Author response:

The following is the authors’ response to the previous reviews

Reviewer #2 (Recommendations for the authors):

Major:

Over-interpretation of data. There are a few instances of this:

The authors claim "Our work shows that MgdE interacts with both WDR5 and ASH2L and inhibits the methyltransferase activity of the COMPASS complex" (Line 318). However, they provide no biochemical analysis of methyltransferase activity to support this claim. While they cite Figure 4A-C and Figure 5, these data simply show (slightly) decreased cellular levels of H3K4Me. There are multiple ways H3K4Me could decrease including blocking recruitment of COMPASS to promoters or the enzymatic activity of MgdE itself.

The data itself related to H3K4Me changes (Figure 5D) is difficult to interpret in light of the controls they now provide. Examining the blot itself there seems to be a massive increase in H3K4Me in control cells expressing GFP that is not reflected in the quantification that shows only a ~2x increase in GFP-expressing cells. In addition， there is very little decrease in H3K4Me in the MgdE-expressing cells relative to controls or site-mutant (no change apparent visually and ~10% change per their quantification). However, the authors interpret this as," revealed that cells expressing WT MgdE exhibited lower levels of H3K4me3". In both these cases I would recommend the authors consider modifying their interpretation of the data.

We thank the reviewer for the comment.

(1) We have now revised this interpretation in the manuscript as follows:

Lines 311-312: “Our work shows that MgdE interacts with both WDR5 and ASH2L, leading to a decrease in H3K4me3 levels.”

(2) Figure 5D presents the results of three independent biological replicates. The bar graph shows the average signal intensity of H3K4me3 normalized to the corresponding loading controls. Accordingly, we have revised the analysis and description of the experimental results.

Lines 214-217: “Immunoblot analysis of nuclear extracts showed that cells expressing WT MgdE had ~25% lower H3K4me3 levels than EGFP-expressing cells and ~40% lower levels than those expressing the D244A/H47A mutant (Figure 5D).”

Minor

What is "CK"? Please clarify (Figure 2F).

We thank the reviewer for the comment. In this context, "CK" refers to the uninfected control group, which serves as the negative control in the experiment. We have revised the label in Figure 2F.

How many times was the BCG mouse experiment performed? This should be indicated in the figure legend? (Figure 7A).

We thank the reviewer for the comment. The BCG mouse experiment was performed once, and we have added this information to the figure legend of Figure 7A.

It is unclear why the secreted protein (after signal peptide removal) migrates at the same size as the full-length protein (Figure S2).

We thank the reviewer for the comment. The precursors of secreted proteins after translation in the cytoplasm will be translated into the periplasm immediately. Therefore, MgdE or Ag85B obtained from the whole-cell lysate (Figure S2A) mostly have had the signal peptides removed. This is also validated in the case of Rv0455c secretion by Mtb (Zhang et al., Nature Communications, 2022). This explains why MgdE (or Ag85B) proteins from whole-cell lysates or from supernatants show same size in SDS-PAGE gels.

It is still unclear why the transcripts with very little fold-change in expression (in grey) have the most significant p-values for being different (Figure 6).

We thank the reviewer for the comment. The p-value calculation takes into account not only the magnitude of expression change but also the consistency of expression levels within each group and the number of biological replicates. When the variation among replicates is minimal, even a small difference in group means can result in a statistically significant p-value. In our RNA-seq analysis, we used DESeq2 with three biological replicates per group. DESeq2 employs a model based on the negative binomial distribution and accounts for multiple factors, including the mean expression level, within-group variance (dispersion), sample size, and normalization accuracy. As a result, it is common to observe that genes with small variability and strong consistency between replicates may show significant p-values even with modest fold changes. Conversely, genes with larger fold changes but greater variability might not reach statistical significance.

Reference

Zhang L, Kent JE, Whitaker M, Young DC, Herrmann D, Aleshin AE, Ko YH, Cingolani G, Saad JS, Moody DB, Marassi FM, Ehrt S, Niederweis M (2022) A periplasmic cinched protein is required for siderophore secretion and virulence of Mycobacterium tuberculosis Nat Commun 13(1):2255.

eLife Assessment

In their valuable study, Beaudet, Berger and Hendricks provide a mechanistic link between disease-associated tau hyperphosphorylation, loss of cooperative tau envelope formation on microtubules, and dysregulation of axonal transport prior to aggregation. Using complementary in vitro reconstitution and human iPSC-derived neuronal assays with phosphodeficient and phosphomimetic tau constructs targeting 14 disease-relevant sites, the authors convincingly show that phosphorylation state alters tau organization on microtubules and differentially impacts kinesin- and lysosome-based transport. The evidence is solid and well aligned with the conclusions, yet the work could be further strengthened by incorporating additional controls and motor-specific assays to refine the mechanistic depth.

Reviewer #1 (Public review):

Summary:

This work by Beaudet and colleagues aims at exploring the effect of phosphorylation on the formation of tau envelopes and consequently on axonal transport, both in vitro on reconstituted microtubules and in human excitatory neurons derived from IPSCs.

The authors found that a relatively widely used construct in which 14 serine or threonine residues, often hyperphosphorylated in Alzheimer's disease, are mutated to alanines (phosphodeficient), increases the density of tau envelopes compared to wildtype tau, whereas a phosphomimetic (same residues mutated to glutamic acid) reduces envelope density both in vitro and in human excitatory neurons derived from IPSCs.

By analysing the trafficking of different kinesins (KIF1a and KIF5C), they observed different effects of tau phosphorylation status on the movement of these two motors.

They then analyse transport of lysosomes by employing live imaging of lysotracker in human excitatory neurons derived from IPSCs transfected with wildtype, phosphodeficient or phosphomimetic tau, observing that phosphodeficient tau seems to reduce transport of lysosomes while phosphomimetic increases transport compared to wildtype tau.

Strengths:

(1) The work aims to study a novel and underexplored topic in the tau field, tau envelopes, and investigate their relevance to Alzheimer's disease pathology.

(2) Experiments are well conducted and of high quality.

Weaknesses:

Relying only on in vitro reconstituted microtubules and human neurons derived from IPSCs leaves some doubts about the relevance of these results for Alzheimer's disease, considering the embryonic state of IPSCs-derived neurons.

Reviewer #2 (Public review):

This manuscript examines how disease-associated hyperphosphorylation disrupts tau's role as a cooperative microtubule-binding regulator of intracellular transport. Using in vitro reconstitution assays and live-cell imaging in iPSC-derived neurons, the authors employ phosphomutant tau constructs (E14 to mimic hyperphosphorylation, AP to prevent phosphorylation) at 14 disease-associated residues to isolate phosphorylation effects independent of expression system-dependent PTM heterogeneity. The results show that hyperphosphorylated tau fails to form cooperative envelope-like structures on microtubules, instead binding diffusely and dissociating rapidly. In contrast, wild-type and phospho-resistant tau form cohesive envelopes that regulate motor protein access. At the single-molecule level, hyperphosphorylation reduces KIF5C inhibition while maintaining or enhancing KIF1A inhibition through altered processivity and detachment rates. In live neurons, hyperphosphorylated tau phenocopies tau knockout conditions, weakening tau-mediated inhibition of lysosome transport and increasing processive motility. The authors quantify tau binding using Gaussian mixture model-based image analysis and measure tau kinetics via FRAP, demonstrating that hyperphosphorylation-induced loss of cooperative binding correlates with dysregulated organelle transport. These findings establish a mechanism by which phosphorylation-driven disruption of tau's gatekeeper function on microtubules compromises axonal transport prior to aggregation in tauopathies. The paper provides interesting new knowledge for the field, but there are outstanding concerns that could be further addressed by the authors to strengthen and clarify the current manuscript:

(1) Lack of Phosphatase-Treated Control and Explicit WT Phosphorylation Quantification

Wild-type tau expressed in insect and mammalian cells is known to be phosphorylated by endogenous kinases (eg, GSK3, CDK5, MARK). The manuscript acknowledges this in the Discussion but provides no phosphatase-treated lysate control or quantification of endogenous phosphorylation on WT tau via phospho-specific Western blots. This leaves ambiguity about whether observed differences between WT and E14 reflect purely the introduced mutations or confounding baseline differences in phosphostate content.

(2) Limited Normalization of Motor Effects to Measured Tau Lattice Occupancy

Although kinesin trajectories are classified inside vs. outside tau envelopes (inherently normalizing to local tau density), motor parameters are not systematically reported as functions of tau fluorescence intensity across all constructs. Co-purifying MAPs or microtubule-modifying enzymes in cell lysates is not quantified or excluded, leaving residual uncertainty about tau-specificity of observed motor inhibition. This should be at least acknowledged in the results section.

(3) Insufficient Citation of Prior Neuronal Tau Envelope Evidence

In the Introduction, the authors state, "it was an open question if tau forms envelopes in neurons," but this understates existing evidence. Tan et al. (2019) report tau neuronal staining consistent with envelope formation, while Siahaan et al. (2021) provide more direct evidence in non-neuronal cells. The framing should acknowledge and integrate these prior findings.

(4) Unclear Wording on Expression System-Dependent Phosphorylation

The sentence "The phosphostate of tau is strongly dependent on the expression system" requires rewording. It is ambiguous whether this refers to the final phosphostate achieved after expression or the inherent phosphorylating capacity of each system. Clearer language would strengthen the methodological justification.

(5) Insufficient Quantification of Motor and Lysosome Transport Effect Magnitudes in Results Section

The data on molecular motor motility and lysosome transport are densely described. The magnitude of effects (fold-changes, percentage differences) should be explicitly stated in the Results section when first presenting findings to orient readers to biological significance. For example, effect magnitudes for lysosome run lengths, velocities, and directional bias should be quantified in text, not left to figure inspection.

(6) Incomplete Discussion of Projection Domain Necessity for Envelope Formation

The Discussion states the projection domain is "a critical regulator of both tau-tau and tau-microtubule interactions," but does not engage with prior domain dissection work. Tan et al. (2019) found that the entire projection domain is not necessary for envelope formation in vitro. The authors should discuss which projection domain regions are specifically regulated by phosphorylation vs. required for cooperativity, providing a more nuanced interpretation than implied by their current framing.

Author response:

We thank the reviewers for their thoughtful and constructive feedback. Addressing these points will strengthen the manuscript and improve its clarity.

A primary concern involved the justification for using COS7 cell lysates in reconstitution approaches and iPSC-derived neuronal model systems as models for AD. We will clarify the language throughout the manuscript to more explicitly state the study’s goals, emphasize that these systems were selected as robust, well-controlled platforms to test the mechanisms through which tau hyperphosphorylation affects microtubule interactions and tau’s role in regulating intracellular transport, and the limitations of in vitro and iPSC models.

Reviewers also raised the possibility that background phosphorylation could contribute to the effects observed in the pseudo-phosphorylation model. We cite two recent preprints that provide insight into this question through quantitatively assessing tau phosphorylation across expression systems. In the revised manuscript, we will elaborate on how their assessment of tau phosphorylation fits within the scope of our approach and clarify how our experimental controls effectively minimize uncertainty related to background phosphorylation.

Another point concerned the potential influence of other microtubule-associated proteins in lysates and the impact of tau lattice occupancy on motility outcomes. To further strengthen this aspect, we will include additional analyses correlating tau intensity along microtubules with kinesin intensity and motility behavior, and we will more clearly explain how the AP and WT controls provide confidence in the robustness of the system.

Detailed responses to each reviewer comment are provided below point by point. The planned revisions, which include clearer language, stronger justification of the experimental approaches, and additional supporting analyses, will substantially improve the clarity, rationale, and overall impact of the study.

Public Reviews:

Reviewer #1 (Public review):

Summary:

This work by Beaudet and colleagues aims at exploring the effect of phosphorylation on the formation of tau envelopes and consequently on axonal transport, both in vitro on reconstituted microtubules and in human excitatory neurons derived from IPSCs.

The authors found that a relatively widely used construct in which 14 serine or threonine residues, often hyperphosphorylated in Alzheimer's disease, are mutated to alanines (phosphodeficient), increases the density of tau envelopes compared to wildtype tau, whereas a phosphomimetic (same residues mutated to glutamic acid) reduces envelope density both in vitro and in human excitatory neurons derived from IPSCs.

By analysing the trafficking of different kinesins (KIF1a and KIF5C), they observed different effects of tau phosphorylation status on the movement of these two motors.

They then analyse transport of lysosomes by employing live imaging of lysotracker in human excitatory neurons derived from IPSCs transfected with wildtype, phosphodeficient or phosphomimetic tau, observing that phosphodeficient tau seems to reduce transport of lysosomes while phosphomimetic increases transport compared to wildtype tau.

Strengths:

(1) The work aims to study a novel and underexplored topic in the tau field, tau envelopes, and investigate their relevance to Alzheimer's disease pathology.

(2) Experiments are well conducted and of high quality.

Weaknesses:

Relying only on in vitro reconstituted microtubules and human neurons derived from IPSCs leaves some doubts about the relevance of these results for Alzheimer's disease, considering the embryonic state of IPSCs-derived neurons.

We agree with the reviewer that iPSC-derived neurons represent an immature state compared with the neurons affected in Alzheimer’s disease. However, iPSC-derived neurons, together with in vitro reconstitution, provide insight into (1) whether tau hyperphosphorylation influences its association with microtubules and its ability to form envelope-like structures thought to regulate transport, (2) how tau hyperphosphorylation affects the motility of kinesin motors that are strongly inhibited by tau, and (3) how transport of endogenous degradative organelles such as lysosomes are impacted by tau hyperphosphorylation. We hope that our studies will help to inform future studies examining how tau-related dysfunction evolves in more mature neurons and contributes to the more severe pathological effects observed at later disease stages.

We will include a paragraph in the Discussion section addressing the limitations of this study to better contextualize our findings within the broader effort to understand tauopathies and Alzheimer’s disease.

Reviewer #2 (Public review):

This manuscript examines how disease-associated hyperphosphorylation disrupts tau's role as a cooperative microtubule-binding regulator of intracellular transport. Using in vitro reconstitution assays and live-cell imaging in iPSC-derived neurons, the authors employ phosphomutant tau constructs (E14 to mimic hyperphosphorylation, AP to prevent phosphorylation) at 14 disease-associated residues to isolate phosphorylation effects independent of expression system-dependent PTM heterogeneity. The results show that hyperphosphorylated tau fails to form cooperative envelope-like structures on microtubules, instead binding diffusely and dissociating rapidly. In contrast, wild-type and phospho-resistant tau form cohesive envelopes that regulate motor protein access. At the single-molecule level, hyperphosphorylation reduces KIF5C inhibition while maintaining or enhancing KIF1A inhibition through altered processivity and detachment rates. In live neurons, hyperphosphorylated tau phenocopies tau knockout conditions, weakening tau-mediated inhibition of lysosome transport and increasing processive motility. The authors quantify tau binding using Gaussian mixture model-based image analysis and measure tau kinetics via FRAP, demonstrating that hyperphosphorylation-induced loss of cooperative binding correlates with dysregulated organelle transport. These findings establish a mechanism by which phosphorylation-driven disruption of tau's gatekeeper function on microtubules compromises axonal transport prior to aggregation in tauopathies. The paper provides interesting new knowledge for the field, but there are outstanding concerns that could be further addressed by the authors to strengthen and clarify the current manuscript:

(1) Lack of Phosphatase-Treated Control and Explicit WT Phosphorylation Quantification

Wild-type tau expressed in insect and mammalian cells is known to be phosphorylated by endogenous kinases (eg, GSK3, CDK5, MARK). The manuscript acknowledges this in the Discussion but provides no phosphatase-treated lysate control or quantification of endogenous phosphorylation on WT tau via phospho-specific Western blots. This leaves ambiguity about whether observed differences between WT and E14 reflect purely the introduced mutations or confounding baseline differences in phosphostate content.

Tau contains ~85 putative phosphorylation sites and is modified by several kinases in cells. Studies by Siahaan et al. (2024) and Fan et al. (2025) provide detailed insight into tau phosphorylation, its role in protecting the microtubule lattice from severing enzymes, and the implications of phosphorylation patterns for aggregate formation. Specifically, Fan et al. (2025) show that HEK-expressed tau is phosphorylated by endogenous kinases at 58 residues, with most phospho-occupancy levels below 15%, indicating substantial heterogeneity among individual tau molecules. In the revised manuscript, we will (1) provide justification for the use of the pseudo-phosphorylation model system as an approach to limit heterogeneity among tau molecules, (2) clarify the importance of the WT and AP controls, (3) discuss that E14, WT, and AP tau likely exhibit similar degrees of background phospho-heterogeneity, with WT tau likely exhibiting some overlap between background phosphorylation and the 14 AD-associated sites examined, and (4) expand the discussion to emphasize that although background phosphorylation is present, our results do not suggest that it contributes significantly to the observations reported in this study.

(2) Limited Normalization of Motor Effects to Measured Tau Lattice Occupancy

Although kinesin trajectories are classified inside vs. outside tau envelopes (inherently normalizing to local tau density), motor parameters are not systematically reported as functions of tau fluorescence intensity across all constructs. Co-purifying MAPs or microtubule-modifying enzymes in cell lysates is not quantified or excluded, leaving residual uncertainty about tau-specificity of observed motor inhibition. This should be at least acknowledged in the results section.

The reviewer raises a valid point. It is challenging to compare conditions where the occupancy of tau on microtubules is similar across conditions, as phosphorylation strongly effects the interaction between tau and microtubules. We will quantify and report tau intensity in single-molecule motility assays. On the second point, while effects from other MAPs or motor proteins could potentially affect kinesin motility, we would expect that these effects would be similar for all tau phosphomutant constructs, such that the effect of tau phospho-states on kinesin motility can be assessed.

(3) Insufficient Citation of Prior Neuronal Tau Envelope Evidence

In the Introduction, the authors state, "it was an open question if tau forms envelopes in neurons," but this understates existing evidence. Tan et al. (2019) report tau neuronal staining consistent with envelope formation, while Siahaan et al. (2021) provide more direct evidence in non-neuronal cells. The framing should acknowledge and integrate these prior findings.

We agree with the reviewer that evidence from several studies using reconstitution systems, fixed neurons, and live cultured cells provides evidence of tau envelope formation in neurons. Specifically, tau envelopes have been observed along taxol-stabilized or GMPCPP-capped GDP microtubules in vitro (e.g., Dixit et al., 2008; Monroy et al., 2018; Tan et al., 2019; Siahaan et al., 2019), in 4% PFA-fixed and Triton X-100–extracted DIV7 mouse hippocampal neurons (Tan et al., 2019), and in live, non-neuronal U-2 OS cells following taxol treatment (Siahaan et al., 2022) or elevated pH (Siahaan et al., 2024). However, to our knowledge, our study is the first to demonstrate tau envelope formation in live neuronal cells under normal cell culture conditions. We will revise this sentence in the manuscript to more precisely position our findings within the context of prior studies.

(4) Unclear Wording on Expression System-Dependent Phosphorylation

The sentence "The phosphostate of tau is strongly dependent on the expression system" requires rewording. It is ambiguous whether this refers to the final phosphostate achieved after expression or the inherent phosphorylating capacity of each system. Clearer language would strengthen the methodological justification.

We agree that the wording here is ambiguous and requires clarification. In the revised manuscript, we will clarify that tau phosphorylation depends on the expression system used; bacterial systems lack the capacity for many post-translational modifications compared with insect and mammalian systems. We will also emphasize that in insect and mammalian expression systems, tau phosphorylation occurs heterogeneously, as demonstrated in previous studies by Siahaan et al. (2024) and Fan et al. (2025).

(5) Insufficient Quantification of Motor and Lysosome Transport Effect Magnitudes in Results Section

The data on molecular motor motility and lysosome transport are densely described. The magnitude of effects (fold-changes, percentage differences) should be explicitly stated in the Results section when first presenting findings to orient readers to biological significance. For example, effect magnitudes for lysosome run lengths, velocities, and directional bias should be quantified in text, not left to figure inspection.

Our initial justification for omitting quantitative data from the results text was to improve readability; however, in doing so, we may have reduced the accessibility and clarity regarding the significance of the findings. In the revised manuscript, we will incorporate the relevant quantifications and statistical significance for the motility data in the text.

(6) Incomplete Discussion of Projection Domain Necessity for Envelope Formation

The Discussion states the projection domain is "a critical regulator of both tau-tau and tau-microtubule interactions," but does not engage with prior domain dissection work. Tan et al. (2019) found that the entire projection domain is not necessary for envelope formation in vitro. The authors should discuss which projection domain regions are specifically regulated by phosphorylation vs. required for cooperativity, providing a more nuanced interpretation than implied by their current framing.

We agree with the reviewer. Tan et al. (2019) demonstrated that the proline-rich region (residues 198–244) within the projection domain of full-length 2N4R tau is the minimal region required to maintain tau’s ability to form envelopes along microtubules. We will incorporate this work on the dissection of the projection domain and discuss how the phosphorylation sites examined in our study are primarily located within this region. Together, these data highlight the proline-rich region as a potential major regulator of tau–tau cooperativity.

eLife Assessment

This study is a valuable contribution that comprehensively identifies and characterizes LC3B-binding peptides through a bacterial cell-surface display screen covering approximately 500,000 human peptides. The data presented are solid, although this approach has limitations (e.g., it cannot assess the effects of post-translational modifications, which are often relevant to LIR-mediated interactions). Validation of the newly identified binding peptides by demonstrating their interactions with full-length proteins in cells would further strengthen this manuscript.

Reviewer #1 (Public review):

Summary:

This study uses high-throughput bacterial cell-surface display to identify LC3B-interacting peptides in the human proteome. The screen is unbiased, and this type of assay has not previously been used for selecting LC3B-interacting peptides. The screen was done with a library of 500,000 peptides, and they ended up with 427 peptides that they scored as high-confidence LC3B binders. The experiments performed are solid, and data are analyzed using well-documented methods and statistics.

The aim of the authors was to isolate LC3B-interacting peptides from the human proteome, and the screen succeeded in doing so. The selected set of peptides included several previously reported LIR motifs, but also many novel LC3B binding peptides that either contained or did not contain the canonical core LIR motif [WFY]xx[LVI].

Another aim was to identify binding determinants important for the LC3B interaction, and they made an interesting sequence logo based on selected LIR-containing peptides. However, this study does not really extend our knowledge related to binding determinants essential for LIR motifs in LC3B binding. They basically verify known characteristics, including the importance of varied types of electrostatic interactions supporting the docking of the core LIR into the LDS of LC3B.

Strengths:

The approach used here (high-throughput bacterial-surface-display) is new. The screen is unbiased, and the fact that peptides are directly tested for LC3B binding may facilitate the discovery of non-canonical LIR motifs. The screen appears to be highly selective and manages to distinguish between peptides that interact with LC3B and peptides that do not interact.

Weaknesses:

It is a limitation that no proteins are analyzed in this study. Further work is therefore needed to verify that identified LIR motifs are functional in full-length proteins and in cells.

Reviewer #2 (Public review):

Summary:

To discover peptides that interact with autophagy-related protein LC3B and profile the key binding determinants, the authors screened a library of ~500,000 36-residue peptides derived from the human proteome using bacterial cell-surface display. Analysis of the screening data revealed exceptions to the reported LIR motif and a strong preference for negatively charged residues adjacent to the LIR.<br /> These results support a refinement of the LIR motif definition and expand the network of candidate LC3B interaction partners.

Strengths:

High-throughput approach.

Weaknesses:

Lack of in vitro data and molecular dynamics simulations.

Reviewer #3 (Public review):

Summary:

The LC3 family of proteins, which includes LC3B, are ubiquitin-like proteins that are covalently linked to phosphatidylethanolamine in the expanding autophagosomal membrane during autophagy. LC3 family members bind to short sequences of amino acids that reside within dynamic regions in a wide variety of proteins. These sequences, termed LC3 Interacting Regions (LIRs), were initially thought to function primarily to link LIR-containing autophagy cargo receptors to LC3 family members to help facilitate their capture during autophagy. However, the functional importance of LIRs in autophagy has broadened to include more general functions in autophagy as well. While a general consensus for LIR sequences has been described as [FWY]0-X1-X2-[LVI]3, recent work has suggested that additional sequences outside of the canonical LIR sequence can bind LC3 family members and play important roles in autophagy. In this manuscript by Kosmatka et al, the authors perform a high-throughput screen using bacterial surface display coupled with fluorescence-associated cell sorting to identify which human sequences can bind to LC3B. They identify a variety of peptides capable of binding LC3B, including peptides from proteins that have not previously been described as LC3B-binding proteins. The results from the bacterial surface display were then used to guide sequence analysis, mutational analysis, and structural studies to further characterize the range of LIR sequences that are capable of binding LC3B. Taken together, this work adds to the growing knowledge of how LIR sequences interact with LC3 family members and demonstrates which amino acids both inside and outside of the LIR sequence aid in binding. This work also identifies new potential LC3 binding proteins, which may play unknown roles in autophagy regulation. Lastly, this work reinforces the importance of alternative LIR sequences such as the [WFY]0-X1-X2-[WFY]3 sequence, which the authors have dubbed the LIR+ sequence.

Strengths:

The manuscript uses a robust approach to identify and characterize different peptide sequences that can interact with LC3B. They validate a large number of sequences using biolayer interferometry (BLI) and attempt to correlate different amino acids with their binding affinity for LC3B. The large number of LC3B binding sequences and their dissociation constants adds significant new information to the field that will help others understand what sequences can bind to LC3B. The authors are also very careful to accurately report on their data and not overly interpret their findings.

Weaknesses:

After the authors identify proteins from their bacterial display assay, the remainder of the manuscript is focused on characterizing the different types of sequences that are identified in addition to validating the LC3B-LIR interactions using biochemical approaches, including BLI and X-ray crystallography. However, it's not entirely clear if the screen identified novel LC3B binders that interact with LC3B in cells. While I acknowledge that the focus of the manuscript is on the characterization of LIR sequences that can bind LC3B, it seems like a missed opportunity not to validate a few of the novel LC3B binders in vivo. This may result in the demonstration of novel binders of LC3B in cells and may further demonstrate the strength of this approach for identifying LC3 family member binding partners. Therefore, it would be helpful to look at a few proteins identified in the HC set that have not previously been identified as LC3B binders in cells to determine if they CO-IP with LC3B or interact with LC3B using a different approach.

eLife Assessment

The work convincingly demonstrates the role of the mycobacterial secreted effector protein MmpE, which translocates to the host nucleus and exhibits phosphatase activity. The study is particularly valuable in showing that both the nuclear localization signal sequences and residues critical for phosphatase function are essential for host gene regulation, lysosomal biogenesis, and intracellular survival. Future studies will be needed to explore additional host pathways modulated by MmpE, particularly in the context of infection with a fully virulent Mycobacterium tuberculosis strain.

Reviewer #1 (Public review):

Summary:

The study provides insightful characterization of the mycobacterial secreted effector protein MmpE which translocates to the host nucleus and exhibits phosphatase activity. The study characterizes the nuclear localization signal sequences and residues critical for the phosphatase activity, both of which are required for intracellular survival

Strengths:

(1) The study addresses the role of nucleomodulins, an understudied aspect in mycobacterial infections.

(2) The authors employ a combination of biochemical and computational analyses along with in vitro and in vivo validations to characterize the role of MmpE.

Weaknesses:

(1) While the study establishes that the phosphatase activity of MmpE operates independently of its NLS, there is a clear gap in understanding how this phosphatase activity supports mycobacterial infection. The investigation lacks experimental data on specific substrates of MmpE or pathways influenced by this virulence factor.

(2) The study does not explore whether the phosphatase activity of MmpE is dependent on the NLS within macrophages, which would provide critical insights into its biological relevance in host cells. Conducting experiments with double knockout/mutant strains and comparing their intracellular survival with single mutants could elucidate these dependencies and further validate the significance of MmpE's dual functions.

(3) The study does not provide direct experimental validation of the MmpE deletion on lysosomal trafficking of the bacteria.

(4) The role of MmpE as a mycobacterial effector would be more relevant using virulent mycobacterial strains such as H37Rv.

Comments on revisions:

I appreciate the work the authors have done to address reviewers comments. The revised manuscript looks significantly improved. My major concern in the revised version is the microscopy data where the BCG staining using the DiD fluorescent stain does not bring out the rod-shaped bacilli structure. I suggest the authors either use a GFP reporter or some other fluorescent stain to address this issue.

Reviewer #2 (Public review):

Summary:

In this paper, the authors have characterized Rv2577 as a Fe3+/Zn2+ -dependent metallophosphatase and a nucleomodulin protein. The authors have also identified His348 and Asn359 as critical residues for Fe3+ coordination. The authors show that the proteins encode for two nuclease localization signals. Using C-terminal Flag expression constructs, the authors have shown that MmpE protein is secretory. The authors have prepared genetic deletion strains and show that MmpE is essential for intracellular survival of M. bovis BCG in THP-1 macrophages, RAW264.7 macrophages and mice model of infection. The authors have also performed RNA-seq analysis to compare the transcriptional profiles of macrophages infected with wild type and mmpE mutant strain. The relative levels of ~ 175 transcripts were altered in mmpE mutant infected macrophages and majority of these were associated with various immune and inflammatory signalling pathways. Using these deletion strains, the authors proposed that MmpE inhibits inflammatory gene expression by binding to the promoter region of vitamin D receptor. The authors also showed that MmpE arrests phagosome maturation by regulating the expression of several lysosome associated genes such as TFEB, LAMP1, LAMP2 etc. These findings reveal a sophisticated mechanism by which a bacterial effector protein manipulates gene transcription and promotes intracellular survival.

Strength:

The authors have used a combination of cell biology, microbiology and transcriptomics to elucidate the mechanisms by which Rv2577 contributes to intracellular survival.

Weakness:

The authors should thoroughly check the mice data and show individual replicate values in bar graphs.

Comments on revisions:

Thanks to the authors for addressing the concerns raised during the review of the original manuscript. The data is now presented with clarity, and discrepancies in mouse experiments have also been addressed with additional experiments.

Reviewer #3 (Public review):

Summary:

In this manuscript titled "Mycobacterial Metallophosphatase MmpE Acts as a Nucleomodulin to Regulate Host Gene Expression and Promote Intracellular Survival", Chen et al describe biochemical characterisation, localisation and potential functions of the gene using a genetic approach in M. bovis BCG and perform macrophage and mice infections to understand the roles of this potentially secreted protein in the host cell nucleus. The findings demonstrate the role of a secreted phosphatase of M. bovis BCG in shaping the transcriptional profile of infected macrophages, potentially through nuclear localisation and direct binding to transcriptional start sites, thereby regulating the inflammatory response to infection.

Strengths:

The authors demonstrate using a transient transfection method that MmpE when expressed as a GFP-tagged protein in HEK293T cells, exhibits nuclear localisation. The authors identify two NLS motifs that together are required for nuclear localisation of the protein. A deletion of the gene in M. bovis BCG results in poorer survival compared to the wild type parent strain, which is also killed by macrophages. Relative to the WT strain infected macrophages, macrophages infected with the mmpE strain exhibited differential gene expression. Overexpression of the gene in HEK293T led to occupancy of the transcription start site of several genes, including the Vitamin D Receptor. Expression of VDR in THP1 macrophages was lower in case of mmpE infection compared to WT infection. This data supports the utility of the overexpression system in identifying potential target loci of MmpE using the HEK293T transfection model. The authors also demonstrate that the protein is a phosphatase and the phosphatase activity of the protein is partially required for bacterial survival but not for regulation of the VDR gene expression.

Weaknesses:

There are significant differences in lysosomal retention between M. tuberculosis and M. bovis BCG. This study uses BCG and MMPE overexpression to draw conclusions about the impact of the MMPE gene on host gene expression and the bacteria's lysosomal localisation. While the authors have convincingly supported their claims with this model system, the relevance of this mechanism in M. tuberculosis infection remains unaddressed.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

Review of the manuscript titled " Mycobacterial Metallophosphatase MmpE acts as a nucleomodulin to regulate host gene expression and promotes intracellular survival".

The study provides an insightful characterization of the mycobacterial secreted effector protein MmpE, which translocates to the host nucleus and exhibits phosphatase activity. The study characterizes the nuclear localization signal sequences and residues critical for the phosphatase activity, both of which are required for intracellular survival.

Strengths:

(1) The study addresses the role of nucleomodulins, an understudied aspect in mycobacterial infections.

(2) The authors employ a combination of biochemical and computational analyses along with in vitro and in vivo validations to characterize the role of MmpE.

Weaknesses:

(1) While the study establishes that the phosphatase activity of MmpE operates independently of its NLS, there is a clear gap in understanding how this phosphatase activity supports mycobacterial infection. The investigation lacks experimental data on specific substrates of MmpE or pathways influenced by this virulence factor.

We thank the reviewer for this insightful comment and agree that identification of the substrates of MmpE is important to fully understand its role in mycobacterial infection. MmpE is a putative purple acid phosphatase (PAP) and a member of the metallophosphoesterase (MPE) superfamily. Enzymes in this family are known for their catalytic promiscuity and broad substrate specificity, acting on phosphomonoesters, phosphodiesters, and phosphotriesters (Matange et al., Biochem J, 2015). In bacteria, several characterized MPEs have been shown to hydrolyze substrates such as cyclic nucleotides (e.g., cAMP) (Keppetipola et al., J Biol Chem, 2008; Shenoy et al., J Mol Biol, 2007), nucleotide derivatives (e.g., AMP, UDP-glucose) (Innokentev et al., mBio, 2025), and pyrophosphate-containing compounds (e.g., Ap4A, UDP-DAGn) (Matange et al., Biochem J., 2015). Although the binding motif of MmpE has been identified, determining its physiological substrates remains challenging due to the low abundance and instability of potential metabolites, as well as the limited sensitivity and coverage of current metabolomic technologies in mycobacteria.

(2) The study does not explore whether the phosphatase activity of MmpE is dependent on the NLS within macrophages, which would provide critical insights into its biological relevance in host cells. Conducting experiments with double knockout/mutant strains and comparing their intracellular survival with single mutants could elucidate these dependencies and further validate the significance of MmpE's dual functions.

We thank the reviewer for the comment. Deletion of the NLS motifs did not impair MmpE’s phosphatase activity in vitro (Figure 2F), indicating that MmpE's enzymatic function operates independently of its nuclear localization. Indeed, we confirmed that Fe³⁺-binding ability via the residues H348 and N359 is required for enzymatic activity of MmpE. We have expanded on this point in the Discussion section “MmpE is a bifunctional virulence factor in Mtb”.

(3) The study does not provide direct experimental validation of the MmpE deletion on lysosomal trafficking of the bacteria.

We thank the reviewer for the comment. To validate the role of MmpE in lysosome maturation during infection, we conducted fluorescence colocalization assays in THP-1 macrophages infected with BCG strains, including WT, ∆MmpE, Comp-MmpE, Comp-MmpE^ΔNLS1, Comp-MmpE^ΔNLS2, Comp-MmpE^ΔNLS1-2. These strains were stained with the lipophilic membrane dye DiD, while macrophages were treated with the acidotropic probe LysoTracker^TM Green (Martins et al., Autophagy, 2019). The result indicated that ΔMmpE and MmpE^NLS1-2 mutants exhibited significantly higher co-localization with LysoTracker compared to WT and Comp-MmpE strains (New Figure 5G), suggesting that MmpE deletion leads to enhanced lysosomal maturation during infection.

(4) The role of MmpE as a mycobacterial effector would be more relevant using virulent mycobacterial strains such as H37Rv.

We thank the reviewer for the comment. Previously, the role of Rv2577/MmpE as a virulence factor has been demonstrated in M. tuberculosis CDC 1551, where its deletion significantly reduced bacterial replication in mouse lungs at 30 days post-infection (Forrellad et al., Front Microbiol, 2020). However, that study did not explore the underlying mechanism of MmpE function. In our study, we found that MmpE enhances M. bovis BCG survival in macrophages (THP-1 and RAW264.7 both) and in mice (Figure 3, Figure 7A), consistent with its proposed role in virulence. To investigate the molecular mechanism by which MmpE promotes intracellular survival, we used M. bovis BCG as a biosafe surrogate and this model is widely accepted for studying mycobacterial pathogenesis (Wang et al., Nat Immunol, 2015; Wang et al., Nat Commun, 2017; Péan et al., Nat Commun, 2017).

Reviewer #2 (Public review):

Summary:

In this paper, the authors have characterized Rv2577 as a Fe3+/Zn2+ -dependent metallophosphatase and a nucleomodulin protein. The authors have also identified His348 and Asn359 as critical residues for Fe3+ coordination. The authors show that the proteins encode for two nuclease localization signals. Using C-terminal Flag expression constructs, the authors have shown that the MmpE protein is secretory. The authors have prepared genetic deletion strains and show that MmpE is essential for intracellular survival of M. bovis BCG in THP-1 macrophages, RAW264.7 macrophages, and a mouse model of infection. The authors have also performed RNA-seq analysis to compare the transcriptional profiles of macrophages infected with wild-type and MmpE mutant strains. The relative levels of ~ 175 transcripts were altered in MmpE mutant-infected macrophages and the majority of these were associated with various immune and inflammatory signalling pathways. Using these deletion strains, the authors proposed that MmpE inhibits inflammatory gene expression by binding to the promoter region of a vitamin D receptor. The authors also showed that MmpE arrests phagosome maturation by regulating the expression of several lysosome-associated genes such as TFEB, LAMP1, LAMP2, etc. These findings reveal a sophisticated mechanism by which a bacterial effector protein manipulates gene transcription and promotes intracellular survival.

Strength:

The authors have used a combination of cell biology, microbiology, and transcriptomics to elucidate the mechanisms by which Rv2577 contributes to intracellular survival.

Weakness:

The authors should thoroughly check the mice data and show individual replicate values in bar graphs.

We kindly appreciate the reviewer for the advice. We have now updated the relevant mice data in the revised manuscript.

Reviewer #3 (Public review):

Summary:

In this manuscript titled "Mycobacterial Metallophosphatase MmpE Acts as a Nucleomodulin to Regulate Host Gene Expression and Promote Intracellular Survival", Chen et al describe biochemical characterisation, localisation and potential functions of the gene using a genetic approach in M. bovis BCG and perform macrophage and mice infections to understand the roles of this potentially secreted protein in the host cell nucleus. The findings demonstrate the role of a secreted phosphatase of M. bovis BCG in shaping the transcriptional profile of infected macrophages, potentially through nuclear localisation and direct binding to transcriptional start sites, thereby regulating the inflammatory response to infection.

Strengths:

The authors demonstrate using a transient transfection method that MmpE when expressed as a GFP-tagged protein in HEK293T cells, exhibits nuclear localisation. The authors identify two NLS motifs that together are required for nuclear localisation of the protein. A deletion of the gene in M. bovis BCG results in poorer survival compared to the wild-type parent strain, which is also killed by macrophages. Relative to the WT strain-infected macrophages, macrophages infected with the ∆mmpE strain exhibited differential gene expression. Overexpression of the gene in HEK293T led to occupancy of the transcription start site of several genes, including the Vitamin D Receptor. Expression of VDR in THP1 macrophages was lower in the case of ∆mmpE infection compared to WT infection. This data supports the utility of the overexpression system in identifying potential target loci of MmpE using the HEK293T transfection model. The authors also demonstrate that the protein is a phosphatase, and the phosphatase activity of the protein is partially required for bacterial survival but not for the regulation of the VDR gene expression.

Weaknesses:

(1) While the motifs can most certainly behave as NLSs, the overexpression of a mycobacterial protein in HEK293T cells can also result in artefacts of nuclear localisation. This is not unprecedented. Therefore, to prove that the protein is indeed secreted from BCG, and is able to elicit transcriptional changes during infection, I recommend that the authors (i) establish that the protein is indeed secreted into the host cell nucleus, and (ii) the NLS mutation prevents its localisation to the nucleus without disrupting its secretion.

We kindly appreciate the reviewer for this insightful comment. To confirm the translocation of MmpE into the host nucleus during BCG infection, we first detected the secretion of MmpE by M. bovis BCG, using Ag85B as a positive control and GlpX as a negative control (Zhang et al., Nat commun, 2022). Our results showed that MmpE- Flag was present in the culture supernatant, indicating that MmpE is secreted by BCG indeed (new Figure S1C).

Next, we performed immunoblot analysis of the nuclear fractions from infected THP-1 macrophages expressing FLAG-tagged wild-type MmpE and NLS mutants. The results revealed that only wild-type MmpE was detected in the nucleus, while MmpE^ΔNLS1, MmpE^ΔNLS2 and MmpE^ΔNLS1-2 were not detectable in the nucleus (New Figure S1D). Taken together, these findings demonstrated that MmpE is a secreted protein and that its nuclear translocation during infection requires both NLS motifs.

Demonstration that the protein is secreted: Supplementary Figure 3 - Immunoblotting should be performed for a cytosolic protein, also to rule out detection of proteins from lysis of dead cells. Also, for detecting proteins in the secreted fraction, it would be better to use Sauton's media without detergent, and grow the cultures without agitation or with gentle agitation. The method used by the authors is not a recommended protocol for obtaining the secreted fraction of mycobacteria.

