted TE families. 2. Relationship between the screening phenotype and the proposed biological functions of selected KZFPs

A central conceptual issue throughout the manuscript is that the downstream functional analyses of the selected KZFPs remain largely disconnected from the original screening phenotype. The four candidates were prioritized based on proliferation defects observed upon overexpression in K562 cells; however, the subsequent analyses (with the only exception being a more in-depth experimental analysis of ZNF498 in ciliogenesis, which stands out as comparatively more directly supported by experimental evidence) primarily rely on correlative expression patterns and KZFP ChIP-seq datasets to infer potential biological functions in unrelated cellular contexts. As a result, it remains unclear whether the proposed transcriptional programs are mechanistically linked to the proliferation phenotypes that motivated candidate selection in the first place.

This issue is evident across multiple sections of the manuscript. For example, the proposed role of ZNF43 in regulating fatty acid metabolism and detoxification pathways is primarily inferred from tissue-level expression correlations. While these analyses focus on genes identified as potential ZNF43 targets, the underlying ChIP-seq datasets were themselves generated under ZNF43 overexpression conditions. Therefore, the current analyses do not establish whether ZNF43 regulates these pathways under physiological expression levels or within a relevant cellular context, nor how such regulation relates to the proliferation defect observed in K562 cells. Moreover, several proposed target genes remain substantially expressed in tissues where ZNF43 expression is not particularly low (e.g. kidney and heart muscle), suggesting that additional regulators are likely involved.

Similarly, the proposed model of ZNF257-mediated regulation of MAGEA genes during spermatogenesis is intriguing but does not fully account for the expression behavior of all MAGEA family members, particularly MAGEA2B, which displays strong expression in spermatocytes despite high ZNF257 expression. This expression pattern should be acknowledged in the main text and reflected in Fig. 3K. In addition, the labels for MAGEA6 and MAGEA2B in Fig. 3C appear to be inverted. More broadly, the proposed regulatory model is difficult to reconcile with the generally restricted expression pattern of MAGEA genes across adult tissues, as their expression does not appear to consistently correlate with ZNF257 levels outside the germline context.

Related concerns also apply to the analyses of ZNF498 and ZNF18, where the proposed functions in cilium formation and sperm maturation remain disconnected from the proliferation defects identified in the initial screen. In addition, interpretation of the SCAN-deletion experiments is complicated by the reduced expression levels of the deletion constructs relative to the corresponding full-length proteins, making it difficult to determine whether the observed proliferation phenotypes are pathway-specific or partially driven by differential expression. Finally, while the proteomics results aimed at identifying SCAN-dependent interactors are of interest, several aspects of the experimental design and data analysis remain unclear. In particular, it is not specified whether the experiment was performed in biological replicates or as a single measurement. This is important, as it directly affects how the data can be interpreted and how stringent downstream filtering can be. In the Results section, the authors state that "we identified a set of SCAN-dependent interactors, i.e. proteins that co-immunoprecipitated with the full-length construct but were absent in controls and lost upon deletion of the SCAN domain," which suggests a relatively binary, "presence/absence" filtering strategy. However, this description does not specify whether any quantitative threshold (e.g. enrichment ratio) was applied when comparing full-length constructs to deletion mutants. In contrast, the Methods section states that "proteins lacking signal above background were excluded and proteins were additionally required to show stronger signal in at least one bait condition than in GFP controls based on heatmap clustering (see script)," which instead suggests that a threshold-based criterion was used to define enrichment relative to controls and deletion mutants. If this is the case, the exact criteria and thresholds used for filtering should be clearly stated and consistently reported between the Results and Methods sections. If replicate measurements were not performed, this should be explicitly acknowledged, as peptide-level variability may substantially influence the identification of high-confidence interactors, particularly if the applied cutoffs are not highly stringent.

Overall, many of the proposed biological functions are currently supported primarily by correlative analyses and would benefit either from additional functional validation or from a more cautious framing of the conclusions.

Minor comments

• In the Abstract and in the "Limitations of the study" section, the term "annotation" is used. It would be preferable to specify "functional characterization" instead of "annotation".
• In the Introduction, there may be a minor citation confusion. Following the sentence: "Characterized by an N-terminal KRAB domain and a C-terminal tandem array of C2H2 zinc fingers, KZFPs primarily target transposable element (TE)-embedded sequences," the cited references are predominantly experimental studies supporting this statement. However, the inclusion of the review "Bruno, Mahgoub and Macfarlan, 2019" appears less appropriate in this context, as it does not directly present ChIP-seq data supporting this claim. More relevant primary studies from the same research area include "Wolf et al. 2020" and "Bruno et al. 2025.".
• In Fig. 1A, "D10" appears inconsistent with the text and other figures (Fig. 1B, 1G, 1H), which refer to 9 days post-induction.
• In Fig. S1, there may be a mismatch in the highlighted plate: the zoomed image appears to correspond to the first plate from the top. The correct plate should be highlighted for consistency.
• In Fig. 1B, there is a typographical error ("K ZFPs" instead of "KZFPs").
• In Fig. S1E, it is unclear what "other" refers to. Please clarify whether this represents the mean of all remaining KZFPs or a defined subset, ideally in the figure description.
• In Fig. 2A, readability could be improved by adjusting the layering of points, as the darker dots (in particular the red ones) are currently obscured by lighter ones. Alternatively, removing the outline of the points (which is not transparent) may also improve visibility, but in that case the legend for point size would need to be updated accordingly.
• In Fig. S2E, "SetDB1" should be corrected to "SETDB1".
• In Fig. 3B, it is unclear what distinguishes the upper and lower "Diverse REs". A brief clarification in the figure legend would improve interpretability, particularly regarding the transposable element families included.
• In Fig. S3C, the x-axis labels appear slightly misaligned and shifted to the right.
• In Fig. 3C, the labels for MAGEA6 and MAGEA2B appear to be inverted.
• In Fig. 3K, "MAGE3" should be corrected to "MAGEA3".
• In the ZNF498 section, line 4, the punctuation should be corrected so that the period appears after the figure reference ("promoters (Fig. S1E).").
• In the final sentence of the ZNF498 section, a noun appears to be missing after "cytoskeleton-dependent," possibly "processes".
• In the last section of the Results and corresponding figures and their descriptions, "SCAN dependant" should be corrected to "SCAN-dependent".

Significance

General assessment

This study presents a large-scale inducible overexpression platform aimed at systematically exploring the functional diversity of human KZFPs. The screening framework itself represents a potentially useful resource for prioritizing candidate KZFPs for downstream investigation and may be of interest to researchers studying KZFPs, transcriptional regulation, and transposable element biology. A notable strength of the study is the breadth of the screening effort and the attempt to integrate multiple orthogonal datasets to generate functional hypotheses for relatively understudied KZFPs. The more in-depth experimental analysis of ZNF498-mediated ciliogenesis also provides an example of how the platform may be used to identify biologically relevant candidates for further characterization. At the same time, many of the functional conclusions currently remain preliminary and are supported primarily by correlative analyses integrating overexpression phenotypes, expression datasets, and KZFP binding preferences also determined by overexpressing KZFP constructs. In several cases, the proposed biological functions remain insufficiently connected to the original proliferation phenotype used for candidate prioritization. As a result, the current study is best viewed as an exploratory and hypothesis-generating framework rather than a definitive functional characterization of the selected KZFPs. Clarifying these limitations and moderating some of the broader conclusions would substantially strengthen the manuscript.

Advance

The principal advance of the work is therefore primarily technical and resource-oriented, providing a scalable experimental framework for systematic KZFP prioritization and downstream functional exploration. While the study does not yet provide extensive mechanistic validation for most proposed functions, it may nonetheless serve as a useful starting point for future investigations into KZFP biology and transcriptional regulation.

Audience

The manuscript will likely be of greatest interest to a specialized basic research audience working on KZFPs, transposable element regulation, epigenetic regulation, and transcriptional control. Researchers interested in large-scale functional screening approaches may also find the methodological framework useful.

Field of expertise: transposable elements, KRAB-zinc finger proteins, epigenetic regulation, functional genomics, genome regulation.

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

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Reply to the reviewers

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

This interesting manuscript uses single cell RNAseq of developing C. elegans larvae to identify temporal pulses or oscillations in gene expression within glia and many other epithelial cell types - mostly in genes related to cuticle synthesis or remodeling. It identifies different sets of genes that oscillate within different cell types, and identifies many apparent oscillatory genes that were missed in prior studies because they are expressed in smaller populations of cells (whereas bulk data mainly report on oscillations within the major hypodermis).

A second major contribution of this manuscript is to pioneer analysis methods for detecting oscillatory gene expression in scRNAseq datasets. That said, it's important to state that the methods for estimating phase coherence, GAM, perplexity, etc. make sense to me intuitively but I can't assess the math and other details, which are outside of my expertise.

Most of my comments are minor ones about suggested clarifications to the text or figures. Some may require additional analyses, but none should require additional data collection.

1. The manuscript focuses much of its analysis on one specific glial cell type (ILso), yet the authors tell us almost nothing about this cell type or why they would care about it. It would be helpful to include just a little more background on glial biology and the epithelial-like characteristics of socket glia.

We added the following to the second paragraph of Results:

"To this end, we used C. elegans strains expressing GFP specifically in ILso glia or in all glia (grl-18pro::GFP or mir-228pro::GFP, respectively). In C. elegans, all glia are found in sense organs. Most sense organs consist of one or more sensory neurons – each of which is specialized to detect different types of stimuli – and exactly two glia, called the sheath and socket. The sheath and socket glia form an epithelial tube continuous with the skin, through which the ciliated dendritic endings of sensory neurons protrude to sense cues in the external environment. In prior work we found that, in some sense organs, the socket glia produce cuticle specializations around specific sensory neuron cilia, but how these are coordinated with general cuticle synthesis was unknown (Fung et al. 2023)."

Many transcriptomic studies of epithelia (including the Purice et al study of adult glia) use single NUCLEI RNAseq rather than single cells because of the challenges in separating cells connected by tight junctions. In C. elegans there are also various epithelial syncytia to contend with. In text or Methods, the authors should comment on why they think cells were appropriate to look at in this instance, and whether there are certain cell types that were missed or could only be obtained as cell fragments based on that choice.

We added the following to the Methods section:

"Presumably, fine cellular projections such as axons or glial processes are lost during cell dissociation, leaving mainly cell soma with nuclei. There is a risk that some cell types could be undersampled in cell sorting, as compared to sorting isolated nuclei, due to differences in how readily they undergo dissociation. On the other hand, retention of cytoplasmic material in this approach may better represent the total mRNA complement of the cell"

1. Related to above, the authors do not mention any detection or exclusion of likely doublets. Is there reason to think that doublets were not present in any substantial numbers? I'm not super concerned about this since doublets containing hyp7 fragments should have worked against them in detecting glia-specific oscillations, but I do think the issue should be addressed in the text or Methods.

We added the following in Methods:

"Ambient RNA was subtracted using SoupX (Young and Behjati 2020). Potential doublets were assessed using DoubletFinder (McGinnis et al. 2019), but no cells were excluded on this basis. "

1. p. 4 "previously unappreciated local differences in cuticle patterning." This statement should be tempered since many stage- or tissue-specific differences in cuticle patterning have been described previously (including in papers from the Heiman lab and others that are cited here). This study uncovers many additional examples but it's not a completely new finding.

We have revised this:

"Surprisingly, most pulsatile genes are specific to small sets of cell types, suggesting that previously unappreciated local differences in cuticle patterning are more widespread than previously recognized."

1. Table 1 and text: the distinction between pulsatile and oscillatory should be explained more at the outset. These terms sometimes seem to be used interchangeably, but then Table 1 seems to make a distinction, not discussed until the final "limitations" section.

We added the following definition to the Introduction:

"Within a single larval stage, oscillatory genes display a characteristic sharp single peak of expression and we define rigorous metrics for identifying this signature, which we call "pulsatile expression."

• *

We also added a further clarification in the Results section under "De novo identification of pulsatile genes":

"We reasoned that for individual genes, if gene expression in a given cell type were plotted as a function of pseudotime, oscillatory genes would display a distinct peak because they are expressed at a particular pseudotime (Fig. 4A). We refer to this transcriptional signature as "pulsatile" when viewed in a single developmental stage; genes with pulsatile expression are predicted to be oscillatory when viewed across all of larval development, but there may be important exceptions (see "Limitations of the study")."

1. Figure 1 and Figure 3A,B. These UMAPs look very unusual, with no discernable individual dots. Is this just a resolution issue? Or, if relevant, please add info to legend and/or Methods explaining what data smoothing was done here to make them look this way and why.

We have reduced the size of the dots (to point size 1 from point size 2) in the UMAPs in Fig. 1 and Fig. 3 to make individual dots more apparent. The noted effect is due only to the size of the dots; the UMAPs are plotted in the conventional way. The effect of different point sizes on the Fig. 3 UMAP is shown below [IMAGE CANNOT BE ATTACHED HERE]

1. Figure 2C and Figure 6B. In the pseudotime plots, it would be natural for readers to assume that 0 is the beginning of the larval stage and 360 is the end, but that is not actually the way the Meeuse 2020 phase angles work - instead the beginning of the larval stage falls around 160. Please make sure this is made clear, especially when referring to "early and late groups" of TF targets. In Fig 6B, Early and Late categories appear reversed because of the way the data are plotted.

We have replotted Fig. 6B using percent of larval stage progression rather than phase angles in degrees, with 0% corresponding to the peak of dpy-6 expression, to make the timing more intuitive. We have revised the description of the early and late groups in the Discussion.

As Fig. 2C compares our data directly with the phases defined by Meeuse et al., we prefer to keep it consistent with that publication.

1. Figure 3B and Figure 5D-G. The authors group many unidentified clusters into the catchall "skin" category but don't clearly define it in the main text. Table S2 suggests this category includes anterior and posterior skin cells but possibly also other cuticle-lined tubular epithelia that aren't properly referred to as skin (e.g. vulva cells, excretory socket or pore cells). It may also include things like rectum, buccal cavity, excretory duct. Please define your criteria for "skin" more precisely in the main text (any cuticle-lined cell type that is not glia?), and perhaps a more general term such as external epithelia would be more appropriate.

We have changed this in the text to "skin-related cell types" to clarify that it includes hyp, seam, and some unidentified skin-related clusters (which may include some of the cell types you mention, for example the "skin_5" cluster may include vulval epithelia or their precursors as shown in Table S2).

1. Also related to cluster assignments: please specify if "excretory" category includes canal, duct, pore, gland all together, or only a subset of these. Only the duct and pore are cuticle lined and therefore expected to have oscillatory matrix gene expression.

We have changed this to "excretory cell" (or "exc cell") for clarity. We did not examine markers for the excretory duct, pore, or gland.

1. Figure 5. This figure feels disjointed and could be broken up into two figures (panels A-C and panels D-G). The first 3 panels seem more related to Figures 3 & 4 - identifying which cell types have strong pulsatile gene expression - whereas the later panels get into the degree of cell type specificity in matrix gene expression.

We appreciate the merit of this point and in fact we strongly considered splitting up this figure (in various ways) while writing. While we agree that the figure covers a lot of ground in this format, we feel that the subparts do not hold up as their own independent figures on equal footing with the other figures in the manuscript.

1. Figure 5D-E. The very low degree of sharing is fascinating but could be an underestimate that depends on the thresholds chosen for calling a gene "pulsatile". It may be helpful to test a range of thresholds to see how much this matters. For those ~2,500 genes that appear pulsatile in just one cell type, are they called expressed but non-pulsatile in other cell types? That would seem odd to me biologically and most likely a threshold artifact.

We have added the following caveat to the Results:

"Put another way, 45% (2,390 of 5,268) of the genes we identified were expressed and pulsatile exclusively in a single cell type while only 17% (915 of 5,268) were pulsatile in five or more cell types (Fig. 5E). A potential caveat to this conclusion would be if some genes are not categorized as pulsatile in particular cell types due to lower expression (e.g., falling into Cluster 7 with high peak amplitude in one cell type, and Cluster 8 with low peak amplitude in other cell types; see Fig. 4B-C). However, if this occurs, it affects only a minority of cases: among genes categorized as pulsatile in only one cell type, 82% are not detected as expressed in any of the other oscillatory cell types, indicating that the apparent specificity most likely reflects cell-type-specific gene expression rather than thresholding effects."

1. Figure 5F and p.21 Methods, the authors analyze only 140 collagen genes and 38 ZP domain genes retrieved from InterPro, but there are at least 173 cuticle collagen genes and 43 ZP domain genes described in the literature. Therefore, their lists are incomplete and the Methods should say so.

Thank you for pointing this out. We changed the gene list to the cuticular collagens listed in Teuscher (2019). This did not affect the figure in a major way. We retrieved 44 ZP domain genes from InterPro, which match the ones listed by Cohen (2019) with the addition of cutl-19.

1. If most oscillatory gene expression is truly a function of the molt cycle, as suggested by the matrix gene families in Figure 5, then one might expect that most of the detected oscillatory genes would no longer be expressed in adults, or at least wouldn't appear "pulsatile" in adults. Is this true? There now are a variety of published adult data sets, including the Purice et al data on glia, that could be examined to address this.

PCA of adult cells does not exhibit the circular structure necessary to assess pulsatile expression. Previous work showed that most oscillatory genes are not expressed in adults, as expected (Meeuse et al. 2020).

**Referees cross-commenting**

I agree with the other reviewers' critiques, including the point of Reviewer #2 that orthogonal confirmation methods (such as by imaging) could have been nice but are not necessary. The question of Reviewer #3 about tissue synchrony/asynchrony is a very important one but I am not confident it can be addressed with these types of data.

Reviewer #1 (Significance (Required)):

As a molting invertebrate, C. elegans must build and shed its protective cuticle at multiple times across its life cycle, and this requires temporal control of many genes involved in matrix structure and processing. Although temporal oscillations were already well documented from bulk RNAseq data, this manuscript extends those prior findings by showing that different sets of genes oscillate within different cell types (including sensory glia), and by identifying many apparent oscillatory genes that were missed in prior studies because they are expressed in smaller populations of cells (whereas bulk data mainly report on oscillations within the major hypodermis). These data about cell-type specific temporal programs and gene sets emphasize the exquisite specificity of apical matrix and will be broadly useful to researchers in the C. elegans community.

A second major contribution of this manuscript is to pioneer analysis methods for detecting oscillatory gene expression in scRNAseq datasets, even where bulk temporal data may not exist. This will be valuable for others doing sRNAseq studies in nematodes but also in other systems where cells may have molt cycle- or circadian-regulated oscillations.

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

SECTION A - 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 use single cell sequencing (scRNA-Seq ) of cells obtained from larval stages of C elegans -- primarily the L4 stage, but also the L2. Worms are disrupted and individual cells are sorted by expression of fluorescent markers specific to glial cells, a cell type that is relatively rare in the population, and of particular interest to the focus of the study. In this fashion, the samples were enriched for glial cells but, bedcause the soting is not perfect, also contain representations of other cell populations, including hypodermal (skin) and other epithelial cells, muscles, and neurons. 2D representation of the scRNA-Seq data in principle component (PC) space reveals sets of cells of the same cell type (for example glia or skin cells) arranged in roughly circular patterns, indicative of rhythmic gene expression in those cell types. Much of this circular PC behavior is shown to be driven by genes that had previously been shown, by bulk RNAseq of staged larvae, to undergo rhythmic gene expression in conjunction with the larval stages and the molts that punctuate the larval stages. Based on the previously published relative timing of expression of these cycling genes, and the pattern of peak expression of each gene in the scRNA-Seq 2D PC space, the authors could calculate a phase angle of expression of each gene relative to its peak in each cell, and thereby calculate an average phase angle of all cycling gene for each cell, and place that metric in register with the roughly circular pattern of cell types in the 2D PC plot.

The authors show that many of these rhythmic genes encode extracellular matrix (ECM) proteins or other proteins related to cuticle synthesis and assembly, or molting. Cell types exhibiting cyclic gene expression included skin, pharyngeal epithelial, as well as several types of glia, notably socket glia, which synthesize a specialized ECM that surrounds and protects sensory neurons.

Finally, the authors analyze the patterns of cyclic gene expression in several cell types with respect to the expression of transcription factors (TFs) that are expressed in the cell type, including TFs that appear to likewise cycle, and whose predicted targets are enriched for cycling genes. From this computational analysis, the authors derive sets of hypothetical transcriptional regulatory circuits underlying phased expression of cycling genes.

Major comments:

• Are the key conclusions convincing?

1) Yes, the data support the conclusion that the authors' approach and methodology can take a list of genes known to cycle in expression level at larval stages and identify the cycling gene expression profiles of those genes in single cell sequencing datasets. It is also convincing that the authors' data analysis methods can identify cycling genes from the scRNA-Seq data that had not been previously identified as cycling from bulk RNAseq. Furthermore, the enrichment of genes encoding collagens and other ECM components is clear from the data.

2) The above being said, it is noteworthy that the conclusions of the manuscript - including the sets of predicted novel cycling genes, and the predicted transcription factor-target circuits -- were not confirmed experimentally using independent samples or orthogonal methodology. I think it is OK for the authors to leave these predictions for later experimental confirmation, but it would be appropriate for the authors to discuss this caveat about the need for strategic experimental tests to confirm the more novel findings presented here, while at the same time pointing out predictions from their analysis that fit with previous experimental findings (for example cases such as NHR-85 and NHR-23 where previous studies support that the relevant TF is involved in regulating molting-associated transcriptional activity.)

We have added the following sentence to "Limitations of the study":

"Further, while our results are consistent with other studies (Meeuse et al. 2020; Gaidatzis et al. 2025) and successfully identify known regulators such as NHR-23 and NHR-85, it will be important in future work to test expression of the novel oscillatory genes and the roles of novel regulators we have predicted."

3) There is an issue of concern that is perhaps about terminology, and not necessarily conceptual: Throughout the manuscript the authors variously use the terms, "oscillatory", "transient", and "pulsatile" to refer to cyclic gene expression. It seems that each of these terms could have distinct meanings, based on their English usage: The term "oscillatory" gene expression would seem to be a general term for gene expression that varies in a regular, rhythmic fashion. "Transient" gene expression seems like a general term for ON/OFF dynamics, albeit not necessarily oscillatory. "Pulsatile" gene expression implies oscillatory dynamics where the rise and fall of gene expression is relatively abrupt and might also imply ON/Off dynamics (between zero to some positive value). These terms are used seemingly interchangeably in the early parts of the manuscript, and then later, "pulsatile" is used increasingly, so the reader starts to wonder why. The authors should define these terms precisely and use the terminology deliberately and consistently.

We have clarified the important point about oscillatory vs. pulsatile in the text. Please see our response to Reviewer 1, Point 5. Additionally, we have removed the use of "transient" except in the context of the phrase "transient aECM" that has been established in the literature.

4) Related to the above, the authors should address how lowly-expressed genes behave in scRNA-Seq data, where the transcriptome is not fully sampled in each cell, and how that phenomenon could affect the apparent variation of gene expression within a population. My understanding is that if the expression level of a gene goes below some threshold percentage of the total transcriptome, it may not show up at all in the reads from that cell, even though the gene may still be expressed. Therefore, a gene can display apparent on/off behavior within a population of cells whilst the underlying variation in mRNA levels for that gene may be far less abrupt. How might this phenomenon affect the interpretation of a gene's dynamics as "pulsatile"?

We added the following to clarify that sampling variation among cells was mitigated by applying a smoothing function based on each cell's five nearest neighbors in PCA space:

"We then fitted the expression pattern of each gene with a generalized additive model (GAM) to obtain smoothed expression profiles. Because the GAM is fitted across many cells ordered along pseudotime, it captures the underlying expression trend even when individual cells show zero counts due to incomplete transcriptome sampling (e.g., Fig. 4A, black dots at y = 0)."

As further described in Methods, our pipeline also incorporates several features that mitigate this valid concern:

• First, before fitting gene-level dynamics, we retain only genes detected in at least 20 cells and in at least 5% of cells of a given cell type (Methods). While this filter may exclude some genuinely low-expressed oscillating genes, it ensures that pulsatile calls are made on genes where expression is reliably measurable.
• Second, we apply two levels of smoothing. Prior to PCA, k-nearest-neighbor smoothing ensures that each cell's expression profile reflects a local average of transcriptionally similar cells rather than a single noisy measurement. When modeling gene expression along pseudotime, we fit a generalized additive model (GAM) with cyclic cubic splines, pooling information across many cells. The curves we score as pulsatile therefore reflect averaged expression across neighborhoods of cells, rather than raw per-cell counts subject to dropout.
• Critically, dropouts arising from incomplete transcriptome sampling are independent of pseudotime (e.g., see dnj-1 in Fig. S3A). Our pulsatility criterion explicitly requires a low baseline combined with a well-shaped, high-amplitude peak in a specific pseudotime window, which dropout noise alone cannot generate. Indeed, as shown in Fig. 4A, the method readily identifies peaks even when many individual cells have zero detected reads (black dots at y = 0), demonstrating that the smoothed fit recovers the underlying dynamics from sparse data.
• Finally, during development we also tested a logistic GAM that models the probability of detecting at least one read per cell, rather than read counts directly, which produced comparable results, though it saturated for highly expressed genes.

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

5) Page 12: "Taken together, our results suggest that cuticle formation is the main commonality among pulsatile genes, and that distinct cell types use very different gene expression programs during this process. Thus, while cuticle aECM is typically perceived as a single homogeneous meshwork, our results suggest that the cuticle is actually a patchwork matrix with different patterning and composition contributed by distinct cell types."

It is not necessarily surprising that the cuticle made by skin cells could have composition non-identical to the cuticle made by glial cells or pharyngeal cells. But by describing the cuticle as a 'patchwork' elicits in the reader's mind an image of the skin of the animal (seam + Hyp) being mosaic for distinct cuticle compositions. Is that what the authors intend to say? It would be interesting if there were differences in composition of cuticle between skin cell types, and so it would be helpful if the authors could comment on how the transcript profiles compare for hypodermal seam cells vs multinucleate Hyp cells.