We kindly appreciate the reviewer for the advice. To avoid the effects of bacterial lysis, we cultured the BCG strains expressing MmpE-Flag in Middlebrook 7H9 broth with 0.5% glycerol, 0.02% Tyloxapol, and 50 µg/mL kanamycin at 37 °C with gentle agitation (80 rpm) until an OD₆₀₀ of approximately 0.6 (Zhang et al., Nat Commun, 2022). Subsequently, we assessed the secretion of MmpE-Flag in the culture supernatant, using Ag85B as a positive control and GlpX as a negative control (New Figure S1C). The results showed that GlpX was not detected in the supernatant, while MmpE and Ag85B were detected, indicating that MmpE is indeed a secreted protein in BCG.

Demonstration that the protein localises to the host cell nucleus upon infection: Perform an infection followed by immunofluorescence to demonstrate that the endogenous protein of BCG can translocate to the host cell nucleus. This should be done for an NLS1-2 mutant expressing cell also.

We thank the reviewer for the suggestion. We agree that this experiment would be helpful to further verify the ability of MmpE for nuclear import. However, MmpE specific antibody is not available for us for immunofluorescence experiment. Alternatively, we performed nuclear-cytoplasmic fractionation for the THP-1 cells infected with the M. bovis BCG strains expressing FLAG-tagged wild-type MmpE, as well as NLS deletion mutants (MmpE^ΔNLS1, MmpE^ΔNLS2, and MmpE^ΔNLS1-2). The WT MmpE is detectable in both cytoplasmic and nuclear compartments, while MmpE^ΔNLS1, MmpE^ΔNLS2 or MmpE^ΔNLS1-2 were almost undetectable in nuclear fractions (New Figure S1D), suggesting that both NLS motifs are necessary for nuclear import.

(2) In the RNA-seq analysis, the directionality of change of each of the reported pathways is not apparent in the way the data have been presented. For example, are genes in the cytokine-cytokine receptor interaction or TNF signalling pathway expressed more, or less in the ∆mmpE strain?

We thank the reviewer for the comment. The KEGG pathway enrichment diagrams in our RNA-seq analysis primarily reflect the statistical significance of pathway enrichment based on differentially expressed genes, but do not indicate the directionality of genes expression changes. To address this concern, we conducted qRT-PCR on genes associated with the cytokine-cytokine receptor interaction pathway, specifically IL23A, CSF2, and IL12B. The results showed that, compared to the WT strain, infection with the ΔMmpE strain resulted in significantly increased expression levels of these genes in THP-1 cells (Figure 4F, Figure S4B), consistent with the RNA-seq data. Furthermore, we have submitted the complete RNA-seq dataset to the NCBI GEO repository [GSE312039], which includes normalized expression values and differential expression results for all detected genes.

(3) Several of these pathways are affected as a result of infection, while others are not induced by BCG infection. For example, BCG infection does not, on its own, produce changes in IL1β levels. As the author s did not compare the uninfected macrophages as a control, it is difficult to interpret whether ∆mmpE induced higher expression than the WT strain, or simply did not induce a gene while the WT strain suppressed expression of a gene. This is particularly important because the strain is attenuated. Does the attenuation have anything to do with the ability of the protein to induce lysosomal pathway genes? Does induction of this pathway lead to attenuation of the strain? Similarly, for pathways that seem to be downregulated in the ∆mmpE strain compared to the WT strain, these might have been induced upon infection with the WT strain but not sufficiently by the ∆mmpE strain due to its attenuation/ lower bacterial burden.

We thank the reviewer for the comment. Previous studies have shown that wild-type BCG induces relatively low levels of IL-1β, while retaining partial capacity to activate the inflammasome (Qu et al., Sci Adv, 2020). Our data (Figures 3G) show that infection with the ΔMmpE strain results in enhanced IL-1β expression, consistent with findings by Master et al. (Cell Host Microbe, 2008), in which deletion of zmp1 in BCG or M. tuberculosis led to increased IL-1β levels due to reduced inhibition of inflammasome activation.

In the revised manuscript, we have provided additional qRT-PCR data using uninfected macrophages as a baseline control. These results demonstrate that the WT strain suppresses lysosome-associated gene expression, whereas the ΔMmpE strain upregulates these genes, indicating that MmpE inhibits lysosome-related genes expression (Figure 4G). Furthermore, bacterial burden analysis revealed that ∆mmpE exhibited ~3-fold lower intracellular survival than the WT strain in THP-1 cells. However, when lysosomal maturation was inhibited, the difference in bacterial load between the two strains was reduced to ~1-fold (New Figures S6B and C). These findings indicate that MmpE promotes intracellular survival primarily by inhibiting lysosomal maturation, which is consistent with a previous study (Chandra et al., Sci Rep, 2015).

(4) CHIP-seq should be performed in THP1 macrophages, and not in HEK293T. Overexpression of a nuclear-localised protein in a non-relevant line is likely to lead to several transcriptional changes that do not inform us of the role of the gene as a transcriptional regulator during infection.

We thank the reviewer for the comment. We performed ChIP-seq in HEK293T cells based on their high transfection efficiency, robust nuclear protein expression, and well-annotated genome (Lampe et al., Nat Biotechnol, 2024; Marasco et al., Cell, 2022). These characteristics make HEK293T an ideal system for the initial identification of genome-wide chromatin binding profiles by MmpE.

Further, we performed comprehensive validation of the ChIP-seq findings in THP-1 macrophages. First, CUT&Tag and RNA-seq analyses in THP-1 cells revealed that MmpE modulates genes involved in the PI3K–AKT signaling and lysosomal maturation pathways (Figure 4C; Figure S5A-B). Correspondingly, we found that infection with the ΔMmpE strain led to reduced phosphorylation of AKT (S473), mTOR (S2448), and p70S6K (T389) (New Figure 5E-F), and upregulation of lysosomal genes such as TFEB, LAMP1, and LAMP2 (Figure 4G), compared to infection with the WT strain, and lysosomal maturation in cells infected with the ΔMmpE strain more obviously (New Figure 5G). Additionally, CUT&Tag profiling identified MmpE binding at the promoter region of the VDR gene, which was further validated by EMSA and ChIP-qPCR. Also, qRT-PCR demonstrated that MmpE suppresses VDR transcription, supporting its role as a transcriptional regulator (Figure 6). Collectively, these data confirm the biological relevance and functional significance of the ChIP-seq findings obtained in HEK293T cells.

(5) I would not expect to see such large inflammatory reactions persisting 56 days post-infection with M. bovis BCG. Is this something peculiar for an intratracheal infection with 1x107 bacilli? For images of animal tissue, the authors should provide images of the entire lung lobe with the zoomed-in image indicated as an inset.

We thank the reviewer for the comment. The lung inflammation peaked at days 21–28 and had clearly subsided by day 56 across all groups (New Figure 7B), consistent with the expected resolution of immune responses to an attenuated strain like M. bovis BCG. This temporal pattern is in line with previous studies using intravenous or intratracheal BCG vaccination in mice and macaques, which also demonstrated robust early immune activation followed by resolution over time (Smith et al., Nat Microbiol, 2025; Darrah et al., Nature, 2020).

In this study, the infectious dose (1×10⁷ CFU intratracheal) was selected based on previous studies in which intratracheal delivery of 1×10⁷ CFU produced consistent and measurable lung immune responses and pathology without causing overt illness or mortality (Xu et al., Sci Rep, 2017; Niroula et al., Sci Rep, 2025). We have provided whole-lung lobe images with zoomed-in insets in the source dataset.

(6) For the qRT-PCR based validation, infections should be performed with the MmpE-complemented strain in the same experiments as those for the WT and ∆mmpE strain so that they can be on the same graph, in the main manuscript file. Supplementary Figure 4 has three complementary strains. Again, the absence of the uninfected, WT, and ∆mmpE infected condition makes interpretation of these data very difficult.

We thank the reviewer for the comment. As suggested, we have conducted the qRT-PCR experiment including the uninfected, WT, ∆mmpE, Comp-MmpE, and the three complementary strains infecting THP-1 cells (Figure 4F and G; New Figure S4B–D).

(7) The abstract mentions that MmpE represses the PI3K-Akt-mTOR pathway, which arrests phagosome maturation. There is not enough data in this manuscript in support of this claim. Supplementary Figure 5 does provide qRT-PCR validation of genes of this pathway, but the data do not indicate that higher expression of these pathways, whether by VDR repression or otherwise, is driving the growth restriction of the ∆mmpE strain.

We thank the reviewer for the comment. In the updated manuscript, we have provided more evidence. First, the RNA-seq analysis indicated that MmpE affects the PI3K-AKT signaling pathway (Figure 4C). Second, CUT&Tag analysis suggested that MmpE binds to the promoter regions of key pathway components, including PRKCB, PLCG2, and PIK3CB (Figure S5A). Third, confocal microscopy showed that ΔMmpE strain promotes significantly increased lysosomal maturation compared to the WT, a process downstream of the PI3K-AKT-mTOR axis (New Figure 5G).

Further, we measured protein phosphorylation for validating activation of the pathway (Zhang et al., Stem Cell Reports, 2017). Our results showed that cells infected with WT strains exhibited significantly higher phosphorylation of Akt, mTOR, and p70S6K compared to those infected with ΔMmpE strains (New Figures 5E and F). Moreover, the dual PI3K/mTOR inhibitor BEZ235 abolished the survival advantage of WT strains over ΔMmpE mutants in THP-1 macrophages (New Figure S6B and C). Collectively, these results support that MmpE activates the PI3K–Akt–mTOR signaling pathway to enhance bacterial survival within the host.

(8) The relevance of the NLS and the phosphatase activity is not completely clear in the CFU assays and in the gene expression data. Firstly, there needs to be immunoblot data provided for the expression and secretion of the NLS-deficient and phosphatase mutants. Secondly, CFU data in Figure 3A, C, and E must consistently include both the WT and ∆mmpE strain.

We thank the reviewer for the comment. We have now added immunoblot analysis for expression and secretion of MmpE mutants. The result show that NLS-deficient and phosphatase mutants can detected in supernatant (New Figure S1C). Additionally, we have revised Figures 3A, 3C, and 3E to consistently include both the WT and ΔMmpE strains in the CFU assays (Figures 3A, 3C, and 3E).

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

The authors should attempt to address the following comments:

(1) Please perform densitometric analysis for the western blot shown in Figure 1E.

We sincerely thank the reviewer for the suggestion. In the updated manuscript, we have performed densitometric analysis of the western blot shown in New Figure 1F and G.

(2) Is it possible to measure the protein levels for MmpE in lysates prepared from infected macrophages.

We thank the reviewer for the comment. In the revised manuscript, we performed immunoblot analysis to measure MmpE levels in lysates from infected macrophages. The results demonstrated that wild-type MmpE was present in both the cytoplasmic and nuclear fractions during infection in THP-1 cells (New Figure S1D).

(3) The authors should perform circular dichroism studies to compare the secondary structure of wild type and mutant proteins (in particular MmpEHis348 and MmpEAsn359.

We thank the reviewer for this valuable suggestion. We agree that circular dichroism spectroscopy could provide useful information in comparison of the differences on the secondary structures. However, due to the technical limitations, we instead compared the structures of wild-type MmpE and the His348 and Asn359 mutant proteins predicted by AlphaFold. These structural models showed almost no differences in secondary structures between the wild-type and mutants (Figure S1B).

(4) The authors should perform more experiments to determine the binding motif for MmpE in the promoter region of VDR.

We thank the reviewer for this suggestion. In the current study, we have identified the MmpE-binding motif within the promoter region of VDR using CUT&Tag sequencing. This prediction was further validated by ChIP-qPCR and EMSA (Figure 6). These complementary approaches collectively support the identification of a specific MmpE-binding motif and demonstrate its functional relevance. Such approach was acceptable in many publications (Wen et al., Commun Biol, 2020; Li et al., Nat Commun, 2022).

(5) Were the transcript levels of VDR also measured in the lung tissues of infected animals?

We thank the reviewer for this suggestion. In the revised manuscript, we have performed qRT-PCR to assess VDR transcript levels in the lung tissues of infected mice (New Figure S8B).

(6) How does MmpE regulate the expression of lysosome-associated genes?

We thank the reviewer for this question. Our experiments suggested that MmpE suppresses lysosomal maturation probably by activating the host PI3K–AKT–mTOR signaling pathway (New Figure 5E–I). This pathway is well established as a negative regulator of lysosome biogenesis and function (Yang et al., Signal Transduct Target Ther, 2020; Cui et al., Nature, 2023; Cui et al., Nature, 2025). During infection, THP-1 cells infected with the WT showed increased phosphorylation of Akt, mTOR, and p70S6K compared to those infected with ΔMmpE (New Figure S5C, New Figure 5E and F), and concurrently downregulated key lysosomal maturation markers, including TFEB, LAMP1, LAMP2, and multiple V-ATPase subunits (Figure 4G). Given that PI3K–AKT–mTOR signaling suppresses TFEB activity and lysosomal gene transcription (Palmieri et al., Nat Commun, 2017), we propose that MmpE modulates lysosome-associated gene expression and lysosomal function probably by PI3K–AKT–mTOR signaling pathway.

(7) Mice experiment:

(a) The methods section states that mice were infected intranasally, but the legend for Figure 6 states intratracheally. Kindly check?

(b) Supplementary Figure 7 - this is not clear. The legend says bacterial loads in spleens (CFU/g) instead of DNA expression, as shown in the figure.

(c) The data in Figure 6 and Figure S7 seem to be derived from the same experiment, but the number of animals is different. In Figure 6, it is n = 6, and in Figure S7, it is n=3.

We thank the reviewer for the comments.

(a) The infection was performed intranasally, and the figure legend for New Figure 7 has now been corrected.

(b) We adopted quantitative PCR method to measure bacterial DNA levels in the spleens of infected mice. We have now revised the legend.

(c) We have conducted new experiments where each experiment now includes six mice. The results are showed in Figure 7B and C, as well as in the new Figure S8.

(8) The authors should show individual values for various replicates in bar graphs (for all figures).

We thank the reviewer for this helpful suggestion. We have now updated all relevant bar graphs to include individual data points for each biological replicate.

(9) The authors should validate the relative levels of a few DEGs shown in Figure 3F, Figure 3G, and Figure S4C, in the lung tissues of mice infected with wild-type, mutant, and complemented strains.

We thank the reviewer for this suggestion. In the revised manuscript, we have performed qRT-PCR to validate the expression levels of selected DEGs, including inflammation-related and lysosome-associated genes, in lung tissues from mice infected with wild-type, mutant, and complemented strains (New Figure S8C-H).

(10) Did the authors perform an animal experiment using a mutant strain complemented with the phosphatase-deficient MmpE (Comp-MmpE-H348AN359H)?

We appreciate the reviewer's comment. We agree that an additional animal experiment would be useful to assess the effects of the phosphatase. However, our study mainly focused on interpreting the function of the nuclear localization of MmpE during BCG infection. Additionally, we have assessed the role of the phosphatase of MmpE during infection with cell model (Figure 3E).

Minor comment:

The mutant strain should be verified by either Southern blot or whole genome sequencing.

We thank the reviewer for this comment. We verified deletion of mmpE gene by PCR method (Figure S3A-D) which was acceptable in many publications (Zhang et al., PLoS Pathog, 2020; Zhang et al., Nat Commun, 2022).

Reviewer #3 (Recommendations for the authors):

(1) Line 195: cytokine.

We thank the reviewer for the comments. We have now corrected it.

(2) Line 225: rewording required.

Corrected.

(3) Figure 4A. "No difference" instead of "No different".

Corrected.

(4) "KommpE" should be replaced with "∆mmpE strain" (∆=delta symbol).

Corrected.

(5) Supplementary Figure 7. The figure legend states CFU assays, but the y-axis and the graph seem to depict IS1081 quantification.

We thank the reviewer for the comment. The figure is based on IS1081 quantification using qRT-PCR, not CFU assays. We have now revised the legend for New Figure S8A.

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eLife Assessment

The authors provide a useful resource and approach to identify early-stage biomarkers of MASLD progression, notably when no other apparent symptoms have arisen. The strength of evidence to support new MASLD signatures is solid as the work combines metabolomic and transcriptomic measures in blood and liver biopsies.

[Editors' note: this paper was reviewed by Review Commons.]

Reviewer #1 (Public review):

Summary:

Metabolic dysfunction-associated steatotic liver disease (MASLD) ranges from simple steatosis, steatohepatitis, fibrosis/cirrhosis, and hepatocellular carcinoma. In the current study, the authors aimed to determine the early molecular signatures differentiating patients with MASLD associated fibrosis from those patients with early MASLD but no symptoms. The authors recruited 109 obese individuals before bariatric surgery. They separated the cohorts as no MASLD (without histological abnormalities) and MASLD. The liver samples were then subjected to transcriptomic and metabolomic analysis. The serum samples were subjected to metabolomic analysis. The authors identified dysregulated lipid metabolism, including glyceride lipids, in the liver samples of MASLD patients compared to the no MASLD ones. Circulating metabolomic changes in lipid profiles slightly correlated with MASLD, possibly due to the no MASLD samples derived from obese patients. Several genes involved in lipid droplet formation were also found elevated in MASLD patients. Besides, elevated levels of amino acids, which are possibly related to collagen synthesis, were observed in MASLD patients. Several antioxidant metabolites were increased in MASLD patients. Furthermore, dysregulated genes involved in mitochondrial function and autophagy were identified in MASLD patients, likely linking oxidative stress to MASLD progression. The authors then determined the representative gene signatures in the development of fibrosis by comparing this cohort with the other two published cohorts. Top enriched pathways in fibrotic patients included GTPas signaling and innate immune responses, suggesting the involvement of GTPas in MASLD progression to fibrosis. The authors then challenged human patient derived 3D spheroid system with a dual PPARa/d agonist and found that this treatment restored the expression levels of GTPase-related genes in MASLD 3D spheroids. In conclusion, the authors suggested the involvement of upregulated GTPase-related genes during fibrosis initiation.

Significance:

Overall, the current study might provide some new resources regarding transcriptomic and metabolomic data derived from obese patients with and without MASLD. The MASLD research community will be interested in the resource data.

Comments on revised version:

I have no further comments. Thank you.

Reviewer #3 (Public review):

Summary:

Metabolic dysfunction associated liver disease (MASLD) describes a spectrum of progressive liver pathologies linked to life style-associated metabolic alterations (such as increased body weight and elevated blood sugar levels), reaching from steatosis over steatohepatitis to fibrosis and finally end stage complications, such as liver failure and hepatocellular carcinoma. Treatment options for MASLD include diet adjustments, weight loss, and the receptor-β (THR-β) agonist resmetirom, but remain limited at this stage, motivating further studies to elucidate molecular disease mechanisms to identify novel therapeutic targets.

In their present study, the authors aim to identify early molecular changes in MASLD linked to obesity. To this end, they study a cohort of 109 obese individuals with no or early-stage MASLD combining measurements from two anatomic sides: 1. bulk RNA-sequencing and metabolomics of liver biopsies, and 2. metabolomics from patient blood. Their major finding is that GTPase-related genes are transcriptionally altered in livers of individuals with steatosis with fibrosis compared to steatosis without fibrosis.

Major comments:

(1) Confounders (such as (pre-)diabetes)

The patient table shows significant differences in non-MASLD vs. MASLD individuals, with the latter suffering more often from diabetes or hypertriglyceridemia. Rather than just stating corrections, subgroup analyses should be performed (accompanied with designated statistical power analyses) to infer the degree to which these conditions contribute to the observations. I.e., major findings stating MASLD-associated changes should hold true in the subgroup of MASLD patients without diabetes/of female sex and so forth (testing for each of the significant differences between groups).

Post-rebuttal update: The authors have performed the requested sub-group analysis and find the gene signatures hold for the non-diabetic sub-cohort, but not the diabetic subgroup. They denote a likely interaction between fibrosis and diabetes, that was not corrected for in the original analysis.

Post-post-rebuttal update: I thank the authors for having added Figure 5-figure supplement 2 to show this analysis.

(2) External validation

Additionally, to back up the major GTPase signature findings, it would be desirable to analyze an external dataset of (pre)diabetes patients (other biased groups) for alternations in these genes. It would be important to know if this signature also shows in non-MASLD diabetic patients vs. healthy patients or is a feature specific to MASLD. Also, could the matched metabolic data be used to validate metabolite alterations that would be expected under GTPase-associated protein dysregulation?

Post-rebuttal update: The authors confirm that with the present data, insulin resistance cannot be fully ruled out as a confounder to the GTP-ase related gene signature. They however plan future mouse model experiments to study whether the GTPase-fibrosis signature differs in diabetic vs. non-diabetic conditions.

(3) 3D liver spheroid MASH model, Fig. 6D/E

This 3D experiment is technically not an external validation of GTPase-related genes being involved in MASLD, since patient-derived cells may only retain changes that have happened in vivo. To demonstrate that the GTPase expression signature is specifically invoked by fibrosis the LX-2 set up is more convincing, however, the up-regulation of the GTPase-related genes upon fibrosis induction with TGF-beta, in concordance with the patient data, needs to be shown first (qPCR or RNA-seq). Additionally, the description of the 3D model is too uncritical. The maintenance of functional PHHs is a major challenge (PMID: 38750036, PMID: 21953633, PMID: 40240606, PMID: 31023926). It cannot be ruled out that their findings are largely attributable to either 1) the (other present) mesenchymal cells (i.e., mesenchyme-derived cells, such as for example hepatic stellate cells, not to be confused with mesenchymal stem cells, MSCs), or 2) related to potential changes in PHHs in culture, and these limitations need to be stated.

Post-rebuttal update: To address the concern of other cells than hepatocytes contributing to the observed effects in culture, the authors performed TGF-beta treatment in independent mono-cultures (Figure R4): LX-2 and hepatocytes, and the spheroid system. Surprisingly, important genes highlighted in Figure 6E for the spheroid system (RAB6A, ARL4A, RAB27B, DIRAS2) are all absent from this qPCR(?) validation experiment. The authors evaluate instead RAC1, RHOU, VAV1, DOCK2, RAB32. ­In spheroids, RHOU and RAB32 are down-regulated with TGF-B. In hepatocytes DOCK2 and RAC seemed up-regulated. They find no difference in these genes in LX-2 cells. Surprisingly, ACTA2 expression values are missing for LX-2 cells. Together, it is hard to judge which individual cell type recapitulates the changes observed in patients in this validation experiment, as the major genes called out in Figure 6E are not analyzed.

Post-post-rebuttal update: I thank the authors for having added Figure 6-figure supplement 5 to show qPCR results for this question.

Unfortunately, the 3D liver spheroid model used (as presente­d in PMID39605182) lacks important functional validation tests of maintained hepatocyte identity in culture (at the very least Albumin expression and secretion plus CYP3A4 assay). This functional data (acquired at the time point in culture when the RNA expression analysis in 6E was performed) is indispensable prior to stating that mature hepatocytes cause the observed effects.

Post-post-rebuttal update: I thank the authors for having added more references, I still think a quick functional validation of the system (at the time point in culture when the RNA expression analysis in 6E was performed) would be beneficial.

(4) Novelty / references

Similar studies that also combined liver and blood lipidomics/metabolomics in obese individuals with and without MASLD (e.g. PMID 39731853, 39653777) should be cited. Additionally, it would benefit the quality of the discussion to state how findings in this study add new insights over previous studies, if their findings/insights differ, and if so, why.

Post-rebuttal update: The authors have included the studies into their discussion.

Overall post-post-rebuttal update: I thank the authors for having added more data, important discussion points, and references, and have no further requests.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public Review):

Thank you for the authors' responses to my concerns. I do not have any further comments.

We thank this reviewer for the positive and constructive evaluation of our manuscript.

Reviewer #2 (Public Review):

I have no further comment about this amended version, aside from suggesting to add (if known) the time at which biopsies were collected. Time-of-day is an important yet often overlooked parameter of gene expression variation, and along the same line, the imposed fasting to bariatric surgery patients is also a matter of variation of gene expression and of metabolite abundance. It is hoped that future investigations will more precisely characterize the role of the newly identified targets in MASLD.

We agree with this and are fully aware that metabolism in the liver is controlled by circadian rhythm and therefore the time-of-day is an important parameter when liver samples are collected. All liver samples were collected between 8am and 1pm, and this information has been added to the Methods section. We are already working on the characterization of the newly identified targets. Thank you for the positive and constructive evaluation of our manuscript.

Reviewer #3 (Public Review):

(1) Confounders (such as (pre-)diabetes)

The patient table shows significant differences in non-MASLD vs. MASLD individuals, with the latter suffering more often from diabetes or hypertriglyceridemia. Rather than just stating corrections, subgroup analyses should be performed (accompanied with designated statistical power analyses) to infer the degree to which these conditions contribute to the observations. I.e., major findings stating MASLD-associated changes should hold true in the subgroup of MASLD patients without diabetes/of female sex and so forth (testing for each of the significant differences between groups).

Post-rebuttal update: The authors have performed the requested sub-group analysis and find the gene signatures hold for the non-diabetic sub-cohort, but not the diabetic subgroup. They denote a likely interaction between fibrosis and diabetes, that was not corrected for in the original analysis.

(2) External validation

Additionally, to back up the major GTPase signature findings, it would be desirable to analyze an external dataset of (pre)diabetes patients (other biased groups) for alternations in these genes. It would be important to know if this signature also shows in non-MASLD diabetic patients vs. healthy patients or is a feature specific to MASLD. Also, could the matched metabolic data be used to validate metabolite alterations that would be expected under GTPase-associated protein dysregulation?

Post-rebuttal update: The authors confirm that with the present data, insulin resistance cannot be fully ruled out as a confounder to the GTPase related gene signature. They however plan future mouse model experiments to study whether the GTPase-fibrosis signature differs in diabetic vs. non-diabetic conditions.

(3) 3D liver spheroid MASH model, Fig. 6D/E

This 3D experiment is technically not an external validation of GTPase-related genes being involved in MASLD, since patient-derived cells may only retain changes that have happened in vivo. To demonstrate that the GTPase expression signature is specifically invoked by fibrosis the LX-2 set up is more convincing, however, the up-regulation of the GTPase-related genes upon fibrosis induction with TGF-beta, in concordance with the patient data, needs to be shown first (qPCR or RNA-seq). Additionally, the description of the 3D model is too uncritical. The maintenance of functional PHHs is a major challenge (PMID: 38750036, PMID: 21953633, PMID: 40240606, PMID: 31023926). It cannot be ruled out that their findings are largely attributable to either 1) the (other present) mesenchymal cells (i.e., mesenchyme-derived cells, such as for example hepatic stellate cells, not to be confused with mesenchymal stem cells, MSCs), or 2) related to potential changes in PHHs in culture, and these limitations need to be stated.

Post-rebuttal update: To address the concern of other cells than hepatocytes contributing to the observed effects in culture, the authors performed TGF-beta treatment in independent mono-cultures (Figure R4): LX-2 and hepatocytes, and the spheroid system. Surprisingly, important genes highlighted in Figure 6E for the spheroid system (RAB6A, ARL4A, RAB27B, DIRAS2) are all absent from this qPCR(?) validation experiment. The authors evaluate instead RAC1, RHOU, VAV1, DOCK2, RAB32. -In spheroids, RHOU and RAB32 are down-regulated with TGF-B. In hepatocytes DOCK2 and RAC seemed up-regulated. They find no difference in these genes in LX-2 cells. Surprisingly, ACTA2 expression values are missing for LX-2 cells. Together, it is hard to judge which individual cell type recapitulates the changes observed in patients in this validation experiment, as the major genes called out in Figure 6E are not analyzed.

All biological experiments show variations and especially when analyzing various cell types (lines), we are not completely surprised that not all results are completely aligned. In other words, some of the GTPases will be upregulated in hepatocytes, while other may be upregulated in hepatic stellate cells due to the complex signaling arrangement in each cell. To address this reviewer’s concerns, we have done qPCR for RAB6A, ARL4A, RAB27B, DIRAS2 in LX-2 cells and the results are shown in the revised now Figure 6– figure supplement 5. To align all three graphs displaying the same genes analyzed, we have now depicted the gene expression for the co-culture (hepatocytes, hepatic stellate cells, and Kupffer cells) and mono-culture (hepatocytes only) from RNAseq analysis.

Unfortunately, the 3D liver spheroid model used (as presente-d in PMID39605182) lacks important functional validation tests of maintained hepatocyte identity in culture (at the very least Albumin expression and secretion plus CYP3A4 assay). This functional data (acquired at the time point in culture when the RNA expression analysis in 6E was performed) is indispensable prior to stating that mature hepatocytes cause the observed effects.

We agree that the characterization of the liver spheroid model derived from human patient samples is important. The functional characterization has already been published in these papers:

(1) Bell, C. C. et al. Transcriptional, Functional, and Mechanistic Comparisons of Stem Cell–Derived Hepatocytes, HepaRG Cells, and Three-Dimensional Human Hepatocyte Spheroids as Predictive In Vitro Systems for Drug-Induced Liver Injury. Drug Metab. Dispos. 45, 419–429 (2017).

(2) Bell, C. C. et al. Characterization of primary human hepatocyte spheroids as a model system for drug-induced liver injury, liver function and disease. Sci. Rep. 6, 25187 (2016). 3.Vorrink, S. U. et al. Endogenous and xenobiotic metabolic stability of primary human hepatocytes in long‐term 3D spheroid cultures revealed by a combination of targeted and untargeted metabolomics. FASEB J. 31, 2696–2708 (2017).

(4) Messner, S. et al. Transcriptomic, Proteomic, and Functional Long-Term Characterization of Multicellular Three-Dimensional Human Liver Microtissues. Appl. In Vitro Toxicol. 4, 1–12 (2018).

(5) Bell, C. C. et al. Comparison of Hepatic 2D Sandwich Cultures and 3D Spheroids for Long-term Toxicity Applications: A Multicenter Study. Toxicol. Sci. 162, 655–666 (2018). We have mentioned this now in the manuscript on page 18 to make this point clear.

(4) Novelty / references

Similar studies that also combined liver and blood lipidomics/metabolomics in obese individuals with and without MASLD (e.g. PMID 39731853, 39653777) should be cited. Additionally, it would benefit the quality of the discussion to state how findings in this study add new insights over previous studies, if their findings/insights differ, and if so, why.

Post-rebuttal update: The authors have included the studies into their discussion.

Recommendations for the authors:

Reviewer #3 (Recommendations for the authors):

(1) Add the plots showing diabetes/non-diabetes sub-group analysis and power estimates to the Supplementary Figures (rather than just as a Supplementary table)

We have added this as Figure 5-figure supplement 2 in the revised manuscript (R2).

(2) Add a short note on the validity of the results limiting to the non-diabetes subgroup to the limitations section

We have done this in the revised manuscript (R2).

(3) Add a short note on the missing adjustment for fibrosis/diabetes interactions in the study to the limitations paragraph

We appreciate the reviewer’s suggestion to address the lack of adjustment for potential fibrosis–diabetes interaction. We added a note to the limitations paragraph in the Limitations section. Although diabetes considerably modulates the risk for steatohepatitis, only a small number of participants had diabetes (29 of 109) in our study, undermining statistical power to detect meaningful interaction effects.

Author response table 1.

(4) Fig S10/6E: In vitro TGF-b stimulation on spheroids, LX-2 cells, hepatocytes: evaluate expression of RAB6A, ARL4A, RAB27B, DIRAS2 genes from 6E to create consistency between the findings. Confirm ACTA2 up-regulation in LX-2 cells treated with TGF-β as a positive control. Also specify methods for gene expression analysis in spheroids and the cell types in the figure legends (RNA-Seq? qPCR?)

To address this reviewer’s concerns, we have done qPCR for RAB6A, ARL4A, RAB27B, DIRAS2 in LX-2 cells stimulated with TGF-β and the results are shown in the revised now Figure 6–figure supplement 5. To align all three graphs displaying the same genes analyzed, we have now depicted the gene expression for the co-culture (hepatocytes, hepatic stellate cells, and Kupffer cells) and mono-culture (hepatocytes only) from RNAseq analysis. We have also updated the methods that we used in the figure legend.

(5) Validate the functionality of hepatocytes in the 3D liver spheroid model used (PMID: 39605182) at the time points of which the experiments have been performed (e.g. Albumin secretion, CYP-assays).

We agree that the characterization of the liver spheroids from human patients using fully differentiated cells, is important but this has already been done and is published in these papers:

(1) Bell, C. C. et al. Transcriptional, Functional, and Mechanistic Comparisons of Stem Cell–Derived Hepatocytes, HepaRG Cells, and Three-Dimensional Human Hepatocyte Spheroids as Predictive In Vitro Systems for Drug-Induced Liver Injury. Drug Metab. Dispos. 45, 419–429 (2017).

(2) Bell, C. C. et al. Characterization of primary human hepatocyte spheroids as a model system for drug-induced liver injury, liver function and disease. Sci. Rep. 6, 25187 (2016). 3.Vorrink, S. U. et al. Endogenous and xenobiotic metabolic stability of primary human hepatocytes in long‐term 3D spheroid cultures revealed by a combination of targeted and untargeted metabolomics. FASEB J. 31, 2696–2708 (2017).

(4) Messner, S. et al. Transcriptomic, Proteomic, and Functional Long-Term Characterization of Multicellular Three-Dimensional Human Liver Microtissues. Appl. In Vitro Toxicol. 4, 1–12 (2018).

(5) Bell, C. C. et al. Comparison of Hepatic 2D Sandwich Cultures and 3D Spheroids for Long-term Toxicity Applications: A Multicenter Study. Toxicol. Sci. 162, 655–666 (2018).

We have mentioned this now in the manuscript on page 18 and also the Limitation section to make this point clear.

(6) Add a note on limitations of the PHH-spheroid and cell line in vitro models to the limitations section and discuss the need for future experiments to examine the cellular crosstalk and cell types potentially responsible for the proposed GTPase-gene dysregulation.

We have added this to the limitation section on page 13 this in the revised manuscript (R2).

eLife Assessment

Kambali et al use optogenetic manipulations to examine whether the ventral hippocampal Schaffer collateral (vCA3-to-vCA1) and temporoammonic (EC-to-vCA1) pathways regulate anxiety- and fear-related behaviors in mice. They find that both pathways regulate the expression of fear (freezing) responses to a context and auditory conditioned stimulus paired with foot shock (trace conditioning protocol), but only the Schaffer collateral pathway regulates the expression of anxiety-related behaviors in the elevated plus maze, open field test, and Vogel conflict test. Overall, the study is valuable: it detects bidirectional effects of optogenetic excitation and inhibition in both pathways. However, the strength of the evidence in support of its main claims is incomplete.

Reviewer #1 (Public review):

Summary:

The hippocampus, especially the ventral subregion, has been related to emotional processing. However, the specific circuitry involved deserves further investigation. By using a bidirectional optogenetic modulation, Kambali et al. have investigated the role of different inputs to vCA1 (i.e., from vCA3 and entorhinal cortex) in anxiety- and fear-related responses. The major findings of this work suggested that both inputs to vCA1 control fear-related responses, whereas only the projection between vCA3 and vCA1 controls anxiety-related behavior. Overall, the authors used an advanced methodological approach, which allows them to modulate specific brain circuits, to study specific hippocampal projections, providing some new information regarding the hippocampal function in anxiety and fear.

Strengths:

(1) The manuscript is well written, clear and has a detailed and specific discussion.

(2) Results from each optogenetic manipulation are clear in different anxiety- and fear-related tasks, demonstrating the robustness of the findings.

(3) The overall conclusions are very interesting and might be relevant for the field of mental health disorders accompanied by anxiety- and fear-related alterations.

Weaknesses:

(1) The major differences in basal behavioral performance in the different paradigms between the two optogenetic modulations prevent the achievement of strong conclusive results.

(2) Data presentation and representative figures need a major revision.

(3) No analysis has been performed to analyze potential sex differences in behavioral domains where sex is important.

Reviewer #2 (Public review):

Summary:

This paper uses an optogenetic approach to either activate or inhibit separate neural pathways projecting to the ventral CA1 hippocampal subregion, from either CA3 or the entorhinal cortex. The authors report that manipulation of the vCA3→vCA1 pathway affected behavioural performance on a number of tasks: elevated plus maze, open field, Vogel conflict test and freezing behaviour to both context and a trace CS cue. In contrast, optogenetic manipulation of neural activity in the EC→vCA1 pathway only affected behaviour on the trace CS/context fear memory test but had no effect on the elevated plus maze, open field or Vogel conflict test. The authors suggest different roles for these two ventral hippocampal pathways in fear versus anxiety.

Strengths:

This is an interesting study addressing an important question in a highly topical subject area. The experiments are well conducted and have generated interesting and important data.

Weaknesses:

While I am broadly sympathetic to the overall narrative of the paper, I have some questions/comments around the specific interpretation of the results presented. In my view, the authors' claims may not be completely supported by their data, but the data are interesting nonetheless.

In terms of the framework presented by the authors for interpreting their data, many would argue that freezing (or at least reduced activity/behavioural inhibition) to the context provides a readout of conditioned anxiety rather than fear. In this sense, the context is a signal of potential threat (i.e. the context becomes associated with both shock and with the absence of shock) and thus generates anxiety rather than fear. Likewise, the trace CS cue could be considered as an ambiguous predictor of shock in that the shock doesn't occur straight away. In contrast, a punctate CS cue which co-terminates with shock would be a reliable signal of imminent threat and thus generates a fear response. Thus, it might be argued that all of the assays adopted by the authors are readouts of anxiety (albeit comprising tests of both conditioned and unconditioned anxiety). For example, from the authors' perspective, it is not clear a priori why the Vogel conflict test is considered anxiety, but contextual freezing is considered fear? Indeed, in the Discussion, the authors mention another study in which the data from the Vogel conflict test align with fear assays rather than anxiety tests. Can the authors elaborate on their distinction? I appreciate that, in practice, it might be difficult to distinguish between fear and anxiety at the behavioural level in rodents (although opposing effects of fear and anxiety on pain responses might be one option). At the very least, this issue merits further discussion.

Another question is whether rather than representing a qualitative difference between the contributions of the vCA3→vCA1 and EC→vCA1 pathways to different aspects of fear/anxiety behaviours, the different results reflect a quantitative difference between the magnitude of effects in vCA1 that are generated from optogenetic manipulation of the two pathways, coupled with the possibility that behaviour on the trace CS/context fear memory task is more sensitive to manipulation than the "anxiety tests". The possibility that vCA3→vCA1 stimulation is more effective is potentially supported by the c-fos measurements in vCA1. vCA3→vCA1 stimulation produced a much bigger vCA1 c-fos response (approx. 350% c-fos cell activation; see Figure 1E) compared to activation of the EC→vCA1 pathway (approx. 170% c-fos cell activation; see Figure 4E).

Furthermore, in some studies, there seem to be quite large differences between the laser OFF conditions for the different groups (which presumably one would not expect to be different). For example, compare laser OFF for the Inhibition group for time in open arms of EPM in Figure 5C (> 40%) versus laser OFF for the Inhibition group for time in open arms of EPM in Fig. 2C (< 20%). This could potentially result in ceiling effects, such that it is very hard to see a further increase in time in the open arms from a level already above 40% when the laser is then switched on. This could complicate the interpretation of the laser ON condition.

Likewise, there is a big difference between the behavioral performance of the two SHAM groups in Figure 3 (compare SHAM in 3 B, C and SHAM in 3 D, E). How is this explained? Could this generate a ceiling effect? This may also merit some discussion. More details on the SHAM procedure(s) in the main manuscript may also be helpful.

According to Figure 3A, the test of freezing response to the trace Tone CS is conducted in a different context from the conditioning context. The data presented in Figure 3 for tone fear are the levels of freezing during the presentation of this cue in the different contexts. It would be important to present both pre-CS and CS freezing levels here to determine how much of the freezing is actually driven by the punctate tone CS. The pre-CS freezing levels in this different context would also provide a nice control for the contextual fear conditioning.

Reviewer #3 (Public review):

Summary:

In their paper entitled "Ventral hippocampal temporoammonic and Schaffer collateral pathways differential control fear- and anxiety-related behaviors" the authors use a bidirectional optogenetic approach to elucidate the role of temporammonic (TA) and Schaffer collateral (SC) inputs to the ventral hippocampus (CA1) in modulating both fear and anxiety-related behaviors. While fear and anxiety behaviors are often considered on a continuous spectrum, identifying neural pathways that are differentially activated represents an important open question in the field. The authors find that optogenetic stimulation or inhibition of the Schaffer Collateral pathway in the ventral hippocampus (CA3-CA1) bidirectionally modulates both fear-related and anxiety-related behavioral paradigms. More specifically, optogenetic excitation of the CA3-CA1 pathway using ChR2-expressing viral constructs increases anxiety-like behaviors in numerous behavioral paradigms (elevated plus maze, open field, Vogel conflict test). Conversely, optogenetic inhibition using halorhodopsin reduced anxiety-like behaviours. To examine fear behaviors, the authors examined contextual and trace fear conditioning. Similar to their results with anxiety-like behaviors, the authors observed bidirectional fear modulation following optogenetic stimulation of the vCA3-vCA1 pathway. The authors next examined the temporammonic pathway originating from the lateral entorhinal cortex to vCA1. Unlike with SC stimulation, stimulation of the TA pathway had no effect on anxiety-like behaviors but did bidirectionally modulate contextual fear conditioning. Together, these results differentiate the SC and TA pathways in the ventral hippocampus as distinct regulators of affective behavior.