We have expanded on this idea:

"Taken together, our results suggest that cuticle formation is the main commonality among pulsatile genes, and that distinct cell types use very different gene expression programs during this process. Classical work showed that the cuticle exhibits regionalized specializations – for example, alae are present only over seam cells; annuli and struts are present over hyp7 but not near the nose; the vulval cuticle is thought to present structural or chemical signatures for recognition during mating; and the pharyngeal cuticle exhibits three short projections in the buccal cavity, sieve-like fingers between the metacorpus and isthmus, and grinder elements in the posterior bulb. However, the extent to which these structural differences correspond to distinct molecular composition was not known. Thus, while cuticle aECM is typically perceived as a single homogeneous meshwork, our Our results suggest that the cuticle is actually a patchwork matrix with different patterning and molecular composition contributed by distinct cell types."

• Would additional experiments be essential to support the claims of the paper?

6) The data here are mostly from L4 stage larvae, with a possible (but unknown) contribution from L2 larvae. It would be helpful, in terms of broader understanding of their roles in larval progression, if some of the oscillatory genes identified here (especially the novel ones) were tested by orthogonal methodology (such as fluorescent protein tagging) for oscillatory expression at other stages. However, these experiments are arguably beyond the scope of this paper, and as long as the authors note the importance of such confirmatory experiments in their Discussion, I don't think that further experimentation is critical for this paper.

We agree about the importance of these confirmatory experiments, and have added a comment in the Discussion (see response to Point 2 above).

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

7) In general, yes.

• Are the experiments adequately replicated and statistical analysis adequate?

8) Yes.

Minor comments:

• Specific experimental issues that are easily addressable.

9) Page 4: Regarding the single cell sequencing approach, the authors should comment on the extent to which mRNAs are efficiently recovered from hypodermal syncytial cells (Hyp), which are multinucleate. Could the data from Hyp be chiefly from nuclear transcripts? If so, how might that affect the interpretation of the data?

We have added a comment in Methods related to caveats of cell sorting vs. nuclei sorting (see response to Reviewer 1, Point 2). As the proportion of immature (unspliced) mRNA and reads corresponding to the mitochondrial genome are not noticeably different in the hypodermal cells than in other cell types, we do not think the data are chiefly from nuclear transcripts.

10) It is confusing that Table S1 lists male-enriched samples that were apparently sequenced, but only hermaphrodite data were analyzed for the paper. To prevent confusion, the male samples should not be listed.

We have clarified in the Methods that these samples are included in Table S1 because we wanted to share the datasets with the community:

"(Supp. Table S1; note this table includes related samples that were not used in the present analysis but that are deposited in the Gene Expression Omnibus (GEO) repository as a public resource)"

11) Page 5, bottom: The following analysis requires clarification (at least for this reader): "To test if such oscillatory gene expression is present in ILso glia, we computed the average phase of each cell (Fig. 2B). Specifically, for each cell, we computed a weighted circular average of the peak phases of oscillating genes (derived from the previous bulk RNA-Seq data), using the gene expression levels in that cell as weights."

In reading this part of the main text, this reader struggled to understand how one can compute the phase angle for a given gene in a cell by comparing its level of expression in that cell to measurement of the level of that gene in previous bulk RNA-Seq data. Of course, there is far more to the analysis than that, which the Methods and Materials section on page 18 describes in more detail, where one learns that the level if each gene in each cell is scaled to its maximum expression across all the cells analyzed, and that the previous bulk sequence analysis is used to simply provide a phase angle for the gene's peak expression relative to an arbitrary framework (which corresponds to a larval stage, one assumes). The presentation of this analysis on Page 5 in the main text should be revised to include a full description of what was done so the reader can follow along and understand it without having to read the Methods section. But moreover, the Methods section treatment of this analysis is still not entirely clear; for example, certain variables (W, s, and c) are not defined. The presentation of the mathematics should be clarified so that the reader can understand the analysis without having to look up scTransform-normalization.

We have expanded and clarified this section:

"To test if such oscillatory gene expression is present in ILso glia, we computed the average phase of each cell (Fig. 2B). Specifically, for each cell in our dataset, we considered its expression level of each of the 3,739 previously described oscillatory genes (Meeuse et al. 2020). To avoid biasing towards inherently highly-expressed genes (e.g., those encoding structural proteins), the expression of each gene in a given cell was scaled to its maximum expression across all cells. We then computed the average phase of each cell by taking the known phase for each gene (Meeuse et al. 2020) and calculating a weighted circular average, using the scaled expression of each gene in that cell as weights (Fig. 2B; each colored line represents one oscillatory gene with its angle representing its known phase and its length representing its scaled expression in that cell). we computed a weighted circular average of the peak phases of oscillating genes (derived from the previous bulk RNA-Seq data), using the gene expression levels in that cell as weights. This average results in a vector whose direction reflects the average phase of genes expressed in that cell, and whose length reflects how consistently the genes’ peak times align in that cell (Fig. 2B, black arrow)."

In the Methods, we have moved the definitions of W, s, and c so that they precede the formula for the average angle .

• Are prior studies referenced appropriately?

12) yes

• Are the text and figures clear and accurate? - Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

13) Figure S3 Panel A: What does the green line mean? Figure S3 Panel C: The use of the "predictors" tem is confusing because on page 8, the part of the narrative referring to Figure S3, the term used is "descriptors". Is that an meningful switch in terminology?

We have expanded and clarified the Supp. Fig. S3 legend. For simplicity, we now use the term "metrics" to refer to the parameters used for hierarchical clustering of pulsatile expression (peak amplitude, baseline, fit, shape). This replaces our previous uses of "predictors" and "descriptors".

14) The legend to Figure S3 requires more details to enable the reader understand the Figure. The same critique applies to most of the Supplemental Figure legends, where more details are required to allow the reader to understand each Figure without having to refer back to the main text.

Thank you for pointing this out. We have revised and expanded all of the Supplemental Figure legends.

15) Page 19: "The cells were grouped by cell type independent of the stage of collection (L2 or L4), and each cell type was processed individually."

Why were L2s and L4s pooled? How does this affect the analysis and/or the outcomes? Could there be confounding effects from pooling the samples that could affect the analysis or the conclusions?

We added the following clarification in the main text:

"Because we found that cells clustered together based on their cell type rather than developmental stage, L2 and L4 cells of the same cell type were pooled for all downstream analyses (see Methods)."

as well as the following explanation in the Methods:

"The cells corresponding to the same cell type at different stages were then merged for subsequent analysis. After annotation, cells of the same cell type from L2 and L4 datasets were pooled for downstream analysis, such that each cell type is represented as a single combined cluster across stages. This provides two advantages: it increases statistical power by increasing the number of cells, and it favors genes that are oscillating in both larval stages. Because L2 representation is more limited (Table S1), the pooled pseudotime is dominated by L4 dynamics, ensuring that L2 cells are anchored on the L4-defined trajectory."

**Referees cross-commenting**

There is substantial agreement amongst all three reviewers, regarding the signifcance of the findings and that the conclusions are well enough supported by the data such that no additional experiments are required. We all recommend revisions to clarify or expand the description of the experiments and/or analysis. Many comments are reiterated by more than one Reviewer. I agree with all the other reviewers' critiques.

Reviewer #2 (Significance (Required)):

SECTION B - Significance

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

The finding of oscillatory and molting-related gene expression patterns in glial cells emphasizes the importance of molting-related ECM/cuticle production by these sensory-accessory cells and will serve as a platform for further studies and further understanding the structural and molecular basis of glial cell support functions, especially in the context of changing roles for sensory neurons during developmental progression.

The methodology and data analysis of C. elegans scRNA-Seq data presented here offers several significant advances, especially since it had been known that thousands of genes cycle in rhythm with the C. elegans molting cycle, yet that was based on previous bulk sequencing, so it was not possible to resolve cell-type specific expression. This paper presents methods for analysis of cycling gene expression in specific cell types.

The manuscript derives hypothetical TF-target regulatory interactions that are proposed do underly cyclic gene expression in specific cell types. This is a significant resource for future work to explore and delineate upstream oscillator mechanisms, and answer questions such as, Is there a central oscillator for all of larval stage rhythmic gene expression? and, How are different genes expressed with different phases of the larval stages? etc.

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

The authors cite important previous studeis that used scRNA-Seq to profile gene expression in specific C. elegans cell type in various developmental and physiological settings, and previous studies that used bulk RNAseq to identify genes whose transcripts cycle along with the larval stages. This manuscript reports the first study to examine cyclic gene express in C. elegans on the single-cell level.

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

Moderately broad audience of biologists interested in biological oscillators; developmental biologists interested in gene regulatory control of developmental cell fate timing and reiterative developmental processes; neurobiologists interested in glial cell function in developmental contexts.

• Define your field of expertise with a few keywords to help the authors contextualize your point of view.

• C. elegans larval development; temporal control of cell fate progression. Are there are any parts of the paper that you do not have sufficient expertise to evaluate.

Honestly, some of the mathematical analysis is beyond my ability to judge whether the chosen approach is the best choice for the particular setting.

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

This study describes both new scRNA-seq data from C. elegans, targeting glia/epidermal cell types and especially the ILso glial cell, and analytical approaches to identify periodically expressed genes in the dataset. Overall the data appear of high quality so have value as a resource, and the analysis provides a substantial improvement in our understanding of how different cell types vary in their cyclic expression across the molt cycles. While I have make many suggestions, overall this is a very nice study as is and definitely seems likely to be an impactful publication.

Major

Figure 2:

• The dataset includes cells from multiple stages (L2 and L4 mentioned in the text, adult as well listed in Supplemental Table 1). There is a superficial display in Figure S1 which seems to imply that whether the same cell type clusters together across stages vs making stage specific clusters might be complex. But this isn't really discussed at all in the paper. For Figure 2 specifically it seems critical to know whether stages were pooled or separated for this analysis, and the question of whether the cyclic program varies across stages (at least for well sampled cells like ILso) is important.

Please see our response to Reviewer 2, Point 15.

Figure 3

• This approach overall is good for cells that cycle in a way their signature comes up in Meeuse but would it detect rare cell type cycles? Maybe the PCA space velocity approach could be a way to screen for cell types that cycle in a way that isn't detected in the whole organism time course data (or rule out the presence of large cycling gene sets)? For example "pharyngeal gland" seems to have a weak cycling signature using the Meeuse gene set (Fig. 3D) but fairly clear "circular UMAP" structure (Fig 3B).

We added the following to emphasize that our rationale for developing the perplexity metric is to identify oscillatory cell types de novo, i.e. without relying on the Meeuse et al. dataset:

"We hypothesized that this [perplexity] metric would distinguish between pulsatile cell types (corresponding to relatively high perplexity) and non-pulsatile cell types (corresponding to low perplexity), without relying on prior bulk annotations that may be insensitive to rare cell types."

Consistent with the reviewer's intuition, this approach does identify cell types missed by the Meeuse-based local phase coherence analysis, specifically coelomocytes and PHsh glia, which have perplexity >30 but did not reach significance by phase coherence (Fig. 5C).

Regarding the pharyngeal gland, this cell type has intermediate scores by both metrics and falls below our conservative thresholds (Fig. 5C). It is possible that it has a genuine but weak oscillatory program that our methods are underpowered to detect given the number of cells recovered for this cell type.

We considered using RNA velocity, but we have not succeeded in developing a satisfying quantitative score; therefore, the perplexity metric serves this role in our current analysis.

• Do these data say anything about the question of whether all cell types in an organism are synchronized in the same phase as each other, or whether some might be systematically earlier or later in the cycle at a given time? It seems like if individual samples have enough stage bias (as an illustrative but made up example, if sample "230421_AM" has mostly early L4 while "230421_PM" has mostly late L4), then these data could be used to see if for example ILso cells tend to have earlier or later phases in the same sample compared to hyp cells. In my view, this is an important enough general question in the field to be worth addressing if the data are sufficient. And it could also provide an independent way to support/refute the presence of additional cycling cells (see Fig. 5 comments)

This is an interesting idea, but unfortunately our synchronization at the population level is not sufficiently precise, and each sample contains cells spanning nearly the full phase range (shown below [IMAGE CANNOT BE ATTACHED HERE]). Under these conditions, between-sample phase offsets are dominated by within-sample dispersion, and we cannot reliably estimate systematic phase differences between cell types.

Figure 5

• This seems a nice approach to address the earlier question about detecting cell type specific oscillations. But then only results for the cell types previously identified as oscillatory are reported. It seems important to report the potential cycling genes for the other cell types (PHsh, Coelomocytes, maybe Pharyngeal Gland) so their cycling status could be tested by others in the future.

We revised the text to highlight that these gene lists are in Supp. Tables S3 and S4.:

"We limit our subsequent analyses to the 17 high-confidence cell types that appear oscillatory using both approaches (local phase coherence and perplexity), which together contain 5,268 pulsatile genes. Pulsatile gene lists for these and other cell types are provided in Supp. Tables S3 and S4 to facilitate independent assessment of their cycling status. A summary of pulsatile genes in these 17 cell types is shown in Table 1."

• Regarding the last section ("only 17% were pulsatile in five or more cell types", "only 10 genes were pulsatile in all 17 oscillatory cell types" etc) - thresholding of a dataset like this can lead to false negatives resulting from incomplete (and cell type specific differences in power) which is a common source of technical non-overlap in this type of comparison. Indeed it is notable that the highest overlap was with ILso (specific sort target, likely to be especially well powered) and CEPso. There are various approaches to estimate not just confident overlap but also confident non-overlap, for example the "irreproducible discovery rate" (IDR) approach commonly used for ChIP-seq data. While clearly based on gene set enrichment there is cell type specificity, I'd suggest toning down the interpretation of the fractional overlap in the text if this can't be resolved.

We toned down the interpretation of the fractional overlap:

"To what extent are the same sets of pulsatile genes shared between cell types? To address this question, we examined the overlap between the pulsatile genes we identified in each cell type (Fig. 5D), noting that because power to detect pulsatile expression varies across cell types, the overlap values we report are likely to underestimate the true sharing between cell types.

[…]

Put another way, 45% (2,390 of 5,268) of the genes we identified were detected as expressed and pulsatile exclusively in a single cell type while only 17% (915 of 5,268) were pulsatile in five or more cell types (Fig. 5E)."

Minor

Figure 1:

• I was a little unclear about the coloring in Fig 1C (are the colors by annotated tissue or something else like clusters?) - suggest specifying in the legend.

We updated the legend: "UMAP of the same cells as in B, with each cell colored by its annotated tissue identity."

• More details on clustering and annotations approaches in the methods would be useful.

We have substantially expanded the corresponding section.

• I have mixed feelings about the word "skin" in the figure panels - while more accessible to a broad audience, hypodermis or hyp subset labels (hyp 7 etc) might be more precise.

We have changed many of these to "skin-related." We cannot use the anatomical terms because we cannot confidently distinguish, for example, hyp1 vs hyp2, due to the lack of known markers for each cell type. We therefore refer to skin-related cluster 3 as "skin 3," because calling it "hyp 3" would lead to confusion with the anatomical term.

• Table S2 would benefit from including the number of cells annotated with each cell type name

We have added the number of cells per cell type to Supp. Table S2, with separate columns for L2, L4, and the total.

Figure 2

• Fig 2B is nice - clearly shows the difference in expression of phase specific genes in the two example cells and conceptual framework for averaging. I was struck by the relatively broad range of phase values though (For example the bottom cell has highly expressed genes with phases ranging from ~100 degrees to ~280). It seems this could reflect technical noise in the single cell data or imprecision in the phase calls in Meeuse. But there is also the interesting possibility that there is biological flexibility in the order/expression of phased genes at this single cell level. Not sure if there is an obvious way to address this or whether it should be in the scope of this work but maybe at least worthy of a mention

A parsimonious explanation for the broad range of phase values in a single cell is the shape of the peak: examining the data from Meeuse et al, oscillatory genes do not generally display a sharp peak, but rather elevated expression over a span of ~3h (out of a larval stage of ~8h), which would correspond to expression over 100°. Indeed, the decentered genes in Fig. 2B correspond to the genes F53F4.2 and cutl-10 which have their peak expression at ~135° (26 h of larval development in the Meeuse dataset) but are still expressed at ~180° (28 h of larval development in the Meeuse dataset). Importantly, expression peaks tend to be roughly symmetric around the cell's true phase and therefore reduce the length of the phase vector but do not affect the average phase itself.

Figure 3

• The class Alter et al SVD paper https://www.pnas.org/doi/full/10.1073/pnas.97.18.10101 was the first use case of SVD/PCA in genome wide expression data and used (cell cycle) periodic expression as the main use case. The plots in Figures 2 and 3 are very similar to that approach, which basically used the relevant (~sin and ~cos correlated) principle components to define phases of both samples and genes. I mention this mostly in case it is useful to see how they approached the question and maybe as a relevant citation.

We added the citation.

Figure 4

• Minor method clarification - how was DTW adapted to deal with circular data, specifically to identify cases where the peak is centered at pseudotime == 0/1? It seems from the figures that maybe some approach was used to center the raw data on the peak but I didn't see a description of how this was done (apologies if I missed it)

We edited the Methods to make the connection with the previous section more explicit:

"We used the trained model to predict expression of each gene along a grid of 128 regularly spaced pseudotime values, resulting in a smoothed expression profile. Further, for each gene, we shifted the pseudotime values to center the maximal expression value, and fitted a GAM as described above. To facilitate comparison of profile shapes across genes with different peak times, we additionally produced a centered version of each profile. For each gene, we identified the pseudotime at which the uncentered profile reached its maximum, then circularly shifted the pseudotime values so that this maximum fell at the center of the range (pseudotime 0.5). A new GAM was fit on the shifted data as described above, and used to predict expression along the same regular grid. This yielded a centered, smoothed expression profile for each gene in which all genes have their peak at the center of the pseudotime axis. These centered profiles were used in the subsequent section to compute both the baseline and shape metrics of each gene.

[…]

We then scaled the curve by its maximum value and centered it around its maximal value. We then scaled the centered smoothed expression profile (defined in the previous section) by its maximum value. The Dynamic Time Warp distance between the scaled and centered expression and an ideal sharp peak defined as the density of a normal distribution of mean 0.5 and standard deviation 0.01 was computed with the dtw package."

• The 2-PC view of ILso seems to align well with phase, but some of the other cell types (such as Seam in Figure 3C) are more complex - and also it seems possible that there could be cell types where the phase information is in e.g. PC2 and 3 instead of 1 and 2; how customizable is the approach and how dependent is it on a clean circular pattern in the PC plot?

• *

We have expanded the Discussion to include this point:

"This could indicate either a genuine absence of oscillatory programs; the presence of oscillations driven by only a few genes that are insufficient to shape PCA structure; or oscillations that are present but reside in higher principal components dominated in PCs 1-2 by other sources of cell-to-cell variation."

By using an Elastic Principal Cycle (ElPiGraph) to fit pseudotime rather than relying on angle from the origin (as is common for this type of data), we accommodate trajectories within PCs 1-2 that deviate from perfect circularity, including elongated or asymmetric shapes such as in seam cells (Fig. 3C). However, when phase information resides in higher-order PCs, in the absence of an independent timing reference there is no principled way to identify which PCs carry oscillatory signal versus other gradients of cell-to-cell variation. Recovering oscillations in such cell types would therefore require complementary approaches, such as synchronized time-course sampling, rather than a modification of the current pipeline.

• It would be useful to annotate the examples (Fig 4A, lower panels) with whether they were newly identified or known from the bulk time course. And consider a larger supplemental figure with a sampling of newly identified genes in a similar format across a range of amplitudes etc

We added Supplementary Figure S4C with examples across a range of amplitudes.

• The examples are all relatively tight peaks (width We developed an approach to quantify the width of peaks in the Meeuse data (Methods); we display the distribution of peak width for genes expressed in ILso and seam cells in the new Supplementary Figure S4A. Our approach did not display a systematic bias to detect narrow or wide peaks. We added the following in the Results:

“More generally, our classification captures a range of expression profile morphologies without apparent bias (Supp. Fig. S4).”

Figure 5

• There are important caveats in the interpretation of perplexity. For example a cell type that oscillates but with the vast majority of genes expressed uniformly or at one specific phase, would get a low perplexity, while a cell with multiple distinct states that don't cycle (this may be why body muscle has a modestly elevated sore) might achieve high perplexity. Worth addressing at some point.

We added these caveats:

"Potential caveats are that some non-oscillatory cell types might have high perplexity, for example if there are other sources of complex transcriptional heterogeneity among cells, while some oscillatory cell types might have low perplexity, for example if oscillating genes do not dominate the PCA structure."

• Fig 5C raises the question of how power (for each of these metrics) relates to number of cycling genes in a cell type and the density of its sampling across time (for example is glia 4 just a poorly sampled cell type, or is it qualitatively different in what fraction of its transcriptome is cycling?). Just recoloring this plot by number of single cells per annotation might touch on this, or could try a subsampling approach.

We added this with the new Supp. Fig. S5C:

"To test whether differences in perplexity could be explained by differences in the number of sampled cells, we recomputed perplexity after subsampling to progressively smaller numbers of cells for several representative cell types. Perplexity values were largely stable across subsample sizes, indicating that the classification of cell types as oscillatory or non-oscillatory is not driven by differences in statistical power (Supp. Fig. S5C)."

• The identification of pharyngeal muscle and epithelial oscillatory genes is a nice resource aspect of this paper given past work by EM showing these cells changing across the life cycle; it appears these cells have distinct enrichments (Fig 5G) and I think talking about these differences more explicitly could add to the closing paragraph in this section about aECM heterogeneity

We have added the following:

"In addition, the nematode astacin (NAS) metalloproteases appeared enriched in pulsatile genes in glia and pharynx, but not hypodermis (Fig. 5G, Supp. Table S6), consistent with ultrastructural observations that the pharyngeal muscle becomes secretory during molts and that the protease NAS-6 is required to digest the old pharyngeal cuticle (Sparacio et al., 2020)."

Figure 6

• This section is great and a very useful resource for future work. A detailed analysis may be beyond the scope of this work, but for Fig 6B I wondered whether the TF oscillation phase matched/preceded the timing of its predicted targets (for the subset of TFs that were themselves oscillatory in that cell type)? Even a qualitative analysis of this would be informative.

We added a new supplementary Figure S7 and commented on it in the text:

"__For the subset of TFs that are themselves pulsatile, we asked whether their peak expression coincides with or precedes that of their predicted targets. We found that pulsatile targets are modestly enriched in a temporal window around the TF's own peak (Supp. Fig S7), consistent with near-simultaneous expression of TFs and their targets, as previously observed for nhr-23 (Johnson et al., 2023). This temporal enrichment was most consistent for nhr-23 and nhr-25, which showed significant enrichment across most cell types, while other TFs showed more variable patterns (Supp. Fig. S7)."__

Open-ended/discretionary

A general challenge in single cell data analysis is that standard methods like clustering can give misleading or hard to interpret results when multiple processes occur simultaneously. For example, cells can have signatures of cell fate and cell cycle and depending on the genes used for clustering and strengths of those signals, naïve clustering may cause them to group by either fate of cell cycle phase. This is a long-winded way to say an application of the approach reported here would be to identify cycling genes shared between cell types that could be removed from the "variably expressed genes" lists prior to clustering to improve cell type separation, or used exclusively to allow clustering by phase rather than cell type. (definitely discretionary to consider this but could be mentioned in Discussion as a possible application)

**Referees cross-commenting**

I agree with all of this, including Reviewer #1 that asynchrony may be hard to address with current data, and with both reviewers that the dataset stands on its own.

Reviewer #3 (Significance (Required)):

This paper addresses the problem of how to identify cycling genes in single cell data, using the C. elegans larval/molt cycle as a model system. The system has emerged as a powerful model for understanding regulation of periodic gene expression, with past bulk RNA-seq time course have identified 1000s of cycling genes. However, how cyclic gene expression varies across cell types was not known. This study uses single cell RNA-seq and develops new analysis approaches to identify cycling genes across dozens of C. elegans cell types. Strengths are the generation of a new single cell data enriched for larval glia, identification of cyclic gene expression across many C. elegans cell types, an improved analytical framework for identifying cycling genes that could be applied in other datasets, and substantial analysis of pathways and regulators involved. Weaknesses are limited, and include minor overinterpretations of the data and missed opportunities for additional analyses. The work should be of interest to a broad audience including not just C. elegans researchers but also the single cell and chronobiology communities.

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

Learn more at Review Commons

Referee #3

Evidence, reproducibility and clarity

This study describes both new scRNA-seq data from C. elegans, targeting glia/epidermal cell types and especially the ILso glial cell, and analytical approaches to identify periodically expressed genes in the dataset. Overall the data appear of high quality so have value as a resource, and the analysis provides a substantial improvement in our understanding of how different cell types vary in their cyclic expression across the molt cycles. While I have make many suggestions, overall this is a very nice study as is and definitely seems likely to be an impactful publication.

Major

Figure 2:

• The dataset includes cells from multiple stages (L2 and L4 mentioned in the text, adult as well listed in Supplemental Table 1). There is a superficial display in Figure S1 which seems to imply that whether the same cell type clusters together across stages vs making stage specific clusters might be complex. But this isn't really discussed at all in the paper. For Figure 2 specifically it seems critical to know whether stages were pooled or separated for this analysis, and the question of whether the cyclic program varies across stages (at least for well sampled cells like ILso) is important.