Strengths:

The paper has numerous technical strengths, including dissecting the role of both excitation and inhibition of both pathways and the use of behavioral measures of anxiety and fear. This balanced and internally controlled design allows readers to evaluate the effects of both pathways in a single study, thereby reducing technical complications from experiments being completed across laboratories and experimental conditions.

Weaknesses:

There are a few limitations of the study, however, which bear discussion.

(1) The authors use halorhodopsin to achieve optogenetic inhibition. Halorhodopsin is generally considered a first-generation optogenetic actuator, as it is a Cl- pump rather than an ion channel. This limits the degree of inhibition (i.e. by preventing shunting inhibition) and can result in altered chloride gradients in the period immediately following optogenetic stimulation. This is of particular concern in this paper as the stimulation parameters and behavioral analysis are not temporally correlated, therefore confounds of disrupted chloride cannot be experimentally accounted for or controlled.

(2) The authors use an AAV-CaMKII-eGFP as a control (Sham) throughout the dataset; however, in the trace fear conditioning experiments, there are no AAV-CaMKII-ChR2-eYFP or AAV-CaMKII-eNpHR3.0-eYFP controls without optogenetic stimulation. Therefore, it is unclear the extent to which viral expression of optogenetic actuators impacts behavior. Additionally, the authors only provided optogenetic stimulation during contextual fear recall and tone fear recall. Additional experiments disrupting each pathway during trace conditioning would have provided additional insight into the role of each pathway in the initial encoding of fear memories.

(3) The location and extent of viral expression across animals were not systematically quantified.

Overall, however, these weaknesses do not significantly detract from the main conclusions of the paper. The authors' data convincingly demonstrates that disruption of the trisynaptic circuit bidirectionally modulates both fear- and anxiety-like behaviors while disruption of the temporammonic pathway has no effect on anxiety-like behaviors but disrupts fear-related behaviors. It is interesting to note, however, that the TA activation had no effect on tone-related fear conditioning, suggesting a potential specialized role of the temporammonic pathway specifically in contextual fear memory.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

The hippocampus, especially the ventral subregion, has been related to emotional processing. However, the specific circuitry involved deserves further investigation. By using a bidirectional optogenetic modulation, Kambali et al. have investigated the role of different inputs to vCA1 (i.e., from vCA3 and entorhinal cortex) in anxiety- and fear-related responses. The major findings of this work suggested that both inputs to vCA1 control fear-related responses, whereas only the projection between vCA3 and vCA1 controls anxiety-related behavior. Overall, the authors used an advanced methodological approach, which allows them to modulate specific brain circuits, to study specific hippocampal projections, providing some new information regarding the hippocampal function in anxiety and fear.

Strengths:

(1) The manuscript is well written, clear and has a detailed and specific discussion.

(2) Results from each optogenetic manipulation are clear in different anxiety- and fear-related tasks, demonstrating the robustness of the findings.

(3) The overall conclusions are very interesting and might be relevant for the field of mental health disorders accompanied by anxiety- and fear-related alterations.

Weaknesses:

(1) The major differences in basal behavioral performance in the different paradigms between the two optogenetic modulations prevent the achievement of strong conclusive results.

The two projections of ventral CA1 were studied independently in different cohorts of animals tested at different times during the study. This difference in timing may have contributed to variations in the basal behavioral performance between the two projections. Importantly we found that within each cohort – control and optogenetic manipulation, the basal performance within each set of experiments (i.e., corresponding to projections) is highly consistent, e.g., basal cued and contextual freezing responses and responses to OFF conditions in Vogel conflict test. Moreover, the ANOVA statistics conducted across the baseline and ON conditions for each task revealed robust significant effects of bidirectional optogenetic modulation for each cohort. In case of the fear responses, a point to note is that the freezing levels in SHAM controls differ between projections but are consistent between two types of assessments (tone and context) within each projection. We will mention these limitations in the revised manuscript.

(2) Data presentation and representative figures need a major revision.

The figures will be rearranged according to the projections. The anxiety-related figures and fear response related figures will be grouped for each projection to improve clarity and readability. The revised manuscript will include representative heat maps for each behavioral task for both projections in addition to population quantification data.

(3) No analysis has been performed to analyze potential sex differences in behavioral domains where sex is important.

This assessment was not done in the original submission. We will perform statistical analysis for male and female mice separately and if the results are sex-dependent, we will present separate figures. Otherwise, the combined data presentation will be followed.

Reviewer #2 (Public review):

Summary:

This paper uses an optogenetic approach to either activate or inhibit separate neural pathways projecting to the ventral CA1 hippocampal subregion, from either CA3 or the entorhinal cortex. The authors report that manipulation of the vCA3→vCA1 pathway affected behavioural performance on a number of tasks: elevated plus maze, open field, Vogel conflict test and freezing behaviour to both context and a trace CS cue. In contrast, optogenetic manipulation of neural activity in the EC→vCA1 pathway only affected behaviour on the trace CS/context fear memory test but had no effect on the elevated plus maze, open field or Vogel conflict test. The authors suggest different roles for these two ventral hippocampal pathways in fear versus anxiety.

Strengths:

This is an interesting study addressing an important question in a highly topical subject area. The experiments are well conducted and have generated interesting and important data.

Weaknesses:

While I am broadly sympathetic to the overall narrative of the paper, I have some questions/comments around the specific interpretation of the results presented. In my view, the authors' claims may not be completely supported by their data, but the data are interesting nonetheless.

In terms of the framework presented by the authors for interpreting their data, many would argue that freezing (or at least reduced activity/behavioural inhibition) to the context provides a readout of conditioned anxiety rather than fear. In this sense, the context is a signal of potential threat (i.e. the context becomes associated with both shock and with the absence of shock) and thus generates anxiety rather than fear. Likewise, the trace CS cue could be considered as an ambiguous predictor of shock in that the shock doesn't occur straight away.

In contrast, a punctate CS cue which co-terminates with shock would be a reliable signal of imminent threat and thus generates a fear response. Thus, it might be argued that all of the assays adopted by the authors are readouts of anxiety (albeit comprising tests of both conditioned and unconditioned anxiety).

We agree with the reviewer that context and trace fear conditioning do not represent an “imminent” threat as severe as would likely be internalized in delay fear conditioning. However, the goal of the study was to probe hippocampal dependent processes (contextual and trace fear conditioning are strongly modulated by the hippocampus while delay conditioning is not). Consistent with several other studies, we believe the conditional nature of the task (context and trace are invariably linked to shock) provides support for a “non-ambiguous” relationship that is conducive for measuring the assessment of fear-based behavior.

Several studies show clear differences in the involvement of amygdala and hippocampus in delay vs. trace fear conditioning. Inactivating amygdala led to deficits in contextual and delay conditioning but had no effect on trace conditioning. In contrast, inactivating hippocampus led to deficits in trace and contextual but not delay fear conditioning. These findings suggest that a temporal gap between the CS and US can generate amygdala-independent but hippocampal-dependent fear conditioning (Raybuck J. D., Lattal K. M 2011, PMID: 21283812). Lesions of the entorhinal cortex impair the acquisition of trace fear conditioning but not the acquisition of delay fear conditioning (Raybuck J. D., Lattal K. M 2011, PMID: 21283812) . Further, using single unit recording during fear retention tests after delay or trace fear conditioning, the study showed that entorhinal neurons specifically respond after trace but not after delay fear conditioning (Kong et al 2023, PMID: 36919333). These findings demonstrate that trace fear conditioning and delay fear conditioning may involve overlapping but largely different neuronal circuits. A knockdown of the expression of the α5-subunit–containing GABA_𝐴 receptors in the CA1 region (α5CA1KO mice) leads to improved spatial learning and enhanced trace fear conditioning memory, actually to the level of delay fear conditioning, suggesting that α5GABA_𝐴Rs in CA1 pyramidal neurons normally constrain hippocampus-dependent memory processes and that trace fear conditioning in the absence of a5-GABA_𝐴 receptors in CA1 has the same effect size as delay fear conditioning (Engin et al 2020, PMID: 32934095), supporting the view that trace fear conditioning is not “ambiguous”.

For example, from the authors' perspective, it is not clear a priori why the Vogel conflict test is considered anxiety, but contextual freezing is considered fear? Indeed, in the Discussion, the authors mention another study in which the data from the Vogel conflict test align with fear assays rather than anxiety tests. Can the authors elaborate on their distinction? I appreciate that, in practice, it might be difficult to distinguish between fear and anxiety at the behavioral level in rodents (although opposing effects of fear and anxiety on pain responses might be one option). At the very least, this issue merits further discussion.

We will make this distinction clearer in the revisions. Briefly, behavioral actions in the Vogel conflict test are generally considered to be most pertinent to general anxiety disorders in humans and anxiolytics have high predictive validity in animals in this task. In particular, the robust actions of benzodiazepines and 5-HT_1A partial agonists parallel their clinical efficacy in patients (McMillan and Brocco, 2003, PMID: 12600703).

Our previous study (Engin et al 2016, PMID: 26971710) used global diazepam-induced neuronal inhibition and identified that positive modulation of α2-GABA_𝐴Rs in dentate gyrus granule cells and CA3 pyramidal neurons is required to reduce anxiety-like behaviors while inhibition of positive modulation of α2-GABA_𝐴Rs in CA1 pyramidal neurons is required to reduce fear-related behaviors. The effects were absent when α2-GABA_𝐴Rs was knocked out in the respective subregions. These results indicate that these intrahippocampal subregions can modulate fear and anxiety-like behaviors independently of the amygdala. In the previous study we used conditional α2-GABA_𝐴R knockouts in hippocampal subregions and subjected these mice to systemic diazepam. In these experiments, diazepam still acts on α1-, α3- and α5-_𝐴Rs in the hippocampal subregions and cell types in which when α2-GABA_𝐴Rs are lacking. Therefore, for example when α2CA1KO mice were administered diazepam, diazepam still led to inhibition of pyramidal neurons in CA3 and DG via α1-, α2-, α3- and α5- GABA_𝐴Rs, and in addition, diazepam also inhibited α1-, α3- and α5- GABA_𝐴Rs in CA1 itself. Diazepam also acted on GABA_𝐴Rs in amygdala or other brain regions. These are fundamentally different experimental conditions compared to the optogenetic experiment described in this paper. Moreover, in contrast to the current paper, the previous work did not examine projections but used global diazepam-induced neuronal inhibition as a baseline. Moreover, whereas the previous paper examined whether a specific neuronal cell type was required for anxiolytic-like or fear-like actions, the current manuscript examined whether activation or inhibition of neuronal projections is sufficient to modulate anxiety- and fear-related behaviors. Overall, one cannot easily compare the results in the Vogel conflict test in both papers.

Another question is whether rather than representing a qualitative difference between the contributions of the vCA3→vCA1 and EC→vCA1 pathways to different aspects of fear/anxiety behaviours, the different results reflect a quantitative difference between the magnitude of effects in vCA1 that are generated from optogenetic manipulation of the two pathways, coupled with the possibility that behaviour on the trace CS/context fear memory task is more sensitive to manipulation than the "anxiety tests". The possibility that vCA3→vCA1 stimulation is more effective is potentially supported by the c-fos measurements in vCA1. vCA3→vCA1 stimulation produced a much bigger vCA1 c-fos response (approx. 350% c-fos cell activation; see Figure 1E) compared to activation of the EC→vCA1 pathway (approx. 170% c-fos cell activation; see Figure 4E).

Furthermore, in some studies, there seem to be quite large differences between the laser OFF conditions for the different groups (which presumably one would not expect to be different). For example, compare laser OFF for the Inhibition group for time in open arms of EPM in Figure 5C (> 40%) versus laser OFF for the Inhibition group for time in open arms of EPM in Fig. 2C (< 20%). This could potentially result in ceiling effects, such that it is very hard to see a further increase in time in the open arms from a level already above 40% when the laser is then switched on. This could complicate the interpretation of the laser ON condition.

The magnitude of activation as evidenced by c-fos measurements differs between the two projections. This might reflect different levels of modulations of CA1 neuronal activity. The fact that the two projections were studied at different time points (see response to reviewer 1) may also have contributed to the difference. The revised manuscript will include a formal discussion about magnitude of modulation that could contribute to differential sensitivity for the modulation of anxiety-like behaviors. However, the inputs from these two projections systems target different regions of CA1 pyramidal neurons and each pathway has distinct roles in other processes (sensory versus memory-based completion) – thus a dissociation may also be present for other types of behavior as well including the modulation of anxiety-like behaviors.

While it is possible that ceiling effects could impact our interpretation, we believe ceiling effects would only impact one direction of the optogenetic manipulation and there was no effect of activation (Fig. 5C) or bidirectional modulation of anxiety-related behavior in the novel open field test (Fig. 5F) which has levels of behavior comparable to Figure 2F.

Likewise, there is a big difference between the behavioral performance of the two SHAM groups in Figure 3 (compare SHAM in 3 B, C and SHAM in 3 D, E). How is this explained? Could this generate a ceiling effect? This may also merit some discussion. More details on the SHAM procedure(s) in the main manuscript may also be helpful.

With respect to contextual fear, ceiling effects are not a major factor as we still see enhanced freezing in the activation condition. With tone fear, we cannot formally exclude a ceiling effect, and this will be addressed as a potential confound in the manuscript.

According to Figure 3A, the test of freezing response to the trace Tone CS is conducted in a different context from the conditioning context. The data presented in Figure 3 for tone fear are the levels of freezing during the presentation of this cue in different contexts. It would be important to present both pre-CS and CS freezing levels here to determine how much of the freezing is actually driven by the punctate tone CS. The pre-CS freezing levels in this different context would also provide a nice control for the contextual fear conditioning.

We agree and will analyze and report the pre-CS freezing data in the revision.

Reviewer #3 (Public review):

Summary:

In their paper entitled "Ventral hippocampal temporoammonic and Schaffer collateral pathways differential control fear- and anxiety-related behaviors" the authors use a bidirectional optogenetic approach to elucidate the role of temporammonic (TA) and Schaffer collateral (SC) inputs to the ventral hippocampus (CA1) in modulating both fear and anxiety-related behaviors. While fear and anxiety behaviors are often considered on a continuous spectrum, identifying neural pathways that are differentially activated represents an important open question in the field. The authors find that optogenetic stimulation or inhibition of the Schaffer Collateral pathway in the ventral hippocampus (CA3-CA1) bidirectionally modulates both fear-related and anxiety-related behavioral paradigms. More specifically, optogenetic excitation of the CA3-CA1 pathway using ChR2-expressing viral constructs increases anxiety-like behaviors in numerous behavioral paradigms (elevated plus maze, open field, Vogel conflict test). Conversely, optogenetic inhibition using halorhodopsin reduced anxiety-like behaviours. To examine fear behaviors, the authors examined contextual and trace fear conditioning. Similar to their results with anxiety-like behaviors, the authors observed bidirectional fear modulation following optogenetic stimulation of the vCA3-vCA1 pathway. The authors next examined the temporammonic pathway originating from the lateral entorhinal cortex to vCA1. Unlike with SC stimulation, stimulation of the TA pathway had no effect on anxiety-like behaviors but did bidirectionally modulate contextual fear conditioning. Together, these results differentiate the SC and TA pathways in the ventral hippocampus as distinct regulators of affective behavior.

Strengths:

The paper has numerous technical strengths, including dissecting the role of both excitation and inhibition of both pathways and the use of behavioral measures of anxiety and fear. This balanced and internally controlled design allows readers to evaluate the effects of both pathways in a single study, thereby reducing technical complications from experiments being completed across laboratories and experimental conditions.

Weaknesses:

There are a few limitations of the study, however, which bear discussion.

(1) The authors use halorhodopsin to achieve optogenetic inhibition. Halorhodopsin is generally considered a first-generation optogenetic actuator, as it is a Cl- pump rather than an ion channel. This limits the degree of inhibition (i.e. by preventing shunting inhibition) and can result in altered chloride gradients in the period immediately following optogenetic stimulation. This is of particular concern in this paper as the stimulation parameters and behavioral analysis are not temporally correlated, therefore confounds of disrupted chloride cannot be experimentally accounted for or controlled.

Choice of halorhodopsin was in part influenced by a report that spontaneous archaerhodopsin activation was paradoxically associated with increased spontaneous release of neurotransmitter from presynaptic terminals, whereas activation of chloride-reducing halorhodopsin triggered neurotransmitter release upon light onset (Mahn et al., PMID: 26950004), suggesting that halorhodospin may be advantageous in studies inhibiting presynaptic nerve terminals. Halorhodpsin has been used in several studies to effectively silence activity and had substantial influence on behavioral in our studies that was inversely proportional to ChR2 stimulation. While perhaps not optimal out of an abundance of caution, we chose it over Archaerhodopsin based on the cited literature.

(2) The authors use an AAV-CaMKII-eGFP as a control (Sham) throughout the dataset; however, in the trace fear conditioning experiments, there are no AAV-CaMKII-ChR2-eYFP or AAV-CaMKII-eNpHR3.0-eYFP controls without optogenetic stimulation. Therefore, it is unclear the extent to which viral expression of optogenetic actuators impacts behavior. Additionally, the authors only provided optogenetic stimulation during contextual fear recall and tone fear recall. Additional experiments disrupting each pathway during trace conditioning would have provided additional insight into the role of each pathway in the initial encoding of fear memories.

Thank you for your observation. We have used a SHAM control that was injected with the AAV vector without any opsins. In fear conditioning experiments we performed optogenetic manipulations only during the fear response either with context or cue recall. This aligned well with our hypothesis to test whether the intrahippocampal projections play any role in fear response modulation. Investigating the role of each pathway during acquisition of trace and/or contextual fear conditioning is also highly relevant; however, evaluating these projections in fear memory formation was beyond the scope of this study. The observation that we can bidirectionally modulate fear responses with light is consistent with (although it does not prove) a light-specific modulation. In any case, even if there were baseline effects without light, they would still be suggestive of the effects observed being mediated by the optogenetic actuators.

(3) The location and extent of viral expression across animals were not systematically quantified.Overall, however, these weaknesses do not significantly detract from the main conclusions of the paper. The authors' data convincingly demonstrates that disruption of the trisynaptic circuit bidirectionally modulates both fear- and anxiety-like behaviors while disruption of the temporammonic pathway has no effect on anxiety-like behaviors but disrupts fear-related behaviors. It is interesting to note, however, that the TA activation had no effect on tone-related fear conditioning, suggesting a potential specialized role of the temporammonic pathway specifically in contextual fear memory.

Thank you for your thoughtful description of the present study. It is true that TA pathway is distinct from vCA3 to vCA1 pathway in various ways, one being the synapse formation of these two projections are at different locations or layers on vCA1 neurons i.e., the TA pathway synapses on the stratum lacunosum-moleculare (LMol) layer while the vCA3 to vCA1 pathway synapses at stratum radiatum (Rad), close to the CA1 pyramidal cell layer, which is in line with differential functions of the two projections They modulate the pyramidal cell activity in a different way, with TA pathway synapses being distinct from vCA3 to vCA1 synapses on the pyramidal cell layer, which may result in different computational properties of the two projections. Additionally, TA projections are modulated by dopamine while projections from vCA3 are not, but the projections from vCA3 receive inputs from various sources including collaterals, and entorhinal via dentate gyrus. These distinct features of the two projections may contribute to differential modulation of vCA1 activity. We note that cue-related fear is not affected by the TA activation, however even in this case, the TA pathway activation by channelrhodopsin or inhibition by halorhodopsin results in a decrease or an increase of the contextual fear response, respectively.

eLife Assessment

This study provides valuable insights into the regulation of myogenic differentiation by identifying Leiomodin 1 as a modulator of proteome dynamics during myogenic differentiation. The combination of quantitative proteomics with functional perturbation experiments offers solid evidence supporting the idea that SIRT1 influences perturbations of myogenic differentiation upon LMOD1 inactivation. These findings advance our understanding of muscle differentiation and will be of interest to researchers studying muscle development and related pathologies

Reviewer #1 (Public review):

The main significance of this work is characterizing the function of a new gene Lmod1 in muscle stem cell biology. The study suggests an intriguing regulatory mechanism by which Sirt1 sequesters Lmod1 in a specific temporal window during myogenesis.

Comments on revisions:

The authors have satisfactorily addressed my inquires. Thank you.

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors identify Leiomodin-1 (LMOD1) as a key regulator of early myogenic differentiation, demonstrating its interaction with SIRT1 to influence SIRT1's cellular localization and gene expression. The authors propose that LMOD1 translocates SIRT1 from the nucleus to the cytoplasm to permit the expression of myogenic differentiating genes such as MYOD or Myogenin.

Strengths:

A major strength of this work lies in the robust temporal resolution achieved through a time-course mass spectrometry analysis of in vitro muscle differentiation. This provides novel insights into the dynamic process of myogenic differentiation, often under explored in terms of temporal progression. The authors provide a strong mechanistic case for how LMOD1 exerts its role on muscle differentiation which opens avenues to modulate.

Weaknesses:

In the revised manuscript, the authors begin to translate their in vitro findings to an in vivo context by examining SIRT1 expression across a regeneration time course (Fig. 4I). They observe an increase in SIRT1 expression concomitant with LMOD1, supporting a potential role for SIRT1 in myogenic differentiation. Future studies will be required to provide deeper mechanistic insight into SIRT1 function in vivo.

Discussion:

Overall, the study emphasizes the importance of understanding the temporal dynamics of molecular players during myogenic differentiation and provides valuable proteomic data that will benefit the field. Future studies should explore whether LMOD1 modulates the nuclear-cytoplasmic shuttling of other transcription factors during muscle development and how these processes are mechanistically achieved. Investigating whether LMOD1 can be therapeutically targeted to enhance muscle regeneration in contexts such as exercise, aging, and disease will be critical for translational applications. Additionally, elucidating the interplay among LMOD1, LMOD2, and LMOD3 could uncover broader implications for actin cytoskeletal regulation in muscle biology. The authors have nicely updated their discussion.

Reviewer #3 (Public review):

Summary:

In this manuscript, the investigators identified LMOD1 as one of a subset of cytoskeletal proteins that levels increase in early stages of myogenic differentiation. Lmod1 is understudied in striated muscle and in particular in myogenic differentiation. Thus, this is an important study. It is also a very thorough study, with perhaps even too much data presented. Importantly, the investigators observed that LMOD1 appears to be important for skeletal regeneration, myogenic differentiation and that it interacts with SIRT1. Both primary myoblast differentiation and skeletal muscle regeneration were studied. Rescue experiments confirmed these observations: SIRT1 can rescue perturbations of myogenic differentiation as a result of LMOD1 knockdown.

Strengths:

Particular strengths include: an important topic, the use of primary skeletal cultures, the use of both cell culture and in vivo approaches, careful biomarker analysis of primary mouse myoblast differentiation, the use of two methods to probe the function of the Lmod1/SIRT1 pathway via using depletion approaches and inhibitors, and the generation of six independent myoblast cultures. Results support their conclusions.

Weaknesses:

(1) Figure 1. Images of cells in Figure 1A are too small to be meaningful (especially in comparison to the other data presented in this figure). Perhaps make graphs smaller?

(2) Line 148 "We found LMOD2 to be the most abundant Lmod in whole skeletal muscle." This is confusing since most, if not all, prior studies have shown that Lmod3 is the predominant isoform in skeletal muscle. The two papers that are cited are incorrectly cited. Clarification to resolve this discrepancy is needed.

(3) Figure 2. Immunofluorescence (IF) panels are too small to be meaningful. Perhaps the graphs could be made smaller and more space allocated for the IF panels? This issue is apparent for just about all IF panels - they are simply too small to be meaningful. Additionally, in many of the immunofluorescence figures, the colors that were used make it difficult to discern the stained cellular structures. For example, in Figure S1, orange and purple are used - they do not stand out as well as other colors that are more commonly used.

(4) There is huge variability in many experiments presented - as such, more samples appear to be required to allow for meaningful data to be obtained. For example, Figure S2. Many experimental groups, only have 3 samples - this is highly problematic - I would estimate that 5-6 would be the minimum.

(5) Ponceau S staining is often used as a loading control in this manuscript for western blots. The area/molecular weight range actually used should be specified. Not clear why in some experiments GAPDH staining is used, in other experiments Ponceau S staining is used, and in some, both are used. In some experiments the variability of total protein loaded from lane-to-lane is disconcerting. For example, in Figure S4C there appears to be more than normal variability. Can the protein assay be redone and the samples run again?

(6) Figure S3 - Lmod3 is included in the figure but no mention of it occurs in the title of the figure and/or legend.

(7) Abstract, line 25. "overexpression accelerates and improves the formation of myotubes". This is a confusing sentence. How is it improving the formation? A little more information about how they are different than developing myotubes in normal/healthy muscle would be helpful

(8) Impossible from IF figures presented to determine where Lmod1 localizes in the myocytes. Information on its subcellular localization is important. Does it localize with Lmod2 and Lmod3 at thin filament pointed ends?

Comments on revisions:

Many comments have been adequately addressed. However, some concerns remain.

Former Concern #2. The issue with the lack of detection of LMOD3 in their muscle samples is troublesome and has not been adequately resolved in the revised manuscript. It is a fact that most, if not all, studies on Lmod3 report that it is the most abundant isoform in skeletal muscle. This issue should be discussed in the manuscript. It is recognized that a different assay was utilized in this paper. The papers that are cited continue to remain incorrect. Specifically:

Tsukada et al., reports abundance of LMOD2 in cardiac muscle, not in skeletal muscle.

Nworu et al., 2015 reports on LMOD3 in skeletal muscle.

Kiss et al.,2020. While this paper reveals an important function for Lmod2 in thin filament length regulation, it is clearly shows many examples of high expression of Lmod3 in various skeletal muscles isolated from mice.

Former Concern #3. With respect to small sample numbers. Hopefully a statistical editor is available to comment. While this reviewer is happy that other assays were used to verify their data, the problem still remains that many experimental groups only have 3 samples (with high variability).

Former Concern #3. Many immunofluorescence panels are hard to evaluate because of their small size.

Author response:

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

eLife Assessment

This valuable study offers insights into the role of Leiomodin-1 (LMOD1) in muscle stem cell biology, advancing our understanding of myogenic differentiation and indicating LMOD1 as a regulator of muscle regeneration, aging, and exercise adaptation. The integration of in vitro and in vivo approaches, complemented by proteomic and imaging methodologies, is solid. However, certain aspects require further attention to improve the clarity, impact, and overall significance of the work, particularly in substantiating the in vivo relevance. This work will provide a starting point that will be of value to medical biologists and biochemists working on LMOD and its variants in muscle biology.

Thank you for the positive feedback on our manuscript and the constructive criticism provided by the reviewers that helped us improve our manuscript.

Public Reviews:

Reviewer #1 (Public review):

This manuscript by Ori and colleagues investigates the role of Lmod1 in muscle stem cell activation and differentiation. The study begins with a time-course mass spectrometry analysis of primary muscle stem cells, identifying Lmod1 as a pro-myogenic candidate (Figure 1). While the initial approach is robust, the subsequent characterization lacks depth and clarity. Although the data suggest that Lmod1 promotes myogenesis, the underlying mechanisms remain vague, and key experiments are missing. Please find my comments below.

We thank the reviewer for the positive feedback on our manuscript and the helpful comments, which helped improve it.

(1) The authors mainly rely on coarse and less-established readouts such as myotube length and spherical Myh-positive cells. More comprehensive and standard analyses, such as co-staining for Pax7, MyoD, and Myogenin, would allow quantification of quiescent, activated, and differentiating stem cells in knockdown and overexpression experiments. The exact stage at which Lmod1 functions (stem cell, progenitor, or post-fusion) is unclear due to the limited depth of the analysis. Performing similar experiments on cultured single EDL fibers would add valuable insights.

We thank the reviewer for this comment. In addition to performing standard measurements such as staining for Myogenin and Myosin Heavy Chain (Figure S2H), we focused on morphological readouts, such as myotube formation, because LMOD1 is an actin cytoskeleton-associated protein. Therefore, we reasoned its function would be most directly reflected in structural changes during differentiation, rather than solely in early transcriptional markers. 

Regarding the use of standard markers, we have already performed co-staining for Myogenin and Myosin Heavy Chain (MHC), which effectively quantifies early myogenic committed (Myogenin+/MHC-) and terminally differentiating (Myogenin+/MHC+) cells (Figure S2H). We did not include Pax7 as our primary culture system consists of already activated myoblasts, where Pax7 is not a reliable marker of quiescence. Our data also suggest that Lmod1 is important in regulating differentiation with comparably only mild effects on proliferation (S2D-E), therefore, we focused on this stage of myogenesis.

Our focus on differentiation over activation is further supported by multiple lines of evidence. First, analysis of publicly available transcriptome datasets reveals that Lmod1 mRNA levels actually decrease upon Muscle Stem Cell (MuSC) activation, suggesting its primary role is not during this initial phase. We added this data for clarification to Figure S1B. This aligns perfectly with our in vivo data from cardiotoxin-induced muscle regeneration, where abundance of LMOD1 protein peaks at days 4-7 post-injury — a time point coinciding with new myofiber formation and maturation — rather than during the initial activation and proliferation phase (days 1-3) (Figure 4I).

Given this strong evidence pointing to a primary role for LMOD1 during the later stages of differentiation, we believe our current analyses are the most relevant. While single EDL fiber cultures are valuable for studying the quiescence-to-activation transition, they would not provide significant additional insight into the specific differentiation-centric mechanism we are investigating here. We are confident that our chosen readouts appropriately address Lmod1's function in the differentiation of myoblasts and formation of myotubes.

(2) In supplementary Figure 2E, the distinction between Hoechst-positive cells and total cell counts is unclear. The authors should clarify why Hoechst-positive cells increase and relabel "reserve cells," as the term is confusing without reading the legend.

We thank the reviewer for pointing out the confusion regarding the naming of the cell populations and the increase in Hoechst-positive cells. We have now modified this and revised the terminology used in Figure S2E to improve clarity. Specifically, we have relabeled "reserve cells" as "non-proliferating myoblasts (Ki67-/Hoechst+)" to describe these cells more accurately without requiring the legend for interpretation. Regarding the increase in Hoechst-positive cells, we observed a slight (26%) but significant decrease in the number of proliferating myoblasts (Ki67+/Hoechst+) (Figures S2D and S2E). The relative increase in non-proliferating (Ki67-/Hoechst+) cells is a consequence of the significant reduction in the number of proliferating cells (Ki67+/Hoechst+) cells. Importantly, the total cell count (sum of Ki67-/Hoechst+) and (Ki67+/Hoechst+) remained stable. This has been clarified in the revised figure legend and main text as follows:

“This was accompanied by a proportional increase in non-proliferating myoblasts (Ki67-/Hoechst+), while the total Hoechst-positive cell count (Ki67+/Hoechst+ and Ki67-/Hoechst+) remained unchanged (Figure S2E).”

(3) The specificity of Lmod1 and Sirt1 immunostaining needs validation using siRNA-treated samples, especially as these data form the basis of the mechanistic conclusions.

We have validated the specificity of the LMOD1 antibody using multiple approaches. Specifically, we performed immunofluorescence and immunoblotting on Lmod1 siRNA-transfected samples, where we observed a significant reduction in the Lmod1 protein signal compared to control conditions (see manuscript data from Figure S2G).

Additionally, LMOD1 overexpression experiments demonstrated a corresponding increase in the signal for LMOD1 using immunofluorescence analyses, confirming the specificity of the antibody for detecting LMOD1.

For the reviewers’ interest, we add Author response image 1:

Author response image 1.

Specificity of antibodies detecting LMOD1. Representative immunofluorescence images of LMOD1 in primary myoblast cultures following siLmod1 knockdown, LMOD1 overexpression, or controls transfected with a non-targeting siRNA (siCtrl) after one day of differentiation. LMOD1 (purple), SIRT1 (yellow), and nuclei (Hoechst, blue). Scale bar: 10 µm.

For the SIRT1 antibody used in our immunostaining, the specificity was validated by transfecting primary myoblasts with siRNA targeting Sirt1 and performing immunoblot analyses (Figure S5A). These showed a significant reduction in SIRT1 protein levels, confirming both the effectiveness of the siRNA and, critically, the antibody's ability to specifically recognize and detect SIRT1 protein. Furthermore, the same SIRT1 antibody was utilized in our nuclear-cytoplasmic fractionation experiments (Figure S4C), and its ability to detect SIRT1 in the expected subcellular compartments further supports its specific binding to SIRT1. While direct immunofluorescence on Sirt1 siRNA-transfected samples was not performed, the robust demonstration of the antibody's specificity for Sirt1 protein via immunoblotting (i.e., correct molecular weight band, significantly reduced by Sirt1 siRNA) and its distribution in subcellular fractions, which is fully consistent with the localization immunostaining performed at the same time points (compare Figure S4C and 5A), provide strong evidence on the antibody’s specificity, also in immunofluorescence experiments.

(4) The authors must test the effect of Lmod1 siRNA on Sirt1 localization, as only overexpression experiments are shown

We carefully considered performing this experiment. However, the knockdown of Lmod1 significantly impairs myogenic differentiation, a crucial cellular process that itself can influence protein localization. Consequently, if SIRT1 localization would be altered following knockdown of Lmod1, it would be challenging to disentangle whether this was a direct result of LMOD1 absence impacting SIRT1 trafficking or an indirect consequence of the cells failing to differentiate properly. This would make it difficult to draw clear conclusions regarding a direct causal link between LMOD1 and SIRT1 localization from such an experiment. Therefore, we focused on overexpression experiments, where we could demonstrate that altering LMOD1 levels is sufficient to affect SIRT1 localization. Our nuclear-cytoplasmic fractionation experiments clearly show that LMOD1 overexpression leads to changes in SIRT1 distribution (Figure 5H-K). These findings provide evidence that LMOD1 can directly modulate SIRT1 localization, supporting our mechanistic conclusions.

(5) In Figure S3, the biotin signal in LMOD2 samples appears weak. The authors need to address whether comparing LMOD1 and LMOD2 is valid given the apparent difference in reaction efficiency. It would also help to highlight where Sirt1 falls on the volcano plot in S3B.

We agree that the overall biotin signal on the streptavidin blot for the LMOD2-BirA* sample appears weaker than for LMOD1-BirA*. To provide a more direct comparison of the bait proteins themselves, we have now added a bar graph to the revised Figure S3D, which quantifies the relative abundance of LMOD1 and LMOD2 bait proteins in the pull down experiments. This analysis shows that the levels of LMOD1-BirA* and LMOD2-BirA* were comparable in our BioID samples. Furthermore, the validity of the LMOD2 BioID experiment is strongly supported by the identification of several known LMOD1 and LMOD2 interaction partners. As shown in the dataset, well-established interactors such as TMOD1, TPM3, and TMOD3 were identified, with some even showing stronger enrichment with LMOD2 than with LMOD1. This confirms that the biotinylation reaction was efficient enough to capture proximal proteins for both baits.

Regarding SIRT1, we have now highlighted in yellow its position on the volcano plot in the revised Figure S3E. As can be seen, SIRT1 was identified in the LMOD1-BirA sample and showed enrichment. We believe these clarifications, along with the additional expression data and the successful identification of known interactors, confirm the validity of our comparative BioID analysis.

(6) The immunostaining data suggest that Lmod1 remains cytoplasmic throughout differentiation, whereas Sirt1 shows transient cytoplasmic localization at day 1 of differentiation. The authors should explain why Sirt1 is not constantly sequestered if Lmod1's cytoplasmic localization is consistent. It is also unclear whether day 1 is the key time point for Lmod1 function, as its precise role during myogenesis remains ambiguous.

We thank the reviewer for this comment. We have no data explaining why SIRT1 is not constantly sequestered while LMOD1 remains consistently cytoplasmic. We can only speculate that the transient cytoplasmic localization of SIRT1 may be linked to the availability and functional role of LMOD1 throughout the differentiation process. While LMOD1 is present at low levels in proliferating primary myoblasts, its expression increases upon the initiation of differentiation (Figure 2A). Initially, during the early stages of differentiation, LMOD1 may not be required for actin nucleation as the major remodeling of the cytoskeleton has not yet begun. During this phase, LMOD1 might have the capacity to sequester SIRT1 in the cytoplasm.

However, as differentiation progresses and morphological changes take place, LMOD1 may switch its functional role to actin nucleation, thereby releasing SIRT1. This transition could explain why SIRT1 is free to localize transiently to the cytoplasm, particularly at day 1, when cytoskeletal remodeling is beginning but not yet fully established.

Additionally, as LMOD1 and SIRT1 are known to colocalize in the nucleus, they may exit the nucleus together. Once in the cytoplasm, LMOD1 may become engaged in actin nucleation, allowing SIRT1 to function independently, which could explain the transient nature of SIRT1’s cytoplasmic localization.

We have acknowledged this gap in our understanding in the discussion of the revised manuscript:

“Our immunostaining data show that while LMOD1 is consistently cytoplasmic, its partner SIRT1 is only transiently localized in the cytoplasm. This suggests that their interaction is dynamically regulated. We hypothesize that the function of LMOD1 is determined by the changing availability of its binding partners during differentiation. During the initial phase, LMOD1 may primarily function to sequester SIRT1, a key regulator of myogenic genes. As differentiation proceeds, the increased expression of cytoskeletal components, such as its canonical partners TMODs and TPMs, likely shifts the function of LMOD1 towards its role in actin nucleation. This molecular switch, potentially driven by a change in the interactome of LMOD1, could then result in the release of SIRT1 from the cytoplasm. Such a mechanism may coordinate transcriptional regulation with cytoskeletal remodeling during myoblast differentiation.”

(7) The introduction does not sufficiently establish the motivation or knowledge gap this work aims to address. Instead, it reads like a narration of disparate topics in a single paragraph. The authors should clarify the statement in line 150, "since this protein has been...,".

We thank the reviewer for requesting clarification regarding our focus on LMOD1 (Introduction and Line 150 in the original submission). In the revised manuscript, we shortened the introduction and more clearly emphasized the motivation of our study:

“Although these mechanisms contribute to remodeling the cellular architecture of MuSCs, a comprehensive understanding of the temporal dynamics of proteome remodeling during differentiation remains lacking. To address this knowledge gap, we performed an unbiased proteomic analysis of the early stages of myogenic differentiation to identify previously unrecognized proteins involved in this process and to examine how they functionally interact with established regulatory pathways.”

Our decision to focus on LMOD1 was driven by its significant upregulation in our temporal proteome dataset, together with its previously uncharacterized role in primary myoblasts. Furthermore, to strengthen the interpretation of LMOD1’s role, particularly in the context of aging, we have integrated a new analysis of published transcriptomic datasets. This can be found in the main text as follows:

“Surprisingly, we detected LMOD1 in freshly isolated muscle stem cells (MuSCs), but not LMOD2. Additionally, we observed that the protein levels of LMOD1 increased in MuSCs isolated from older mice (Figure 2C and Figure S1B). We further analyzed published transcriptomic data sets that describe changes between young and old MuSCs in both quiescent and activated states in young and old animals (Liu et al. 2013; Lukjanenko et al. 2016). In these analyzed transcriptomic data sets, Lmod1 was found to be significantly downregulated during the activation of MuSCs in both young and old mice (see Figure S1B).

To assess the in vivo relevance of our finding, we queried two proteomic datasets of freshly isolated MuSCs and four different skeletal muscles (gastrocnemius, G; soleus, S; tibialis anterior, TA; extensor digitorum longus, EDL) (Schüler et al. 2021). We found LMOD2 to be the most abundant leiomodin protein in whole skeletal muscle, consistent with data from (Tsukada et al. 2010; Nworu et al. 2015; Kiss et al. 2020), while the overall abundance of LMOD1 was lower since this protein has been mainly associated with smooth muscle cells (Nanda and Miano 2012; Conley et al. 2001; Nanda et al. 2018) (Figure 2B).”

Overall, while the identification of Lmod1 as a pro-myogenic factor is convincing, the mechanistic insights are insufficient, and the manuscript would benefit from addressing these concerns.

We thank the reviewer for their constructive criticism. In the revised manuscript, we have strengthened our mechanistic insights and the validation of our findings by implementing the suggestions of the reviewers and including new experimental data to address their concerns.

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors identify Leiomodin-1 (LMOD1) as a key regulator of early myogenic differentiation, demonstrating its interaction with SIRT1 to influence SIRT1's cellular localization and gene expression. The authors propose that LMOD1 translocates SIRT1 from the nucleus to the cytoplasm to permit the expression of myogenic differentiation genes such as MYOD or Myogenin.

Strengths:

A major strength of this work lies in the robust temporal resolution achieved through a time-course mass spectrometry analysis of in vitro muscle differentiation. This provides novel insights into the dynamic process of myogenic differentiation, often under-explored in terms of temporal progression. The authors provide a strong mechanistic case for how LMOD1 exerts its role in muscle differentiation which opens avenues to modulate.