Figure 3

• This approach overall is good for cells that cycle in a way their signature comes up in Meeuse but would it detect rare cell type cycles? Maybe the PCA space velocity approach could be a way to screen for cell types that cycle in a way that isn't detected in the whole organism time course data (or rule out the presence of large cycling gene sets)? For example "pharyngeal gland" seems to have a weak cycling signature using the Meeuse gene set (Fig. 3D) but fairly clear "circular UMAP" structure (Fig 3B).
• Do these data say anything about the question of whether all cell types in an organism are synchronized in the same phase as each other, or whether some might be systematically earlier or later in the cycle at a given time? It seems like if individual samples have enough stage bias (as an illustrative but made up example, if sample "230421_AM" has mostly early L4 while "230421_PM" has mostly late L4), then these data could be used to see if for example ILso cells tend to have earlier or later phases in the same sample compared to hyp cells. In my view, this is an important enough general question in the field to be worth addressing if the data are sufficient. And it could also provide an independent way to support/refute the presence of additional cycling cells (see Fig. 5 comments)

Figure 5

• This seems a nice approach to address the earlier question about detecting cell type specific oscillations. But then only results for the cell types previously identified as oscillatory are reported. It seems important to report the potential cycling genes for the other cell types (PHsh, Coelomocytes, maybe Pharyngeal Gland) so their cycling status could be tested by others in the future.
• Regarding the last section ("only 17% were pulsatile in five or more cell types", "only 10 genes were pulsatile in all 17 oscillatory cell types" etc) - thresholding of a dataset like this can lead to false negatives resulting from incomplete (and cell type specific differences in power) which is a common source of technical non-overlap in this type of comparison. Indeed it is notable that the highest overlap was with ILso (specific sort target, likely to be especially well powered) and CEPso. There are various approaches to estimate not just confident overlap but also confident non-overlap, for example the "irreproducible discovery rate" (IDR) approach commonly used for ChIP-seq data. While clearly based on gene set enrichment there is cell type specificity, I'd suggest toning down the interpretation of the fractional overlap in the text if this can't be resolved.

Minor

Figure 1:

• I was a little unclear about the coloring in Fig 1C (are the colors by annotated tissue or something else like clusters?) - suggest specifying in the legend.
• More details on clustering and annotations approaches in the methods would be useful.
• I have mixed feelings about the word "skin" in the figure panels - while more accessible to a broad audience, hypodermis or hyp subset labels (hyp 7 etc) might be more precise.
• Table S2 would benefit from including the number of cells annotated with each cell type name

Figure 2

• Fig 2B is nice - clearly shows the difference in expression of phase specific genes in the two example cells and conceptual framework for averaging. I was struck by the relatively broad range of phase values though (For example the bottom cell has highly expressed genes with phases ranging from ~100 degrees to ~280). It seems this could reflect technical noise in the single cell data or imprecision in the phase calls in Meeuse. But there is also the interesting possibility that there is biological flexibility in the order/expression of phased genes at this single cell level. Not sure if there is an obvious way to address this or whether it should be in the scope of this work but maybe at least worthy of a mention

Figure 3

• The class Alter et al SVD paper https://www.pnas.org/doi/full/10.1073/pnas.97.18.10101 was the first use case of SVD/PCA in genome wide expression data and used (cell cycle) periodic expression as the main use case. The plots in Figures 2 and 3 are very similar to that approach, which basically used the relevant (~sin and ~cos correlated) principle components to define phases of both samples and genes. I mention this mostly in case it is useful to see how they approached the question and maybe as a relevant citation.

Figure 4

• Minor method clarification - how was DTW adapted to deal with circular data, specifically to identify cases where the peak is centered at pseudotime == 0/1? It seems from the figures that maybe some approach was used to center the raw data on the peak but I didn't see a description of how this was done (apologies if I missed it)
• The 2-PC view of ILso seems to align well with phase, but some of the other cell types (such as Seam in Figure 3C) are more complex - and also it seems possible that there could be cell types where the phase information is in e.g. PC2 and 3 instead of 1 and 2; how customizable is the approach and how dependent is it on a clean circular pattern in the PC plot?
• It would be useful to annotate the examples (Fig 4A, lower panels) with whether they were newly identified or known from the bulk time course. And consider a larger supplemental figure with a sampling of newly identified genes in a similar format across a range of amplitudes etc
• The examples are all relatively tight peaks (width <0.5 pseudotime units) - is this approach able to identify genes with wider "plateau" patterns (and do such patterns exist?) Figure 5
• There are important caveats in the interpretation of perplexity. For example a cell type that oscillates but with the vast majority of genes expressed uniformly or at one specific phase, would get a low perplexity, while a cell with multiple distinct states that don't cycle (this may be why body muscle has a modestly elevated sore) might achieve high perplexity. Worth addressing at some point.
• Fig 5C raises the question of how power (for each of these metrics) relates to number of cycling genes in a cell type and the density of its sampling across time (for example is glia 4 just a poorly sampled cell type, or is it qualitatively different in what fraction of its transcriptome is cycling?). Just recoloring this plot by number of single cells per annotation might touch on this, or could try a subsampling approach.
• The identification of pharyngeal muscle and epithelial oscillatory genes is a nice resource aspect of this paper given past work by EM showing these cells changing across the life cycle; it appears these cells have distinct enrichments (Fig 5G) and I think talking about these differences more explicitly could add to the closing paragraph in this section about aECM heterogeneity

Figure 6

• This section is great and a very useful resource for future work. A detailed analysis may be beyond the scope of this work, but for Fig 6B I wondered whether the TF oscillation phase matched/preceded the timing of its predicted targets (for the subset of TFs that were themselves oscillatory in that cell type)? Even a qualitative analysis of this would be informative.

Open-ended/discretionary

A general challenge in single cell data analysis is that standard methods like clustering can give misleading or hard to interpret results when multiple processes occur simultaneously. For example, cells can have signatures of cell fate and cell cycle and depending on the genes used for clustering and strengths of those signals, naïve clustering may cause them to group by either fate of cell cycle phase. This is a long-winded way to say an application of the approach reported here would be to identify cycling genes shared between cell types that could be removed from the "variably expressed genes" lists prior to clustering to improve cell type separation, or used exclusively to allow clustering by phase rather than cell type. (definitely discretionary to consider this but could be mentioned in Discussion as a possible application)

Referees cross-commenting

I agree with all of this, including Reviewer #1 that asynchrony may be hard to address with current data, and with both reviewers that the dataset stands on its own.

Significance

This paper addresses the problem of how to identify cycling genes in single cell data, using the C. elegans larval/molt cycle as a model system. The system has emerged as a powerful model for understanding regulation of periodic gene expression, with past bulk RNA-seq time course have identified 1000s of cycling genes. However, how cyclic gene expression varies across cell types was not known. This study uses single cell RNA-seq and develops new analysis approaches to identify cycling genes across dozens of C. elegans cell types. Strengths are the generation of a new single cell data enriched for larval glia, identification of cyclic gene expression across many C. elegans cell types, an improved analytical framework for identifying cycling genes that could be applied in other datasets, and substantial analysis of pathways and regulators involved. Weaknesses are limited, and include minor overinterpretations of the data and missed opportunities for additional analyses. The work should be of interest to a broad audience including not just C. elegans researchers but also the single cell and chronobiology communities.

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

Learn more at Review Commons

Referee #2

Evidence, reproducibility and clarity

Summary:

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

The authors use single cell sequencing (scRNA-Seq ) of cells obtained from larval stages of C elegans -- primarily the L4 stage, but also the L2. Worms are disrupted and individual cells are sorted by expression of fluorescent markers specific to glial cells, a cell type that is relatively rare in the population, and of particular interest to the focus of the study. In this fashion, the samples were enriched for glial cells but, bedcause the soting is not perfect, also contain representations of other cell populations, including hypodermal (skin) and other epithelial cells, muscles, and neurons. 2D representation of the scRNA-Seq data in principle component (PC) space reveals sets of cells of the same cell type (for example glia or skin cells) arranged in roughly circular patterns, indicative of rhythmic gene expression in those cell types. Much of this circular PC behavior is shown to be driven by genes that had previously been shown, by bulk RNAseq of staged larvae, to undergo rhythmic gene expression in conjunction with the larval stages and the molts that punctuate the larval stages. Based on the previously published relative timing of expression of these cycling genes, and the pattern of peak expression of each gene in the scRNA-Seq 2D PC space, the authors could calculate a phase angle of expression of each gene relative to its peak in each cell, and thereby calculate an average phase angle of all cycling gene for each cell, and place that metric in register with the roughly circular pattern of cell types in the 2D PC plot.

The authors show that many of these rhythmic genes encode extracellular matrix (ECM) proteins or other proteins related to cuticle synthesis and assembly, or molting. Cell types exhibiting cyclic gene expression included skin, pharyngeal epithelial, as well as several types of glia, notably socket glia, which synthesize a specialized ECM that surrounds and protects sensory neurons.

Finally, the authors analyze the patterns of cyclic gene expression in several cell types with respect to the expression of transcription factors (TFs) that are expressed in the cell type, including TFs that appear to likewise cycle, and whose predicted targets are enriched for cycling genes. From this computational analysis, the authors derive sets of hypothetical transcriptional regulatory circuits underlying phased expression of cycling genes.

Major comments:

• Are the key conclusions convincing?

1) Yes, the data support the conclusion that the authors' approach and methodology can take a list of genes known to cycle in expression level at larval stages and identify the cycling gene expression profiles of those genes in single cell sequencing datasets. It is also convincing that the authors' data analysis methods can identify cycling genes from the scRNA-Seq data that had not been previously identified as cycling from bulk RNAseq. Furthermore, the enrichment of genes encoding collagens and other ECM components is clear from the data.

2) The above being said, it is noteworthy that the conclusions of the manuscript - including the sets of predicted novel cycling genes, and the predicted transcription factor-target circuits -- were not confirmed experimentally using independent samples or orthogonal methodology. I think it is OK for the authors to leave these predictions for later experimental confirmation, but it would be appropriate for the authors to discuss this caveat about the need for strategic experimental tests to confirm the more novel findings presented here, while at the same time pointing out predictions from their analysis that fit with previous experimental findings (for example cases such as NHR-85 and NHR-23 where previous studies support that the relevant TF is involved in regulating molting-associated transcriptional activity.)

3) There is an issue of concern that is perhaps about terminology, and not necessarily conceptual: Throughout the manuscript the authors variously use the terms, "oscillatory", "transient", and "pulsatile" to refer to cyclic gene expression. It seems that each of these terms could have distinct meanings, based on their English usage: The term "oscillatory" gene expression would seem to be a general term for gene expression that varies in a regular, rhythmic fashion. "Transient" gene expression seems like a general term for ON/OFF dynamics, albeit not necessarily oscillatory. "Pulsatile" gene expression implies oscillatory dynamics where the rise and fall of gene expression is relatively abrupt and might also imply ON/Off dynamics (between zero to some positive value). These terms are used seemingly interchangeably in the early parts of the manuscript, and then later, "pulsatile" is used increasingly, so the reader starts to wonder why. The authors should define these terms precisely and use the terminology deliberately and consistently.

4) Related to the above, the authors should address how lowly-expressed genes behave in scRNA-Seq data, where the transcriptome is not fully sampled in each cell, and how that phenomenon could affect the apparent variation of gene expression within a population. My understanding is that if the expression level of a gene goes below some threshold percentage of the total transcriptome, it may not show up at all in the reads from that cell, even though the gene may still be expressed. Therefore, a gene can display apparent on/off behavior within a population of cells whilst the underlying variation in mRNA levels for that gene may be far less abrupt. How might this phenomenon affect the interpretation of a gene's dynamics as "pulsatile"? - Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether?

5) Page 12: "Taken together, our results suggest that cuticle formation is the main commonality among pulsatile genes, and that distinct cell types use very different gene expression programs during this process. Thus, while cuticle aECM is typically perceived as a single homogeneous meshwork, our results suggest that the cuticle is actually a patchwork matrix with different patterning and composition contributed by distinct cell types."

It is not necessarily surprising that the cuticle made by skin cells could have composition non-identical to the cuticle made by glial cells or pharyngeal cells. But by describing the cuticle as a 'patchwork' elicits in the reader's mind an image of the skin of the animal (seam + Hyp) being mosaic for distinct cuticle compositions. Is that what the authors intend to say? It would be interesting if there were differences in composition of cuticle between skin cell types, and so it would be helpful if the authors could comment on how the transcript profiles compare for hypodermal seam cells vs multinucleate Hyp cells. - Would additional experiments be essential to support the claims of the paper?

6) The data here are mostly from L4 stage larvae, with a possible (but unknown) contribution from L2 larvae. It would be helpful, in terms of broader understanding of their roles in larval progression, if some of the oscillatory genes identified here (especially the novel ones) were tested by orthogonal methodology (such as fluorescent protein tagging) for oscillatory expression at other stages. However, these experiments are arguably beyond the scope of this paper, and as long as the authors note the importance of such confirmatory experiments in their Discussion, I don't think that further experimentation is critical for this paper. - Are the data and the methods presented in such a way that they can be reproduced?

7) In general, yes. - Are the experiments adequately replicated and statistical analysis adequate?

8) Yes.

Minor comments:

• Specific experimental issues that are easily addressable.

9) Page 4: Regarding the single cell sequencing approach, the authors should comment on the extent to which mRNAs are efficiently recovered from hypodermal syncytial cells (Hyp), which are multinucleate. Could the data from Hyp be chiefly from nuclear transcripts? If so, how might that affect the interpretation of the data?

10) It is confusing that Table S1 lists male-enriched samples that were apparently sequenced, but only hermaphrodite data were analyzed for the paper. To prevent confusion, the male samples should not be listed.

11) Page 5, bottom: The following analysis requires clarification (at least for this reader): "To test if such oscillatory gene expression is present in ILso glia, we computed the average phase of each cell (Fig. 2B). Specifically, for each cell, we computed a weighted circular average of the peak phases of oscillating genes (derived from the previous bulk RNA-Seq data), using the gene expression levels in that cell as weights."

In reading this part of the main text, this reader struggled to understand how one can compute the phase angle for a given gene in a cell by comparing its level of expression in that cell to measurement of the level of that gene in previous bulk RNA-Seq data. Of course, there is far more to the analysis than that, which the Methods and Materials section on page 18 describes in more detail, where one learns that the level if each gene in each cell is scaled to its maximum expression across all the cells analyzed, and that the previous bulk sequence analysis is used to simply provide a phase angle for the gene's peak expression relative to an arbitrary framework (which corresponds to a larval stage, one assumes). The presentation of this analysis on Page 5 in the main text should be revised to include a full description of what was done so the reader can follow along and understand it without having to read the Methods section. But moreover, the Methods section treatment of this analysis is still not entirely clear; for example, certain variables (W, s, and c) are not defined. The presentation of the mathematics should be clarified so that the reader can understand the analysis without having to look up scTransform-normalization. - Are prior studies referenced appropriately?

12) yes - Are the text and figures clear and accurate? - Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

13) Figure S3 Panel A: What does the green line mean? Figure S3 Panel C: The use of the "predictors" tem is confusing because on page 8, the part of the narrative referring to Figure S3, the term used is "descriptors". Is that an meningful switch in terminology?

14) The legend to Figure S3 requires more details to enable the reader understand the Figure. The same critique applies to most of the Supplemental Figure legends, where more details are required to allow the reader to understand each Figure without having to refer back to the main text.

15) Page 19: "The cells were grouped by cell type independent of the stage of collection (L2 or L4), and each cell type was processed individually."

Why were L2s and L4s pooled? How does this affect the analysis and/or the outcomes? Could there be confounding effects from pooling the samples that could affect the analysis or the conclusions?

Referees cross-commenting

There is substantial agreement amongst all three reviewers, regarding the signifcance of the findings and that the conclusions are well enough supported by the data such that no additional experiments are required. We all recommend revisions to clarify or expand the description of the experiments and/or analysis. Many comments are reiterated by more than one Reviewer. I agree with all the other reviewers' critiques.

Significance

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

The finding of oscillatory and molting-related gene expression patterns in glial cells emphasizes the importance of molting-related ECM/cuticle production by these sensory-accessory cells and will serve as a platform for further studies and further understanding the structural and molecular basis of glial cell support functions, especially in the context of changing roles for sensory neurons during developmental progression.

The methodology and data analysis of C. elegans scRNA-Seq data presented here offers several significant advances, especially since it had been known that thousands of genes cycle in rhythm with the C. elegans molting cycle, yet that was based on previous bulk sequencing, so it was not possible to resolve cell-type specific expression. This paper presents methods for analysis of cycling gene expression in specific cell types.

The manuscript derives hypothetical TF-target regulatory interactions that are proposed do underly cyclic gene expression in specific cell types. This is a significant resource for future work to explore and delineate upstream oscillator mechanisms, and answer questions such as, Is there a central oscillator for all of larval stage rhythmic gene expression? and, How are different genes expressed with different phases of the larval stages? etc. - Place the work in the context of the existing literature (provide references, where appropriate).

The authors cite important previous studeis that used scRNA-Seq to profile gene expression in specific C. elegans cell type in various developmental and physiological settings, and previous studies that used bulk RNAseq to identify genes whose transcripts cycle along with the larval stages. This manuscript reports the first study to examine cyclic gene express in C. elegans on the single-cell level. - State what audience might be interested in and influenced by the reported findings.

Moderately broad audience of biologists interested in biological oscillators; developmental biologists interested in gene regulatory control of developmental cell fate timing and reiterative developmental processes; neurobiologists interested in glial cell function in developmental contexts. - Define your field of expertise with a few keywords to help the authors contextualize your point of view.

C. elegans larval development; temporal control of cell fate progression.

Are there are any parts of the paper that you do not have sufficient expertise to evaluate.

Honestly, some of the mathematical analysis is beyond my ability to judge whether the chosen approach is the best choice for the particular setting.

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Referee #1

Evidence, reproducibility and clarity

This interesting manuscript uses single cell RNAseq of developing C. elegans larvae to identify temporal pulses or oscillations in gene expression within glia and many other epithelial cell types - mostly in genes related to cuticle synthesis or remodeling. It identifies different sets of genes that oscillate within different cell types, and identifies many apparent oscillatory genes that were missed in prior studies because they are expressed in smaller populations of cells (whereas bulk data mainly report on oscillations within the major hypodermis).

A second major contribution of this manuscript is to pioneer analysis methods for detecting oscillatory gene expression in scRNAseq datasets. That said, it's important to state that the methods for estimating phase coherence, GAM, perplexity, etc. make sense to me intuitively but I can't assess the math and other details, which are outside of my expertise.

Most of my comments are minor ones about suggested clarifications to the text or figures. Some may require additional analyses, but none should require additional data collection.

1. The manuscript focuses much of its analysis on one specific glial cell type (ILso), yet the authors tell us almost nothing about this cell type or why they would care about it. It would be helpful to include just a little more background on glial biology and the epithelial-like characteristics of socket glia.
2. Many transcriptomic studies of epithelia (including the Purice et al study of adult glia) use single NUCLEI RNAseq rather than single cells because of the challenges in separating cells connected by tight junctions. In C. elegans there are also various epithelial syncytia to contend with. In text or Methods, the authors should comment on why they think cells were appropriate to look at in this instance, and whether there are certain cell types that were missed or could only be obtained as cell fragments based on that choice.
3. Related to above, the authors do not mention any detection or exclusion of likely doublets. Is there reason to think that doublets were not present in any substantial numbers? I'm not super concerned about this since doublets containing hyp7 fragments should have worked against them in detecting glia-specific oscillations, but I do think the issue should be addressed in the text or Methods.
4. p. 4 "previously unappreciated local differences in cuticle patterning." This statement should be tempered since many stage- or tissue-specific differences in cuticle patterning have been described previously (including in papers from the Heiman lab and others that are cited here). This study uncovers many additional examples but it's not a completely new finding.
5. Table 1 and text: the distinction between pulsatile and oscillatory should be explained more at the outset. These terms sometimes seem to be used interchangeably, but then Table 1 seems to make a distinction, not discussed until the final "limitations" section.
6. Figure 1 and Figure 3A,B. These UMAPs look very unusual, with no discernable individual dots. Is this just a resolution issue? Or, if relevant, please add info to legend and/or Methods explaining what data smoothing was done here to make them look this way and why.
7. Figure 2C and Figure 6B. In the pseudotime plots, it would be natural for readers to assume that 0 is the beginning of the larval stage and 360 is the end, but that is not actually the way the Meeuse 2020 phase angles work - instead the beginning of the larval stage falls around 160. Please make sure this is made clear, especially when referring to "early and late groups" of TF targets. In Fig 6B, Early and Late categories appear reversed because of the way the data are plotted.
8. Figure 3B and Figure 5D-G. The authors group many unidentified clusters into the catchall "skin" category but don't clearly define it in the main text. Table S2 suggests this category includes anterior and posterior skin cells but possibly also other cuticle-lined tubular epithelia that aren't properly referred to as skin (e.g. vulva cells, excretory socket or pore cells). It may also include things like rectum, buccal cavity, excretory duct. Please define your criteria for "skin" more precisely in the main text (any cuticle-lined cell type that is not glia?), and perhaps a more general term such as external epithelia would be more appropriate.
9. Also related to cluster assignments: please specify if "excretory" category includes canal, duct, pore, gland all together, or only a subset of these. Only the duct and pore are cuticle lined and therefore expected to have oscillatory matrix gene expression.
10. Figure 5. This figure feels disjointed and could be broken up into two figures (panels A-C and panels D-G). The first 3 panels seem more related to Figures 3 & 4 - identifying which cell types have strong pulsatile gene expression - whereas the later panels get into the degree of cell type specificity in matrix gene expression.
11. Figure 5D-E. The very low degree of sharing is fascinating but could be an underestimate that depends on the thresholds chosen for calling a gene "pulsatile". It may be helpful to test a range of thresholds to see how much this matters. For those ~2,500 genes that appear pulsatile in just one cell type, are they called expressed but non-pulsatile in other cell types? That would seem odd to me biologically and most likely a threshold artifact.
12. Figure 5F and p.21 Methods, the authors analyze only 140 collagen genes and 38 ZP domain genes retrieved from InterPro, but there are at least 173 cuticle collagen genes and 43 ZP domain genes described in the literature. Therefore, their lists are incomplete and the Methods should say so.

https://pubmed.ncbi.nlm.nih.gov/33543001/ https://pubmed.ncbi.nlm.nih.gov/30409789/ 13. If most oscillatory gene expression is truly a function of the molt cycle, as suggested by the matrix gene families in Figure 5, then one might expect that most of the detected oscillatory genes would no longer be expressed in adults, or at least wouldn't appear "pulsatile" in adults. Is this true? There now are a variety of published adult data sets, including the Purice et al data on glia, that could be examined to address this.

Referees cross-commenting

I agree with the other reviewers' critiques, including the point of Reviewer #2 that orthogonal confirmation methods (such as by imaging) could have been nice but are not necessary. The question of Reviewer #3 about tissue synchrony/asynchrony is a very important one but I am not confident it can be addressed with these types of data.

Significance

As a molting invertebrate, C. elegans must build and shed its protective cuticle at multiple times across its life cycle, and this requires temporal control of many genes involved in matrix structure and processing. Although temporal oscillations were already well documented from bulk RNAseq data, this manuscript extends those prior findings by showing that different sets of genes oscillate within different cell types (including sensory glia), and by identifying many apparent oscillatory genes that were missed in prior studies because they are expressed in smaller populations of cells (whereas bulk data mainly report on oscillations within the major hypodermis). These data about cell-type specific temporal programs and gene sets emphasize the exquisite specificity of apical matrix and will be broadly useful to researchers in the C. elegans community.

A second major contribution of this manuscript is to pioneer analysis methods for detecting oscillatory gene expression in scRNAseq datasets, even where bulk temporal data may not exist. This will be valuable for others doing sRNAseq studies in nematodes but also in other systems where cells may have molt cycle- or circadian-regulated oscillations.

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Reply to the reviewers

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

Summary In this study, Phalora et al identified the selective autophagy receptor SQSTM1/p62 as a MR1 interacting protein by proteomics approach using a cell line overexpressing MR1. While SQSTM1/p62 is implicated in autophagy regulation and autophagosome formation, genetic ablation of SQSTM1/p62 resulted in enhanced MAIT cell activation upon challenge with E. coli, but not with a synthetic agonist 5-OP-RU. In contrast, knockout of Atg5 and Atg7, both of which are involved in phagophore expansion engendered increased activation of MAIT cells upon both stimuli. From these data, the authors concluded that some factors in autophagy controlled the MR1 activity, thus the autophagy is a pivotal regulator of cellular antigen presentation.

Major comments: 1. The notion that "This regulation appears to occur at an early step in the trafficking pathway." in the summary appears not to be compatible with the present data. What the authors have shown in the study is possible implication of autophagy components such as SQSTM1/p62, Atg5, and Atg7 that are implicated in autophagosome and phagophore formation. Should the authors highlight an "early step of trafficking", Atg14L, Atg13, and/or Atg101 must be analyzed by genetic knockout in addition to PI3 kinase inhibitors that are supposed to affect an early step in autophagy. Such an approach could confirm whether the regulation of MR1 occurs at an early step of trafficking, or at least, at an early step of autophagy.__

The reviewer may have misinterpreted our conclusion. When we state ‘an early step in the trafficking pathway’ we are referring to MR1 trafficking (from the ER to the PM) and not to early steps in the autophagy pathway. We have modified the text to make this clearer.

__ In Figure 2, while the degree of β2M depletion from B1 appears to be superior to that in B6 (Figure 2A), why the former was more potent in producing IFN-γ relative to the latter upon E. coli and 5-OP-RU (Figure 2D)?__

We cannot conclusively say why MAIT cell activation is reduced to a greater extent in clone B6 compared to clone B1, whereas the protein depletion is not as pronounced. Most likely as these are clonal cells there may be genetic/phenotypic differences apart from depletion of B2M that may impact upon antigen presentation. Importantly both B1 and B6 are significantly decreased in terms of MR1 surface expression and MAIT cell activation compared to the control as would be expected.

__ In Figure 3B, right column, what is Ac-6-FP? The left histograms show MR1 expression level upon DMSO, E. coli, and 5-OP-RU challenge. There is no explanation.__

We thank the reviewer for pointing this out. The bar chart was mislabelled and should read 5-OP-RU (as in the histogram). This has now been corrected in the figure.

__ Also in the same figure, was MR1 geomeans in Control, 5-1, 5-2, 5-3, 7-1, 7-2, and 7-3 upon Ac-6-FP superior to DMSO? If so or not, please explain the rational.__

The difference in MR1 geomeans between DMSO and 5-OP-RU treated cells was significantly different. However as stated in the text the difference between control and Atg depleted cells for each condition was not statistically significant although there is a trend for increasing MR1 expression in KD cells.