We thank the reviewer for the positive feedback on our manuscript and the insightful comments which helped to improve the manuscript!

Weaknesses:

One limitation of the study is the in vivo data. Although the authors do translate their findings in vivo for LMOD1 localization and expression, the cross-sectional imaging is not highly convincing. Longitudinal cuts or isolated fibers could have been more useful specimens to answer these questions. Moreover, the authors do not assess their in vitro SIRT1 findings in vivo. A few key experiments in regenerating or aged mice would strengthen the mechanistic insight of the findings.

We agree that longitudinal cuts and isolated fibers can provide excellent morphological detail for specific questions. However, for our primary objective in this study, which was to assess the temporal expression and localization of LMOD1 across the tissue during the regeneration process, we decided that cross-sectional analysis provided the most robust and reliable overview. Cross-sectional imaging effectively captures the spatial distribution of LMOD1 across multiple myofibers and their surrounding microenvironment, simultaneously assessing the whole cross-sectional area. By using this approach, we were able to evaluate the broader tissue architecture and cellular context, which was essential for understanding the dynamic changes occurring during regeneration. We were also able to investigate all myofibers of a muscle, and not only a small proportion, which we would analyze with longitudinal sections and isolated myofibers. Therefore, we continued using cross-sections for further analyses.

We fully agree with the reviewer that validating our in vitro SIRT1 findings in an in vivo context is an essential next step. To address this, we performed additional analyses on our existing regenerating muscle samples and incorporated new immunostainings for SIRT1 and PAX7 into the regeneration time-course (now shown in revised Figure 4I), providing further in vivo support for our proposed mechanism. We focused specifically on cross-sections collected at day 5 post-injury, a time point selected based on the peak in LMOD1 expression, to assess whether SIRT1 levels increase in parallel with LMOD1 during regeneration. Notably, SIRT1 abundance is elevated at day 5 post-injury, underscoring its involvement in early myogenic differentiation. This conclusion is further supported by the localization of SIRT1 within mononucleated cells and newly formed myofibers at this stage of regeneration.

Finally, we agree that further mechanistic studies in vivo would be highly valuable. While we were able to address SIRT1 dynamics in our regeneration model as suggested, an aged mouse cohort was unfortunately not available to us for this kind of study. Furthermore, more extensive in vivo experiments, such as those involving genetic manipulation, were beyond the scope of the current study, partly due to constraints related to animal welfare regulations and our approved experimental protocols.

Discussion:

Overall, the study emphasizes the importance of understanding the temporal dynamics of molecular players during myogenic differentiation and provides valuable proteomic data that will benefit the field. Future studies should explore whether LMOD1 modulates the nuclear-cytoplasmic shuttling of other transcription factors during muscle development and how these processes are mechanistically achieved. Investigating whether LMOD1 can be therapeutically targeted to enhance muscle regeneration in contexts such as exercise, aging, and disease will be critical for translational applications. Additionally, elucidating the interplay among LMOD1, LMOD2, and LMOD3 could uncover broader implications for actin cytoskeletal regulation in muscle biology.

We thank the reviewer for this excellent suggestion for future analyses. We have included these important considerations and future avenues in the Discussion of the revised manuscript:

“Our immunostaining data show that while LMOD1 is consistently cytoplasmic, its partner SIRT1 is only transiently localized in the cytoplasm. This suggests that their interaction is dynamically regulated. We hypothesize that the function of LMOD1 is determined by the changing availability of its binding partners during differentiation. During the initial phase, LMOD1 may primarily function to sequester SIRT1, a key regulator of myogenic genes. As differentiation proceeds, the increased expression of cytoskeletal components, such as its canonical partners TMODs and TPMs, likely shifts the function of LMOD1 towards its role in actin nucleation. This molecular switch, potentially driven by a change in the interactome of LMOD1, could then result in the release of SIRT1 from the cytoplasm. Such a mechanism may coordinate transcriptional regulation with cytoskeletal remodeling during myoblast differentiation.”

“Moreover, delineating the functional specialization and potential redundancy among leiomodin proteins represents an important next step. Our data indicate that LMOD1 primarily regulates early myogenic differentiation (Figure 3). In contrast, the lack of an early functional phenotype upon LMOD2 depletion, together with its upregulation at later stages (Figure S2A), suggests a temporal shift in regulatory control. Accordingly, a systematic comparative analysis of LMOD1, LMOD2, and LMOD3 will be required to elucidate their distinct roles in actin cytoskeleton regulation across the myogenic program, particularly with respect to myofibril maturation and maintenance.”

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

Major Changes:

(1) In Vivo Data on SIRT1:

The inclusion of in vivo data on SIRT1 localization and expression would significantly strengthen the manuscript. Similar staining techniques used for LMOD1 could be applied to SIRT1. Additionally, imaging muscle specimens such as longitudinal sections or isolated myofibers would provide clearer insights into SIRT1's spatial distribution and improve upon the less convincing cross-sectional images currently presented (Figure 2).

We fully agree that providing in vivo data on SIRT1 localization and expression is a crucial step to support our in vitro findings. Following the reviewer's suggestion, we have performed new experiments on muscle regeneration samples using the analyses of cross-sections as done for the analysis of LMOD1 localization. Specifically, we performed immunostaining for SIRT1 on cross-sections from muscle samples collected at day 5 post-injury, a time point selected based on the observed peak in LMOD1 expression. These new data (now included in revised Figure 4I) allowed us to assess whether SIRT1 levels increase during regeneration in parallel with an increase in LMOD1 abundance.

Regarding the suggestion to use longitudinal sections or isolated myofibers, we agree that these preparations offer excellent answers for certain questions. For the primary goal of our study, to assess the temporal expression changes across the entire regenerating tissue at different time points, we found that cross-sections provided the most comprehensive and robust overview and therefore did not use longitudinal sections or isolated myofibers. 

Performing additional animal experiments to obtain these specific preparations was beyond the scope of the current study and subject to constraints from our approved animal welfare protocols.

(2) Morphology of siLmod1 Cells:

The morphology of siLmod1-treated cells in vitro (Figure 3) raises concerns. Assessing cell viability or cell death in these experiments would help ensure that differences are not due to dead or unhealthy cells being quantified. There is also a notable discrepancy between the control panels in Figures 3C and 3H compared to the experimental conditions in 3F and 3K, particularly in terms of cell length and morphology. These inconsistencies should be addressed or clarified.

We acknowledge the visual discrepancies in cell morphology noted by the reviewer (e.g., between Figures 3C/3H and 3F/3K). These differences can be attributed to biological variability between primary myoblast cultures isolated from different mice. Such variability includes differences in myogenic potential and the fact that cells are not synchronized, leading to variations in differentiation efficiency, baseline morphology, and cell length across cultures (Cornelison 2008; Vaughan and Lamia 2019). To account for this, we decided to use n=6 biological replicates, i.e., primary myoblast cultures isolated from 6 different mice, for immunofluorescence analysis, ensuring robust quantitative data. Furthermore, we confirmed that this phenotype was not an artifact of culture conditions, as we consistently observed the same effect of Lmod1 knockdown independently of the passage number of the myoblasts or the donor mouse.

To address the concerns that morphological changes in siLmod1-treated cells might reflect cell death, we performed a TUNEL assay (transfection at day 1, analysis at day 3 of differentiation). This revealed no significant increase in TUNEL-positive (apoptotic) cells in siLmod1- (or siSirt1-) transfected samples versus siCtrl-transfected cells. These new data have been added to the revised manuscript as Supplementary Figure S2I. The TUNEL data indicate that the observed morphological changes upon knockdown of Lmod1 are not due to induced cell death. Supported by these results, our interpretation is that knockdown of Lmod1 impairs or arrests differentiation rather than causing cell death. Furthermore, our quantification of different cell populations showed shifts indicative of impaired differentiation (e.g., accumulation of cells at earlier stages) without exhibiting significant loss in cell numbers. For example, the numbers of myogenin+/MHC- and myogenin+/MHC+ cell populations, and differentiated myotubes, were not significantly reduced after transfection with siLmod1. A slight, not significant trend towards fewer non-proliferating myoblasts/reserve cells characterized by the expression of Myogenin-/MHC-Hoechst+ (Figure S2H) was noted. Overall, cells appeared to be 'stuck' in differentiation, consistent with the role of Lmod1 in impairing differentiation but not causing cell death. We have further clarified this aspect in the revised manuscript.

(3) LMOD1 and SIRT1 Interaction in Myogenic Cells:

Strengthening the connection between LMOD1 and SIRT1 within the myogenic system would enhance the manuscript. Could proximity ligation assays (PLA) be performed in myogenic cells, as was done in HEK293T cells? Additionally, investigating whether SIRT1 remains in the nucleus upon LMOD1 knockdown using siRNA would provide mechanistic insight into their interaction during myogenic differentiation.

We would like to clarify that the Proximity Ligation Assays (PLA) shown in Figure 4H were indeed performed in primary myoblasts, confirming the LMOD1-SIRT1 interaction directly in a myogenic context. We have modified the text to clarify that primary myoblasts were used for the PLA assays.

Minor Points:

(1) Was Lmod1 knockdown confirmed in vivo?

To target Lmod1 in Muscle Stem Cells (MuSCs) in vivo, we utilized self-delivering Accell siRNAs. This delivery system has been previously validated and shown to be highly effective for targeting MuSCs in regenerating muscle (Bentzinger et al., Cell Stem Cell, 2013).

While this is an established method for delivery, confirming knockdown specifically within the rare MuSC population is technically challenging using bulk tissue analysis, as the target signal is diluted by numerous other cell types. 

Therefore, to ensure the efficacy of our specific siRNA, we performed in vitro validation. For the reviewers' interest, we add Author response image 2 showing the efficiency of the respective siRNAs:

Author response image 2.

Knockdown efficiency of siRNAs targeting Lmod1 and Lmod2 following using the same self-delivering siRNA in proliferating primary myoblasts as used in in vivo experiments. Self-delivering Accell siRNA was added to primary myoblasts cultured in low serum media for 48 hours. Relative mRNA expression levels of Lmod1 and Lmod2 were measured after self-delivering Accell siRNA transfection targeting either Lmod1 (siLmod1) or Lmod2 (siLmod2). Expression levels were compared to control siRNA-transfected cells (siCtrl) and normalized to Gapdh expression.

Based on the documented efficacy of this delivery system from prior literature and our own validation of the specific siRNAs used here, we are confident in the knockdown efficiency of the respective siRNAs. We decided not to perform additional animal experiments due to animal welfare considerations.

(2) Some of the western blot bands do not appear to match the expected patterns for the tested proteins compared to controls (e.g., Figure S2J, S4C). Ensure that these are accurately labeled and include the entire membrane for transparency and reproducibility.

Regarding Figure S2J, we agree that the presentation could be confusing to the reader. The blot shows LMOD1 and LMOD2 knockdown, while the bar plot quantifies only the change in LMOD2 levels. We have now revised the figure legend to explicitly state this. We hope this makes the presentation of our data clearer.

For Figure S4C, we believe the concern about 'patterns' relates to loading variability. In this experiment, we manually counted the nuclei before lysis to ensure that each nuclear fraction started with an equal amount of material. We then loaded the cytoplasmic fractions in proportion to these counts. The purity of the fractions was additionally confirmed using nuclear (H4) and cytoplasmic (ALDOA) markers. As stated in the figure, the nuclear/cytoplasmic ratio of LMOD1 or SIRT1 was normalized across the entire lane of the Ponceau S staining, which we have now clarified in the relevant figure legends.

Finally, regarding transparency, the presented immunoblot images are representative crops, which is standard practice for clarity. We are committed to reproducibility and will provide full, uncropped scans of all blots in the final version of the manuscript, in line with eLife publishing guidelines. 

(3) Figure S1B appears to reuse images from Figure 2D (rotated). Verify that this is acceptable for the journal's guidelines, and if necessary, provide additional justification or clarification.

We acknowledge that the image presented in Figure S1B was accidentally reused as a representative example in Figure 2D. To address this and prevent any potential redundancy or confusion, we have revised Figure S1B by replacing the duplicated image with a different, representative example from our dataset. The updated figure now contains unique image data, and we believe this revision fully resolves the concern.

(4) Ensure consistent scale bars across images, particularly in Figures 3C and 3H, where discrepancies might affect interpretation.

We thank the reviewer for pointing this out, we have now standardized all scale bars throughout the manuscript to ensure consistency. All immunofluorescence images of cultured cells (including Fig 3C and 3H) now have a 50 µm scale bar, and all tissue cross-sections have a 100 µm scale bar. This change has been implemented in the revised figures.

Reviewer #3 (Public review):

Summary:

In this manuscript, the investigators identified LMOD1 as one of a subset of cytoskeletal proteins whose levels increase in the early stages of myogenic differentiation. Lmod1 is understudied in striated muscle and in particular in myogenic differentiation. Thus, this is an important study. It is also a very thorough study - with perhaps even too much data presented. Importantly, the investigators observed that LMOD1 appears to be important for skeletal regeneration, and myogenic differentiation and that it interacts with SIRT1. Both primary myoblast differentiation and skeletal muscle regeneration were studied. Rescue experiments confirmed these observations: SIRT1 can rescue perturbations of myogenic differentiation as a result of LMOD1 knockdown.

Strengths:

Particular strengths include: important topic, the use of primary skeletal cultures, the use of both cell culture and in vivo approaches, careful biomarker analysis of primary mouse myoblast differentiation, the use of two methods to probe the function of the Lmod1/SIRT1 pathway via using depletion approaches and inhibitors, and generation of six independent myoblast cultures. Results support their conclusions.

We thank the reviewer for the positive assessment of our work and the helpful comments for improving our manuscript.

Weaknesses:

(1) Figure 1. Images of cells in Figure 1A are too small to be meaningful (especially in comparison to the other data presented in this figure). Perhaps the authors could make graphs smaller?

We have adjusted the size of the images across all figure panels to ensure better visibility and clarity. We hope these adjustments improve the presentation of the data.

(2) Line 148 "We found LMOD2 to be the most abundant Lmod in the whole skeletal muscle." This is confusing since most, if not all, prior studies have shown that Lmod3 is the predominant isoform in skeletal muscle. The two papers that are cited are incorrectly cited. Clarification to resolve this discrepancy is needed.

We acknowledge that LMOD2 and LMOD3 are predominantly expressed in skeletal and cardiac muscles (Tsukada et al. 2010; Nworu et al. 2015), www.proteinatlas.org) and LMOD3’s transcription is directly regulated by MRTF/SRF and MEF2 to coordinate sarcomeric assembly (Cenik et al. 2015). However, our statement refers specifically to the analysis of the proteomic datasets from freshly isolated MuSCs and four distinct skeletal muscles (G, S, TA, EDL) generated by Schüler et al. 2021. Crucially, LMOD3 was not detected in the quantitative mass spectrometry data for the EDL, G, S, or TA muscle samples analyzed in this specific study. In the context of this particular dataset, LMOD2 was the most highly abundant Leiomodin isoform detected in the whole skeletal muscle samples. This finding suggests a differential expression and function between LMOD isoforms depending on the muscle type and/or developmental/regenerative state. We have revised and corrected this clarification in the manuscript, including correcting the initial citations.

(3) Figure 2. Immunoflorescence (IF) panels are too small to be meaningful. Perhaps the graphs could be made smaller and more space allocated for the IF panels? This issue is apparent for just about all IF panels - they are simply too small to be meaningful. Additionally, in many of the immunofluorescence figures, the colors that were used make it difficult to discern the stained cellular structures. For example, in Figure S1, orange and purple are used - they do not stand out as well as other colors that are more commonly used.

We agree that the IF panels were too small for optimal interpretation and have adjusted them in Figure 2 and throughout the manuscript. Regarding the color choices, we appreciate the reviewer's comments. Our initial selection (e.g., orange and purple in Figure S1) was intended to enhance accessibility for individuals with common color vision deficiencies, including red-green color blindness. However, we acknowledge the reviewer's point that these combinations provided insufficient contrast for discerning cellular structures. Therefore, we have revised the color schemes to use green, red, and blue, which should offer improved contrast.

(4) There is huge variability in many experiments presented - as such, more samples appear to be required to allow for meaningful data to be obtained. For example, Figure S2. Many experimental groups, only have 3 samples - this is highly problematic - I would estimate that 5-6 would be the minimum.

We thank the reviewer for the comment regarding experimental variability and sample size. In our study, n=3 biological replicates, i.e., independent primary cell cultures obtained from different mice, were primarily used for immunoblots. We acknowledge that variability can be observed between distinct primary cell cultures due to factors such as inherent differences in myogenic potential, cell cycle state (as cells were not synchronized), and passage number. Importantly, despite this inter-sample variation, the investigated phenotypes showed consistent trends across biological replicates. Rather than increasing the number of replicates for immunoblots, we opted for validating our key findings using independent approaches with a higher number of replicates. For instance, qRT-PCR analyses (to confirm knockdown efficiency) and immunofluorescence analyses were mostly performed using five to six independent myoblast cultures (biological replicates).

(5) Ponceau S staining is often used as a loading control in this manuscript for western blots. The area/molecular weight range actually used should be specified. Not clear why in some experiments GAPDH staining is used, in other experiments Ponceau S staining is used, and in some, both are used. In some experiments, the variability of total protein loaded from lane to lane is disconcerting. For example, in Figure S4C there appears to be more than normal variability. Can the protein assay be redone and samples run again?

We have clarified in the relevant figure legends that Ponceau S normalization, when used, was based on the quantification of the entire lane. Our standard loading control is GAPDH. We used Ponceau S for normalization only when GAPDH was deemed unsuitable, e.g., in nuclear-cytoplasmic fractionation experiments where GAPDH is not present in all fractions.

Concerning the variability observed in Figure S4C, we manually counted the nuclei before lysis to ensure that each nuclear fraction started with an equal amount of material. We then loaded the cytoplasmic fractions in proportion to these counts. The purity of the fractions was additionally confirmed using nuclear (H4) and cytoplasmic (ALDOA) markers. The nuclear/cytoplasmic ratio of LMOD1 or SIRT1 was normalized across the entire lane of the Ponceau S staining, which we have now clarified in the relevant figure legends.

(6) Figure S3 - Lmod3 is included in the figure but no mention of it occurs in the title of the figure and/or legend.

We wish to clarify that the protein identified in Figure S3 is TMOD3 (Tropomodulin 3), not LMOD3. TMOD3 is a known pointed-end capping protein regulating the actin filament nucleation process together with LMODs (Fowler and Dominguez 2017; Boczkowska et al. 2015), so its presence in our dataset was expected and helps validate our results.

(7) Abstract, line 25. "overexpression accelerates and improves the formation of myotubes". This is a confusing sentence. How is it improving the formation? A little more information about how they are different than developing myotubes in normal/healthy muscles would be helpful.

We thank the reviewer for the comment. To clarify, we have revised the sentence in line 25 to "improves the initiation of myotube formation." This change reflects our observation that overexpression of LMOD1 leads to a more rapid onset of myotube formation, as evidenced by earlier expression of differentiation markers and accelerated fusion of myoblasts into myotubes compared to GFP overexpression myoblast cell line. These findings suggest that LMOD1 overexpression enhances the efficiency of the early stages of differentiation and fusion, thereby contributing to improved initiation of myotube formation.

(8) It is impossible from the IF figures presented to determine where Lmod1 localizes in the myocytes. Information on its subcellular localization is important. Does it localize with Lmod2 and Lmod3 at thin filament pointed ends?

Several publications suggest that LMODs are involved in actin nucleation and interact with TMODs at the thin filament pointed ends (Boczkowska et al. 2015; Fowler and Dominguez 2017; Fowler, Greenfield, and Moyer 2003; Tsukada et al. 2010; Rao, Madasu, and Dominguez 2014). We performed F-actin (Phalloidin) staining together with LMOD1 staining and observed possible co-localization (see Author response image 3). Specifically, we noted an accumulation of LMOD1 at the ends of myocytes, indicating that LMOD1 might play a role in the elongation and guidance of myotube differentiation. For the reviewer’s interest, we include Author response image 3 as it was not part of the original manuscript. While performing subcellular localization stainings, we added the F-actin/Phalloidin staining to explore potential interactions, but this aspect was not further investigated in the current study.

Author response image 3.

Co-staining of LMOD1 and Phalloidin in differentiating myocytes.Example image showing immunofluorescence staining of LMOD1 (purple) and F-actin (green; Phalloidin) in differentiating primary myocytes. LMOD1 appears to accumulate at the ends of elongated myocytes and co-localizes with actin structures (highlighted in boxes), suggesting a potential role in myotube elongation and guidance during differentiation.

Our study focused on a distinct role for LMOD1, independent from its function in actin filament nucleation, and we therefore did not pursue further co-localization staining with LMOD2 or LMOD3. We recognize the potential importance of exploring these interactions and their relevance to thin filament organization in skeletal muscle. However, although this was beyond the scope of our current work, we will investigate this aspect in the future.

References

Boczkowska, Malgorzata, Grzegorz Rebowski, Elena Kremneva, Pekka Lappalainen, and Roberto Dominguez. 2015. “How Leiomodin and Tropomodulin Use a Common Fold for Different Actin Assembly Functions.” Nature Communications 6 (1): 8314.

Cenik, Bercin K., Ankit Garg, John R. McAnally, John M. Shelton, James A. Richardson, Rhonda Bassel-Duby, Eric N. Olson, and Ning Liu. 2015. “Severe Myopathy in Mice Lacking the MEF2/SRF-Dependent Gene Leiomodin-3.” The Journal of Clinical Investigation 125 (4): 1569–78.

Cornelison, D. D. W. 2008. “Context Matters: In Vivo and in Vitro Influences on Muscle Satellite Cell Activity.” Journal of Cellular Biochemistry 105 (3): 663–69.

Fowler, Velia M., and Roberto Dominguez. 2017. “Tropomodulins and Leiomodins: Actin Pointed End Caps and Nucleators in Muscles.” Biophysical Journal 112 (9): 1742–60.

Fowler, Velia M., Norma J. Greenfield, and Jeannette Moyer. 2003. “Tropomodulin Contains Two Actin Filament Pointed End-Capping Domains.” The Journal of Biological Chemistry 278 (41): 40000–9.

Liu, Ling, Tom H. Cheung, Gregory W. Charville, Bernadette Marie Ceniza Hurgo, Tripp Leavitt, Johnathan Shih, Anne Brunet, and Thomas A. Rando. 2013. “Chromatin Modifications as Determinants of Muscle Stem Cell Quiescence and Chronological Aging.” Cell Reports 4 (1): 189–204.

Lukjanenko, Laura, M. Juliane Jung, Nagabhooshan Hegde, Claire Perruisseau-Carrier, Eugenia Migliavacca, Michelle Rozo, Sonia Karaz, et al. 2016. “Loss of Fibronectin from the Aged Stem Cell Niche Affects the Regenerative Capacity of Skeletal Muscle in Mice.” Nature Medicine 22 (8): 897–905.

Nworu, Chinedu U., Robert Kraft, Daniel C. Schnurr, Carol C. Gregorio, and Paul A. Krieg. 2015. “Leiomodin 3 and Tropomodulin 4 Have Overlapping Functions during Skeletal Myofibrillogenesis.” Journal of Cell Science 128 (2): 239–50.

Rao, Jampani Nageswara, Yadaiah Madasu, and Roberto Dominguez. 2014. “Mechanism of Actin Filament Pointed-End Capping by Tropomodulin.” Science 345 (6195): 463–67.

Schüler, Svenja C., Joanna M. Kirkpatrick, Manuel Schmidt, Deolinda Santinha, Philipp Koch, Simone Di Sanzo, Emilio Cirri, Martin Hemberg, Alessandro Ori, and Julia von Maltzahn. 2021. “Extensive Remodeling of the Extracellular Matrix during Aging Contributes to Age-Dependent Impairments of Muscle Stem Cell Functionality.” Cell Reports 35 (10): 109223.

Tsukada, Takehiro, Christopher T. Pappas, Natalia Moroz, Parker B. Antin, Alla S. Kostyukova, and Carol C. Gregorio. 2010. “Leiomodin-2 Is an Antagonist of Tropomodulin-1 at the Pointed End of the Thin Filaments in Cardiac Muscle.” Journal of Cell Science 123 (Pt 18): 3136–45.

Vaughan, Megan, and Katja A. Lamia. 2019. “Isolation and Differentiation of Primary Myoblasts from Mouse Skeletal Muscle Explants.” Journal of Visualized Experiments: JoVE, no. 152 (October). https://doi.org/10.3791/60310.

eLife Assessment

This elegant study presents a valuable approach to probing the structural features of the full-length human Hv1 channel as a purified protein, supported by rigorous biochemical assays and spectral FRET analysis, which will interest biophysicists and physiologists studying Hv1 and other ion channels. Overall, the work introduces an interesting labeling strategy and provides methodological observations that are of value in investigating hHV1. However, the analysis appears incomplete, requiring additional structural interpretation and mechanistic insight.

Reviewer #1 (Public review):

In this study, the noncanonical amino acid acridon-2-ylalanine (Acd) was inserted at various positions within the human Hv1 protein using a genetic code expansion approach. The purified mutants with incorporated fluorophore were shown to be functional using a proton flux assay in proteoliposomes. FRET between native tryptophan and tyrosine residues and Acd were quantified using spectral FRET analysis. Predicted FRET efficiencies calculated from an AlphaFold model of the Hv1 dimer were compared to the corresponding experimental values. Spectral FRET analysis was also used to test whether structural rearrangements caused by Zn2+, a well-known Hv1 inhibitor, could be detected. The experimental data provide a good validation of the approach, but further expansion of the analysis will be necessary to differentiate between intra- and intersubunit structural features.

Interestingly, the observed rearrangements induced by Zn2+ were not limited to the protein region proximal to the extracellular binding site but extended to the intracellular side of the channel. This finding agrees with previous studies showing that some extracellular Hv1 inhibitors, such as Zn2+ or AGAP/W38F, can cause long-range structural changes propagating to the intracellular vestibule of the channel (De La Rosa et al. J. Gen. Physiol. 2018, and Tang et al. Brit J. Pharm 2020). The authors should consider adding these references.

Since one of the main goals of this work was to validate Acd incorporation and the spectral FRET analysis approach to detect conformational changes in hHv1 in preparation for future studies, the authors should consider removing one subunit from their dimer model, recalculating FRET efficiencies for the monomer, and comparing the predicted values to the experimental FRET data. This comparison could support the idea that the reported FRET measurements can inform not only on intrasubunit structural features but also on subunit organization.

Reviewer #2 (Public review):

This manuscript by Carmona, Zagotta, and Gordon is generally well-written. It presents a crude and incomplete structural analysis of the voltage-gated proton channel based on measured FRET distances. The primary experimental approach is Förster Resonance Energy Transfer (FRET), using a fluorescent probe attached to a noncanonical amino acid. This strategy is advantageous because the noncanonical amino acid likely occupies less space than conventional labels, allowing more effective incorporation into the channel structure.

Fourteen individual positions within the channel were mutated for site-specific labeling, twelve of which yielded functional protein expression. These twelve labeling sites span discrete regions of the channel, including P1, P2, S0, S1, S2, S3, S4, and the dimer-connecting coiled-coil domain. FRET measurements are achieved using acridon-2-ylalanine (Acd) as the acceptor, with four tryptophan or four tyrosine residues per monomer serving as donors. In addition to estimating distances from FRET efficiency, the authors analyze full FRET spectra and investigate fluorescence lifetimes on the nanosecond timescale.

Despite these strengths, the manuscript does not provide a clear explanation of how channel structure changes during gating. While a discrepancy between AlphaFold structural predictions and the experimental measurements is noted, it remains unclear whether this mismatch arises from limitations of the model or from the experimental approach. No further structural analysis is presented to resolve this issue or to clarify the conformational states of the protein.

The manuscript successfully demonstrates that Acd can be incorporated at specific positions without abolishing channel function, and it is noteworthy that the reconstituted proteins function as voltage-activated proton channels in liposomes. The authors also report reversible zinc inhibition of the channel, suggesting that zinc induces structural changes in certain channel regions that can be reversed by EDTA chelation. However, this observation is not explored in sufficient depth to yield meaningful mechanistic insight.

Overall, while the study introduces an interesting labeling strategy and provides valuable methodological observations, the analysis appears incomplete. Additional structural interpretation and mechanistic insight are needed.

Major Points

(1) Tryptophan and tyrosine exhibit similar quantum yields, but their extinction coefficients differ substantially. Is this difference accounted for in your FRET analysis? Please clarify whether this would result in a stronger weighting of tryptophan compared to tyrosine.

(2) Is the fluorescence of acridon-2-ylalanine (Acd) pH-dependent? If so, could local pH variations within the channel environment influence the probe's photophysical properties and affect the measurements?

(3) Several constructs (e.g., K125Tag, Y134Tag, I217Tag, and Q233Tag) display two bands on SDS-PAGE rather than a single band. Could this indicate incomplete translation or premature termination at the introduced tag site? Please clarify.

(4) In Figure 5F, the comparison between predicted FRET values and experimentally determined ratio values appears largely uninformative. The discussion on page 9 suggests either an inaccurate structural model or insufficient quantification of protein dynamics. If the underlying cause cannot be distinguished, how do the authors propose to improve the structural model of hHV1 or better describe its conformational dynamics?

(5) Cu²⁺, Ru²⁺, and Ni²⁺ are presented as suitable FRET acceptors for Acd. Would Zn²⁺ also be expected to function as an acceptor in this context? If so, could structural information be derived from zinc binding independently of Trp/Tyr?

(6) The investigated structure is most likely dimeric. Previous studies report that zinc stabilizes interactions between hHV1 monomers more strongly than in the native dimeric state. Could this provide an explanation for the observed zinc-dependent effects? Additionally, do the detergent micelles used in this study predominantly contain monomers or dimers?

(7) hHV1 normally inserts into a phospholipid bilayer, as used in the reconstitution experiments. In contrast, detergent micelles may form monolayers rather than bilayers. Could the authors clarify the nature of the micelles used and discuss whether the protein is expected to adopt the same fold in a monolayer environment as in a bilayer?

eLife Assessment

This study addresses a fundamental question in glycobiology by elucidating how a single-site processive enzyme orchestrates the alternating addition of sugars to synthesize complex polysaccharides such as hyaluronan. The findings are compelling, providing a clear mechanistic framework supported by strong experimental validation. Major strengths include the integration of high-resolution structural data with rigorous biochemical analyses, resulting in a well-supported model of hyaluronan assembly.

Reviewer #1 (Public review):

Summary:

This revised manuscript describes critical intermediate reaction steps of a HA synthase at the molecular level; specifically, they examine the 2nd step, polymerization, adding GlcA to GlcNAc to form the initial disaccharide of the repeating HA structure. Unlike the vast majority of known glycosyltransferases, the viral HAS (a convenient proxy extrapolated to resemble the vertebrate forms) uses a single pocket to catalyze both monosaccharide transfer steps. The authors work illustrates the interactions needed to bind & proof-read the UDP-GlcA using direct and '2nd layer' amino acid residues. This step also allows the HAS to distinguish the two UDP-sugars; this is very important as the enzymes are not known or observed to make homopolymers of only GlcA or GlcNAc, but only make the HA disaccharide repeats GlcNAc-GlcA.

Strengths:

Techniques & analysis; overview of HA synthase mechanisms

Weaknesses:

None

Comments on revisions:

Previous clarity issues in the original submission were all resolved. Again, this is a very well done body of work!!

Reviewer #2 (Public review):

Summary:

The paper by Stephens and co-workers provides important mechanistic insight into how hyaluronan synthase (HAS) coordinates alternating GlcNAc and GlcA incorporation using a single Type-I catalytic centre. Through cryo-EM structures capturing both "proofreading" and fully "inserted" binding poses of UDP-GlcA, combined with detailed biochemical analysis, the authors show how the enzyme selectively recognizes the GlcA carboxylate, stabilizes substrates through conformational gating, and requires a priming GlcNAc for productive turnover.

These findings clarify how one active site can manage two chemically distinct donor sugars while simultaneously coupling catalysis to polymer translocation.

The work also reports a DDM-bound, detergent-inhibited conformation that possibly illuminates features of the acceptor pocket, although this appears to be a purification artefact (it is indeed inhibitory) rather than a relevant biological state.

Overall, the study convincingly establishes a unified catalytic mechanism for Type-I HAS enzymes and represents a significant advance in understanding HA biosynthesis at the molecular level.

Strengths:

There are many strengths.

This is a multi-disciplinary study with very high-quality cryo-EM and enzyme kinetics (backed up with orthogonal methods of product analysis) to justify the conclusions discussed above.

Comments on revisions:

The suggestions made in the initial comments have all been responded to very well.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

This manuscript describes critical intermediate reaction steps of a HA synthase at the molecular level; specifically, it examines the 2nd step, polymerization, adding GlcA to GlcNAc to form the initial disaccharide of the repeating HA structure. Unlike the vast majority of known glycosyltransferases, the viral HAS (a convenient proxy extrapolated to resemble the vertebrate forms) uses a single pocket to catalyze both monosaccharide transfer steps. The authors' work illustrates the interactions needed to bind & proof-read the UDP-GlcA using direct and '2nd layer' amino acid residues. This step also allows the HAS to distinguish the two UDP-sugars; this is very important as the enzymes are not known or observed to make homopolymers of only GlcA or GlcNAc, but only make the HA disaccharide repeats GlcNAc-GlcA.

Strengths:

Overall, the strengths of this paper lie in its techniques & analysis.

The authors make significant leaps forward towards understanding this process using a variety of tools and comparisons of wild-type & mutant enzymes. The work is well presented overall with respect to the text and illustrations (especially the 3D representations), and the robustness of the analyses & statistics is also noteworthy.

Furthermore, the authors make some strides towards creating novel sugar polymers using alternative primers & work with detergent binding to the HAS. The authors tested a wide variety of monosaccharides and several disaccharides for primer activity and observed that GlcA could be added to cellobiose and chitobiose, which are moderately close structural analogs to HA disaccharides. Did the authors also test the readily available HA tetramer (HA4, [GlcA-GlcNAc]2) as a primer in their system? This is a highly recommended experiment; if it works, then this molecule may also be useful for cryo-EM studies of CvHAS as well.

The reviewer requested testing whether an HA tetratsaccharide could also serve as an glycosyl transfer acceptor for HAS. The commerically available HA tetrasaccharide (HA4) is terminated at its non-reducing end by GlcA, therein we proceeded to measure its effect on UDP-GlcNAc turnover kientics. Titration of HA4 failed to elicit any detectable change in UDP-GlcNAc turnover rate, indicating no priming. This is now mentioned in the main text and the data is shown in Fig. S9.

Weaknesses:

In the past, another report describing the failed attempt of elongating short primers (HA4 & chitin oligosaccharides larger than the cello- or chitobiose that have activity in this report) with a vertebrate HAS, XlHAS1, an enzyme that seems to behave like the CvHAS ( https://pubmed.ncbi.nlm.nih.gov/10473619/); this work should probably be cited and briefly discussed. It may be that the longer primers in the 1999 paper and/or the different construct or isolation specifics (detergent extract vs crude) were not conducive to the extension reaction, as the authors extracted recombinant enzyme.

We apologize for the oversight. This reference is now cited (ref. 18) together with the description of the failed elongation of HA4 by CvHAS.

There are a few areas that should be addressed for clarity and correctness, especially defining the class of HAS studied here (Class I-NR) as the results may (Class I-R) or may not (Class II) align (see comment (a) below), but overall, a very nicely done body of work that will significantly enhance understanding in the field.

Done as requested

Reviewer #2 (Public review):

Summary:

The paper by Stephens and co-workers provides important mechanistic insight into how hyaluronan synthase (HAS) coordinates alternating GlcNAc and GlcA incorporation using a single Type-I catalytic centre. Through cryo-EM structures capturing both "proofreading" and fully "inserted" binding poses of UDP-GlcA, combined with detailed biochemical analysis, the authors show how the enzyme selectively recognizes the GlcA carboxylate, stabilizes substrates through conformational gating, and requires a priming GlcNAc for productive turnover.

These findings clarify how one active site can manage two chemically distinct donor sugars while simultaneously coupling catalysis to polymer translocation.

The work also reports a DDM-bound, detergent-inhibited conformation that possibly illuminates features of the acceptor pocket, although this appears to be a purification artefact (it is indeed inhibitory) rather than a relevant biological state.

Overall, the study convincingly establishes a unified catalytic mechanism for Type-I HAS enzymes and represents a significant advance in understanding HA biosynthesis at the molecular level.

Strengths:

There are many strengths.

This is a multi-disciplinary study with very high-quality cryo-EM and enzyme kinetics (backed up with orthogonal methods of product analysis) to justify the conclusions discussed above.

Weaknesses:

There are few weaknesses.

The abstract and introduction assume a lot of detailed prior knowledge about hyaluronan synthases, and in doing so, risk lessening the readership pool.

A lot of discussion focuses on detergents (whose presence is totally inhibitory) and transfer to non-biological acceptors (at high concentrations). This risks weakening the manuscript.

The abstract and parts of the introduction have been revised to address the reviewer’s concerns.

Reviewer #1 (Recommendations for the authors):

(1) As noted above, please state in title, abstract & introduction that this work is focused on a "Class I-NR HAS" (as described in Ref. #4), and NOT all HAS families...this is truly essential to note as someone working with the Pasteurella HAS version (Class II) would be totally misled & at this point, no one knows the Streptococcus HAS (Class-IR) mechanistic details which could be different due to its inverse molecular directionality of elongation compared to the CvHAS Class I-NR enzyme.

Done as requested.

(2) Page 6 - for the usefulness of the HAS mutants as being folded correctly, it was stated these mutants are suitable since they all 'purify' similarly...the use of the more proper term should probably be 'chromatograph', similarly suggesting similar hydrodynamic radii without massive folding issues.

This has been revised to state that they all exhibited comparable size exclusion chromatography profiles.

“All mutants share similar size exclusion chromatography profiles with the WT enzyme, suggesting that the substitutions do not cause a folding defect (Fig. S3).”

(3) Page 7 - please check these sentences (& rest of paragraph?) as the meaning is not clear. "First, UDP-GlcNAc was titrated in the presence of excess UDP-GlcA, resulting in a response similar to the acceptor-free condition (Fig. 2C). However, the maximum reaction velocity at 20 mM UDP-GlcNAc was approximately 25% lower than that measured in the presence of UDP-GlcNAc only (Fig. 2C)."

The paragraph has been revised to avoid confusion.

(4) In Methods, please use an italicized 'g' for the centrifugation steps globally.

Changed as requested

(5) Please note the source/vendor for the HA standards on gels.

Done

(6) Page 35 - TLC section.

(a) 'n-butanol' (with italic n) is the most widespread chemical name (not butan-1-ol).

Done

(b) Also, for all of the TLC images, the origin and the solvent front should be marked.

Changed as suggested.

Reviewer #2 (Recommendations for the authors):

A number of minor issues should be addressed.

(1) Abstract

Two comments on the Abstract, which I found surprisingly weak given the quality of the work, and lacking a key detail.

A major conceptual contribution of this work is the demonstration of how a single Type-I catalytic centre discriminates, positions, and transfers two chemically distinct substrates in an alternating pattern. This distinguishes HAS from dual-active-site (Type-II) glycosyltransferases and is important for understanding HA polymerization.

However, this central point is not clearly articulated in the abstract. I suggest explicitly stating that HAS performs both GlcNAc and GlcA transfer reactions within a single catalytic site, and that the proofreading/inserted poses illuminate how this multifunctionality is achieved.

The abstract currently ends with the observation of a DDM-bound, detergent-inhibited state. While this is interesting, it absolutely does not represent the central conceptual advance of the study and gives the abstract an artefactual ending.

I strongly recommend revising the final sentences to emphasize the broader mechanistic insight and not an "artefact" (indeed, the enzyme is inactive in the presence of this detergent; it is thus a very unusual way to conclude an abstract).

That is, finish with the wider implications of how HAS coordinates alternating substrate use, proofreading, and polymer translocation. Ending on the main mechanistic or biological significance would make the abstract considerably stronger and more aligned with the main message of the paper.

The abstract has been revised thoroughly to reflect the important insights gained on CvHAS’ catalytic function and HA biogenesis in general.

(2) Introduction

The distinction between single active-centre enzymes, which transfer both sugars alternately, and twin catalytic domain enzymes that each perform one addition is surely central to the whole paper. But it is not discussed. Surely this has to be covered. There is a lot of work in this space, including, but not limited to:

https://doi.org/10.1093/glycob/cwg085

https://doi.org/10.1093/glycob/10.9.883

https://doi.org/10.1093/glycob/cwad075 (includes this author team)

Originally back to https://doi.org/10.1021/bi990270y

If the authors instead assume such a level of knowledge for the reader, then surely they are writing for a specialist audience, not consistent with the wider readership ambitions of eLife?

The Introduction has been revised as suggested by the reviewer, providing necessary background to frame our description of the Chlorella virus HAS. We made a deliberate effort to put new insights into a broader context.

(3) Results and Discussion

DDM "was observed for >50% of the analysed particles". I struggled with this. I couldn't understand how the authors selected particles that did or did not contain DDM. The main body text states: "To our surprise, careful sorting of the UDP-GlcA supplemented cryo EM dataset revealed a CvHAS subpopulation that was not bound to the substrate, but, instead, a DDM molecule near the active site (Fig 3A and S7). This was observed for >50% of the analyzed particles."

That reads like there is one sample with two populations. But the figures and the methods section suggest differently: they suggest two samples with different data-collection regimes. That does not match the main text. Could this be clarified?

Yes, that wasn’t explained well. We clarified the text to stress that the DDM-bound sample came from a dataset that was intended to resolve an UDP-GlcA-bound state, but instead revealed the inhibition by DDM.

Also in this space, in the modern world, "nominal magnification" has no real meaning, and calibrated pixel size would be more appropriate. Can this be given, please?

The relevant Methods section now states: “imaging of … was performed at a calibrated pixel size of 0.652 Å”.

The discovery of DDM in the active site is surprising. But it is an inhibitory artefact. Is this section pushed a little too hard? Also, "The coordination of DDM's maltoside moiety, an αlinked glucose disaccharide, is consistent with priming by cellobiose and chitobiose." I'm not sure why an α-linked maltose is consistent with the binding of a β-linked cellobiose. That makes no sense. There will be no other enzymes where starch and cellulose oligos are mutually accepted. Consider rewriting.

We like to stress the DDM coordination because it could lead to the development of compounds that can really function as inhibitors, either for HAS or other related enzymes. In the observed DDM binding pose, the alpha-linkage is not recognized. Instead, the reducing end glucosyl unit stacks against Trp342 while the non-reducing unit extends into the catalytic pocket. Hence, a similar binding pose is conceivable for cellobiose and potentially also for chitobiose. The relevant section has been reworded.

eLife Assessment

This important study introduces an approach to discovering antibiotic resistance determinants by leveraging diverse susceptibility profiles among related mycobacterial species, with particular relevance to high-level resistance against natural product-derived antibiotics. The research provides convincing evidence for the role of ADP-ribosylation enzymes in rifamycin resistance among mycobacteria, whilst also demonstrating that antibiotic susceptibility is not correlated with growth rate or intracellular compound concentration. The revision is substantively improved, but some broader claims still require additional experimental support. This work lays a significant foundation for understanding the complexity of antibiotic resistance mechanisms in mycobacteria and opens new avenues for future antimicrobial research.

Reviewer #1 (Public review):

This work analyzes innate resistance to drugs in mycobacteria by comparing minimum inhibitory concentrations (MICs) across a diverse panel of mycobacterial species. The results show that MICs are poorly correlated with growth rate while phylogeny associated with horizontal gene transfer underlies the observed differences in MIC, an important demonstration. A further investigation into the driver for the vast differences in susceptibility profiles shows that for three drugs the MIC is not correlated with intrabacterial drug concentrations where intrabacterial drug concentration is comprised of cytosolic and cell wall associated drug. This is a striking observation. The authors delve into the mechanisms that drive resistance to rifamycins and confirm that resistance is driven by ADP-ribosyltransferases of which two variant groups exist, one of which is kinetically faster and apparently is superior at modifying more hydrophobic rifamycins. The relative role of the two ADP-ribosyltransferases in conferring resistance especially in the species with both orthologs is not fully understood since the modified drug can possibly be further modified and transcriptional downregulation experiments performed in this work do not provide genetic evidence of perturbation of mRNA levels of the respective open reading frames.

Comments on revisions:

Demonstration of the level of transcriptional downregulation of the two Arr orthologs would have been a nice demonstration of (1) the utility of CRISPRi in other mycobacteria, (2) that the difference in rifabutin susceptibility during knockdown of Arr-1 vs Arr-X can fully be ascribed to the role of Arr-X in modifying the drug.

Reviewer #3 (Public review):

This manuscript presents a macroevolutionary approach to identification of novel high-level antibiotic resistance determinants that takes advantage of the natural genetic diversity within a genus (mycobacteria, in this case) by comparing antibiotic resistance profiles across related bacterial species and then using computational, molecular, and cellular approaches to identify and characterize the distinguishing mechanisms of resistance. The approach is contrasted with "microevolutionary" approaches based on comparing resistant and susceptible strains of the same species and approaches based on ecological sampling that may not include clinically relevant pathogens or related species. The potential for new discoveries with the macroevolution-inspired approach is evident in the diversity of drug susceptibility profiles revealed amongst the selected mycobacterial species and the identification and characterization of a new group of rifamycin-modifying ADP-ribosyltransferase (Arr) orthologs of previously described mycobacterial Arr enzymes. Additional findings that intra-bacterial antibiotic accumulation does not always predict potency within this genus, that M. marinum is a better proxy for M. tuberculosis drug susceptibility than the commonly used saprophyte M. smegmatis, and that susceptibility to semi-synthetic antibiotic classes is generally less variable than susceptibility to antibiotics more directly derived from natural products strengthen the claim that the macroevolutionary lens is valuable for elucidating general principles of susceptibility within a genus.

There are some limitations to the work. The argument for the novelty of the approach could be better articulated. While the opportunities for new discoveries presented by identification of discrepant susceptibility results between related species is evident, it is less clear how the macroevolutionary approach is further leveraged for the discovery of truly novel resistance mechanisms. The example of the discovery of Arr-X enzymes presented here relied upon foundational knowledge of previously characterized Arr orthologs. There is less clarity about what the pipeline would look like for discovery of previously unknown determinants when one is agnostic to putative mechanisms. From the point at which interspecies differences in susceptibility are noted, does the framework still remain distinct from other discovery frameworks and approaches?

While the experimentation and analyses performed are generally well designed and rigorous, there are a few instances in which broad claims are based on inferences from sample sets or data sets that are, at present, too limited to provide robust support. For example, the claim that rifampicin modification, and precisely ADP-ribosylation, is the dominant mechanism of resistance to rifampicin in mycobacteria is still a bit premature or at least an over-generalization, as other enzymatic modification mechanisms and other mechanisms such as helR-mediated dissociation of rifampicin-stalled RNA polymerases, efflux, etc were not examined. CRISPR interference was used in a demonstrative example to support this assertion, but would need to be applied more systematically to be more conclusive. The general claim that intra-bacterial antibiotic accumulation does not predict potency in mycobacteria may be another over-generalization based on the limited set of drugs and species studied.

Comments on revisions:

Discussion, lines 321-323: "We found that resistance to these antibiotics in mycobacteria do not correlate with by uptake/efflux mechanisms in the species tested..." is an over-generalization and conflicts with the following statement on lines 199-201: "for BDQ we could observe some correlation between antibiotic potency and [BDQ]IB which could be indicative of efflux playing a role in antibiotic efficacy. Given that the current statement in the Discussion only applies to 2 of 3 drugs tested, a more specific or nuanced interpretation seems warranted.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

This work shows that resistance profiles to a variety of drugs are variable between different mycobacterial species and are not correlated with growth rate or intrabacterial compound concentration (at least for linezolid, bedaquiline, and Rifampicin). Note that intrabacterial compound concentration does not distinguish between cytosolic and periplasmic/cell wall-associated drugs. The susceptibility profiles for a wide range of mycobacteria tested under the same conditions against 15 commonly used antimycobacterial drugs provide the first recorded cross-species comparison which will be a valuable resource for the scientific community. To understand the reasons for the high Rifampicin resistance seen in many mycobacteria, the authors confirm the presence of the arr gene known to encode a Rif ribosyltransferase involved in Rif resistance in M. smegmatis in the resistant mycobacteria after confirming the absence of on-target mutations in the RpoB RRDR. Metabolomic analyses confirm the presence of ribosylated Rif in some of the naturally resistant mycobacteria which may not be entirely surprising but an important confirmation. Presumably M. branderi is highly resistant despite lacking the arr homolog due to the rpoB S45N mutation. M. flavescens has an MIC similar to that of M. smegmatis, despite having both Arr-1 and Arr-X. Various Arr-1 and Arr-X proteins are expressed and characterized for catalytic activity which shows that Arr-X is a faster enzyme,, especially with respect to more hydrophobic rifamycins. M. flavescens has similar MIC values to Rifapentine and Rifabutin to M. smegmatis. Thus, the Arr-1 versus Arr-X comparison does not provide a complete explanation for the underlying reasons driving natural Rif resistance in mycobacteria. Downregulation of Arr-X expression in M. conceptionense confers increased sensitivity to Rifabutin confirming its role as a rifamycin-inactivating enzyme.

Overall, the comparison of cross-species susceptibility profiles is novel; the demonstration that MIC is not correlated with intracellular drug concentration is important but not sufficiently interrogated, the demonstration that Arr-X is also a Rif ADP-ribosyltransferase is a good confirmation and shows that it is more efficient than Arr-1 on hydrophobic rifamycins is interesting but maybe not entirely surprising. The manuscript seems to have two parts that are related, but the rifamycin modification aspect of the work is not strongly linked to the first part since it interrogates the modification of one drug but not the common cause of natural resistance for other drugs.

Reviewer #2 (Public review):

Summary:

The authors use a variety of methods to investigate the mechanisms of innate drug resistance in mycobacteria. They end up focusing on two primary determinants - drug accumulation, which correlates rather poorly with resistance for many species, and, for the rifamycins, ADP-ribosyltransferases. The latter enzymes do appear to account for a good deal of resistance, though it is difficult to extrapolate quantitatively what their relative contributions are.

Overall, they make excellent use of biochemical methods to support their conclusions. Though they set out to draw very broad lessons, much of the focus ends up being on rifamycins. This is still a very interesting set of conclusions.

Strengths:

(1) A very interesting approach and set of questions.

(2) Outstanding technical approaches to measuring intracellular drug concentrations and chemical modification of rifamycins.

(3) Excellent characterization of variant rifamycin ADP-ribosyltransferases

Weaknesses:

(1) Figure 3c/d: These panels show the same experiment done twice, yet they display substantially different results in certain cases. For instance, M. smegmatis appears to show an order of magnitude lower RIF accumulation in panel d compared to M. flavescens, despite them displaying equal accumulation in panel c. The authors should provide justification for this variation, particularly as quantitative intra-species comparisons are central to the conclusions of this figure.

The data in panels 3c and 3d are from different sets of experiments. The reviewer is correct with regards to M. smegmatis. The data indeed is ~ 1 order of magnitude different. However, the data for other species is very similar. The reviewer may also have noticed that the error bars are also larger in 3d, compared to 3c, indicating a greater variation between independent experiments use in 3d. We do not have a good explanation for this, other than the experiments shown in 3d were associated with greater biological variability.

(2) There are several technical concerns with Figure 3 that affect how to interpret the work. According to the methods, the authors did not appear to normalize to an internal standard, only to an external antibiotic standard (which may account for some of the technical variation alluded to above).

We agree that using a labeled drug as an internal standard (IS) would be ideal. However, the experiment initially followed an untargeted metabolomics approach, which later shifted to relative drug quantification. At that stage, normalizing with IS was impractical because proper implementation would require multiple IS across the chromatographic range. Therefore, we opted for total ion current (TIC) normalization, which accounts for variability in overall metabolite abundance—even though the experimental setup was already adjusted for each bacterial species’ growth rate. Additionally, we prepared external standard curves for each drug to enable quantification, and the amount of drug added to each plate was considered when reporting these values.

Second, the authors used different concentrations of drug for each species to try to match the species' MICs. I appreciate the authors' thinking on this, but I think for an uptake experiment it would be more appropriate to treat with the same concentration of drug since uptake is likely saturable at higher drug concentrations. In the current setup, for the species with higher MIC, they have to be able to uptake substantially more antibiotics than the species with low MIC in order to end up with the same normalized uptake value in Figure 3d. It would be helpful to repeat this experiment with a single drug concentration in the media for all species and test whether that gives the same results seen here.

We respectfully disagree with the reviewer. Experiments such as the one proposed by the review work well when MIC values are a few fold apart, for strains of the same species, but have not been tested when MIC values are 100-1000-fold apart, with different species. Furthermore, what would be the interpretation of compound uptake at 1000-fold the MIC for one species and MIC level for another? By using antibiotic concentrations at the respective MIC for each species we are at least under conditions where we know the biological effect of the antibiotic across species is the same, based on its potency.

(3) Figure 4f: This panel seems to argue against the idea that the efficacy of RIF ribosylation is what's driving drug susceptibility. M. flavescens is similarly resistant to RIF as M. smegmatis, yet M. flavescens has dramatically lower riboslyation of RIF. This is perhaps not surprising, as the authors appropriately highlight the number of different rif-modifying enzymes that have been identified that likely also contribute to drug resistance. However, I do think this means that the authors can't make the claim that the resistance they observe is caused by rifamycin modification, so those claims in the text and figure legend should be altered unless the authors can provide further evidence to support them. This experiment also has results that are inconsistent with what appears to be an identical experiment performed in Supplemental Figure 5b. The authors should provide context for why these results differ.

In regard to enzyme efficiency, the apparent rate of all Arr-1 is relatively similar in converting RIF into ADP-Ribosyl-Rif between species. However, Arr-X is much more efficient when compared to Arr-1 in both M. flavescents and M. conceptionense. This is indicated by the apparent rate measured and displayed on figure 5c.

Proteomics data shows that there is upregulation of Arr-1 and Arr-X upon rifampicin treatment in M. flavescens and M. conceptionense. However, the same experiment was not performed in Arr-1 KD. Therefore, we can’t verify through this approach if the activity observed in vivo directly correlates with a higher expression of Arr-X alone. Of note, likely both enzymes contribute to resistance to rifamycins, as per our results with the Arr-X KD and sensitization of M. conceptionense to RIF.

Author response image 1.

It is also worth mentioning that there are other enzymes in the pathway of RIF ribosylation and their efficiency is unknown (Author response image 2). Therefore ADP-Ribosyl-RIF It is not an “end-metabolite” and maybe not the sole determinant of RIF resistance via ADP-ribosylation. Downstream enzymes can also account for the difference observed between M. flavescens and M. smegmatis.

Author response image 2.

It is correct that the Rifampicin MIC for M. flavescens is the same as M. smegmatis.

(4) Fig 4f/5c: M. flavescens has both Arr-1 and Arr-X, yet it appears to not have ribosylated RIF. This result seems to undermine the authors' reliance on the enzyme assay shown in Fig 5c - in that assay, M. flavescens Arr-X is very capable of modifying rifampicin, yet that doesn't appear to translate to the in vivo setting. This is of importance because the authors use this enzyme assay to argue that Arr-X is a fundamentally more powerful RIF resistance mechanism than Arr-1 and that it has specificity for rifabutin. However, the result in Figure 4f would argue that the enzyme assay results cannot be directly translated to in vivo contexts. For the authors to claim that Arr-X is most potent at modifying rifabutin, they could test their CRISPRi knockdowns of Arr-X and Arr-1 under treatment with each of the rifamycins they use in the enzyme assay. The authors mentioned that they didn't do this because all the strains are resistant to those compounds; however, if Arr-X is important for drug resistance, it would be reasonable to expect to see sensitization of the bacteria to those compounds upon knockdown.

The reviewer is reading Fig. 4f incorrectly, probably because it is plotted in a linear scale instead of logarithmic scale. Ribosylated Rif is present in M. flavescens, just at lower levels than M. conceptionense and M. smegmatis. In species where there is no Arr-1 or Arr-3, ribosylated RIF is not detected at all (e.g. M. tuberculosis), i.e., concentration is zero. Therefore, any detection of ribosylated RIF can be considered significant. In addition, as mentioned before, ADP-ribosylation of RIF is not the final product of the reaction and further studies need to be undertaken to understand subsequent reactions.

(5) Figure 5d: The authors use this CRISRPi experiment to claim that ArrX from M. conceptionanse is more potent at inactivating rifabutin than Arr-1. This claim depends on there being equal degrees of knockdown of Arr-1 and Arr-X, so the authors should validate the degree of knockdown they get. This is particularly important because, to my knowledge, nobody has used this system in M. conceptionanse before.

We agree with the reviewer that a qPCR should have been performed to define the extent of interference in the strain. generated Unfortunately, at this time a qPCR was not performed in the strains tested to confirm the extent of down regulation. Although it is the best practice to validate the strain KD, there is no indication that the effect observed is due to unspecific downregulation. The genetic environment in which Arr-X is positioned is different from Arr-1 and the targeting oligonucleotides are specific and would not promiscuously bind to Arr-1. Said that, this is indeed a fault in our setup.

(6) The authors' arguments about Arr-X and Arr-1 would be strengthened by showing by LC/MS that Arr-X knockdown in M. conceptionense results in more loss of ribosyl-rifabutin than knockdown of Arr-1.

We agree with the reviewer that performing the LC-MS analysis of the Arr-x knockdown would have strengthened the argument of our paper. Unfortunately, this experiment was not performed.

Reviewer #3 (Public review):

This manuscript presents a macroevolutionary approach to the identification of novel high-level antibiotic resistance determinants that takes advantage of the natural genetic diversity within a genus (mycobacteria, in this case) by comparing antibiotic resistance profiles across related bacterial species and then using computational, molecular, and cellular approaches to identify and characterize the distinguishing mechanisms of resistance. The approach is contrasted with "microevolutionary" approaches based on comparing resistant and susceptible strains of the same species and approaches based on ecological sampling that may not include clinically relevant pathogens or related species. The potential for new discoveries with the macroevolution-inspired approach is evident in the diversity of drug susceptibility profiles revealed amongst the selected mycobacterial species and the identification and characterization of a new group of rifamycin-modifying ADP-ribosyltransferase (Arr) orthologs of previously described mycobacterial Arr enzymes. Additional findings that intra-bacterial antibiotic accumulation does not always predict potency within this genus, that M. marinum is a better proxy for M. tuberculosis drug susceptibility than the commonly used saprophyte M. smegmatis, and that susceptibility to semi-synthetic antibiotic classes is generally less variable than susceptibility to antibiotics more directly derived from natural products strengthen the claim that the macroevolutionary lens is valuable for elucidating general principles of susceptibility within a genus.

There are some limitations to the work. The argument for the novelty of the approach could be better articulated. While the opportunities for new discoveries presented by the identification of discrepant susceptibility results between related species are evident, it is less clear how the macroevolutionary approach is further leveraged for the discovery of truly novel resistance determinants. The example of the discovery of Arr-X enzymes presented here relied upon foundational knowledge of previously characterized Arr orthologs. There is little clarity on what the pipeline for identifying more novel resistance determinants would look like. In other words, what does the macroevolutionary perspective contribute to discovery from the point of finding interspecies differences in susceptibility? Does the framework still remain distinct from other discovery frameworks and approaches? If so, how?

Thanks for pointing this out, as this is a critical feature of our study and method. Our approach relies on inter-species comparative genomics and phenotypes, and therefore, it is distinct from inter-strains comparison. This difference is dramatic, and it becomes clearer when we are comparing the core genome of M. tuberculosis (one species) 92% with the core genome of the genus, circa of 1%. While we focus on rifamycin in this manuscript, future manuscripts will investigate many of the other dozens of “inconsistencies” observed between the genetic makeup of different mycobacterial species and there actual performance in the presence of different antibiotics.

While the experimentation and analyses performed appear well-designed and rigorous, there are a few instances in which broad claims are based on inferences from sample sets or data sets that are too limited to provide robust support. For example, the claim that rifampicin modification, and precisely ADP-ribosylation, is the dominant mechanism of resistance to rifampicin in mycobacteria may be a bit premature or an over-generalization, as other enzymatic modification mechanisms and other mechanisms such as helR-mediated dissociation of rifampicin-stalled RNA polymerases, efflux, etc were not examined nor were CRISPRi knockdown experiments conducted beyond an experiment to tease out the role of Arr-X and Arr-1 in one strain. The general claim that intra-bacterial antibiotic accumulation does not predict potency in mycobacteria may be another over-generalization based on the limited number of drugs and species studied, but perhaps the intended assertion was that antibiotic accumulation ALONE does not predict potency.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Major comments

(1) The metabolomics is done using mycobacteria grown on filters. Initially, mycobacterial cells are grown on the filters for 5 doublings before being transferred to drug-containing (or free) agar for one doubling. Is this based on calculated doubling time in liquid culture or a true determination of the fact that the biomass increases to what would amount to 5 doublings?

The doubling time used is the one determined in liquid media. Although it is possible that the growth kinetics in solid media is slightly different from liquid (±10%), this experimental design is well established for M. tuberculosis (since Proc Natl Acad Sci U S A. 2010 May 25;107(21):9819-24.) and M. smegmatis (unpublished). Therefore, we used the growth rate as a proxy for having the same biomass of cells for each species tested. A maximum difference of 10% was observed between M. tuberculosis growth in liquid and in solid media, however, cells grow exponentially for much longer in filters. This makes filter-based experiments more reliable, as few growth phase-derived differences are present.

(2) The demonstration that intrabacterial drug concentrations vary between mycobacterial species in a manner not related to MIC for at least LZD and RIF, is an important finding. However, intrabacterial does not mean cytoplasmic since a considerable fraction could be present in the periplasmic/cell wall layers. Ideally, this would need to be determined but would of course be a massive undertaking since the method needs validation & optimization for each mycobacterial species. Nevertheless, this has to be mentioned. In addition, three drugs are limiting. Measuring additional drug concentrations in these 5 mycobacteria would at least establish some confirmation about the extent of this lack of correlation. Thus, could the authors measure concentrations of additional drugs with intracellular targets?

Testing additional drugs can be beneficial and would be an expansion of our paper, which will definitely be on future plans for further studies focusing on other antibiotics described here. It would also provide new insights into other possible mechanisms of resistance in mycobacterial species. However, in this study we aimed to first determine the antibiotic response profile in different mycobacterial species, and once we identified interesting resistance phenotypes that could not be readily explained by known mechanisms of resistance, we narrowed it down to certain drugs and species that would potentially provide insights into new mechanisms of antibiotic resistance. Finally, exploring drug concentration across multiple bacterial compartments is a dauting task and it has not been done extensively with any species, not to mention with multiple species, many of which are still lacking any study of their actual cell envelope.

(3) CRISPRi was used to reduce transcription in M. conceptionense. What was the level of gene downregulation?

As mentioned previously, a setback from our setup is that the level of KD was not measured at this instance.

Minor comments:

(1) The introduction mentions the fast and slow-growing mycobacteria which are classified based on the time that it takes to observe colonies on solid agar. However, in liquid medium, there is less correlation between the reported growth on agar and doubling time in liquid (Figure 1b, Figure 2d). This could be mentioned in the results section. In Figure 2d, the filled circles represent fast-growers but this does not hold well for liquid culture and it might make more sense to not distinguish between fast- and slow-growers in these graphs. A small complication would also be the fact that the doubling time represents growth in a liquid medium with Tyloxapol as a detergent whereas the MIC and metabolomics are done on solid agar with no detergent. The metabolomics is done after a doubling but for those where agar growth and liquid growth have large discrepancies in growth rate, there could be some differences.

Apologies for this misunderstanding. Fast- and slow-growth phenotypes are determined in Lowenstein-Jensen (LJ) agar, not in 7H10 agar (used in our study and most studies of mycobacteria). Furthermore, this is a qualitative definition, not a quantitative one. Therefore, our measurements do not need to correlate with fast- and slow-growth phenotypes, unless we had used that one specific medium. Furthermore, in liquid medium, we determined growth rate directly, which is never done with LJ medium.

In addition to adding the same amount of cells to each filter, we also perform TIC normalization, which should account for how rich the samples were – and therefore how much material we had. Therefore, we do not observe discrepancies due to differences in growth rate and the presence/absence of detergent in the media.

It is also worth mentioning that this experimental set up has been well established in many M. tuberculosis labs that study metabolism. Importantly, the use of detergent drastically affects mass spectrometry, and therefore cannot be used.

(2) Figure 1g in the text should be Figure 1f.

Apologies, it has been fixed.

(3) Figure S1 would be ideal to have in (supplementary) table format.

This data is now being provided in a table format.

(4) Table S1 - ethambutol misspelt.

Spelling has been corrected.

(5) MIC for species such as M. abscessus could depend on medium (7H9-based medium can give different MIC values than CAMH).

Indeed, different media can significantly change MIC values, and this is true for many bacterial species, if not all. For this study we used only species that could be grown in 7H9 broth containing 10 % ADC, 0.05% glycerol 0.05% tyloxapol and 7H10 plates containing 10% OADC and 0.05% glycerol. MIC₉₉ was determined in the latter as we found more efficient and robust to do our tests it in solid media. The goal of our experiment was not to the determined the “true” MIC for the antibiotics tested, as this value does not exist. It was to find lack of correlations between relative values and the presence of genes that can account for it.

(6) The statement "the experiment was performed at a concentration of antibiotic equal to its MIC" initially seems confusing. It was not equal to the MIC but performed at 6-fold the respective MIC of the species in question. Maybe re-phrasing this would help.

Apologies for this oversight. It has been corrected.

(7) Note that some mutations outside the RRDR (eg. V170F and I491F) can also cause Rif resistance.

Author response image 3.

A Rainbow diagram of RpoB X-Ray structure coloured according to sequence conservation. Dark purple indicates high conservation, whereas dark orange indicates low conservation. RIF (showed in magenta) is bound to RpoB. Zoomed view displays that the RIF-binding pocket is considerably conserved. B RpoB protein sequence has an 81bp region called Rifampicin Resistance Determining Region (RRDR) that is known to be important for RIF binding and is where most mutations occur in drug-resistant TB. Sequence alignment displays that the RRDR region is conserved with the exception of M. branderi, which has an Asn instead of a Ser residue in position 456 (numbering is related to the M. tuberculosis sequence), highlighted in bold.

Attached we have a structural alignment of RpoB of the species highlighted on this paper. Although there is variability within the sequences, which is also displayed in Author response image 3 with the conservation analysis, the residues that have been implicated with resistance (including V170 and I491) are conserved. Alignment sent on .fasta file that can be opened in jalview.

(8) Discuss how the RpoB S450N mutation in M. branderi confers the observed level of resistance.

That’s a great point, thank you. Now it reads as:

“The rifampicin (RIF) binding pocket is generally conserved, but Mycobacterium branderi has an S450N mutation in the RRDR region. While this specific mutation hasn't been found in clinical isolates, it's located at the binding site and may confer resistance (273). Although both serine (S) and asparagine (N) have similar side chains, related mutations like S450Q have been linked to resistance (156). Thus, M. branderi may be RIF-resistant due to this mutation. In contrast, M. conceptionense, M. flavescens, and M. smegmatis show no target sequence differences that explain their resistance”

(9) The statement that the three tested NTM are sensitive to rifabutin ("resistant to all rifamycins except for rifabutin") needs to be interpreted considering what sensitivity means. The MIC is still high (1.6-3.1 ug/mL) when compared to that of Mtb. The 2-fold differences in MIC between M. smegmatis and M. conceptionense do not really prove or disprove the role of Arr-X in rifabutin resistance.

We fixed the sentence to be more careful with the language on the text. We agree, but it is worth mentioning that generally with bacteria there is a regulation by the CLSI. Each bacterial species has a range that is considered sensitive or resistant, but these are not available for the species used in this study. In general, bacteria with MIC values above 8 µg/mL are considered resistant to rifampin (J Antibiot 2014 67:625).

(10) Figure 1d: It's hard to quantify the sensitivity of the plates. Can this be done by MIC? Was only rifabutin tested or also rifampicin?

The initial experiments described on the paper were all performed using Rifampicin only. Then, the MIC for the remaining rifamycins was determined for M. smegmatis, M. flavescens and M. conceptionense, and can be perused on “Supplementary table 4”. Figure 5d is to illustrate the effect of the KD in M. conceptionense sensitivity to rifabutin.

(11) Is there data to show the ADP-ribosylation of rifabutin in M. conceptionense and the CRISPRi strains?

Unfortunately, we did not perform LC-MS analysis on M. conceptionense CRISPRi strains exposed to rifabutin to measure potential ADP-ribosylation.

Reviewer #2 (Recommendations for the authors):

(1) It would be useful if the authors would complete Figure 1A by determining growth rates for the remaining 18 strains that they currently omitted.

These growth rates were obtained using roller bottles and in at least 3 independent experiments, unfortunately the throughput is far ideal. The goal of the experiment was to highlight difference in growth rate, beyond fast- and slow-growth, which we did. Adding the remaining values would not change this conclusion. Growth rate variation in 7H9 is significant and the point is made in our figure.

(2) The authors should justify their choice of species used in Figures 3-4. It would be useful to know, for instance, if the authors chose these species in an unbiased fashion, or if they were chosen because the authors had already determined that they possess rifamycin-modifying enzymes of interest. In that case, they wouldn't necessarily be a representative sample to use for the correlation analysis of antibiotic uptake and potency in Figure 3.

They were chosen because of their resistance profile for BDQ, LZD and RIF. This has been addressed in the text, which now reads “Given the antibiotic response profiles observed, we selected BDQ, LZD and RIF to explore the molecular causes of these dramatic changes in antibiotic potency observed across the Mycobacterium genus.”

(3) Figure 4b: The data in this panel appear inconsistent - for instance, M. houstonense appears to grow at 10X Mtb MIC, but fails to grow at 1X Mtb MIC. Repeating this experiment would better establish the validity of the authors' claims about the relative susceptibility of these strains to RIF.

The figures got rotated when exported from illustrator. Corrected figure is uploaded, and original plate photos are also uploaded for clarity.

(4) Figure 4e: Does Arr-X get upregulated in these proteomic datasets? The authors' argument that proteomic upregulation correlates with important drug resistance genes would imply that it might be, so that would be useful information to provide.

Arr-X is slightly upregulated, but not statistically significant – this could be due to the native expression of Arr-1. Data is displayed in a previous answer.

(5) I wasn't able to find the supplementary tables that the authors allude to - not sure if that was a file mixup, but those tables would be useful for interpreting the manuscript.

We are sorry that you couldn’t access the table. It must be a file corruption issues, as the other reviewers were able to. We will make sure that all tables are available and accessible.

(6) For LC/MS, the authors use peak height instead of peak area, which they argue correlates better with the amount of drug in cells because of the poor peak shape they observed for linezolid. This is not standard practice, so the authors should provide evidence to support this claim by running an LC/MS standard curve, then showing the correlation between peak height and amount of compound added as well as the correlation between peak area and compound.

Thank you for pointing that out, accuracy calculated and displayed. Both peak area and height can be used, but indeed area is standard practice.

(7) The authors should provide methods information about the LC column and the gradient settings used for LC-MS, as well as the settings of the MS.

The full method has been added to the paper.

Reviewer #3 (Recommendations for the authors):

I have only minor comments aside from the information in the Public Review:

(1) Results, section on Intra-bacterial antibiotic accumulation, line 8: "experiment was performed at a concentration of antibiotic PROPORTIONAL to its MIC" would be more accurate?

Agreed and adjusted according to Reviewer’s suggestion.

(2) Results, section on A minor role for pre-existing target modification, last sentence: the mere presence of RIF-ribosylating enzymes does not, in and of itself indicate that "RIF modification, and precisely ADP-ribosylation, is the dominant mechanism of resistance to RIF in mycobacteria", as other mechanisms and other forms of modifying enzymes are known to confer rifamycin resistance, with redundancy (e.g., other rifampicin-modifying enzymes, or helR-mediated dissociation of rifampicin-stalled RNA polymerases from DNA). It would be more appropriate to suggest the results presented to this point indicate RIF modification is common among mycobacteria. The evidence from the CRISPRi knockdown of Arrs shown in Fig 5d is the kind of evidence that suggests ribosylation as a dominant mechanism, at least against rifabutin in this particular species.

Absolutely, there are other possible modifying enzymes that could be encoded by these mycobacterial species. There is a possibility that M. flavescens and M. smegmatis encode for a putative helR (attached alignment) but further experiments would need to be carried out to confirm its ability to displace RIF in the RNAP. Interestingly, the presence of both Arr and HelR has been studied in M. abscessus and those mechanisms of resistance are independent from each other (Molecular Cell 2022 82(17):3166-3177.e5).

(3) Discussion, 2nd sentence needs grammatical editing.

Rephrased and it reads “Using our mycobacterial library, we identified for the first time high- and ultra-high-level intrinsic resistance (3) to many of the antibiotics tested. Of note, the resistant phenotype is naturally occurring and not a result of mutations due to exposure to the antibiotic in the clinic – which is the more traditional approach for probing mechanisms of antibiotic resistance. Our observations revealed that resistance profiles are highly variable across the genus and do not follow phylogeny, implicating HGT as the key mechanism for acquisition of resistance determinants and evolution of antibiotic resistance in mycobacteria (42).”

(4) Discussion, page 7, first line: the inclusion of LZD and BDQ in this statement seems at odds with Figure 2c and the statements in the first paragraph of page 5 highlighting these as examples of drugs to which most mycobacteria are susceptible.

Indeed, many of the species are susceptible, however the MIC₉₉ levels observed have never been reported before, and therefore we found it to be an interesting finding to highlight. From a treatment perspective, knowing which species are sensitive to which drugs is of course the most useful outcome of our study.

(5) The next sentence..."We found that resistance to these antibiotics in mycobacteria cannot be explained by uptake/efflux mechanisms..." is a bit of an over-generalization and conflicts with the evidence presented earlier that efflux could be playing a role in BDQ resistance and the published evidence establishing a clinically significant role for efflux-mediated BDQ resistance in M. tuberculosis, M. avium complex and M. abscessus complex.

We rephrased it to make it more specific to our findings. It reads “We found that resistance to these antibiotics in mycobacteria do not correlate with by uptake/efflux mechanisms in the species tested and it does not correlate with growth rate. Identification of mycobacterial species highly resistant to BDQ and LZD is worrisome as most of this species, if not all, have never been exposed to these drugs.”

(6) Methods, section on In vitro activity assay of Arr enzymes, line 1: reference(s) should be provided for previously reported methods.

Reference now added.

(7) Figure 2d: the low end of the susceptibility range is not well defined.

In this figure the susceptibility is not defined as the lowest area of the graph, but the lower concentrations are indeed harder to be defined. Hopefully supplementary figure 1 and the additional table containing the MIC can be informative to address this comment.

(8) Figures 3c,d: the presentation of the relative antibiotic concentrations could be harmonized between the graphs in 3c and those in 3d to enable a more ready comparison.

We disagree. The goal of these different panels is exactly to illustrate two distinct points. C gives the relative concentration of antibiotic, while D correlates relative concentration with MIC99. The use of log scale in D further clarifies that there is no correlation between intracellular antibiotic concentration and potency (MIC). This information is not present in C.

(9) Figure 4f and Supplementary Figure 5b: it is difficult to understand the limited amount of ribsosyl-RIF in M. flavescens in Fig 4f relative to Supplementary Figure 5b (esp. when considering M. smeg as a common comparator); and, further, to understand the seeming lack of correlation between RIF susceptibility, ribosylation and Arr number and catalytic efficiency for these two strains without considering additional resistance mechanisms.

In reality the difference between figure 4f and Supplementary figure 5b is mainly due to M. smegmatis – that has an apparent lower production of ribosyl-RIF in the experiment described in the supplementary figure. The values for M. flavescens are relatively similar. In addition, the ADP-Ribosyl-RIF is not the final metabolite of the pathway.

In regards of having the entire picture, it is true that we were unable to completely unravel and correlate MIC value, expression of Arr-1, expression of Arr-3, efficiency of each enzyme, production of ADP-Ribosyl-RIF and the presence of other possible mechanisms of resistance and this is indeed a setback in our study, and of most studies ever published, which usually focus on one resistant determinant.

eLife Assessment

This valuable study used genetic and pharmacological manipulations of insulin/IGF signaling in renal glomerular podocytes to address the role of insulin/IGF axis in podocytes. Solid data are presented to demonstrate that co-inhibition of insulin/IGF signaling in podocytes led to aberrant splicing of mRNAs, which could contribute to the loss of podocytes in vitro and in vivo in mice. As it stands, the study lacks the assessment of developmental phenotype of podocytes in the mouse model.

[Editors' note: this paper was reviewed by Review Commons.]

Reviewer #1 (Public review):

Summary:

In this manuscript, the role of the insulin receptor and the insulin growth factor receptor was investigated in podocytes. Mice, where both receptors were deleted, developed glomerular dysfunction and developed proteinuria and glomerulrosclerosis over several months. Because of concerns about incomplete KO, the authors generated and studied podocyte cell lines where both receptors were deleted. Loss of both receptors was highly deleterious with greater than 50% cell death. To elucidate the mechanism of cell death, the authors performed global proteomics and found that spliceosome proteins were downregulated. They confirmed this directly by using long-read sequencing. These results suggest a novel role for insulin and IGF1R signaling in RNA splicing in podocytes.

This is primarily a descriptive study and no technical concerns are raised. The mechanism of how insulin and IGF1 signaling regulates splicing is not directly addressed but implicates potentially the phosphorylation downstream of these receptors. In the revised manuscript, it is shown that the mouse KO is incomplete potentially explaining the slow onset of renal insufficiency. Direct measurement of GFR and serial serum creatinines might also enhance our understanding of progression of disease, proteinuria is a strong sign of renal injury. An attempt to rescue the phenotype by overexpression of SF3B4 would also be useful but may be masked by defects in other spliceosome genes. As insulin and IGF are regulators of metabolism, some assessment of metabolic parameters would be an optional add-on.

Significance:

With the GLP1 agonists providing renal protection, there is great interest in understanding the role of insulin and other incretins in kidney cell biology. It is already known that Insulin and IGFR signaling play important roles in other cells of the kidney. So, there is great interest in understanding these pathways in podocytes. The major advance is that these two pathways appear to have a role in RNA metabolism.

Comments on revised version:

I'm satisfied with the revised manuscript and the responses to my previous concerns.

Reviewer #2 (Public review):

Summary:

In this manuscript, submitted to Review Commons (journal agnostic), Coward and colleagues report on the role of insulin/IGF axis in podocyte gene transcription. They knocked out both the insulin and IGFR1 mice. Dual KO mice manifested a severe phenotype, with albuminuria, glomerulosclerosis, renal failure and death at 4-24 weeks.

Long read RNA sequencing was used to assess splicing events. Podocyte transcripts manifesting intron retention were identified. Dual knock-out podocytes manifested more transcripts with intron retention (18%) compared wild-type controls (18%), with an overlap between experiments of ~30%.

Transcript productivity was also assessed using FLAIR-mark-intron-retention software. Intron retention w seen in 18% of ciDKO podocyte transcripts compared to 14% of wild-type podocyte transcripts (P=0.004), with an overlap between experiments of ~30% (indicating the variability of results with this method). Interestingly, ciDKO podocytes showed downregulation of proteins involved in spliceosome function and RNA processing, as suggested by LC/MS and confirmed by Western blot.

Pladienolide (a spliceosome inhibitor) was cytotoxic to HeLa cells and to mouse podocytes but no toxicity was seen in murine glomerular endothelial cells.

The manuscript is generally clear and well-written. Mouse work was approved in advance. The four figures are generally well-designed, bars/superimposed dot-plots.

Methods are generally well described.

Comments on revised version:

Coward and colleagues have done an excellent job of responding to all the reviewer comments.

Reviewer #4 (Public review):

Summary and background:

This report entitled "The insulin/IGF axis is critically important (for) controlling gene transcription in the podocyte" from Hurcombe et al is based on a mouse double knockdown of the IR and IGF1R and a parallel cultured mouse podocyte model. Insulin/IGF signaling system in mammals evolved as three gene reduplicated peptides (insulin, IGF-1, and IGF-2) and their two receptors IR and IGF1R that cross-react to variable extents with the peptides, are ubiquitously expressed, and signal through parallel pathways. The major downstream effect of insulin is to regulate glucose uptake and metabolism, while that of the IGF pathways is to regulate growth and cell cycling in part through mTORC1. The GH-IGF-1-IGF1R pathway regulates post-natal growth. IGF-2 signaling is thought to play a major role in regulating intrauterine growth and development, although IGF-2 is also present at high levels in post-natal life. Thus, one would anticipate that reducing IR/IGF1R signaling in any cell would slow growth and cell cycling by reducing growth factor and metabolic mTORC1-mediated and other processes including the splicing of RNA for protein synthesis.

Mouse IR/IGF1R double knockdown model:

A double knockdown mouse model was generated by interbreeding mice with different genetic backgrounds carrying floxed sites for IR and IGF-1R to produce mixed background offspring with both floxed IR and IGF-1R genes. These mice were crossed so that the podocin promoter driven-Cre (that comes on at about embryonic day 12 bas podocytes are developing) would delete IR and IGF-1R genes. Since podocin is believed to be an absolutely podocyte-specific protein, this podocin promoter this is predicted to specifically knock down the IR and IGF1R genes only in podocytes. The weight and growth of double KO offspring was not different from controls, but some proportion of the double knockdown mice subsequently developed proteinuria by 6 months and 20% died, although no specific data is provided to identify the cause of the deaths since eGFR was not decreased. Surviving mice were evaluated at 6 months of age. The efficacy of knockdown was not demonstrated in the mouse model itself, although a temperature-sensitive cell line developed from these double knockdown mice showed that expression of IR and IGF-1R proteins in the Cre-treated cell line were both reduced by about 50% (no statistical analysis of this result provided). In the knockout mice, proteinuria was significantly increased by 6 months, but not at earlier time points. Histologic analysis showed proteinaceous casts, glomerulosclerosis and interstitial fibrosis. Podocyte number was stated to be reduced by about 30% in double knockdown mice, although the method by which this was evaluated seems to have been by counting WT1 positive nuclei in glomerular cross-sections, an approach that is well-known not to be a reliable way of assessing true podocyte number. No information is provided about podocyte size, density or glomerular volume.