__ Figure 3C is highly intentional. If the authors put two left panels together (Control, 5-1, 5-2, and 5-3), is there still statistical difference among them?__

The data for Atg5.3 was displayed separately as the experiments for this cell line were performed at a later timepoint using different donor cells. Therefore, it would be inappropriate to combine and/or compare them with the data for Atg 5.1 and 5.2. For clarity the figure has now been modified and this explanation added to the figure legend.

__ There was no explanation for Figure 4B why the authors used Hela-MR1-HA. Other cell lines were used in the rest of the experiments. It is highly desirable to perform the experiment with THP1-MR1-HA in terms of logical development.__

As the reviewer correctly states, it would be ideal to use Thp.MR1.HA cells for these microscopy experiments as they have been used throughout the rest of the paper. However, Thp1 cells can be difficult to image and HeLa cells which are more amenable to this technique are commonly used instead, generally and for MR1 studies. We have validated the HeLa.MR1.HA cell lines and can show that they upregulate MR1 at the cell surface in response to antigen and can activate MAIT cells. This data is now included as a supplementary figure (Supplementary Figure 11) and the rationale for the use of these cells explained in the main text.

__ In addition, Figure 4B represent only the non-activated status. Given that association of SQSTM1/p62 with MR1 is dependent on E.coli and/or 5-OP-RU (Figure 1A), the same immuno-fluorescent imaging in the presence of the inhibitors upon stimulation with these reagents would also be desirable. It will uncover whether MR1 and SQSTM1/p62 colocalize upon stimulation, and such colocalization is perturbed in the presence of the inhibitors.__

The aim of this microscopy experiment was to demonstrate that perturbations to the autophagy pathway induced by different drug treatments also affected MR1 localisation and/or expression to complement the other experiments in that figure (Figure 4A and 4C). SQSTM1 expression was included as a control as it is known to be regulated by autophagy. Although assessing the interaction between MR1 and SQSTM1 under different autophagy conditions may be of interest we did not find it to be particularly relevant in this case as our focus shifted to the autophagy pathway in general rather than the specific interaction between MR1 and SQSTM1.

__ Whereas the authors addressed the question as to at which stage MR1 is regulated in trafficking in Figure 5, there was no experiments with 5-OP-RU (an agonist for MAIT cells). This casts the doubt whether observed phenotype really represented the true MR1 trafficking, because there is no guarantee that the trafficking pathway for antagonist (Ac-6-FP) is same as that for agonist.__

5-OP-RU and Ac-6-FP are small chemically synthesised molecules and an agonist and antagonist of MR1 antigen presentation respectively There is no evidence to suggest that apart from activation of MAIT cells (5-OP-RU is stimulatory, Ac-6-FP is not) that they would behave any differently in terms of trafficking and interaction with MR1. Indeed, both are used interchangeably in the MR1 field.

__ Given the importance of MR1 overexpression in showing the association between MR1 and SQSTM1/p62, it is worthwhile to consider performing the knockout experiments with Thp1-MR1-HA rather than Thp1. It will further clarify the role(s) of SQSTM1/p62, Atg5, and Atg7 in MR1 trafficking and resultant MAIT cell activation.__

The interaction studies had to be performed with overexpressed MR1 as the endogenous protein is very difficult to detect for these types of experiments. The majority of the functional studies were performed with the endogenous protein which avoids any issues concerned with the use of overexpressed and tagged proteins and addresses concerns that interactions observed with the overexpressed protein are simply artifactual. As the functional assays validate the interaction data, we believe it is not necessary to repeat the depletion experiments in the MR1 overexpressed cell lines.

__ Minor comments: 1.Please explain why the authors failed to detect IL23A in the coimmunoprecipitation. Should MR1-IL23A interaction be specific, what is a biological significance?__

This point is addressed in the discussion. It is sometimes the case that interactions identified by mass spec cannot be recapitulated by co-immunoprecipitation and alternative methods may need to be employed to verify the interaction. Since this work concentrates on the autophagy pathway further experiments involving IL23A were deemed beyond the scope of this manuscript. Of note, IL23A will be strongly induced over very low background levels by E coli, which would amplify the impact of any weak interactions.

__ When Hela-MR1-HA was used, did the authors obtain the same results as Thp1-MR1-HA as shown in Figure 1C-D? This is relevant to the specificity in the interaction between MR1 and SQSTM1/p62 as shown in Figure 4B.__

The interaction between MR1 and SQSTM1 in the presence of E.coli was not confirmed in the HeLa.MR1.HA cells. SQSTM1 is included as a positive control as it is known to be regulated by autophagy. As these experiments were performed in the absence of any antigen, we would not expect to observe an interaction in this instance.

__ While S1, S2, S3, and S4 showed a similar degree of SQSTM1 depletion in Figure 2A, there was difference in the potential of IFN-γ production from MAIT cells among the clones. Only S4 showed decreased potential for IFN-γ upon 5-OP-RU, though E. coli failed to so. Contrary to 5-OP-RU, S1-S3 showed an enhanced potential while S4 failed to do so. Why is that so?__

As the SQSTM1 knockout cells are clonal cells there may be other genetic/phenotypic differences, besides depletion of SQSTM1, that can account for the observed differences in MAIT cell activation. To mitigate for these differences, we tested 4 different clonal cell lines, with 3 out of 4 clones displaying the same phenotype with respect to activation of MAIT cells.

__ Given that there was little correlation between MR1 expression level and the potential of S1-S4 to promote or inhibit the ligand-dependent production of IFN-γ (Figure 2C right panel and Figure 2D), it is difficult to conclude that the factors implicated in autophagy play a pivotal role in MR1-dependent MAIT cell activation.__

Surface MR1 levels on the whole are difficult to detect even in the presence of antigen as MR1 surface expression appears to be very tightly controlled. Although MR1 surface expression levels between the different SQSTM1 clones appeared to be somewhat variable, in the Atg depleted cells they showed a more consistent upregulation compared to the control (although these differences were not statistically significant). In both cases, stimulation with E.coli resulted in increased MAIT activation demonstrating that these autophagy proteins did affect MR1 presentation and that small (perhaps undetectable in some cases) changes in surface expression did impact MR1 function. Therefore, we have concluded that autophagy factors are able to regulate MR1 antigen presentation but to what extent and how remains unclear. We have removed the word ‘pivotal’ from the abstract as we agree with the reviewer that the impact of these interactions has not been conclusively established.

__ There was no consistency in the experimental design for Figure 5. Please explain the rational why the authors have used 7.1 in A and C, but not in B, D and E?__

---

For some of the experiments it was not possible to display and thus quantify all the cell lines in one figure eg the western blot data for the EndoH experiments (Figure 5D). Therefore, one representative cell line from Atg5 and Atg7 depleted cells was chosen, as on the whole all the cell lines behaved similarly. This rationale is now included in the main text.

__ The control appeared to behave as 7.1 did. Was there statistical difference between 7.1 and 7.2 in Figure 5C? If so, what is the interpretation.__

As the reviewer correctly notes, in Figure 5C the Atg7.1 cell line had similar kinetics to the control cell line in terms of MR1 surface expression. In other experiments Atg7.1 shows increased MR1 surface expression compared to the control (Figure 3B, although not statistically significant). One major difference between these experiments is the timing, Figure 3B is measured after an overnight incubation while Figure 5C is measured over 6 hours. It may be the case that in this cell line MR1 takes slightly longer to accumulate at the cell surface compared to Atg7.2. As these are heterogenous cell populations, there may be other factors that account for these differences apart from depletion of Atg7. Statistical analysis has now also been included for this data.

__ Time course over 6 h will be required to assess the MR1 expression in Figure 5C.__

It has been demonstrated by others that MR1 is able to reach the cell surface within 4 hours of antigen exposure (McWilliams et al, 2016), therefore a time course over 6 hours to measure MR1 surface expression was deemed sufficient.__

Reviewer #1 (Significance (Required)):

The present study uncovered the possible implication of autophagy factors in MR1 trafficking, in other words, MAIT cell activation. Although the previous study has demonstrated the importance of the protein loading factors (McWilliam et al., PNAS,117 24974-24985 2020), this study adds another pathway for MAIT cell activation. However, the conceptual significance is limited in that depletion of the factors pertinent to autophagy such as Atg5 and Atg7 in Thp1 resulted in rather weak interference in terms of MR1 trafficking and MAIT cell activation. Thus, this study will interest those who work in basic immunology, in particular, in regulation of antigen-presentation molecules and T cells as well as those who are in the field of MAIT cell biology. Although the field of this reviewer covers biochemistry, molecular biology, developmental biology, immunology and regenerative medicine, proteomics approach (in detailed technique) as seen here to identify the associated molecules is somewhat beyond the reviewer's expert.

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

Summary

The authors used a mass spectrometry proteomics approach to screen for proteins which interact with the MHC-I-related molecule MR1. In addition to expected interacting partners, they identified SQSTM1/p62, a selective autophagy mediator, and demonstrated that MAIT cell responses to fixed E. coli were increased with knockout of SQSTM1. The authors further investigated the role of autophagy in regulating MR1 ligand presentation through knockout of two key autophagy proteins, Atg5 and Atg7, or treatment with various autophagy inhibitors. MR1 surface expression and MAIT cell activation were variably increased following interruption of autophagy in the context of fixed E. coli or synthetic ligand treatment of human monocytes and B cell lines. The authors concluded that preformed pools of MR1 are regulated by autophagy.

Major comments

Overall, this is an interesting study that is the first to identify autophagy as a potential regulatory mechanism for MR1. There are a number of conceptual questions relevant to the model system. The main concerns regard a number of the conclusions made, given the analysis of the data as presented. These concerns are described in more detail below.

Conceptual concerns:

1. The investigators rightly note the challenge in studying MR1 protein due to low endogenous expression. However, the use of over-expressed MR1 protein begs some questions with regard to the identification of ER degradation and autophagy proteins (which as they note are also involved in the degradation of damaged and defective cellular components). Although they have previously shown that MR1-HA tagged protein goes to the cell surface and presents antigen, it is impossible to know what proportion of the over-expressed molecules are functional, and it is plausible that a proportion of these molecules that end up in ER degradation or autophagy pathways identified, but would still IP with the HA tag. In the data shown, it is not entirely clear that the impacts of the molecules are actually impacting MR1 protein absent overexpression. Example: In Figure 2, there is very little impact of the complete KO of SQSTM1 on MR1 protein expression in WT THP1 cells, despite this protein only interacting with MR1 in E.coli infected cells. In contrast, in the 5-OP-RU incubated cells, there is a difference in MR1 expression in the SQSTM1 mutant clones, but no impact to MAIT cell activation. The authors note these issues and discuss the possibility that the other functions of SQSTM1 are coming in to play and further look at Atg5 and Atg7, however the absence of these proteins also have no significant impact on the expression of MR1 protein. Can the authors comment on this? The authors state that the increase in MAIT cell responses to fixed E. coli-treated polyclonal populations of SQSTM1 KO cells (same cells as SF2D) was blocked by the use of an anti-MR1 antibody, but do not show this data. Why not done with clonal populations? It is unclear why this data was not shown as it would help to support that the impact of inhibited autophagy is really on the functional MR1 protein pool, rather than a pool of non-functional but still HA tagged MR1 that has been shunted to degradation or autophagy pathways.__

The reviewer rightly acknowledges the challenges associated with detecting endogenous MR1 protein levels which can be difficult to measure even after antigen exposure. For this reason, many researchers use a tagged protein in overexpressing cell lines to study MR1 as we (and others) have done for the proteomics analysis and validation studies. The use of tagged overexpressed proteins can be problematic because they may not recapitulate endogenous protein structure, localisation and/or function. Although we have previously demonstrated that HA tagged MR1 behaves similarly to its endogenous counterpart in terms of trafficking to the cell surface and presentation to MAIT cells (Ussher et al, 2016), there is still a possibility that there is a population of non-functional protein that is targeted for degradation. As we understand, it is the reviewer’s concern that it is this protein pool that is immunoprecipitating with autophagy components.

Firstly, although the interaction studies were necessarily performed using tagged overexpressed protein, the majority of the functional studies (ie measuring surface MR1 levels and MAIT cell activation in SQSTM1 and Atg depleted cells, Figures 2 and 3) were performed in wildtype Thp1 cells, expressing endogenous levels of MR1. As explained in response to reviewer 1, MR1 surface levels as displayed in Figures 2C and 3B, are very tightly controlled and can be difficult to detect even after antigen exposure as demonstrated in the accompanying histograms. Therefore, subtle differences in MR1 surface levels are to be expected especially when measuring an increase rather than a decrease in expression. Although for SQSTM1 depletion there was some variability in MR1 surface levels, for Atg depletion there was a clear trend towards increased expression, although these differences were not statistically significant. In both cases (depletion of SQSTM1 and Atg) there was a definite effect on MR1 presentation as MAIT cell activation was increased in nearly all cases. It is well established in the literature that MAIT activation, in the 5 hour timecourse of our experiments, is wholly MR1 dependent. Therefore, these subtle, and perhaps sometimes undetectable, differences on endogenous MR1 surface expression do have an effect on MR1 function and we believe this validates the data from the interaction studies using overexpressed protein.