Comment: If IR/IGF1R deletion plays a significant role in normal podocyte function sufficient to cause proteinuria and glomerulosclerosis then the effect of reduced IR and IGF1R protein expression on podocyte function would have been expected to produce a phenotype before 6 months. A more likely scenario to explain the overall result is that deleting the IR and IGF1R genes at about embryonic day12 impacted podocyte development to a variable extent such that some mice developed fewer podocytes per glomerulus than other mice. As mice grow and their glomeruli and glomerular capillary area increases, those mice with fewer podocytes would not be able to completely cover the filtration surface with foot processes and would develop proteinuria and glomerulosclerosis. If reduced podocyte number per glomerulus is the proximate cause of the observed proteinuria, then modulation of the body and kidney growth rate by calorie restriction to slow growth (lower circulating IGF-1 levels) would be expected to be protective, while a high protein high calorie diet (higher circulating IGF-1 levels) or uni-nephrectomy to increase kidney growth rate would be expected to enhance proteinuria and glomerulosclerosis.

The model as used may be more representative of a variable degree of podocyte depletion than an effect of impaired IR/IGF1R signaling. Therefore, although the phenotype may be ultimately attributable to the IR/IGF1R gene deletions the proteinuria and glomerulosclerotic phenotype itself was probably a consequence of defective podocyte development. Examining podocyte number, size, density and glomerular volume at earlier time points (4 weeks) would help to answer this question. Therefore, a more appropriate title would be "The insulin/IGF axis is critically important (for) normal podocyte development and deployment". In this context the effect of the knockdowns on splicing would make more sense.

Cell culture studies. A cell line was generated using a temperature sensitive SV40 system that has been previously reported from this laboratory. A detailed analysis is provided to show that double knockout cells exhibited abnormal spliceosome activity. This forms the basis for the conclusion that "The insulin/IGF axis is critically important (for) controlling gene transcription in the podocyte". There are several concerns that weaken this conclusion.

(1) In the double knockdown cell culture system about 30% of cells were "lost" by 3 days and about 70% of cells were "lost" by 5days. The studies were done at the 3 day time point. It is not clear whether "lost" cells were in the process of dying, stress-induced detachment, or just growing more slowly than control due to reduced IR and IGF-1R signaling. These processes could have impacted splicing in a non-specific way independent of IR/IGF1R signaling itself.

(2) Can a single cell line derived from the double floxed mice be relied on to provide an unbiased picture of the effect of deleting IR and IGF-1R? Presumably, the transfection and selection process will select for cells that survive thereby including unknown biases, possibly related to spliceosome function. Is a single cell line adequate? These investigators have extensive experience with this type of analysis, but this question is not addressed in the discussion.

(3) To determine whether the effect is specific to reduced IR/IGFR signaling the deletion of IR and IGF-1R could be corrected by transfecting full length IR and IGF-1R cDNAs into the cells to restore normal IR/IGF1R signaling. If transfected cells with intact IR and IGF-1R expression and activity returns spliceosome activity to normal this would be evidence that receptors themselves play some role in spliceosome activity, as opposed to the downstream effect on growth limitation/stress on the cells.

(4) Other ways of testing whether the splicing effect is specifically due to reduced IR/IGF-1R signaling would be to (a) block IR and IGF1R receptors using available inhibitors, (b) remove or reduce insulin, IGF-1 and IGF-2 levels in the culture medium, (c) use low glucose and amino acid culture medium to slow growth rate independent of receptor function, (d) or block intra-cellular signaling via the IR and IGF-1R receptors through mTORC1 inhibition using rapamycin or other signaling targets.

(5) It would be useful to determine whether the cultured cells stressed in other ways (e.g. ischemia, toxins, etc.) also results in the same splicing abnormalities.

Author response:

The following is the authors’ response to the original reviews

Many thanks for your helpful and constructive comments for our work examining the effect of inhibiting both the insulin receptor (IR) and IGF1 receptor (IGF1R) in the podocyte. We are pleased to submit an updated manuscript addressing your concerns.

(1) A major concern was a lack of mechanistic insight into how deletion (or knock-down) of both receptors caused the spliceosomal phenotype (Reviewer 1 and Reviewer 3).

We now think this is due to the lack of a network of insulin/IGF phospho-signalling events to a variety of spliceosomal proteins and kinases. The reasons for this are as follows:

A. Since submitting our paper Turewicz et al have published a comprehensive phospho-proteomic paper examining the effects of 100nM insulin on human primary myotubes (DOI: 10.1038/s41467-025-56335-6). They discovered that multiple post-translational phosphorylation events occur in a variety of spliceosomal proteins at differing time points (1 minute to 60 minutes). Furthermore, they show that mRNA splicing is rapidly modified in response to insulin stimulation in their cells. This follows elegant work from Bastista et al who studied diabetic and non-diabetic iPSC derived human myositis and also detected a spliceosome phosphorylation signature (DOI: 10.1016/j.cmet.2020.08.007).

B. We have examined phospho-proteosome changes that occur in wild -type podocytes (expressing both the IR and IGF1R) compared to double (IR and IGF1R) knockout cells using phosho-proteomics. We have done this 3 days after inducing receptor knockdown, before major cell loss, and have stimulated the cells with either 10nM insulin or 100mg IGF1.

Interestingly, we detected several post-translational modifications (PTM) in our data set that are also present in Turewicz’s studies. Of note, 100nM insulin (as used by Turewicz) will signal through both the insulin and IGF1 receptor (and hybrid Insulin/IGF1 receptors) which is relevant to our studies.

Our work shows a cascade of phospho- signalling events affecting multiple components of the spliceosomal complex and evidence of kinase modulation (phosphorylation) (New Figure 7 and supplementary Figure 5). Also new results section in paper (lines 391-425 in track changes version). We acknowledge that we only studied a single time point after stimulation (10 minutes) and could have missed other PTM in the spliceosomal complex and other kinases. This is mentioned in our new limitations of study section (lines 595-606). This will be a focus of future work. We did not find major PTM differences when stimulating with either insulin or IGF1 in our studies and suspect that the doses of insulin (10nM) and IGF1 (100mg) used are still able to signal through cognate receptors.

Furthermore, we have examined the relative contributions of the insulin and IGF1 receptor in detail in the model (addressed in point 13 below).

(2) The phenotype of the mouse is only superficially addressed. The main issues are that the completeness of the mouse KO is never assessed nor is the completeness of the KO in cell lines. The absence of this data is a significant weakness. (Reviewer 1)

We apologise for not making this clear, but we did assess the level of receptor knockdown in both the animal and cell models. The in vivo model showed variable and non-complete levels of insulin receptor and IGF1 receptor podocyte knock down (shown in supplementary Figure 1C). This is why we made the in vitro floxed podocyte cell lines in which we could robustly knockdown both the IR and IGF1R. We show this using Western blotting (shown in Figure 2A). We agree that calling the models knockout is misleading and have changed all to knock down (KD) now.

(3) The mouse experiments would be improved if the serum creatinine’s were measured to provide some idea how severe the kidney injury is. (Reviewer 1)

There is variability in creatinine levels which is not uncommon in transgenic mouse models (probably partly due to variability in receptor knock down levels with cre-lox system). This is part of rationale of developing the robust double receptor knockout cell models where we robustly knocked out both receptors by >80%. We have added measured creatinine levels in a subset of mice in supplementary data (New Supplementary Figure 1E) and mention this in the text (lines 285-286). As some mice died we expect they may have developed acute kidney injury, but we did not serially measure the creatinine’s in every mouse over time. We could have assessed the GFR in a more sensitive way to look at differences. However, we consider the highly significant levels of albuminuria and histological damage observed in our models show a significant kidney phenotype.

(4) An attempt to rescue the phenotype by overexpression of SF3B4 would also be useful. If this didn't work, an explanation in the text would suffice. (Reviewer 1).

We did consider doing this but on reflection think it is very unlikely to rescue the phenotype as an array of different spliceosomal proteins quantitatively changed and were differentially phosphorylated / dephosphorylated throughout the complex (as we hope our revised work illustrates now). We think a single protein rescue is highly unlikely to work. We hope this is an appropriate explanation for this action. We have mentioned this in the text now in our discussion (lines 601-602).

(5) As insulin and IGF are regulators of metabolism, some assessment of metabolic parameters would be an optional add-on. (Reviewer 1).

Thank you for this suggestion. We did not extensively examine the metabolism of the mice however we did perform blood glucose measurement and weight which are included in the paper (Figure 1A and Figure 1B).

(6) The authors should caveat the cell experiments by discussing the ramifications of studying the 50% of the cells that survive vs the ones that died. (Reviewer 1).

We appreciate this and this was the rationale behind cells being studied after 3 days differentiation for total and phospho-proteomics before significant cell loss to avoid the issue of studying the 50% of cells that survive (which happened at 7 days). We have made this clearer in the manuscript. We also have added the data showing less cell death at 3 days in the cell model (New Supp Figure 2B).

(7) It would be helpful to say that tissue scoring was performed by an investigator masked to sample identity. (Reviewer 2)

We did this and have added to manuscript (line 113).

(8) Data are presented as mean/SEM. In general, mean/SD or median/IQR are preferred to allow the reader to evaluate the spread of the data. There may be exceptions where only SEM is reasonable. (Reviewer 2)

All graphs have now been changed to SD rather than SEM.

(9) It would be useful to for the reader to be told the number of over-lapping genes (with similar expression between mouse groups) and the results of a statistical test comparing WT and KO mice. The overlap of intron retention events between experimental repeats was about 30% in both knock-out podocytes. This seems low and I am curious to know whether this is typical for this method; a reference could be helpful. (Reviewer 2)

This is an excellent question. We had 30% overlap as the parameters used for analysis were very stringent. We suspect we could get more than 30% by being less stringent, which still be considered as similar events if requested. Our methods were based on FLAIR analysis (PMID: 32188845). We have added this reference to the manuscript (Line 242 & 680).

(10) With the GLP1 agonists providing renal protection, there is great interest in understanding the role of insulin and other incretins in kidney cell biology. It is already known that Insulin and IGFR signaling play important roles in other cells of the kidney. So, there is great interest in understanding these pathways in podocytes. The major advance is that these two pathways appear to have a role in RNA metabolism, the major limitations are the lack of information regarding the completeness of the KO's. If, for example, they can determine that in the mice, the KO is complete, that the GFR is relatively normal, then the phenotype they describe is relatively mild. (Reviewer 1)

Thank you. The receptor knock-out (KO) in the mice is highly unlikely to be complete (Please see comments above and Supplementary Figure 1C). There are many examples of “KO” animal models targeting other tissues showing that complete KO of these receptors seems difficult to achieve, particularly in reference to the IGF1 receptor. In the brain, which also contains terminally differentiated cells, barely 50% of IGF1R knockdown was achieved in the target cells (PMID:28595357). In ovarian granulosa cells (PMID:28407051) -several tissue specific drivers tried but couldn't achieve any better than 80%. The paper states that 10% of IGF1R is sufficient for function in these cells so they conclude that their knockdown animals are probably still responding to IGF1. Finally, in our recent IGF1R podocyte knockdown model we found Cre levels were important for excision of a single homozygous floxed gene (PMID: 38706850) hence we were not surprised that trying to excise two homozygous floxed genes (insulin receptor and IGF1 receptor) was challenging. This was the rationale for making the double receptor knockout cell lines to understand processes / biology in more detail. As stated earlier, we have changed our description of the mice and cell lines from knock-out to knock-down throughout the revised manuscript as this is more accurate.

(11) For the in vivo studies, the only information given is for mice at 24 weeks of age. There needs to be a full-time course of when the albuminuria was first seen and the rate of development. Also, GFR was not measured. Since the podocin-Cre utilized was not inducible, there should be a determination of whether there was a developmental defect in glomeruli or podocytes. Were there any differences in wither prenatal post-natal development or number of glomeruli? (Reviewer 3)

We have added further urinary Albumin:creatinine ratio (uACR) data at 12, 16 and 20 weeks to manuscript. We do not think there was a major developmental phenotype as albuminuria did not become significantly different until several months of age (new Supp Figure 1B). We did consider using a doxycycline inducible model but we know the excision efficiency is much less than the constitutive podocin-cre driven model Author response image 1. This would likely give a very mild (if any) phenotype when attempting to knockout both receptors and not reveal the biology adequately. We acknowledge the weaknesses of the animal model and this was the rationale for generating the cell models.

(12) Although the in vitro studies are of interest, there are no studies to determine if this is the underlying mechanism for the in vivo abnormalities seen in the mice. Cultured podocytes may not necessarily reflect what is occurring in podocytes in vivo. (Reviewer 3)

This is a good point. We have now immune-stained the DKD and WT mice for Sf3b4 (a spliceosomal change in our in vitro proteomics) and also find a significant reduction in this protein in podocytes of the DKD mice (New Figure 3F).

(13) Given that both receptors are deleted in the podocyte cell line, it is not clear if the spliceosome defect requires deletion of both receptors or if there is redundancy in the effect. The studies need to be repeated in podocyte cell lines with either IR or IGFR single deletions. (Reviewer 3)

We have now performed proteomics and phospho-proteomics in all 4 cell types (Wild-type, Insulin receptor knock down, IGF1R knockdown and double knockdown) at 3 days (New Figure 8 and supplementary Figure 6. Also new results section lines 425 to 450). This shows that both receptors contribute to the pathways (and hence there is a high level of compensation built into the system). For total proteins we detected that spliceosomal tri-snRNP was only reduced when both receptors were lacking but other proteins / pathways had an incremental effect of losing the insulin or IGF1 receptor. Likewise, the spliceosomal phospho-signaling events can go through either the insulin or igf1 receptors predominantly or through both. We think this reflects the complexity of this system and how evolutioatily it has developed in mammals to protect against its loss.

Finally in revision we have rewritten the discussion with a “limitations of the study” section and hopefully in an easier to read fashion for the readership.

Author response image 1.

(A) mT/mG reporter mouse crossed to constitutional podocin Cre heterozygous mouse. Illustrates podocyte specificity for Cre driver and excision Of reporter Figure shows GFP expression in Cre producing cells (top panel scale bar=250vm; bottom panel scale bar=50pm). Cre expression causes GFP to be switched on. (B) mT/mG reporter mouse crossed to podocin RtTA— tet-o-cre heterozygous mouse shows podocyte specificity for driver and approximately 60% excision. (top and bottom panels scale bar=250pm; middle panel scale bar=50pm). Doxycycline required for expression showing not leaky.

eLife Assessment

In this valuable study, through carefully executed and rigorously controlled experiments, the authors challenged a previously reported role of the Death Receptor 6 (DR6/Tnfrsf21) in Wallerian degeneration (WD). Using two DR6 knockout mouse lines and multiple WD assays, both in vitro and in vivo, the authors provided convincing evidence that loss of DR6 in mice does not protect peripheral axons from WD after injury, at least in the specific contexts of the mice and analyses performed in this study. Due to the lack of certain specific parameters from previous studies (sex, age, mouse strains etc.), the exact reasons underlying the observed inconsistencies between current and previous reports on the protective effects of DR6 remains to be determined. Overall, this is a carefully executed study providing invaluable information toward understanding DR6's role (or lack thereof) in axon degeneration.

Reviewer #1 (Public review):

Summary:

The authors show that genetic deletion of the orphan tumor necrosis factor receptor DR6 in mice does not protect peripheral axons against degeneration after axotomy. Similarly, Schwann cells in DR6 mutant mice react to axotomy similarly to wild type controls. These negative results are important because previous work has indicated that loss or inhibition of DR6 is protective in disease models and also against Wallerian degeneration of axons following injury. This carefully executed counterexample is important for the field to consider.

Strengths:

A strength of the paper is the use of two independent mouse strains that knockout DR6 in slightly different ways. The authors confirm that DR6 mRNA is absent in these models (western blots for DR6 protein are less convincingly null, but given the absence of mRNA, this is likely an issue of antibody specificity). One of the DR6 knockout strains used is the same strain used in a previous paper examining the effects of DR6 on Wallerian degeneration.

The authors use a series of established assays to evaluate axon degeneration, including light and electron microscopy on nerve histological samples and cultured dorsal root ganglion neurons in which axons are mechanically severed and degeneration is scored in time lapse microscopy. These assays consistently show a lack of effect of loss of DR6 on Wallerian degeneration in both mouse strains examined.

Additional strengths are that the authors examine both the axonal response and the Schwann cell response to axotomy and use both in vivo and in vitro assays.

Therefore, these experiments, the author's data support their conclusion that loss of DR6 does not protect against Wallerian degeneration.

Weaknesses:

A weakness of this paper is that no effort is made to determine why the results presented here may differ from previous studies. A notable possibility is that the original mouse strain that showed 5 of 13 mice being protected from Wallerian degeneration was studies on a segregating C57BL/6.129S background.

Finally, it is important to note that previously reported effects of DR6 inhibition, such as protection of cultured cortical neurons from beta-amyloid toxicity, are not necessarily the same as Wallerian degeneration of axons distal to an injury studied here. The negative results presented here showing that loss of DR6 is not protective against Wallerian degeneration induced by injury are important given the interest in DR6 as a therapeutic target. However, care should be taken in attempting to extrapolate these results to other disease contexts such as ALS or Alzheimer's disease.

Reviewer #3 (Public review):

Summary:

The authors revisit the role of DR6 in axon degeneration following physical injury (Wallerian degeneration), examining both its effects on axons and its role in regulating the Schwann cell response to injury. Surprisingly, and in contrast to previous studies, they find that DR6 deletion does not delay the rate of axon degeneration after injury, suggesting that DR6 is not a mediator of this process.

Overall, this is a valuable study. As the authors note, the current literature on DR6 is inconsistent, and these results provide useful new data and clarification. This work will help other researchers interpret their own data and re-evaluate studies related to DR6 and axon degeneration.

Strengths:

(1) The use of two independent DR6 knockout mouse models strengthens the conclusions, particularly when reporting the absence of a phenotype.

(2) The focus on early time points after injury addresses a key limitation of previous studies. This approach reduces the risk of missing subtle protective phenotypes and avoids confounding results with regenerating axons at later time points after axotomy.

Comments on revisions:

I thank the authors for their thorough responses to my previous comments. The revisions have addressed the points raised and have improved the clarity and overall quality of the manuscript. I appreciate the effort taken to strengthen the presentation of the work.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors show that genetic deletion of the orphan tumor necrosis factor receptor DR6 in mice does not protect peripheral axons against degeneration after axotomy. Similarly, Schwann cells in DR6 mutant mice react to axotomy similarly to wild-type controls. These negative results are important because previous work has indicated that loss or inhibition of DR6 is protective in disease models and also against Wallerian degeneration of axons following injury. This carefully executed counterexample is important for the field to consider.

Strengths:

A strength of the paper is the use of two independent mouse strains that knock out DR6 in slightly different ways. The authors confirm that DR6 mRNA is absent in these models (western blots for DR6 protein are less convincingly null, but given the absence of mRNA, this is likely an issue of antibody specificity). One of the DR6 knockout strains used is the same strain used in a previous paper examining the effects of DR6 on Wallerian degeneration.

The authors use a series of established assays to evaluate axon degeneration, including light and electron microscopy on nerve histological samples and cultured dorsal root ganglion neurons in which axons are mechanically severed and degeneration is scored in time-lapse microscopy. These assays consistently show a lack of effect of loss of DR6 on Wallerian degeneration in both mouse strains examined.

Therefore, in the specific context of these experiments, the author's data support their conclusion that loss of DR6 does not protect against Wallerian degeneration.

Weaknesses:

(1) The major weaknesses of this paper include the tone of correcting previously erroneous results and the lack of reporting on important details around animal experiments that would help determine whether the results here really are discordant with previous studies, and if so, why.

The authors do not report the genetic strain background of the mice used, the sex distributions of their experimental cohorts, or the age of the mice at the time the experiments were performed. All of these are important variables.

(Response 1) We thank the reviewer for emphasizing the importance of reporting the sex, age, and genetic background of the experimental animals used in our axon protection analyses. We have incorporated this information into the revised manuscript wherever available. The sole exception concerns the genetic background of the conditional DR6 mice generated by Genentech, which remains unknown. The original publication describing these mice (Tam et al., 2012, Dev Cell, PMID 22340501) did not report this information, and we were unable to obtain it directly from Genentech. Details regarding the genetic background of the Wld^S and aPhr1 mutant mice are provided in their respective original publications, which are cited in our manuscript. Because the Gamage et al. study from the Deppmann laboratory did not report the sex or age of the animals used, we were unable to assess whether these variables might contribute to the differences observed between the two studies. Moreover, we are not aware of published evidence identifying sex or age as modifiers of structural axon preservation in axotomized peripheral nerve stumps in mouse models of delayed Wallerian degeneration. Furthermore, in the original publications describing the phenotypes of transgenic Nmnat2 and Wld^S mice, as well as Sarm1 or Phr1 knockout mice, sex and age of the animals used in the Wallerian degeneration assays were not reported (PMIDs 23995269, 12106171, 22678360, 23665224). Although, to our knowledge, no large-scale systematic studies have been conducted, over the last 15 years we have never observed any sex-based differences in Wallerian degeneration phenotypes in these mutants exhibiting prominent axon protection. This topic was discussed informally at conferences, and we are also not aware of other investigators having observed such effects.

In response to the reviewer’s comment regarding “tone”, we made sure that our data and interpretations are presented in a professional, balanced, and objective manner, including a detailed discussion of potential alternative explanations for the discrepant findings.

(2) The DR6 knockout strain reported in Gamage et al. (2017) was on a C57BL/6.129S segregating background. Gamage et al. reported that loss of DR6 protected axons from Wallerian degeneration for up to 4 weeks, but importantly, only in 38.5% (5 out of 13) mice they examined. In the present paper, the authors speculate on possible causes for differences between the lack of effect seen here and the effects reported in Gamage et al., including possible spontaneous background mutations, epigenetic changes, genetic modifiers, neuroinflammation, and environmental differences. A likely explanation of the incomplete penetrance reported by Gamage et al. is the segregating genetic background and the presence of modifier loci between C57BL/6 and 129S. The authors do not report the genetic background of the mice used in this study, other than to note that the knockout strain was provided by the group in Gamage et al. However, if, for example, that mutation has been made congenic on C57BL/6 in the intervening years, this would be important to know. One could also argue that the results presented here are consistent with 8 out of 13 mice presented in Gamage et al.

(Response 2) As noted above, we now provide information on the genetic background of the mice in the revised manuscript, where available. We have not backcrossed the constitutive DR6 knockout mice obtained from the Deppmann laboratory (Gamage et al.) to a C57BL/6 background; our colony was maintained primarily through intercrosses of heterozygous animals. Similarly, the conditional DR6 mutant mice used in this study were also not backcrossed to C57BL/6 mice.

We respectfully hold a different view regarding the reviewer’s final point. We understand it is not appropriate to infer consistency between two datasets by disregarding the subset of results that do not align. By the same logic, it would be flawed to draw conclusions from the Gamage et al. study based solely on the single Wld^S mouse out of five that did not show axon preservation after nerve injury. Selectively omitting conflicting data does not provide a valid basis for establishing phenotype concordance across studies.

To further strengthen our study, we note that we performed additional analyses on three more nerve samples from constitutive DR6 null mice during the revision process and have incorporated the resulting data in Fig. 1.

(3) Age is also an important variable. The protective effects of the spontaneous WldS mutation decrease with age, for example. It is unclear whether the possible protective effects of DR6 also change with age; perhaps this could explain the variable response seen in Gamage et al. and the lack of response seen here.

(Response 3) As discussed above, we now provide the age information for the mice used for the Wallerian degeneration assessments in the respective figure legends. To our knowledge, there are no prior reports suggesting that age is a significant determinant of structural axon preservation in the indicated mutants. Electrophysiological function and neuromuscular junction preservation decrease with age in axotomized Wld^S mice (e.g., PMIDs 12231635, 19158292, 15654865), but these parameters are not subject of our study, and we have not studied them. Unfortunately, a direct comparison of ages between our DR6 mutant mice and those used in Gamage et al. (2017) is not possible, as the earlier study from the Deppmann laboratory did not report this information.

(4) It is unclear if sex is a factor, but this is part of why it should be reported.

(Response 4) We now report the requested sex information for our axon preservation analyses during nerve injury-induced Wallerian degeneration in the DR6 mouse models in Figs. 1 and 2.

(5) The authors also state that they do not see differences in the Schwann cell response to injury in the absence of DR6 that were reported in Gamage et al., but this is not an accurate comparison. In Gamage et al., they examined Schwann cells around axons that were protected from degeneration 2 and 4 weeks post-injury. Those axons had much thinner myelin, in contrast to axons protected by WldS or loss of Sarm1, where the myelin thickness remained relatively normal. Thus, Gamage et al. concluded that the protection of axons from degeneration and the preservation of Schwann cell myelin thickness are separate processes. Here, since no axon protection was seen, the same analysis cannot be done, and we can only say that when axons degenerate, the Schwann cells respond the same whether DR6 is expressed or not.

(Response 5) We appreciate the reviewer’s detailed comments. Our intention was not to directly compare our findings with those of Gamage et al. regarding the myelin behavior at these time points (because we never observed axon protection), but rather to note that we did not observe any DR6-dependent alterations in Schwann cell responses under conditions where axons undergo normal Wallerian degeneration. As the reviewer correctly points out, Gamage et al. analyzed Schwann cell myelin surrounding axons that were protected from degeneration for extended periods, a context fundamentally different from the complete lack of axon protection observed in our DR6-deficient models. Therefore, the specific dissociation between axon preservation and myelin maintenance claimed by Gamage et al. cannot be evaluated in our study. A statement to make this point clearer has been incorporated in the revised manuscript.

We fully agree with the reviewer’s concluding point: in our experiments, once axons degenerate, Schwann cell responses proceed similarly regardless of DR6 expression. This agreement reinforces one of the central conclusions of our work.

(6) The authors also take issue with Colombo et al. (2018), where it was reported that there is an increase in axon diameter and a change in the g-ratio (axon diameter to fiber diameter - the axon + myelin) in peripheral nerves in DR6 knockout mice. This change resulted in a small population of abnormally large axons that had thinner myelin than one would expect for their size. The change in g-ratio was specific to these axons and driven by the increased axon diameter, not decreased myelin thickness, although those two factors are normally loosely correlated. Here, the authors report no changes in axon size or g-ratio, but this could also be due to how the distribution of axon sizes was binned for analysis, and looking at individual data points in supplemental figure 3A, there are axons in the DR6 knockout mice that are larger than any axons in wild type. Thus, this discrepancy may be down to specifics and how statistics were performed or how histograms were binned, but it is unclear if the results presented here are dramatically at odds with the results in Colombo et al. (2018).

(Response 6) Several points raised by the reviewer appear to reflect differences in interpretation of the findings reported in Colombo et al. (2018). That study did not report altered myelination in DR6 null mice at stages when myelination is largely complete (P21). Instead, modest changes were observed at P1, which were reduced by P7, and P21 mutants were reported to be indistinguishable from controls. No analyses of peripheral nerves in older animals were presented, and the authors concluded in the discussion that myelination in young adult DR6 null mice appears normal. In contrast, our analysis of constitutive DR6 null mice at P1 does not reproduce the increase in the number of myelinated fibers per unit area reported by Colombo et al. We obtained similar results in the independent conditional DR6 knockout mouse line. Differences in nerve tissue processing, embedding, staining, or in the microscopic imaging and quantification of thinly myelinated axons in P1 sciatic nerve cross-sections may have contributed to the observed discrepancy. However, because the relevant methodological details were not described in Colombo et al., the underlying reasons for these differences cannot be determined and remain speculative.

(7) Finally, it is important to note that previously reported effects of DR6 inhibition, such as protection of cultured cortical neurons from beta-amyloid toxicity, are not necessarily the same as Wallerian degeneration of axons distal to an injury studied here. The negative results presented here, showing that loss of DR6 is not protective against Wallerian degeneration induced by injury, are important given the interest in DR6 as a therapeutic target, but they are specific to these mice and this mechanism of induced axon degeneration. The extent to which these findings contradict previous work is difficult to assess due to the lack of detail in describing the mouse experiments, and care should be taken in attempting to extrapolate these results to other disease contexts, such as ALS or Alzheimer's disease.

(Response 7) We agree with the reviewer’s point and emphasize that our manuscript carefully differentiates our data regarding the function of DR6 in Wallerian degeneration from the potential involvement of DR6 in other forms of axon degeneration. Our findings do not conflict with previous work on DR6 in the context of in vitro beta-amyloid and prion toxicity as well as in vitro models of ALS and multiple sclerosis. We believe these distinctions are explicitly and appropriately articulated throughout the entire manuscript and in more detail in the discussion section.

Reviewer #1 (Recommendations for the authors):

(1) The authors should include additional information about the mice used, including strain background for both the DR6 mice and the Cre transgenes crossed into the DR6 conditional knockout, the age of the mice when the nerve crush experiments were performed, and the sex distributions of the experimental cohorts. This information is critical for reproducibility in animal experiments, and that point is compounded here, where the major focus of this paper is taking issue with the reproducibility of previous work.

(Response 8) This information has been included in the revision. See above responses.

(2) In the abstract, reference 5 is cited as a study on the response to Schwann cells to injury in a DR6 background, but this probably should be reference 10.

(Response 9) This typo has been corrected.

(3) "Site-by-site comparison" in line 201 should be side-by-side?

(Response 10) This typo has been corrected.

(4) The paper contains a lot of self-evaluative wording, "surprising contrast," "compelling evidence," "robust results." Whether those adjectives apply should be for the reader to decide, and a drier, more objective tone in the presentation would improve the paper.

(Response 11) We agree that excessive self-evaluative wording can weaken objectivity. In the manuscript, such phrasing is used sparingly and intentionally to highlight differences from previously published studies, guide the reader, and convey scholarly judgment. We do not consider this limited use to be counterproductive. The adjectives “surprising,” “compelling,” and “robust” each appear only one to three times across the entire manuscript, and the specific phrase “robust results” does not appear at all.

(5) In Figure 2A, DR6-/-, there is no significant difference, but there is also a lot of variability, and one could argue the authors are seeing axon protection comparable to WldS in 40% of their samples (2/5), which is very similar to Gamage et al.

(Response 12) We respectfully disagree with this reasoning as it relies on selectively emphasizing only a subset of the data. Please also see our response #2 for more detailed discussion.

(6) Overall, the data presented here are convincing and support the conclusions drawn, but the paper needs to focus more on the negative results at hand and less on bashing previous studies, particularly when the results presented here do definitively show that the previous studies were incorrect and plausible explanations for differences in outcome exist.

(Response 13) We have carefully revisited the wording of the manuscript and are confident that our emphasis remains on the central negative finding that DR6 does not regulate axon degeneration and Schwann cell injury responses during Wallerian degeneration. We do not believe the manuscript “bashes” previous studies; nonetheless, we thoroughly re-examined all relevant sections to ensure that our language is neutral, accurate, and non-inflammatory. We believe the current phrasing presents our interpretations in an appropriately balanced, objective, and professional manner.

Reviewer #2 (Public review):

Summary:

This manuscript by Beirowski, Huang, and Babetto revisits the proposed role of Death Receptor 6 (DR6/Tnfrsf21) in Wallerian degeneration (WD). A prior study (Gamage et al., 2017) suggested that DR6 deletion delays axon degeneration and alters Schwann cell responses following peripheral nerve injury. Here, the authors comprehensively test this claim using two DR6 knockout mouse models (the line used in the earlier report plus a CMV-Cre derived floxed ko line) and multiple WD assays in vivo and in vitro, aligned with three positive controls, Sarm1 WldS and Phr1/Mycbp2 mutants. Contrary to the prior findings, they find no evidence that DR6 deletion affects axon degeneration kinetics or Schwann cell dynamics (assessed by cJun expression or [intact+degenerating] myelin abundance after injury) during WD. Importantly, in DRG explant assays, neurites from DR6-deficient mice degenerated at rates indistinguishable from controls. The authors conclude that DR6 is dispensable for WD, and that previously reported protective effects may have been due to confounding factors such as genetic background or spontaneous mutations.

Strengths:

The authors employ two independently generated DR6 knockout models, one overlapping with the previously published study, and confirm loss of DR6 expression by qPCR and Western blotting. Multiple complementary readouts of WD are applied (structural, ultrastructural, molecular, and functional), providing a robust test of the hypothesis.

Comparisons are drawn with established positive controls (WldS, SARM1, Phr1/Mycbp2 mutants), reinforcing the validity of the assays.

By directly addressing an influential but inconsistent prior report, the manuscript clarifies the role of DR6 and prevents potential misdirection of therapeutic strategies aimed at modulating WD in the PNS. The discussion thoughtfully considers possible explanations for the earlier results, including colony-specific second-site mutations that could explain the incomplete penetrance of the earlier reported phenotype of only 36%.

Weaknesses:

(1) The study focuses on peripheral nerves. The manuscript frequently refers to CNS studies to argue for consistency with their findings. It would be more accurate to frame PNS/CNS similarities as reminiscences rather than as consistencies (e.g., line 205ff in the Discussion).

(Response 14) Axon protection in all key genetic models of delayed axon degeneration, including Wld^S, SARM1, Phr1/Mycbp2 mutants, has been demonstrated in both the peripheral and central nervous systems. This observation supports the view that core molecular mechanisms regulating axon degeneration are conserved across neuronal populations throughout the entire nervous system. We have scrutinized the wording in our manuscript and are not aware that we frequently refer to CNS studies in regards to axon degeneration. Nevertheless, we have replaced the term “consistent” to avoid potential ambiguity when we discuss the earlier study showing normal Wallerian degeneration in the optic nerves from DR6 knockout mice.

(2) The DRG explant assays are convincing, though the slight acceleration of degeneration in the DR6 floxed/Cre condition is intriguing (Figure 4E). Could the authors clarify whether this is statistically robust or biologically meaningful?

(Response 15) We thank the reviewer for noting this aspect of our in vitro data in Fig. 4. The difference observed in the DR6 floxed/Cre condition is statistically significant at the 6h time point following disconnection, as indicated by the p value shown in Fig. 4E. However, a similarly statistically significant acceleration of axon degeneration was not observed in DRG axotomy experiments using constitutive DR6 knockout preparations, although a trend toward more rapid axon breakdown is apparent at 6 h post-axotomy (Fig. 4B). These observations may suggest reduced stability of DR6-deficient axons in this specific neuron-only in vitro context. Further investigation would be required to determine the biological significance of this effect. In contrast, our in vitro quantitative analyses of the initiation and early phases of Wallerian degeneration (Fig. 2) revealed no evidence of accelerated axon disintegration in the DR6 mutant mouse models, highlighting potential differences between in vitro and in vitro systems.

(3) In the summary (line 43), the authors refer to Hu et al. (2013) (reference 5) as the study that previously reported AxD delay and SC response alteration after injury. However, this study did not investigate the PNS, and I believe the authors intended to reference Gamage et al. (2017) (reference 10) at this point.

(Response 16) Thanks for pointing this out. We have corrected this typo in the revised manuscript.

(4) In line 74ff of the results section, the authors claim that developmental myelination is not altered in DR6 mutants at postnatal day 1. However, the variability in Figure S2 appears substantial, and the group size seems underpowered to support this claim. Colombo et al. (2018) (reference 11) reported accelerated myelination at P1, but this study likewise appears underpowered. Possible reasons for these discrepancies and the large variability could be that only a defined cross-sectional area was quantified, rather than the entire nerve cross-section.

(Response 17) We confirm that the quantification of thinly myelinated axons was performed on entire sciatic nerves from P1 mouse pups, as described in the methods section in our original manuscript. The data shown in Fig. S2 were obtained from 5-9 pups per experimental group. Sample sizes were determined based on a priori power analyses using pilot data, which indicated that a minimum of five biological replicates was sufficient to detect statistically significant differences with acceptable confidence. Comparable sample sizes have been used in our previous studies and by other groups to assess early postnatal myelination (e.g., PMIDs 21949390, 28484008). Several published studies have reported analyses using 3-4 animals per group (e.g., PMIDs 28484008, 25310982, 29367382). For comparison, the study by Colombo et al. used 3-8 pups for the analysis presented in their Fig. 3. We note that the apparent variability in Fig. S2 may be accentuated by the scaling of the y-axis, which was chosen to ensure that individual data points are clearly resolved and visible.

(5) The authors stress the data of Gamage et al. (2017) on altered SC responses in DR6 mutants after injury. They employed cJun quantification to show that SC reprogramming after injury is not altered in DR6 mutants. This approach is valid and the conclusion trustworthy. Here, the addition of data showing the combined abundance of intact and degenerated myelin does not add much insight. However, Gamage et al. (2017) reported altered myelin thickness in a subset of axons at 14 days after injury, which is considerably later than the time points analyzed in the present study. While, in the Reviewer's view, the thin myelin observed by Gamage et al. in fact resembles remyelination, the authors may wish to highlight the difference in the time points analyzed.

(Response 18) We consider the additional quantification of the area occupied by intact myelin and myelin debris to provide complementary information that supports the c-Jun-based conclusion that Schwann cell injury responses are normal in DR6-deficient nerves following lesion. We agree with this reviewer that the thin myelin observed by Gamage et al. resembles remyelination, raising the possibility that axon regeneration occurred into the distal nerve stump at the studied 14d post-injury time point (see their Fig. 3). This may have been interpreted as axon protection in this study. In our study, it was impossible to examine such myelin effects since axon protection was never observed in any of the DR6 mutant models at any of the time point we investigated. We have incorporated appropriate additional text to highlight this difference. See also response #5 above.

Reviewer #3 (Public review):

Summary:

The authors revisit the role of DR6 in axon degeneration following physical injury (Wallerian degeneration), examining both its effects on axons and its role in regulating the Schwann cell response to injury. Surprisingly, and in contrast to previous studies, they find that DR6 deletion does not delay the rate of axon degeneration after injury, suggesting that DR6 is not a mediator of this process.

Overall, this is a valuable study. As the authors note, the current literature on DR6 is inconsistent, and these results provide useful new data and clarification. This work will help other researchers interpret their own data and re-evaluate studies related to DR6 and axon degeneration.

Strengths:

(1) The use of two independent DR6 knockout mouse models strengthens the conclusions, particularly when reporting the absence of a phenotype.

(2) The focus on early time points after injury addresses a key limitation of previous studies. This approach reduces the risk of missing subtle protective phenotypes and avoids confounding results with regenerating axons at later time points after axotomy.

Weaknesses:

(1) The study would benefit from including an additional experimental paradigm in which DR6 deficiency is expected to have a protective effect, to increase confidence in the experimental models, and to better contextualize the findings within different pathways of axon degeneration. For example, DR6 deletion has been shown in more than one study to be partially axon protective in the NGF deprivation model in DRGs in vitro. Incorporating such an experiment could be straightforward and would strengthen the paper, especially if some of the neuroprotective effects previously reported are confirmed.

(Response 19) We thank the reviewer for these suggestions. We would like to highlight that our study addresses the role of DR6 in Wallerian degeneration, whereas in vitro NGF deprivation has been used to model developmental axon pruning. Previous work indicates fundamental biological differences between these regressive pathways regulating the stereotyped removal of axon segments. We feel that studying this alternative form of axon degeneration is beyond the scope of the current work and could be addressed in a separate manuscript. Although additional tests will be needed, we note that our preliminary data using samples from both DR6 knockout mouse models suggest no axon protection after NGF-deprivation in DRG neuron preparations in our hands (deprivation of the growth factor and administration of anti-NGF antibody).

(2) The quality of some figures could be improved, particularly the EM images in Figure 2. As presented, they make it difficult to discern subtle differences.

(Response 20) We have pseudocolored intact (turquoise) and degenerated (magenta) myelinated fibers on the high-resolution semithin micrographs (not electron micrographs) in the new Fig. 2 to make the distinction between the two fiber categories clearer.

Reviewer #3 (Recommendations for the authors):

(1) Line 121: The authors mention toluidine blue staining, but it does not appear to be shown in Figure S5.

(Response 21) This appears to be a misunderstanding. Fig. S5A shows the ultrastructure of dedifferentiated Schwann cells in transmission electron micrographs, while Figs. S5B and C show quantification of the area occupied by myelin sheaths and myelin debris profiles on osmium tetroxide and toluidine blue stained nerve sections from the two DR6 mutant models, based on semithin light microscopy. These are two different aspects of the analysis. The text has been modified in the revised manuscript to make the distinction clearer.

(2) Line 175: The authors should add NMNAT2 to the list of enzymes implicated in the regulation of Wallerian degeneration in mammals.

(Response 22) Nmnat2 and a literature reference (Milde et al., 2013) has been incorporated in the discussion of the revised manuscript to address this point.

(3) Line 201: Please correct the typo "site-by-site" to "side-by-side."

(Response 23) This typo has been corrected.

eLife Assessment

This fundamental work significantly advances our understanding of how contact-dependent antagonism enables keystone bacteria to establish and maintain their niche over time. The evidence obtained is convincing, supporting most of the conclusions drawn. This work will be of significant interest to the microbiome research community.

Reviewer #1 (Public review):

Summary:

In this study, the authors investigate the physiological role of the Type VI secretion system (T6SS) in a naturally evolved gut microbiome derived from wild mice (the WildR microbiome). Focusing on Bacteroides acidifaciens, the authors use newly developed genetic tools and strain-replacement strategies to test how T6SS-mediated antagonism influences colonization, persistence, and fitness within a complex gut community. They further show that the T6SS resides on an integrative and conjugative element (ICE), is distributed among select community members, and can be horizontally transferred, with context-dependent effects on colonization and persistence. The authors conclude that the T6SS stabilizes strain presence in the gut microbiome while imposing ecological and physiological constraints that shape its value across contexts.

This study is likely to have a significant impact on the microbiome field by moving experimental tests of T6SS function out of simplified systems and into a naturally co-evolved gut community. The WildR system, together with the strain replacement strategy, ICE-seq approach, and genetic toolkit, represents a powerful and reusable platform for future mechanistic studies of microbial antagonism and mobile genetic elements in vivo.

The datasets, including isolate genomes, metagenomes, and ICE distribution maps, will be a valuable community resource, particularly for researchers interested in strain-resolved dynamics, horizontal gene transfer, and ecological context dependence. Even where mechanistic resolution is incomplete, the work provides a strong experimental foundation upon which such questions can be directly addressed.

Overall, this study occupies a space between system building and mechanistic dissection. The authors demonstrate that the T6SS influences persistence and community structure in vivo, but the physiological basis of these effects remains unresolved. Interpreting the results as evidence of fitness costs or selective advantage, therefore, requires caution, as multiple ecological and host-mediated processes could produce similar abundance trajectories.

Placing the findings within the broader literature on microbial antagonism, particularly work emphasizing measurable costs, benefits, and tradeoffs, would help readers better contextualize what is directly demonstrated here versus what remains an open question. Viewed in this light, the principal contribution of the study is to show that such questions can now be addressed experimentally in a realistic gut ecosystem.

Strengths:

A major strength of this study is that it directly interrogates the physiological role of the T6SS in a naturally evolved gut microbiome, rather than relying on simplified pairwise or in vitro systems. By working within the WildR community, the authors advance beyond descriptive surveys of T6SS prevalence and address function in an ecologically relevant context.

The authors provide clear genetic evidence that Bacteroides acidifaciens uses a T6SS to antagonize co-resident Bacteroidales, and that loss of T6SS function specifically compromises long-term persistence without affecting initial colonization. This temporal separation is well designed and supports the conclusion that the T6SS contributes to maintenance rather than establishment within the community.

Another strength is the identification of the T6SS on an integrative and conjugative element (ICE) and the demonstration that this element is distributed among, and exchanged between, community members. The use of ICE-seq to track distribution and transfer provides strong support for horizontal mobility and adds mechanistic depth to the study.

Finally, the transfer of the T6SS-ICE into Phocaeicola vulgatus and the observation of context-dependent colonization benefits followed by decline is a compelling result that moves the study beyond simple "T6SS is beneficial" narratives and highlights ecological contingency.

Weaknesses:

Despite these strengths, there is a mismatch between the precision of the claims and the precision of the measurements, particularly regarding fitness costs, physiological burden, and the mechanistic role of the T6SS.

First, while the authors conclude that the T6SS "stabilizes strain presence" and that its value is constrained by fitness costs, these costs are not directly measured. Persistence, abundance trajectories, and eventual loss are informative outcomes, but they do not uniquely identify fitness tradeoffs. Decline could arise from multiple non-exclusive mechanisms, including community restructuring, host-mediated effects, incompatibilities of the ICE in new hosts, or ecological retaliation, none of which are disentangled here.

Second, the manuscript frames the T6SS as having a defined physiological role, yet the data do not resolve which physiological processes are under selection. The experiments demonstrate that T6SS activity affects persistence, but they do not distinguish whether this occurs via direct killing, resource release, niche modification, or higher-order community effects. As a result, "physiological role" remains underspecified and risks being conflated with ecological outcome.

Third, although the authors emphasize context dependence, the study offers limited quantitative insight into what aspects of context matter. Differences between native and recipient hosts, or between early and late colonization phases, are described but not mechanistically interrogated, making it difficult to generalize beyond the specific cases examined.

Fourth is the lack of engagement with recent experimental literature demonstrating functional roles of the T6SS beyond simple interference competition. While the authors focus on persistence and competitive outcomes, they do not adequately situate their findings within recent work demonstrating that T6SS-mediated antagonism can serve additional physiological functions, including resource acquisition and DNA uptake, thereby linking killing to measurable benefits and tradeoffs. The absence of this literature makes it difficult to place the authors' conclusions about physiological role and fitness cost within the current conceptual framework of the field. Without this context, the physiological interpretation of the results remains incomplete, and alternative functional explanations for the observed dynamics are underexplored.

A further limitation concerns the taxonomic scope of the functional analysis. The authors state that the role of the T6SS in the murine environment is functionally investigated using genetically tractable Bacteroides species, citing the lack of genetic tools for Mucispirillum schaedleri. While this is a reasonable, practical choice, it means that a substantial fraction of T6SS-encoding species in the WildR community are not experimentally interrogated. Consequently, conclusions about the role of the T6SS in the murine gut necessarily reflect the subset of taxa that are genetically accessible and may not fully capture community-level or niche-specific functions of T6SS activity. Given that M. schaedleri is represented as a metagenome-assembled genome, its isolation and genetic manipulation would be technically challenging. Nonetheless, explicitly acknowledging this limitation and slightly tempering claims of generality would strengthen the manuscript.

Finally, several interpretations would benefit from more cautious language. In particular, claims invoking fitness costs, selective advantage, or physiological burden should be explicitly framed as inferences from persistence dynamics, rather than as direct measurements, unless supported by additional quantitative fitness or growth assays.

Reviewer #2 (Public review):

Summary:

In this study, the authors set out to determine how a contact-dependent bacterial antagonistic system contributes to the ability of specific bacterial strains to persist within a complex, native gut community derived from wild animals. Rather than focusing on simplified or artificial models, the authors aimed to examine this system in a biologically realistic setting that captures the ecological complexity of the gut environment. To achieve this, they combined controlled laboratory experiments with animal colonization studies and sequencing-based tracking approaches that allow individual strains and mobile genetic elements to be followed over time.

Strengths:

A major strength of the work is the integration of multiple complementary approaches to address the same biological question. The use of defined but complex communities, together with in vivo experiments, provides a strong ecological context for interpreting the results. The data consistently show that the antagonistic system is not required for initial establishment but plays a critical role in long-term strain persistence. This insight that moves beyond traditional invasion-based views of microbial competition. The observation that transferable genetic elements can confer only temporary advantages, and may impose longer-term costs depending on community context, adds important nuance to current understanding of microbial fitness.

Weaknesses:

Overall, there is not a lack of evidence, but a deliberate trade-off between ecological realism and mechanistic resolution, which leaves some causal pathways open to interpretation.

Reviewer #3 (Public review):

Summary:

Shen et al. investigate the contribution of the type VI secretion system of Bacteroidales in the gut microbiome assembly and targeting of closely related species. They demonstrate that B. acidifaciens relies on T6SS-mediated antagonism to prevent displacement by co-resident Bacteroidales and other members of the microbiome, allowing B. acidifaciens to persist in the gut.

Strengths:

Using a gnotobiotic model colonized with a wild-mouse microbiome is a significant strength of this study. This approach allows tracking of microbiome changes over time and directly examining targeting by Bacteroidales carrying T6SS in a more natural setting. The development of ICE-seq for mapping the distribution of the T6SS in the microbiome is remarkable, enabling the study of how this bacterial weapon is transferred between microbiome members without requiring long-read metagenomics methods.

Weaknesses:

Some conclusions are based on only four mice per condition. The author should consider increasing the sample size.

Overall, the authors successfully achieved their objectives, and their experimental design and results support their findings. As mentioned in the discussion, it would be important to investigate the role of the T6SS in resilience to disturbances in the microbiome, such as antibiotics, diet, or pathogen invasion. This work represents a step forward in understanding how contact-dependent competition influences the gut microbiome in relevant ecological contexts.

Author response:

We appreciate that the reviewers provided an overall positive assessment of our manuscript and offered constructive suggestions for improvement. All three reviewers noted that a key strength of our study is the implementation of a gut microbiome model for the characterization of interbacterial antagonism pathways such as the type VI secretion system (T6SS) that approaches natural complexity. They note our work represents a significant advance in microbiome research, and generates resources that will be of use to many researchers in the field. Two of the reviewers point out that the complexity of our model limits the nature of measurements we can make, and suggest we temper the strength of the some of the conclusions we draw. As noted in more detail below, in our revised manuscript, we will be more precise in the wording we use to characterize our findings, and we will be more explicit about what the measurements we are able to make allow us to conclude about the physiological role of the T6SS in the gut microbiome.

Reviewer #1 (Public review):

Summary:

In this study, the authors investigate the physiological role of the Type VI secretion system (T6SS) in a naturally evolved gut microbiome derived from wild mice (the WildR microbiome). Focusing on Bacteroides acidifaciens, the authors use newly developed genetic tools and strain-replacement strategies to test how T6SS-mediated antagonism influences colonization, persistence, and fitness within a complex gut community. They further show that the T6SS resides on an integrative and conjugative element (ICE), is distributed among select community members, and can be horizontally transferred, with context-dependent effects on colonization and persistence. The authors conclude that the T6SS stabilizes strain presence in the gut microbiome while imposing ecological and physiological constraints that shape its value across contexts.

This study is likely to have a significant impact on the microbiome field by moving experimental tests of T6SS function out of simplified systems and into a naturally co-evolved gut community. The WildR system, together with the strain replacement strategy, ICE-seq approach, and genetic toolkit, represents a powerful and reusable platform for future mechanistic studies of microbial antagonism and mobile genetic elements in vivo.

The datasets, including isolate genomes, metagenomes, and ICE distribution maps, will be a valuable community resource, particularly for researchers interested in strain-resolved dynamics, horizontal gene transfer, and ecological context dependence. Even where mechanistic resolution is incomplete, the work provides a strong experimental foundation upon which such questions can be directly addressed.

Overall, this study occupies a space between system building and mechanistic dissection. The authors demonstrate that the T6SS influences persistence and community structure in vivo, but the physiological basis of these effects remains unresolved. Interpreting the results as evidence of fitness costs or selective advantage, therefore, requires caution, as multiple ecological and host-mediated processes could produce similar abundance trajectories.

Placing the findings within the broader literature on microbial antagonism, particularly work emphasizing measurable costs, benefits, and tradeoffs, would help readers better contextualize what is directly demonstrated here versus what remains an open question. Viewed in this light, the principal contribution of the study is to show that such questions can now be addressed experimentally in a realistic gut ecosystem.

We thank the reviewer for this thoughtful summary of our study. We were glad to read they conclude our work will have a significant impact on the microbiome field and that the resources we have developed will be of value to the community.

Strengths:

A major strength of this study is that it directly interrogates the physiological role of the T6SS in a naturally evolved gut microbiome, rather than relying on simplified pairwise or in vitro systems. By working within the WildR community, the authors advance beyond descriptive surveys of T6SS prevalence and address function in an ecologically relevant context.

The authors provide clear genetic evidence that Bacteroides acidifaciens uses a T6SS to antagonize co-resident Bacteroidales, and that loss of T6SS function specifically compromises long-term persistence without affecting initial colonization. This temporal separation is well designed and supports the conclusion that the T6SS contributes to maintenance rather than establishment within the community.

Another strength is the identification of the T6SS on an integrative and conjugative element (ICE) and the demonstration that this element is distributed among, and exchanged between, community members. The use of ICE-seq to track distribution and transfer provides strong support for horizontal mobility and adds mechanistic depth to the study.

Finally, the transfer of the T6SS-ICE into Phocaeicola vulgatus and the observation of context-dependent colonization benefits followed by decline is a compelling result that moves the study beyond simple "T6SS is beneficial" narratives and highlights ecological contingency.

We appreciate this detailed and nuanced characterization of the strengths of our study.

Weaknesses:

Despite these strengths, there is a mismatch between the precision of the claims and the precision of the measurements, particularly regarding fitness costs, physiological burden, and the mechanistic role of the T6SS.

We acknowledge that in some places, our manuscript could benefit from greater precision in the language we use when linking the outcomes we observe in our study to their potential underlying causes. Specific revisions we propose to address this concern are described below.

First, while the authors conclude that the T6SS "stabilizes strain presence" and that its value is constrained by fitness costs, these costs are not directly measured. Persistence, abundance trajectories, and eventual loss are informative outcomes, but they do not uniquely identify fitness tradeoffs. Decline could arise from multiple non-exclusive mechanisms, including community restructuring, host-mediated effects, incompatibilities of the ICE in new hosts, or ecological retaliation, none of which are disentangled here.

We agree that multiple mechanisms could explain why P. vulgatus carrying a T6SS-encoding ICE declines over time. Our use of the term “fitness cost” to describe this trend was not meant to imply any particular underlying mechanism, but was rather our attempt to characterize the phenotypic outcome we observed in simplified terms. We note that ecological context is an important determinant of the fitness cost or benefit of any given trait, and our study sheds light on the importance of the presence of the WildR community and the mouse intestinal environment to the fitness contribution of the ICE to P. vulgatus. Nonetheless, to avoid implying an overly simplistic interpretation of our results, we propose to modify the language used in the manuscript when describing the contribution of the T6SS to species persistence in WildR-colonized mice.

Second, the manuscript frames the T6SS as having a defined physiological role, yet the data do not resolve which physiological processes are under selection. The experiments demonstrate that T6SS activity affects persistence, but they do not distinguish whether this occurs via direct killing, resource release, niche modification, or higher-order community effects. As a result, "physiological role" remains underspecified and risks being conflated with ecological outcome.

We acknowledge that our study does not fully resolve the physiological processes under selection that mediate role of the T6SS in maintaining B. acidifaciens populations in WildR-colonized mice. Indeed, several of the outcomes of T6SS activity the reviewer lists, such as target cell killing and nutrient release, are inextricably linked and thus inherently difficult to disentangle. We note that we did attempt to measure higher-order community effects of T6SS activity with metagenomic sequencing, but acknowledge that this approach may not have been sufficiently sensitive to detect small community shifts mediated by a relatively low-abundance species. To address the concern that our current framing implies more of a mechanistic understanding that our study achieves, we propose to substitute “ecological” for “physiological” where appropriate when summarizing our key findings.

Third, although the authors emphasize context dependence, the study offers limited quantitative insight into what aspects of context matter. Differences between native and recipient hosts, or between early and late colonization phases, are described but not mechanistically interrogated, making it difficult to generalize beyond the specific cases examined.

We are not entirely clear what the reviewer means by “differences between native and recipient hosts”, but we agree that additional quantitative studies will be needed to address the generalizability of our findings. Future studies are also needed to address the mechanistic basis for the difference in the benefit conferred by the T6SS that we observed between P. vulgatus and B. acidifaciens.

Fourth is the lack of engagement with recent experimental literature demonstrating functional roles of the T6SS beyond simple interference competition. While the authors focus on persistence and competitive outcomes, they do not adequately situate their findings within recent work demonstrating that T6SS-mediated antagonism can serve additional physiological functions, including resource acquisition and DNA uptake, thereby linking killing to measurable benefits and tradeoffs. The absence of this literature makes it difficult to place the authors' conclusions about physiological role and fitness cost within the current conceptual framework of the field. Without this context, the physiological interpretation of the results remains incomplete, and alternative functional explanations for the observed dynamics are underexplored.

We thank the reviewer for specifically highlighting the potential pertinence of this literature to our study. Indeed, we did not cite studies indicating a link between T6SS activity and the uptake of DNA and other resources released by targeted cells. As we note above, the release of intracellular contents from target cells is an inevitable consequence of the delivery of lytic effectors. Thus, distinguishing between fitness benefits conferred from the elimination of competitor species and those arising from scavenging the nutrients released during this process is not straightforward. Measuring the benefits deriving from the uptake of certain released molecules, such as DNA, was not immediately feasible in the system employed in this study and instead we focused on the direct lytic consequences of the effectors delivered via the T6SS. We will revise our Discussion to include reference to how downstream consequences of T6SS activity on target cells could impact the community, and thus the adaptive role of the T6SS in the microbiome.

A further limitation concerns the taxonomic scope of the functional analysis. The authors state that the role of the T6SS in the murine environment is functionally investigated using genetically tractable Bacteroides species, citing the lack of genetic tools for Mucispirillum schaedleri. While this is a reasonable, practical choice, it means that a substantial fraction of T6SS-encoding species in the WildR community are not experimentally interrogated. Consequently, conclusions about the role of the T6SS in the murine gut necessarily reflect the subset of taxa that are genetically accessible and may not fully capture community-level or niche-specific functions of T6SS activity. Given that M. schaedleri is represented as a metagenome-assembled genome, its isolation and genetic manipulation would be technically challenging. Nonetheless, explicitly acknowledging this limitation and slightly tempering claims of generality would strengthen the manuscript.

The reviewer points out that studying the T6SS activity in M. schadleri would potentially expand the generality of our claims. We agree that having an isolate of this species along with genetic tools for its manipulation would allow us to probe the importance of the T6SS in the gut microbiome more broadly. At the suggestion of the reviewer, we will add explicit mention for the need to develop such tools, an endeavor that lies outside of the scope of the current study.

Finally, several interpretations would benefit from more cautious language. In particular, claims invoking fitness costs, selective advantage, or physiological burden should be explicitly framed as inferences from persistence dynamics, rather than as direct measurements, unless supported by additional quantitative fitness or growth assays.

We agree with the reviewer that invoking fitness costs, selective advantages or physiological burdens should be done cautiously, and in our revised manuscript we will carefully re-evalute our usage of those terms. However, we would also argue invoking fitness costs and benefits when describe strain persistence dynamics in mice has substantial precedent in the literature ((Feng et al. 2020, Brown et al. 2021, Park et al. 2022, Segura Munoz et al. 2022), to list a handful of representative examples published by different groups). It is unclear to us what additional in vivo growth measurements could be taken to substantiate our claim that the T6SS provides a fitness benefit to B. acidifaciens during prolonged gut colonization, or that carrying the ICE imposes a fitness cost on P. vulgatus during long-term colonization. Our in vitro experiments evaluating the competitiveness conferred by T6SS activity provide a measure of insight into its fitness benefits, but as our in vivo strain persistence data and the work of many others show, in vitro measurements do not necessarily capture in vivo parameters.

Reviewer #2 (Public review):

Summary:

In this study, the authors set out to determine how a contact-dependent bacterial antagonistic system contributes to the ability of specific bacterial strains to persist within a complex, native gut community derived from wild animals. Rather than focusing on simplified or artificial models, the authors aimed to examine this system in a biologically realistic setting that captures the ecological complexity of the gut environment. To achieve this, they combined controlled laboratory experiments with animal colonization studies and sequencing-based tracking approaches that allow individual strains and mobile genetic elements to be followed over time.

Strengths:

A major strength of the work is the integration of multiple complementary approaches to address the same biological question. The use of defined but complex communities, together with in vivo experiments, provides a strong ecological context for interpreting the results. The data consistently show that the antagonistic system is not required for initial establishment but plays a critical role in long-term strain persistence. This insight that moves beyond traditional invasion-based views of microbial competition. The observation that transferable genetic elements can confer only temporary advantages, and may impose longer-term costs depending on community context, adds important nuance to current understanding of microbial fitness.

We thank the reviewer for the positive feedback and are glad they agree our study provides new insight into the role of interbacterial antagonism in natural communities.

Weaknesses:

Overall, there is not a lack of evidence, but a deliberate trade-off between ecological realism and mechanistic resolution, which leaves some causal pathways open to interpretation.

The reviewer makes a good point that the complexity of the experimental system we employ precludes some lines of experimentation that would yield more mechanistic information. As the reviewer notes, we were aware of the tradeoff between mechanistic resolution and ecological realism when selecting our experimental system. Our deliberate choice to favor biological complexity over mechanistic clarity in this study stemmed from our perception that a major gap in understanding of the T6SS and other antagonism pathways lies in defining their ecological function in complex microbial communities.

Reviewer #3 (Public review):

Summary:

Shen et al. investigate the contribution of the type VI secretion system of Bacteroidales in the gut microbiome assembly and targeting of closely related species. They demonstrate that B. acidifaciens relies on T6SS-mediated antagonism to prevent displacement by co-resident Bacteroidales and other members of the microbiome, allowing B. acidifaciens to persist in the gut.

Strengths:

Using a gnotobiotic model colonized with a wild-mouse microbiome is a significant strength of this study. This approach allows tracking of microbiome changes over time and directly examining targeting by Bacteroidales carrying T6SS in a more natural setting. The development of ICE-seq for mapping the distribution of the T6SS in the microbiome is remarkable, enabling the study of how this bacterial weapon is transferred between microbiome members without requiring long-read metagenomics methods.

We thank the reviewer for their enthusiasm toward our study.

Weaknesses:

Some conclusions are based on only four mice per condition. The author should consider increasing the sample size.

We agree that in some experiments it would be beneficial to increase the sample size from four mice. However, the experiments we performed for this study are time and resource intensive. Additionally, the experiments on which we base our primary conclusions were all independently replicated with similar results. Given these factors, we determined that the extra confidence that might be afforded by increasing our sample size did not merit the delay in publication and investment in resources that would be required.

Overall, the authors successfully achieved their objectives, and their experimental design and results support their findings. As mentioned in the discussion, it would be important to investigate the role of the T6SS in resilience to disturbances in the microbiome, such as antibiotics, diet, or pathogen invasion. This work represents a step forward in understanding how contact-dependent competition influences the gut microbiome in relevant ecological contexts.

We agree that investigating the role of the T6SS during perturbations of the microbiome is a key next step for this work and thank the reviewer for highlighting this important future direction.

References

Brown, E. M., H. Arellano-Santoyo, E. R. Temple, Z. A. Costliow, M. Pichaud, A. B. Hall, K. Liu, M. A. Durney, X. Gu, D. R. Plichta, C. A. Clish, J. A. Porter, H. Vlamakis and R. J. Xavier (2021). "Gut microbiome ADP-ribosyltransferases are widespread phage-encoded fitness factors." Cell Host Microbe 29(9): 1351-1365 e1311.

Feng, L., A. S. Raman, M. C. Hibberd, J. Cheng, N. W. Griffin, Y. Peng, S. A. Leyn, D. A. Rodionov, A. L. Osterman and J. I. Gordon (2020). "Identifying determinants of bacterial fitness in a model of human gut microbial succession." Proc Natl Acad Sci U S A 117(5): 2622-2633.

Park, S. Y., C. Rao, K. Z. Coyte, G. A. Kuziel, Y. Zhang, W. Huang, E. A. Franzosa, J. K. Weng, C. Huttenhower and S. Rakoff-Nahoum (2022). "Strain-level fitness in the gut microbiome is an emergent property of glycans and a single metabolite." Cell 185(3): 513-529 e521.

Segura Munoz, R. R., S. Mantz, I. Martinez, F. Li, R. J. Schmaltz, N. A. Pudlo, K. Urs, E. C. Martens, J. Walter and A. E. Ramer-Tait (2022). "Experimental evaluation of ecological principles to understand and modulate the outcome of bacterial strain competition in gut microbiomes." ISME J 16(6): 1594-1604.

eLife Assessment

This study reports an important and novel finding that TENT5A, an enzyme involved in fine-tuning poly(A) tail length on selected mRNAs, is required for proper enamel mineralization in mice. The evidence supporting the authors' conclusion that reduced expression of enamel matrix proteins (EMPs) in TENT5A-deficient mice results from shortened poly(A) tails remains incomplete, as TENT5A may possess additional functions independent of post-transcriptional regulation that are not addressed in the current study.

Reviewer #1 (Public review):

Summary:

The authors aim to determine whether TENT5A, a post-transcriptional regulator previously implicated in bone formation, also plays a role in enamel development. Using a mouse model lacking TENT5A, they report hypomineralized enamel with structural defects, accompanied by reduced expression, altered poly(A) tail length, and impaired secretion of enamel matrix proteins, particularly amelogenin. By combining ultrastructural imaging, transcriptomics, direct RNA sequencing, and protein localization analyses, the study proposes that TENT5A promotes cytoplasmic polyadenylation and translation of a subset of extracellular matrix transcripts required for enamel biomineralization.

Strengths:

A major strength of this work is its conceptual novelty. To my knowledge, this is the first study to demonstrate that a non-canonical poly(A) polymerase plays a direct role in enamel development, extending post-transcriptional regulation by cytoplasmic polyadenylation from bone to enamel, a biologically distinct and non-regenerative mineralized tissue. The identification of amelogenin as a dominant, tissue-specific target provides a new perspective on how enamel matrix production is regulated beyond transcriptional control.

In addition, the study is supported by a comprehensive and complementary set of approaches linking molecular changes to tissue-level phenotypes. The use of direct RNA sequencing provides strong evidence for selective regulation of poly(A) tail length in specific transcripts rather than global effects on mRNA metabolism, and the phenotypic analyses convincingly connect altered post-transcriptional regulation to defects in enamel structure and mineralization.

Weaknesses:

Although the data support a role for TENT5A in stabilizing and promoting translation of amelogenin and related transcripts, the mechanism underlying substrate specificity remains unresolved. Poly(A) tail length alone does not explain why certain transcripts are regulated while others are not, and the proposed involvement of protein partners or RNA processing steps remains speculative. This limitation should be more clearly framed as an open question rather than an emerging mechanism.

A further limitation is the lack of direct human genetic or clinical evidence linking TENT5A to enamel defects. In humans, loss-of-function variants in TENT5A are known to cause a recessive form of osteogenesis imperfecta, but TENT5A has not been associated with amelogenesis imperfecta or other enamel phenotypes. This limits immediate translational interpretation of the mouse enamel phenotype and highlights the need for future human genetic or clinical studies.

Finally, the manuscript does not address whether other members of the TENT5 family are expressed in ameloblasts or could compensate for the loss of TENT5A, leaving open questions about redundancy and specificity within this family.

Reviewer #2 (Public review):

Summary:

The manuscript by Aranaz-Novaliches describes a study of Tent5a knockout (KO) mice. The authors demonstrate a severe enamel phenotype in these mice, characterized by hypoplastic enamel with markedly disturbed organization of enamel rods. Additionally, they report that Amelx expression is reduced in the mutant compared to wild type (WT) at both mRNA and protein levels. The authors also examine the distribution and co-localization of Amelx and Ambn in ameloblasts and the enamel matrix. These findings are novel and provide important insights into the role of polyadenylation in regulating enamel matrix protein translation and its downstream effects on protein trafficking, secretion, and enamel formation. However, I have multiple concerns regarding the data and its analysis that need to be addressed.

Specific comments:

(1) Introduction

The structure of the introduction is unconventional. The first sentence of the third paragraph states that the goal of this study is to investigate the role of TENT5A in enamel formation, but the rest of the paragraph focuses on enamel in general. The following paragraph claims that the authors discovered the effects of Tent5a deficiency on enamel formation for the first time, yet most of the paragraph discusses enamel proteins and amelogenesis. The choice of references is problematic. The authors cite Sire et al. (2007), which focuses on the origin and evolution of enamel mineralisation genes, a poor fit for this context. A more appropriate source would be a recent review, e.g., Lacruz R et al., Physiol Rev. 2017;97(3):939-993. Ambn constitutes ~5% of the enamel matrix, not 10%. Reference 16 (Martin) is not ideal for murine enamel; more detailed studies exist, e.g., Smith CE et al., J Anat. 2019;234(2):274-290. References on protein-protein interactions (17-19) are also off: Wald et al. studied Ambn-Ambn and Amelx-Amelx interactions separately; Fang et al. focused on Amelx self-assembly only; Kawasaki and Weiss addressed gene evolution. The authors should cite work from Moradian-Oldak's lab, which clearly demonstrates Amelx-Ambn interactions. The last paragraph contains confusing statements, e.g., "TENT5a localized in rER promotes the expression of AmelX and other secreted protein transcripts." Also, the manuscript does not convincingly show disruption of self-assembly beyond overall enamel disorganization.

(2) Results

(a) microCT

Quantitative microCT analyses of WT and KO enamel are needed. At a minimum, enamel thickness and density should be measured from at least three biological replicates per genotype. Severe malocclusion in KO mice is not discussed. The mandibular incisor appears abraded, while the maxillary incisor is overgrown. Is maxillary enamel as affected as mandibular? The age of the mice is not specified. High-resolution scans of isolated mandibular incisors described in Materials and Methods should be included.

(b) SEM

The term "disorganized crystal structure" is incorrect - SEM cannot reveal crystal structure. This requires electron/X-ray diffraction or vibrational spectroscopy. Likely, the authors meant disorganized rods and interrod enamel. The phrase "weak HAP composition" is unclear. Can the increase in interprismatic matrix volume and reduction in rod diameter be quantified? Since rods are secreted by distal Tomes' processes and interrod by proximal Tomes' processes, an imbalance may indicate alterations in the ameloblast secretory apparatus. TEM studies of demineralized incisors are recommended to assess ameloblast ultrastructure.

(c) EMP expression

There is a discrepancy between WB images and data in Figure S2a. In Figure 2b, Amelx band is stronger than Ambn (expected, as Amelx is ~20× more abundant), but in Figure S2a, Ambn appears higher. How was protein intensity in Fig. S2a calculated? Optical density? Was normalization applied? Co-localization in Figure 2d was performed on LS8 cells, which lack a true ameloblast phenotype. Amelx expression in LS8 cells is ~2% of actin (Sarkar et al., 2014), whereas in murine incisors, it is ~600× higher than actin (Bui et al., 2023). Ambn signal is weaker than Amelx, which may affect co-localization results.

(d) Splicing products in Figure 2e

All isoforms except one contain exon 4. The major functional splice product of Amelx lacks exon 4 (Haruyama et al. J Oral Biosci. 2011;53(3):257-266), and there are some indications that the presence of exon 4 can lead to enamel defects. Can it be that the observed phenotype is due to the presence of exon 4?

(e) Co-localization studies

The presented co-localization studies do not demonstrate self-assembly defects; they reflect enamel microstructural defects observed by SEM. Self-assembly occurs at the nanoscale and cannot be assessed by light microscopy except with advanced optical methods. Conclusions based on single images are weak. The authors should perform experiments at least on three biological replicates per genotype, quantify results (e.g., total gray values per ROI of equal pixel size), and use co-localization metrics such as Mander's coefficient. Claims about alternative secretory pathways require much stronger evidence.

The authors should avoid implying that mRNA is inside the ER lumen. It is likely associated with the outer rER surface, which is expected. The resolution of the methods used is insufficient to confirm ER lumen localization.

Reviewer #3 (Public review):

Summary:

It is well established that poly(A) tails at the 3' end of mRNA are critical for mRNA stability, providing another layer of gene regulation. TENT5A is one of the non-canonical poly(A) polymerases that add an extra poly(A) tail. This manuscript demonstrates that the Tent5A mutation leads to mineralization abnormalities in the tooth, shorter poly(A) tails in amelogenin mRNA and some other selected mRNAs, and provides a list of TENT5A interacting proteins.

Strengths:

(1) The authors show in vivo genetic evidence that Tent5a is critical for normal tooth mineralization.

(2) The authors show that the length of the poly(A) tail in amelogenin (AmelX) is 13 bases shorter in Tent5a mutants but not in other mRNAs, such as ameloblastin (Ambn).

(3) Differentially expressed genes (DEGs) in Tent5A mutant tissues (cervical loop) are identified, and some of them show different lengths of poly(A) tails.

(4) TENT5A interacting proteins are identified. Together with the DEGs, these datasets will provide valuable research tools to the community.

Weaknesses:

(1) There is no direct evidence to support the main conclusion; the length of the poly(A) tail is critical for normal tooth mineralization.

(2) The RNAseq data to identify TENT5A substrate is based on the assumption that shorter poly(A) tailed RNA is less stable. However, there are multiple reasons for the differential expression of RNA in Tent5A mutant tissues.

(3) Several TENT5A-interacting proteins have been identified, but, beyond their colocalization with a target mRNA, no mechanistic studies have been conducted.

Author response:

We thank the editors and reviewers for their careful and constructive evaluation of our manuscript. We appreciate the recognition of the conceptual novelty and in vivo relevance of our findings. We have carefully considered all comments and outline below the major revisions and additional analyses we will undertake. For clarity, we address the reviewers’ comments in thematic sections.

Cell-autonomous contribution of Tent5a to phenotype

We agree that the use of a complete knockout model raises the possibility of indirect or non-cell-autonomous effects on tooth development, particularly given the observed dentin alterations. To address this point directly, we are generating and analyzing an ameloblast-specific conditional model we have already on shelf (Ambn-Cre; Tent5a^flox/flox) to determine whether the enamel phenotype arises from cell-autonomous loss of TENT5A in the secretory epithelium. This approach will allow us to distinguish epithelial-intrinsic effects from potential secondary contributions of odontoblasts or mesenchymal tissues. Results from this model will be incorporated into the revised manuscript.

Mechanistic basis and substrate specificity

We agree that the mechanism underlying substrate selectivity of TENT5A requires further clarification. We have performed multiple classical RNA–protein interaction assays, including CLIP-based approaches, without identifying a clear sequence-specific recognition motif. In the revised manuscript, we will present substrate specificity as an open mechanistic question rather than implying a defined recognition mechanism.

To strengthen this aspect, we will extend our analysis to include combined immunoprecipitation strategies and investigation of potential ribosome-associated or co-translational interactions of TENT5A.

In addition, we will further validate selected high-confidence TENT5A interactors identified in our dataset in context of putative changes in AmelX-polyA tail length.

Poly(A) tail length and functional causality

We acknowledge that shortening of the poly(A) tail alone does not formally establish causality. However, our data consistently show that TENT5A-dependent shortening of poly(A) tails correlates with reduced mRNA and protein levels of key enamel matrix components. In the revised manuscript, we will clarify this mechanistic framework more explicitly, integrating poly(A) length, transcript abundance, and protein-level data in a structured manner, while clearly distinguishing correlation from formal proof of causality.

We will also perform additional functional assays, including mRNA stability measurements in vitro in cells with genetic ablation of Tent5a, to further test the link between poly(A) shortening and reduced AmelX protein levels.

Quantitative microCT and enamel morphology

We will include quantitative microCT analyses of enamel thickness and mineral density from multiple biological replicates per genotype (n ≥ 3). Sample numbers will be explicitly stated throughout. Additional high-resolution scans of isolated incisors will be provided. We will also quantify occlusal angle and include whole-skull reconstructions to document malocclusion. Maxillary enamel will be analyzed and quantified alongside mandibular enamel.

SEM terminology will be corrected (e.g., replacing “crystal structure” with “rod/interrod organization”), and structural parameters such as rod diameter and interprismatic matrix proportion will be quantitatively assessed.

We agree that ultrastructural analysis of ameloblast secretory morphology is important. We have experience with TEM analysis of demineralized incisors and will perform additional ultrastructural examination to assess the integrity of Tomes’ processes and the secretory apparatus in Tent5a-deficient ameloblasts. These data will allow us to distinguish between primary alterations in secretory morphology and downstream effects on matrix organization.

Amelx splice variants

We will re-analyze our RNA-seq data with specific attention to exon 4-containing isoforms and clarify the distribution of splice variants in WT and KO samples. These findings will be explicitly discussed in the context of prior literature.

Co-localization and self-assembly claims

We agree that conventional light microscopy cannot directly resolve nanoscale self-assembly events. In Figure 3, our intention was to demonstrate differential subcellular distribution and partial segregation of AMELX and AMBN within secretory compartments, rather than to claim direct visualization of molecular self-assembly. In the revised manuscript, we will clarify this distinction, moderate the terminology accordingly, and provide explicit quantitative co-localization analyses across multiple biological replicates.

TENT5 family paralogs

To address potential redundancy within the TENT5 family, we will analyze published single-cell RNA-seq datasets (Sharir et al., 2019; Krivanek et al., 2020) to assess expression of TENT5 paralogs in ameloblasts. These findings will be validated using targeted transcriptional analyses.

Human clinical relevance

We appreciate the suggestion to examine potential human enamel phenotypes. We will pursue retrospective analysis of clinical and imaging data from patients carrying TENT5A variants through our collaborations with rare disease networks and specialized centers in Europe and the United States. Any relevant findings will be incorporated into the revised manuscript.

Tissue sampling clarification

We apologize for imprecise terminology regarding transcriptomic sampling. The analyzed tissue corresponds to the proximal incisor region up to the mineralization stage. We will include a schematic and clarify nomenclature throughout the manuscript.

Language and data clarity

The manuscript will be thoroughly revised for clarity, consistency of terminology, figure referencing, and accuracy of citations. We will explicitly clarify the methodology used for protein quantification, including normalization strategy and densitometric analysis, to address inconsistencies noted in the supplementary data. We will also expand the discussion to address the biological relevance of moderate poly(A) shortening, referencing established literature demonstrating that even subtle changes in tail length can significantly influence translational efficiency.

Although AMELX is the most abundant enamel matrix protein and exhibits a consistent TENT5A-dependent poly(A) shortening phenotype, our data demonstrate that multiple secreted proteins are similarly affected. We will revise the text to clearly articulate that the enamel phenotype likely reflects the combined contribution of multiple TENT5A-regulated secretory factors rather than a single-gene effect.

We believe these revisions will substantially strengthen the mechanistic, quantitative, and conceptual framework of the study and provide a clearer foundation for interpreting TENT5A-dependent regulation of enamel biomineralization.

eLife Assessment

This important study characterizes a cascade of neural processes triggered by memory-based prediction errors. The study uses an impressive collection of approaches and methods to characterize and measure cognitive control, arousal, and memory changes as a function of memory-based violations. The analyses are technically sophisticated and rigorous and, taken together, provide solid evidence that there are multiple processes accompanying prediction errors, and that they differentially relate to successful encoding. The manuscript would be much improved by the addition of a discussion or visual schematic that integrates the numerous findings together into a more coherent model.

Reviewer #1 (Public review):

Summary:

This manuscript describes a multi-modal study of associative learning and memory in humans that combines scalp EEG, pupillometry and behavioral analysis to explore the construct of mnemonic prediction errors (MPEs), in terms of their relationship to attention and cognitive control. Across two pooled studies, participants performed associative memory tasks in which they learned the relationship between a cue word (action verb) and a subsequent picture (animate or inanimate) with a strong vs. weak (4 or 1 repetitions) encoding manipulation. At test, participants were encouraged to generate a prediction following the cue word to determine whether the subsequently presented picture was a match or a mismatch. The timecourse of pupillary responses during match decisions was decomposed using temporal principal components analysis, which identified 6 distinct and overlapping processes. Some of the components (PC3/PC4) exhibited sensitivity to both the strength and mismatch conditions, as well as behavior (both RT and accuracy) and retrieval success on the subsequent trial. Furthermore, relationships were also observed between pupillary responses (specifically for PC4) and both frontal theta and posterior alpha power measures obtained from scalp EEG in Experiment 2, as well as for frontal theta and subsequent learning from mismatch stimuli (assessed using subsequent memory findings from a surprise recognition test). The authors suggest the findings indicate that MPEs elicit changes in attention, arousal and cognitive control which impact subsequent learning.

Strengths:

This manuscript has many strengths, including a clever study design, thoughtful integration of multiple neurocognitive measures, and a set of rigorous and technically sophisticated analyses, which reveal a large set of relationships among the measures and behavior. The findings demonstrating brain/physiology-behavior relationships are particularly important, in that they point to potential functional consequences of MPES.

Weaknesses:

The technical proficiency and complexity of the study and analysis also present a clear limitation and challenge for interpretation. As a reader, even those who are quite knowledgeable about the methods, constructs, and questions being addressed will often struggle (as this reviewer did) to keep the large set of findings in mind and gain an understanding of how they all fit together.

Indeed, it seems like there are many threads running together in the paper, which makes it challenging to find the through-line of the key findings, or to understand how they might relate to some pre-existing hypotheses, rather than merely interesting patterns detected in the data. In the Introduction and Discussion, it seems as if the key question is to understand the pathways by which MPEs impact cognition, but this is a rather broad topic, so it is not clear exactly what the authors are aiming at with this question and study design.