In addition, experiments performed with the MR1 blocking antibody would not necessarily address the reviewers concerns as again these were done on Thp1 cells expressing endogenous levels of MR1 and not the overexpressing cell lines. However, for completeness this data has now been included as a supplementary figure.

Secondly one of the top hits from the proteomics analysis was B2M, a protein known to associate with MR1 and to be functionally important. Other proteins identified by our screen include components of the peptide loading complex which have also been reported to be important for MR1 trafficking and antigen presentation. It should also be noted that SQSTM1 was identified in a similar proteomics screen performed by a different lab (McWilliams et al, 2020). Therefore, we believe that these findings also validate use of the HA tagged MR1 construct to generate true protein interactions.

__ The conclusion that "regulation of MR1 by autophagy is not dependent on new protein synthesis and is most likely occurring on pre-existing pools of MR1" is not strongly supported by the data. If MR1 is processed normally through the golgi in Atg5 and 7 deficient cells (Figure 5D), how can the conclusion be made that the pre-existing pools of MR1 are in the ER? There is a non-significant decrease in MR1 surface expression from CHX treatment in the context of Ac-6-FP stimulation in Atg KO cells. This data is not clear enough to support a firm conclusion in either direction. Have the authors performed this experiment using 5-OP-RU or fixed E. coli as ligand sources? Is there a similar trend seen using the Atg KO C1R cells? Further supporting experiments may be necessary to conclude whether or not this trend is biologically relevant.__

We thank the reviewer for their comment. The statement that pre-existing pools of MR1 are in the ER is based on reports from the literature where it has been shown that unbound ligand receptive MR1 remains in the ER until it comes into contact with antigen. Since we were able to show that MR1 trafficked normally through the Golgi in Atg depleted cells, the effects of autophagy on MR1 expression and function must occur prior to Golgi processing. This would indicate the ER population of MR1 as the likely targets of regulation by autophagy especially considering the function of SQSTM1 which binds to proteins in the ER.

The experiments with CHX treatment were used to establish whether it was new or pre existing protein that was targeted by autophagy. Since CHX had no effect on MR1 surface expression this would indicate that new protein synthesis is not required for MR1 trafficking in Atg depleted cells.

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Analysis of Western Blot data:

1. There are many places throughout the manuscript where statements are made with regard to increases and decreases in the protein expression level with treatment, or comparisons between control and knockout samples. Although the legends generally indicate these experiments were based on at least 3 replicates (except some cases, where noted), there is no quantification of any western blotting data. There is no information in the legends or methods as to how much sample was loaded. Specific examples:

a. Figure 1/Supp Figure 1: Figure 1C and 1D: There are several differences in the inputs between the 2 blots, including differences in the no antigen samples (which should be the same) or presence of multiple bands in one blot for a given marker but not the other. Fig 1C: the band for Calreticulin in the immunoprecipitated E. coli-treated Thp1.MR1.HA samples (right lane) is very weak. Fig. 1D: the bands are weak and there is no clear difference for Calnexin in the immunoprecipitated 5-OP-RU treated Thp1.MR1.HA samples (right lane) compared to no ligand despite the conclusion that Calnexin weakly associates with MR1 in the context of 5-OP-RU ligand. Are some of these weak associations visible due to different inputs? Why are the input blots for anti-HA so different between the no antigen controls in the E coli vs 5-OP-RU blots? Supp Figure 1B: the +5-OP-RU pulldown of MR1.HA appears as to be more (like with E.coli), but no quantification. Why does so little B2M IP with 5-OP-RU MR1? Supp Figure 1D (and others): statements are made about increases and decreases without quantification. All: Presumably HSP90 is used as a loading control for the input, but this is not discussed nor is there quantification.__

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We thank the reviewer for this comment. As western blotting is a multi-step process often over more than one day, there are numerous points at which variation can occur between blots no matter how carefully the conditions are controlled to minimise this. It is for this reason that it is generally not good practice to compare samples that have been run on different gels. Therefore, we do not believe that comparisons between blots in Figures 1C and 1D, relating to differences in input proteins for example, are appropriate nor informative. If we take the top anti-HA blot for Figure 1C there is a big increase in protein expression in the Ip of E.coli treated cells (final lane) which is not as pronounced with 5-OP-RU treatment (Figure 1D, top blot, final lane). This sample will dictate the exposure time of the blot (so as to prevent saturation of this sample) which then affects detectable expression of less well expressing samples on the same blot (such as the input samples in Figure 1C). Therefore there may appear to be less input protein in Figure 1C than Figure 1D but there is also more protein in the E.coli treated pull down than in the 5-OP-RU treated one, which also needs to be taken into account. This is one example of why it is difficult to compare samples across blots. To accurately and correctly compare these input samples they would need to be run on the same gel.

The only useful comparison that can be drawn is between samples from the same blot, so comparing input protein in the presence and absence of E.coli for instance. To take the reviewer’s example, for the anti-calreticulin blot in Figure 1C, there is a weak interaction of calreticulin with MR1 in the presence of E.coli. If we compare the input lanes on this blot (effectively the loading control), there actually appears to be slightly more protein in the E.coli negative sample that the positive one. This would argue against the reviewers claim that this weak interaction is actually due to differences in the input and it is instead more likely to simply be a weak interaction. It is important to point out that this interaction, and others involving components of the peptide loading complex, have also been validated by other groups.

With regards to Calnexin association with MR1 in the presence of 5-OP-RU, we did not mean to imply that this association was only in the presence of 5-OP-RU as it is evident from the data that Calnexin weakly associates even in the absence of antigen. The text has now been changed to make this clearer.

The anti-HSP90 blot has been included to show that a random protein, not identified by our proteomics screen, does not spuriously associate with MR1, and not as a loading control for the input samples per se. This explanation has now been included in the text.

Finally with regard to quantification of the co-immunoprecipitation blots, while quantification of western blots in some cases can be informative (eg relative expression of a protein compared to a control), it is at best only a semi-quantitative technique and not generally applied to co-immunoprecipitation data. As we are looking for a binary result (presence/absence of a particular protein) rather than a relative value, we do not see how quantification of this data will make it any more informative. We have included more detail of the sample loading in the methods section as requested by the reviewer and have added quantification of other blots where appropriate. __

b. Supp Figure 5: The authors conclude there are no difference in protein interactions with MR1 in Atg5 or 7 deficient cells. By eye, there appear to in fact be differences, but there is no quantification to support the conclusions either iway. These data are subsequently used to make interpretive statements about the data in Figure 5. There is no indication of the number of times this experiment was performed.__

In supplementary figure 5, we aimed to determine whether depletion of Atg 5 or 7 negatively affected the MR1 proteome ie whether interactions that were previously observed were disrupted and whether this contributed to the effects on MR1 antigen presentation observed in these cell lines. The interactions between MR1 and the tested proteins remained intact in Atg depleted cells. However, as Atg depletion increased MR1 protein expression some of these interactions are more pronounced in the depleted cell lines compared to the control cell line. Thus, the reviewer is correct in stating that there are differences in the protein interactions between the cell lines but in all cases the protein interactions remain intact which was the focus of our analysis. We have modified the text to make this clearer. The figure legend now also includes the number of replicates for this experiment.

__ Figure 4A: No quantification to support conclusions. Unclear why both blocking and inducing autophagy would both increase the amount of MR1 in cells.__

Quantification of this western blot data has now been included in the figure. Blocking autophagy (3MA and Wort) has a much greater effect on total MR1 protein levels, while inducing autophagy (EBSS) has minimal effects compared to the control. As autophagy is a highly dynamic process with western blotting providing just a snapshot of this process, inhibiting and inducing autophagy can both lead to the same observed phenotype of increased autophagosomes, due to blocking fusion with lysosomes and increased autophagosome formation respectively.

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Analysis of Fluorescence microscopy data (Figure 4B):

1. There are several concerns with the conclusions drawn from the fluorescence microscopy images (Figure 4B). How many images/fields were taken and cells analyzed per condition? How were individual fields chosen for imaging to be unbiased? Overall, the conclusions are observational and require quantification. For example, the authors indicate "an increase in MR1 cytoplasmic signal intensity following treatment...", but there is not data analysis to support this statement. This could be quantified by analyzing average MR1-HA fluorescence intensity across the cell volume compared to the bright fluorescence intensity of the non-cytoplasmic MR1-HA regions. Similarly, the number and intensity of the SQSTM1 foci should be quantified. Quantification is required to make the stated conclusions.__

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We thank the reviewer for their helpful suggestions regarding the microscopy experiments. Quantification of the data has now been added, including MR1 fluorescent intensity and the number of SQSTM1 foci, which supports the data from Figure 4A. The methods and figure legend have been updated to include more details of the analysis pipeline.

__ Other statistical concerns:

1. Some of the figure legends do not clearly state the number of independent experiments performed (2D, 3C-D, 5A, SF2, SF3, SF5). If these experiments were only performed once, additional repeats and appropriate statistical analysis are necessary to validate any conclusions drawn from these results.__

The number of replicates for each experiment are now included in the figure legends. __

1. Was statistical analysis performed on the MR1 mRNA expression in Figure 5A, and how many independent experiments are shown? There appears to be a decrease in MR1 expression in the Stg7.1 KO cells, which might impact the overall MR1 expression. Also, statistical analysis seems to be missing from 5B and 5C.__

This figure has now been altered to reflect the number of replicates (2 biological replicates each consisting of 3 technical replicates) and statistical analysis has also been included. Statistical analysis for Figures 5B and 5C has also now been included. __

1. In figure 5E, were there statistical comparisons between the Atg KO and control cells in the Ac-6-FP-treated non-CHX condition? It is unclear whether the statement "As previously observed, there was an increase in surface MR1 levels in Atg-depleted cells compared to the control in the presence of Ac-6-FP" is referring to the non-significant results in 3B or to this data presented in 5E. This statement should be revised to reflect the statistical significance of these data.__

We thank the reviewer for this point. This figure has been amended to include a timecourse of CHX treatment in control and Atg depleted cell lines and statistical analysis has also been included. The statement has been clarified to highlight the point that CHX treatment does not affect the level of MR1 upregulation in control and knockdown cell lines.

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Throughout the figures, several bar plots are missing the individual data points of experimental or technical replicates.__

All bar plots display either the individual data points where donor cells were used or the average of 3 or more independent experiments with error bars denoting the standard deviation for experiments using cell lines.__

1. The data in Figures 3C-D could be presented and analyzed as paired data (comparing the response from MAIT cells of each PBMC donor to the Ctrl cells vs the Atg KO clones) to better represent the impact of the KO.__

We thank the reviewer for this suggestion. We believe that analysis via ANOVA is more appropriate in this instance due to the number of comparisons made with the control cells.__

Other minor concerns:

1. The conclusion "Overall, in the absence of SQSTM1, cellular changes induced by E. coli result in increased antigen presentation, which is not replicated with 5-OP-RU where MAIT activation may be adversely affected, implying that regulation of MR1 function by SQSTM1 may be dependent on the nature of the antigen" (page 6) is confusing and may need re-wording.__

We are sorry for the confusion and have reworded this sentence to make it clearer. __

1. The x-axis in the bar plots of Fig 3B labels the right group as "Ac-6-FP" in contrast to the histogram label and figure legend, which indicate the cells were treated with 5-OP-RU.__

We thank the reviewer for pointing this out, the bar plot was indeed mislabelled and has now been corrected. __

1. The presentation of data in Figure 5B is confusing. Perhaps the DMSO and Ac-6-FP conditions are mis-labeled? For the DMSO-treated samples, it appears that the data presented are percent surface MR1 GeoMean compared to the 0hr timepoint per cell lines. However, treating cells with Ac-6-FP should result in an increased surface MR1 expression (as seen in the non-CHX samples of Fig 5E, for example). If the data presented are percent of the 0hr DMSO control, wouldn't the % MR1 expression be higher for the Ac-6-FP samples than the DMSO samples? Alternately, it might be clearer to separate these two conditions onto separate plots, with % MR1 calculated relative to the 0 hr control of DMSO or Ac-6-FP treatment, respectively.__

We thank the reviewer for pointing this out, the graph was indeed mislabelled and has now been corrected. The DMSO and Ac-6-FP treated samples are normalised to their own 0-hour timepoint (set at 100%) in order to directly compare the rate of decline of MR1 surface expression between the two conditions. This is now more clearly explained in the figure legend.

__ Unclear in Figures 3 and 5 (and supplements) why all or only some of the Atg5 and 7 clones are used from experiment to experiment.__

Please see our response to reviewer 1 on this point.__

1. The discussion mentions "we found no evidence of an interaction between MR1 and AAKI" on page 9. What data supports this statement?__

We found no evidence of an interaction between MR1 and AAK1 from our proteomics screen, this is now explained in the text.

__ The discussion indicates that "This increase in SQSTM1 protein levels still resulted in increased MR1 surface levels and activation of MAIT cells, the same phenotype observed in SQSTM1-depleted cells" as it relates to the presence of E.coli. This statement is not fully supported by the data as SQSTM1 depletion did not lead to an increase in surface MR1 in E.coli treated cells.__

We thank the reviewer for pointing this out, this sentence has now been corrected. __

1. In the Proteomics/Mass Spec methods section on page 13, the citations to MaxQuant and Andromeda may need to be fixed.__