As an example, authors operationalize frontal theta power as an index of cognitive control demand, and one of the pathways by which MPEs impact cognition. But this point becomes somewhat circular, since it is not clear how or why the Mismatch x Strength interaction in frontal theta reflects that demand. It would have been better to set this pattern up in the Introduction as a theoretically driven hypothesis, since it currently appears more like a post-hoc interpretation. This is mirrored by how the issue is first brought up in the Introduction, where it states somewhat vaguely: "whether MPEs are followed by an increase in frontal theta... warrants closer examination". Later in the results, there are findings relating frontal theta to pupil dilation, posterior alpha suppression and then subsequent memory. It was hard to understand how all the findings might be linked together functionally or conceptually. Are the authors potentially postulating a mediating or mechanistic pathway, in which the MPE leads to increased cognitive control (frontal theta), which then leads to enhanced subsequent memory of those events? If this is the case, then maybe a formal path analysis would be the best way to test or state this hypothesis. It would also be useful to specify more clearly how the pupil components and alpha suppression factor into this mediating path, since it was not clear.

Relatedly, the authors suggest that internal attention and arousal also play relevant roles in this pathway, but these are also not clear. In some cases, it is stated as if this is a distinct pathway from the cognitive control one, since there is a focus in the results on the independence of frontal theta and posterior alpha, but elsewhere they seem to be treated as two aspects, or distinct steps, within a single pathway. Again, these different threads of the findings were quite challenging for the reader to follow. Pathway analyses, such as with multiple mediation or moderated mediation, could be a useful way to address this question. For example, it seems as if readiness-to-remember is another behavioral outcome (like subsequent memory) that could be used in the search for mediators.

At the minimum, it would be quite helpful to have diagrammatic figures that specify the hypothesized and observed relationships between independent variables (Strength, Mismatch), physiological indices (pupil dilation components, frontal theta, posterior alpha) and key outcome measures (accuracy, RT, next-trial retrieval success, subsequent memory), so that the reader can refer back to them as each component of the analyses is conducted.

Minor Points:

Many figures had x-axes showing a pupil component or EEG power metric broken down by quartile or quintile. Yet nowhere is it ever explained why this graphical (or analytic?) approach is used and what it reflects, or how it is decided which break down to use (quartile/quintile). If the data are analyzed as a correlation, why is a scatterplot not shown instead?

It was surprising that, unlike readiness-to-remember, which was analyzed via logistic regression and odds-ratio, subsequent memory was not analyzed in the same fashion (i.e., as a binary outcome variable predicted by frontal theta), rather than in a reverse chronological one (subsequent memory predicting frontal theta). Historically, it was the case that subsequent memory was analyzed in this manner, but that was before the era in which trial-level linear mixed-effect models were in wide usage, as they are implemented in this study. Thus, the choice seems like a wasted opportunity or a step backwards analytically.

Reviewer #2 (Public review):

Summary:

The authors studied cognitive control and attention in response to mnemonic prediction errors (MPEs): situations in which the external reality violates internal memory-based predictions. The behavioral task first established strong versus weak predictions, and then either confirmed or violated these predictions. The authors examined markers of cognitive control (frontal theta) and attention (posterior alpha suppression, pupil response) while strong and weak predictions were confirmed or violated. They found increased cognitive control (frontal theta) for strong MPEs, which correlated with subsequent memory. Markers of attention (alpha suppression, pupil response) also accompanied strong MPEs but did not correlate with subsequent memory. Pupil response was investigated using an interesting approach that decomposes the response into different components, finding that different components respond earlier or later and show different correlations with MPEs and their strength. The authors also investigated how EEG, reaction time, and pupil responses correlated with one another, providing further insight into the mechanism underlying the response to MPEs. Together, the study points toward multiple control and attention mechanisms involved in MPE response and memory.

Strengths:

The study has a clear behavioral paradigm with multiple measures - behavioral, EEG, and pupillometry that offer an investigation into different aspects of MPE response and memory.

The study is also very comprehensive in looking at multiple phases in processing MPEs: the prediction phase (prior to the violation), the response to MPEs, and subsequent memory of MPEs, all within one study. Specifically, the link between neural mechanisms and subsequent memory is a major advancement, as most prior studies did not include this component. Mechanisms underlying subsequent memory of MPEs are theoretically important, as a primary function of MPEs is to promote learning and memory. As the authors mention, the different neural and pupillary signals are not robustly correlated, suggesting multiple mechanisms underlying MPE detections, which is interesting, offers avenues for future research, and can facilitate a better theory of how MPEs are processed in the brain. Finally, the decomposition of pupil response into different components and their correlation with behavior (RT during match/MPE detection) is interesting.

Weaknesses:

The methods are rigorous, and the claims are mostly supported by the data, but there are a few weaknesses or places that could be improved:

(1) The authors conduct PCA analysis to identify different components of the pupillary response to MPE and relate them to behavior. Specifically, the authors identify components PC3 and PC4, which they interpret as related to MPE. However, some parts of the interpretation could be clearer or better justified:

(a) The authors refer to PC4 as "post-decision cognitive processing". But, given that RT was between .5-.7s, and PC3 peaked after more than 1s, wouldn't it be cautious to interpret PC3 as post-decision as well?

(b) MPEs overall elicit longer RTs in this study, suggesting that long RT is a behavioral marker of MPE. Nonetheless, the authors argue on p. 12: "Altogether, these findings indicate that when stronger mnemonic predictions (as indexed by shorter RTs) were violated." And, PC3 is correlated with shorter RTs for mismatches, meaning that behaviorally, these trials were more similar to matches. Thus, how do the authors interpret shorter versus longer RTs for MPEs, and what processes do these RT reflect?

(2) The brain to pupil relationship (p. 13-14): If I understand correctly, this was done on a trial-by-trial basis, but the high temporal resolution allows doing the analysis in a time-resolved manner - does brain activity at a certain time point preceding/following the pupil response correlate with the pupil response? It might be that cognitive control influences attention mechanisms or vice versa (because there is some overlap in the response). Although not testing causality, this temporally resolved correlation would be an interesting way to start probing how signals might influence each other.

(3) The relationships the authors find between brain measures and pupil components were largely not specific to mismatches/matches. However, are they specific to this task? I think it would benefit the paper to show that these relationships are potentially specific to making match/mismatch memory decisions, versus, e.g., any stimulus processing. For example, the authors could run the same analyses locked to stimuli in the study phase, anticipating a different pattern, if indeed these findings are specific to the associative memory task.

(4) During memory retrieval (i.e., before the probe), the authors find that frontal theta, a marker of cognitive control, was associated on a trial-by-trial basis with more posterior alpha (i.e., less alpha suppression, potentially reflecting less attention), and that this association was stronger for weaker predictions. The authors interpreted this as weaker predictions necessitating more cognitive control, and that more cognitive control was recruited specifically in trials where retrieval included less content (memory reinstatement) to attend to. Generally, cognitive control is recruited to facilitate memory retrieval. If so, one possible interpretation is that this correlation reflects cognitive control effort that has failed to produce enough memory reinstatement. The other possibility is that this correlation reflects more specific retrieval of the correct probe, without retrieval of interfering items (i.e., overall less content). I believe that the former explanation predicts that this correlation would be associated with longer RTs (more difficult decisions), while the latter predicts shorter RTs (easier decisions due to successful retrieval), at least for matches.

(5) In section 3, the authors found a positive relationship between alpha during memory retrieval and PC3 during MPE. If I understood correctly, this means that less attention during retrieval (less suppression) is correlated with a stronger PC3 response. How do the authors interpret this? Maybe along the same lines as in (5), specifically retrieving the correct information (i.e., less retrieved content to attend to) means a stronger prediction, leading to a stronger MPE, and a stronger MPE response, as reflected by PC3?

(6) The results with subsequent memory are important and address a major gap in the field that largely did not relate neural effects of MPE to subsequent memory. However, one major limitation of the study is that the authors did not test memory for matches. I understand the logic of avoiding testing matches. Because matches were repeated more times in the study, it's not a fair comparison, and could change participants' overall criterion for old/new decisions. However, one possibility would have been to test only the weak prediction; this could have given some specificity to the neural subsequent memory findings.

(7) The authors nicely characterized the different PC of pupillary MPE response. But, with respect to subsequent memory, they only present pupil size. Unless there is some methodological reason that prevents testing subsequent memory on the PC, I think this will be very informative about the potential mechanisms underlying memory of MPE.

(8) This paper includes many interesting findings, and I am not sure how they all come together into a cohesive mechanistic understanding of MPE response and subsequent memory. I think the paper would benefit from either a conceptual mechanism figure or, in the Discussion, have a summary of a proposed mechanism integrating the findings together.

(9) Relatedly, the section "Immediate, strength-sensitive neurocognitive impacts of MPEs" does not link the arguments to specific data points, so it's hard to follow which data specifically the authors are interpreting.

(10) If I understand correctly, the authors did not find improved memory for strong compared to weak MPE. First, I think this behavioral result should be incorporated in the main paper and in the interpretation of the results. Second, given that the neural effects the authors tested either correlated with memory for strong MPE or did not show a relationship with memory, what neural/pupil response could explain memory for weak MPE?

eLife Assessment

This computational study constitutes an extension to prior work on biophysical calcium-based synaptic plasticity rules with metaplasticity, investigating how single neurons can learn to perform non-linear pattern classification. This important work presents a significantly simpler solution to the studied problem with potentially broad applicability, there is however incomplete evidence to support the core conclusions.

Reviewer #1 (Public review):

Summary:

This computational modelling study addresses the important question of how neurons can learn non-linear functions using biologically realistic plasticity mechanisms. The study extends the previous related work on metaplasticity by Khodadadi et al. (2025), using the same detailed biophysical model and basic study design, while significantly simplifying the synaptic plasticity rule by removing non-linearities, reducing the number of free parameters, and limiting plasticity to only excitatory synapses. The rule itself is supervised by the presence or absence of a binary dopamine reward signal, and gated by separate calcium-sensitive thresholds for potentiation and depression. The author shows that, when paired with a strong form of dendritic non-linearity called a "plateau potential" and appropriate pre-existing dendritic clustering of features, this simpler learning mechanism can solve a non-linear classification task similar to the classic XOR logic operator, with equal or better performance than the previous publication. The primary claims of this publication are that metaplasticity is required for learning non-linear feature classification, and that simultaneous dynamics in two separate thresholds (for potentiation and depression) are critical in this process. By systematically studying the properties of a biophysically plausible supervised learning rule, this paper adds interesting insights into the mechanics of learning complex computations in single neurons.

Strengths:

The simplified form of the learning rule makes it easier to understand and study than previous metaplasticity rules, and makes the conclusions more generalizable, while preserving biological realism. Since similar biophysical mechanisms and dynamics exist in many different cell types across the whole brain, the proposed rule could easily be integrated into a wide range of computational models specializing in brain regions beyond the striatum (which is the focus of this study), making it of broad interest to computational neuroscientists. The general approach of systematically fixing or modifying each variable while observing the effects and interactions with other variables is sound and brings great clarity to understanding the dynamic properties and mechanics of the proposed learning rule.

Weaknesses:

General notes

(1) The credibility of the main claims is mainly limited by the very narrow range of model parameters that was explored, including several seemingly arbitrary choices that were not adequately justified or explored.

(2) The choice to use a morphologically detailed biophysical model, rather than a simpler multi-compartment model, adds a great deal of complexity that further increases uncertainty as to whether the conclusions can generalize beyond the specific choices of model and morphology studied in this paper.

(3) The requirement for pre-existing synaptic clustering, while not implausible, greatly limits the flexibility of this rule to solve non-linear problems more generally.

(4) In order to claim that two thresholds are truly necessary, the author would have to show that other well-known rules with a single threshold (e.g., BCM) cannot solve this problem. No such direct head-to-head comparisons are made, raising the question of whether the same task could be achieved without having two separate plasticity thresholds.

Specific notes

(1) Regarding the limited hyperparameter search:

(a) On page 5, the author introduces the upper LTP threshold Theta_LTP. It is not clear why this upper threshold is necessary when the weights are already bounded by w_max. Since w_max is just another hyperparameter, why not set it to a lower value if the goal is to avoid excessively strong synapses? The values of w_max and Theta_LTP appear to have been chosen arbitrarily, but this question could be resolved by doing a proper hyperparameter search over w_max in the absence of an upper Theta_LTP.

(b) The author does not explore the effect of having separate learning rates for theta_LTP and theta_LTD, which could also improve learning performance in the NFBP. A more comprehensive exploration of these parameters would make the inclusion of theta_max (and the specific value chosen) a lot less arbitrary.

(c) Figure 4 Supplements 3-4: The author shows results for a hyperparameter search of the learning rule parameters, which is important to see. However, the parameter search is very limited: only 3 parameter values were tried, and there is no explanation or rationale for choosing these specific parameters. In particular, the metaplasticity learning rates do not even span one order of magnitude. If the author wants to claim that the learning rule is insensitive to this parameter, it should be explored over a much broader range of values (e.g., something like the range [0.1-10]).

(2) Regarding the similarity to BCM, the author would ideally directly implement the BCM learning rule in their model, but at the least the author could have shown whether a slight variant of their rule presented here can be effective: for example having a single (plastic, not fixed) Ca-dependent threshold that applies to both LTP and LTD, with a single learning rate parameter.

(3) This paper is extremely similar (and essentially an extension) to the work of Khodadadi et al. (2025). Yet this paper is not mentioned at all in the introduction, and the relation between these papers is not made clear until the discussion, leaving me initially puzzled as to what problems this paper addresses that have not already been extensively solved. The introduction could be reworked to make this connection clearer while pointing out the main differences in approach (e.g., the important distinction between "boosting" nonlinearities and plateau potentials).

(4) The introduction is missing some citations of other recent work that has addressed single-neuron non-linear computation and learning, such as Gidon et al (2020); Jones & Kording (2021).

(5) Figure 1: The figure prominently features mGluR next to the CaV channel, but there is no mention of mGluR in the introduction. The introduction should be updated to include this.

(6) Could the author explain why there is a non-monotonic increase/decrease in the [Ca]_L in Figure 2B_4? Perhaps my confusion comes from not understanding what a single line represents. Does each line represent the [Ca] in a single spine (and if so, which spine), or is each line an average of all the spines in a given stim condition?

(7) Row 124 (page 4): L-type Ca microdomains (in which ions don't diffuse and therefore don't interact with Ca_NMDA) is a critical assumption of this model. The references for this appear only in the discussion, so when reading this paper, I found myself a bit confused about why the same ion is treated as two completely independent variables with separate dynamics. Highlighting the assumption (with citations) a bit more clearly in the results section when describing the rule would help with understanding.

(8) Row 149 (page 5): The current formulation of the update rule is not actually multiplicative. The fact that the update is weight-dependent alone does not make it a multiplicative rule, and judging by equation (1) it appears to simply be an additive rule with a weight regularization term that guarantees weight bounds. For example, a similar weight-dependent update is also a core component of BTSP (Milstein et al. 2021; Galloni et al. 2025), which is another well-known *additive* rule. An actual multiplicative rule implies that the update itself is applied via a multiplication, i.e. w_new = w_old * delta_w

For an example of a genuinely multiplicative rule, see: Cornford et al. 2024, "Brain-like learning with exponentiated gradients"). Multiplicative rules have very different properties to additive rules, since larger weights tend to grow quickly while small weights shrink towards 0.

(9) Equation 1 (page 5): Shouldn't the depression term be written as: (w_min - w)? This term would be negative if w is larger than w_min, leading to LTD. As it is written now, a large w and small w_min would just cause further potentiation instead of depression.

(10) In the introduction, the teaching signal is described in binary terms (DA peak, or DA pause), but in Equation 1, it actually appears to take on 3 different values. Could the author clarify what the difference is between a "DA pause" and the "no DA" condition? The way I read it, pause = absence of DA = no DA

(11) Figure 3: In these experimental simulations, DA feedback comes in 400ms after the stimulus. The author could motivate this choice a bit better and explain the significance of this delay. Clearly, the equations have a delta_t term, but as far as the learning algorithm is concerned, it seems like learning would be more effective at delta_t=0. Is the choice of 400ms mainly motivated by experimental observations? On a related note, is it meaningful that the 200ms delta_t before the next stimulus is shorter than the 400ms pause from the first stimulus? Wouldn't the DA that arrives shortly before a stimulus also have an effect on the learning rule?

(12) Figure 4C: How is it possible that the theta_LTP value goes higher than the upper threshold (dashed line)? Equation 3 implies that it should always be lower.

(13) Row 429 (page 11): The statement that "without metaplasticity the NFBP cannot be solved" is overly general and not supported by the evidence presented. There exist many papers in which people solve similar non-linear feature learning problems with Hebbian or other bio-plausible rules that don't have metaplasticity. A more accurate statement that can be made here is that the specific rule presented in this paper requires metaplasticity.

(14) The methods section does not make any mention of publicly available code or a GitHub repository. The author should add a link to the code and put some effort into improving the documentation so that others can more easily assess the code and reproduce the simulations.

Reviewer #2 (Public review):

Summary:

The manuscript proposes interesting synaptic plasticity rules grounded in experimental data. Its main features are:

(1) plasticity depends on local calcium concentration driven by presynaptic activity and is independent of somatic action potentials,

(2) the rules incorporate metaplasticity, and (3) they demonstrate how a single neuron could address the feature-binding problem at the dendritic level.

The work extends a previous study (https://doi.org/10.7554/eLife.97274.2), to which the author also contributed.

The author models two calcium thresholds (LTP/LTD) from two different calcium sources (NMDA/VGCC), and these thresholds are flexible (metaplasticity rule, similar to BCM), which is claimed to be necessary for successful learning of both FBP and NFBP (linear and nonlinear feature binding problem with 1 or 2 patterns). The role of each threshold seems to be opposite and complementary. One extra condition has been added: an upper threshold for LTP. This threshold serves to stop synaptic strengthening once synapses are strong enough to evoke a plateau. With that, synapses are not strengthened to the maximal value, avoiding strong supralinear integration for irrelevant patterns.

Strengths:

The current model implements not only local synaptic plasticity but also metaplasticity and solves the FBP at the dendrite level. Another strong aspect of the model is that metaplasticity in the LTD threshold protects strengthened synapses from weakening. In this way, as the author mentioned, metaplasticity is able to protect learned patterns from being forgotten or weakened and prevent irrelevant patterns from being stored. This is a nice modelling example of metaplasticity being helpful in preventing the catastrophic interference or forgetting (as has been explicitly discussed in a recent article https://doi.org/10.1016/j.tins.2022.06.002 ). The author might want to briefly mention or emphasize this aspect of the model, which might be interesting also for the AI community.

Weaknesses:

(1) What is novel in the current paper as compared to Khodadadi et al. eLife 2025? That is not completely clear and should be made clearer. Is it only a minor difference related to the fact that the new learning rule has metaplasticity in both calcium thresholds and is simpler? This seems to be just an incremental increase in knowledge/methods. Can the author defend his paper against this point from the „devil's advocate"? How is the conclusion of the author in the abstract that „metaplasticity in both thresholds is necessary" reconcilable with his previous publication (Khodadadi et al. eLife 2025), in which only metaplasticity in one threshold was successful in solving the nonlinear feature binding problem?

(2) As far as I can judge without testing the model, metaplasticity causes thresholds to monotonically increase during systematic pattern presentation, which stabilizes weights and allows pattern separation. Due to the closed-loop nature of the current implementation, where metaplasticity only happens if plasticity happens, this also effectively locks patterns in place. However, flexible learning is an essential mechanism for survival. Imagine a mutation event takes place and bananas suddenly become red and/or strawberries turn yellow. It seems that the current model would be unable to adapt to these new patterns even if rewards were to be shifted. While out of the scope of the study, due to its importance, I feel that pattern shifting/relearning should at least be briefly discussed. How could the model be improved to allow relearning?

eLife Assessment

Based on the perceived low efficacy of current therapies targeted to FGFR2 in gastric cancer (GC), the authors investigate an approach which combines SHP2 inhibition with existing FGFR2 inhibitors. The data were largely collected and analysed using solid and validated methodology. There is some useful data regarding combination therapy in a new clinical cohort, which supports previous studies that have reported the potential of targeting RTKs together with phosphatases.

Reviewer #1 (Public review):

The manuscript entitled "Blocking SHP2 1 benefits FGFR2 inhibitor and overcomes its resistance in 2 FGFR2-amplified gastric cancer" by Zhang, et al., reports that FGFR2 was amplification in 6.2% (10/161) of gastric cancer samples and that dual blocking SHP2 and FGFR2 enhanced the effects of FGFR2 inhibitor (FGFR2i) in FGFR2-amplified GC both in vitro and in vivo via suppressing RAS/ERK and PI3K/AKT pathways. Furthermore, the authors also showed that SHP2 blockade suppressed PD-1 expression and promoted IFN-γ secretion of CD8+ 46 T cells, enhancing the cytotoxic functions of T cells. Thus, the authors concluded that dual blocking SHP2 and FGFR2 is a compelling strategy for treatment of FGFR2-amplified gastric cancer. Although the finding is interesting, the finding that FGFR2 is amplified in gastric cancer and that FGFR inhibitors have some effect on treating gastric cancer is not novel. The data quality is not high, the effects of double inhibitions are not significant. It appears that the conclusions are largely overstated, the supporting data is weak and not compelling.

The data in Figure 1 is not novel; similar data have been reported elsewhere.

It is unclear why the two panels in fig 2a and 2b can not be integrated into one panel, which will make it easier to compare the activities.

The synergetic effects of azd4547 and shp099 are not significant in Fig 2e and 2f, as well as in Fig. 3g and Fig. 4f

Data in Fig. 5 is weak and can be removed. It is unclear why FGFR inhibitor has some activities toward t cells since t cells do not express FGFR.

Reviewer #2 (Public review):

Summary:

This manuscript reports the application of a combined targeted therapeutic approach to gastric cancer treatment. The RTK, FGFR2 and the phosphatase, SHP2 are targeted with existing drugs; AZD457 and SHP099, respectively. Having shown increased mRNA levels of FGFR2 and SHP2 in a patient population and highlighted the issue of resistance to single therapies the combination of inhibitors is shown to reduce cancer-related signalling in two gastric cell lines. The efficacy of the dual therapy is further demonstrated in a single patient case study and mouse xenograft models. Finally, the rationale for SHP2 inhibition is shown to be linked to immune response.

Strengths:

The data is generally well presented, and the study invokes a novel patient data set which could have wider value. The study provides additional evidence to support the combined therapeutic approach of RTK and phosphatase inhibition.

Weaknesses:

Combined therapy approaches targeting RTKs and SHP2 have been widely reported. Indeed, SHP099 in combination with FGFR inhibitors has been shown to overcome adaptive resistance in FGFR-driven cancers. Furthermore, the inhibition of SHP2 has been documented to have important implications in both targeting proliferative signalling as well as immune response. Thus, it is difficult to see novelty or a significant scientific advance in this manuscript. Although the data is generally well presented, there is inconsistency in the interpretation of the experimental outcomes from ex vivo, patient and mouse systems investigated. In addition, the study provides only minor or circumstantial understanding of the dual mechanism.

Using data from a 161 patient cohort FGFR2 was identified as displaying amplification of FGFR2 in ~6% with concomitant elevation of mRNA of patients which correlated with PTPN11 (SHP2) mRNA expression. The broader context of this data is of value and could add a different patient demographic to other data on gastric cancer. However, there is no detail on patient stratification or prior therapeutic intervention.

Comments on revisions: This has been attended to in the revised version

In SNU16 and KATOIII cells the combined therapy is shown to be effective and appears to be correlated with increase apoptotic effects (i.e. not immune response).

Fig 2E suggests that the combined therapy in SNU16 cells is little better than FGFR2-directed AZD457 inhibitor alone, particularly at the higher dose.

The individual patient case study described via Fig 3 suggests efficacy of the combined therapy (at very high dosage), however the cell biopsies only show reduced phosphorylation of ERK, but not AKT. This is at odds with the ex vivo cell-based assays. Thus, it is not clear how relevant this study is.

The mouse xenograft study shows a convincing reduction in tumor mass/volume and a clear reduction in pAKT, whilst pERK remains largely unaffected by the combined therapeutic approach. This is in conflict with the previous data which seems to show the opposite effect.

Comments on revisions: The authors have clarified this point

In all, the impact of the dual therapy is unclear with respect to the two pathways mediated by ERK and AKT.

Finally, the authors demonstrate the impact of SHP2 on PD-1 expression and propose that the SHP099/AZD4547 combination therapy significantly induces the production of IFN-γ in CD8+ T cells. This part of the study is unconvincing and would benefit from an investigation of the tumor micro-environment to assess T cell infiltration.

Reviewer #3 (Public review):

Summary:

Fibroblast growth factor receptor 2 (FGFR2) is a receptor tyrosine kinase that can be amplified in gastric cancer and serves as a potential therapeutic target for this patient population. However, targeting FGFR2 has shown limited efficacy. Thus, this study seeks to identify additional molecules that can be effectively targeted in FGFR2 amplified gastric cancer, with a focus on Src homology region 2-containing protein tyrosine phosphatase 2 (SHP2). The authors first demonstrate that 6% of gastric cancer patients in a cohort of human patient samples exhibit FGFR2 amplification. Furthermore, they demonstrate that FGFR2 mRNA expression is positively correlated with PTPN11 gene expression (which is the gene that encodes the SHP2 protein). Using human gastric cancer cell lines with amplified FGFR2, the authors then test the effects of combining the FGFR inhibitor AZD4547 with the SHP2 inhibitor SHP099 on tumor cell death and signaling molecules. They demonstrate that combining the two inhibitors is more effective at tumor cell killing and reducing activation of downstream signaling pathways than either inhibitor alone. In further studies, the authors obtained gastric cancer cells with FGFR2 amplification from a patient that was treated with FGFR2 inhibitor. While this patient initially showed a partial response, the patient ultimately progressed, demonstrating resistance to FGFR2 inhibition. Following isolation of tumor cells from the patient's ascites, the authors demonstrate that these cells are sensitive to the combination treatment of AZD4547 and SHP099. Further studies were performed using a xenograft model using athymic nude mice in which the combination of SHP099 and AZD4547 were found to reduce tumor growth more significantly than either treatment alone. Finally, the authors demonstrate using an in vitro culture model that this combination treatment enhances T cell mediated cytotoxicity. The authors conclude that targeting FGFR2 and SHP2 represents a potential combination strategy in gastric patients with FGFR2 amplification.

Strengths:

The authors demonstrate that FGFR2 amplification positively correlates with PTPN11 in human gastric cancer samples, providing a rationale for combination therapies. Furthermore, convincing data are provided demonstrating that targeting both FGFR and SHP2 is more effective than targeting either pathway alone using in vitro and in vivo models. The use of cells derived from a gastric cancer patient that progressed following treatment with an FGFR inhibitor is also a strength. The findings from this study support the conclusion that SHP2 inhibitors enhance the efficacy of FGFR-targeted therapies in cancer patients. This study also suggests that targeting SHP2 may also be an effective strategy for targeting cancers that are resistant to FGFR-targeted therapies.

Weaknesses:

The main caveat with these studies is the lack of an immune competent model with which to test the finding that this combination therapy enhances T cell cytotoxicity in vivo.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

The data in Figure 1 is not novel, similar data has been reported elsewhere.

We are grateful for the critical evaluation of our finding. Although there have been a few researches indicating the prevalence of FGFR2-amplified GC patients, our research provided a novel dataset of 161 GC patients using next-generation sequencing (NGS) in China, further emphasizing the high frequency of FGFR2 amplification in gastric cancer patients. Moreover, the proportion of FGFR2-amplified GC patients in our center (6.2%) is relatively higher than that of TCGA cohort (5%).

We have transferred the original Figure 1C and 1D to the supplementary figures, and constructed a novel pie chart for Nanjing Drum Tower Hospital cohort to compare with the TCGA cohort.

It is unclear why the two panels in Fig 2a and 2b can not be integrated into one panel, which will make it easier to compare the activities.

Thanks for pointing this out. In the first figure of Figure 2a and 2b, we performed gradient concentration CCK8 detection on the cytotoxicity of SHP099 against tumor cells. In the second figure, we selected 10 μm (IC50) as the fixed concentration of SHP099 for combined efficacy testing with gradient concentration of AZD4547. Moreover, the units of the horizontal axis in both figure 2a and 2b cannot be unified. Therefore, we believe that the two figures in figures 2a and 2b are not suitable for merging into one figure.

For the convenience of observation, we integrated the first panel of figure 2a and 2b into one panel, and integrated the second panel in the same way.

The synergetic effects of azd4547 and shp099 are not significant in Fig 2e and 2f, as well as in Fig. 3g and fig. 4f

In Fig 2e and 2f, we not only analyzed the synergetic effects of 3 nM (a relatively lower dose) AZD4547 and 10 μm SHP099, but also 10 nM (a relatively higher dose) AZD4547 and 10 μm SHP099. The synergetic effects of different dosage combinations should be compared correctly. From our perspective, the combination treatment led to a stronger inhibition of phospho-FGFR, phospho-SHP2 and FGFR2-initiated downstream signaling molecules, especially in KATOIII.

For ease of comparison, we circled 10 μm SHP099, 10nM AZD4547 and 10nM AZD4547+10 μm SHP099 in red.

Author response image 1.

Author response image 2.

We also circled 10μM SHP099, 3nM AZD4547 and 3nM AZD4547+10 μm SHP099 in blue.

Author response image 3.

Author response image 4.

For ease of comparison, we also conducted grayscale value analysis and normalization using image J.

Author response image 5.

Author response image 6.

Author response image 7.

Author response image 8.

In Fig. 3g, the combination therapy exhibited relatively stronger inhibitory effects on phospho-ERK, phospho-AKT and phospho-mTOR.

For ease of comparison, we conducted grayscale value analysis and normalization using image J.

The unclear effect of combination therapy may be due to the presence of impurities other than tumor cells in patient’s ascites.

Author response image 9.

In Fig. 4f, it was obvious that phospho-AKT and phospho-mTOR were further suppressed in combination group.

For ease of comparison, we conducted grayscale value analysis and normalization using image J.

Author response image 10.

Therefore, in our opinions, our data could relatively sufficiently confirm the synergetic effects of AZD4547 and SHP099.

Data in Fig. 5 is weak and can be removed. It is unclear why FGFR inhibitor has some activities toward t cells since t cells do not express FGFR.

The activation effect of SHP099 on T cells has been validated in many articles. In a previous study published in Cancer Immunology Research, it was pointed out that the combination of FGFR2 inhibitor erdafitinib and PD-1 antibody can activate T cells and downregulate T cell surface exhaustion related factors (including PD-1) in vivo Therefore, the anti-tumor immune effect of FGFR2 inhibitor cannot be ignored. Although T cells do not express FGFR, FGFR2 inhibitors may still affect PD-1 expression on the surface of T cells in some other ways, which requires further research. We have deleted fig.5D in our article. We believe that the combination of FGFR2 inhibitor and SHP2 inhibitor not only has a direct killing effect on tumor cells, but also promotes anti-tumor immunity by activating T cells. Therefore, we believe that the in vitro data in Figure 5 is also meaningful.

Reviewer #2 (Public review):

Strengths:

The data is generally well presented and the study invokes a novel patient data set which could have wider value. The study provides additional evidence to support the combined therapeutic approach of RTK and phosphatase inhibition.

We sincerely thank the reviewer for the critical evaluation and appreciation of our findings.

Weaknesses:

Combined therapy approaches targeting RTKs and SHP2 have been widely reported. Indeed, SHP099 in combination with FGFR inhibitors has been shown to overcome adaptive resistance in FGFR-driven cancers. Furthermore, the inhibition of SHP2 has been documented to have important implications in both targeting proliferative signalling as well as immune response. Thus, it is difficult to see novelty or a significant scientific advance in this manuscript. Although the data is generally well presented, there is inconsistency in the interpretation of the experimental outcomes from ex vivo, patient and mouse systems investigated. In addition, the study provides only minor or circumstantial understanding of the dual mechanism.

We acknowledge that our research on the mechanism of dual inhibition is not deep enough. There remain more in-depth mechanisms of the combination of SHP2 inhibitor and RTK inhibitors needed to be explored, and it would be the main direction of our future study.

Using data from a 161 patient cohort FGFR2 was identified as displaying amplification of FGFR2 in ~6% with concomitant elevation of mRNA of patients which correlated with PTPN11 (SHP2) mRNA expression. The broader context of this data is of value and could add a different patient demographic to other data on gastric cancer. However, there is no detail on patient stratification or prior therapeutic intervention.

Thanks for pointing this out and we have added a table on patients’ stratification such as age, gender and so on. Unfortunately, data on patients’ prior therapeutic intervention weren’t collected.

In SNU16 and KATOIII cells the combined therapy is shown to be effective and appears to be correlated with increased apoptotic effects (i.e. not immune response).

Fig 2E suggests that the combined therapy in SNU16 cells is a little better than FGFR2-directed AZD457 inhibitor alone, particularly at the higher dose.

The individual patient case study described via Fig 3 suggests efficacy of the combined therapy (at very high dosage), however, the cell biopsies only show reduced phosphorylation of ERK, but not AKT. This is at odds with the ex vivo cell-based assays. Thus, it is not clear how relevant this study is.

The mouse xenograft study shows a convincing reduction in tumor mass/volume and clear reduction in pAKT, whilst pERK remains largely unaffected by the combined therapeutic approach. This is in conflict with the previous data which seems to show the opposite effect. In all, the impact of the dual therapy is unclear with respect to the two pathways mediated by ERK and AKT.

Thank you for the comment. Previous researches have confirmed that both RAS/ERK and PI3K/AKT pathways are two important downstream signaling of FGFR2. In Fig 2E and F, we observed that in FGFR2-amplified cell lines dual blockade had significant inhibitory effects both on p-ERK and p-AKT, and the inhibitory effect on p-ERK is greater than that on p-AKT. Similarly, in Fig 3G, dual blockade mainly suppressed p-ERK, and slightly inhibited p-AKT and p-mTOR in cancer cells derived from the individual patient. Thus, in the two types in-vitro models, dual inhibition simultaneously inhibited both RAS/ERK and PI3K/AKT pathways, and primarily inhibited RAS/ERK pathway, which is not contradictory.

Author response image 11.

Author response image 12.

Author response image 13.

For the in-vivo animal model. Although dual inhibition had inhibitory effects on both pathways, it mainly suppressed p-AKT.

In both in vivo and in vitro models, combination therapy has a certain inhibitory effect on the RAS/ERK and PI3K/AKT pathways, but the emphasis on the two is not the same in vivo and in vitro. Considering the significant differences between in vivo and in vitro models, we believe that this difference in emphasis is understandable.

Author response image 14.

Finally, the authors demonstrate the impact of SHP2 on PD-1 expression and propose that the SHP099/AZD4547 combination therapy significantly induces the production of IFN-γ in CD8+ T cells. This part of the study is unconvincing and would benefit from the investigation of the tumor micro-environment to assess T cell infiltration.

To investigate the tumor micro-environment to assess T cell infiltration, we have to establish our research model in immunocompetent mice. However, there is currently only one type of gastric cancer cell line derived from mice, MFC, which is not a cell line with FGFR2 amplification. We attempted to transfect FGFR2 amplification plasmids into MFC, but the transfection effect was poor, making it difficult to conduct in vivo animal experiments.

Reviewer #3 (Public review):

Strengths:

The authors demonstrate that FGFR2 amplification positively correlates with PTPN11 in human gastric cancer samples, providing rationale for combination therapies. Furthermore, convincing data are provided demonstrating that targeting both FGFR and SHP2 is more effective than targeting either pathway alone using in vitro and in vivo models. The use of cells derived from a gastric cancer patient that progressed following treatment with an FGFR inhibitor is also a strength. The findings from this study support the conclusion that SHP2 inhibitors enhance the efficacy of FGFR-targeted therapies in cancer patients. This study also suggests that targeting SHP2 may also be an effective strategy for targeting cancers that are resistant to FGFR-targeted therapies.

Weaknesses:

The main caveat with these studies is the lack of an immune competent model with which to test the finding that this combination therapy enhances T cell cytotoxicity in vivo. Discussing this limitation within the context of these findings and future directions for this work, particularly since the combination therapy appears to work quite well without the presence of T cells in the environment, would be beneficial.

Thank you for the great suggestion. To investigate the tumor micro-environment to assess T cell infiltration, we have to establish our research model in immunocompetent mice. However, there is currently only one type of gastric cancer cell line derived from mice, MFC, which is not a cell line with FGFR2 amplification. We attempted to transfect FGFR2 amplification plasmids into MFC, but the transfection effect was poor, making it difficult to conduct in vivo animal experiments.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Minor points. The manuscript is poorly written and loaded with language errors.

We sincerely thank you for your constructive suggestion and we are sorry for the mistake. We have polished the article and corrected these language errors.

Reviewer #2 (Recommendations for the authors):

In addition to the comments made in the Public Review the manuscript lacks detail on statistical analysis of experimental results.

Thank you for your advice. In response to the feedback, we have supplemented detail on statistical analysis of experimental results in the “Methods” part.

Reviewer #3 (Recommendations for the authors):

There are numerous grammatical errors throughout, and incorrect wording is used in some places (such as "syngeneic mouse tumor model" rather than "xenograft tumor model", line 253). Careful proofreading and editing of this manuscript is recommended.

Thank you for your suggestion. We have made corrections to the relevant content of the article.

AZD4547 is an FGFR-selective inhibitor and is not specific for FGFR2 as it also targets FGFR1 and FGFR3, this should be clarified in the text.

Thank you for rasing this point. We have clarified that AZD4547 is an FGFR-selective inhibitor targeting FGFR1-3 in the “Introduction” part.

The specific FGFR inhibitor(s) used to treat the patient with FGFR2 amplification, are the authors able to provide this information?

Thank you for raising this important issue. Indeed, due to the difficulty of small molecule drug development, the fastest clinical progress currently is in FGFR pan inhibitors. Recently, Relay Therapeutics has also developed a highly FGFR2-selective inhibitor, RLY-4008, in phase I/II clinical trials, but lacks preclinical research on gastric cancer.

Figure 2F: the p38 and p-p38 bands are cut off at the bottom

We sincerely thank you for your thoughtful feedback. we have improved our experimental methods and retested the two p38 and p-p38 in Figure 2F by western blotting.

Author response image 15.

eLife Assessment

This study investigates the folding and unfolding behavior of the doubly knotted protein TrmD-Tm1570, providing insight into the molecular mechanisms underlying protein knotting. The findings reveal multiple unfolding pathways and suggest that the formation of double knots may require chaperone assistance, offering valuable insights into topologically complex proteins. The evidence is convincing, supported by consistent agreement between simulation and experiment, though some aspects of the presentation and experimental scope could be clarified or expanded.

Reviewer #1 (Public review):

Summary:

This paper investigates the thermal and mechanical unfolding pathways of the doubly knotted protein TrmD-Tm1570 using molecular simulations, optical tweezers experiments, and other methods. In particular, the detailed analysis of the four major unfolding pathways using a well-established simulation method is an interesting and convincing result.

Strengths:

A key finding that lends credibility to the simulation results is that the molecular simulations at least qualitatively reproduce the characteristic force-extension distance profiles obtained from optical tweezers experiments during mechanical unfolding. Furthermore, a major strength is that the authors have consistently studied the folding and unfolding processes of knotted proteins, and this paper represents a careful advancement building upon that foundation.

Weaknesses:

While optical tweezers experiments offer valuable insights, the knowledge gained from them is limited, as the experiments are restricted to this single technique.

The paper mentions that the high aggregation propensity of the TrmD-Tm1570 protein appears to hinder other types of experiments. This is likely the reason why a key aspect, such as whether a ribosome or molecular chaperones are essential for the folding of TrmD-Tm1570, has not been experimentally clarified, even though it should be possible in principle.

Comments on revisions:

According to reviewers' comments, the authors revised the manuscript appropriately.

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors combined coarse-grained structure-based model simulation, optical tweezer experiments, and AI-based analysis to assess the knotting behavior of the TrmD-Tm1570 protein. Interestingly, they found that while the structure-based model can fold the single knot from TrmD and Tm1570, the double-knot protein TrmD-Tm1570 cannot form a knot itself, suggesting the need for chaperone proteins to facilitate this knotting process. This study has strong potential to understand the molecular mechanism of knotted proteins, supported by many experimental and simulation evidence. However, there are a few places that appear to lack sufficient details, and more clarification in the presentation is needed.

Strengths:

A combination of both experimental and computational studies. The authors have addressed my questions in their revised manuscript. I appreciate their efforts.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

This paper investigates the thermal and mechanical unfolding pathways of the doubly knotted protein TrmD-Tm1570 using molecular simulations, optical tweezers experiments, and other methods. In particular, the detailed analysis of the four major unfolding pathways using a well-established simulation method is an interesting and valuable result.

Strengths:

A key finding that lends credibility to the simulation results is that the molecular simulations at least qualitatively reproduce the characteristic force-extension distance profiles obtained from optical tweezers experiments during mechanical unfolding. Furthermore, a major strength is that the authors have consistently studied the folding and unfolding processes of knotted proteins, and this paper represents a careful advancement building upon that foundation.

We appreciate and we thank the reviewer for reading our manuscript.

Weaknesses:

While optical tweezers experiments offer valuable insights, the knowledge gained from them is limited, as the experiments are restricted to this single technique.

The paper mentions that the high aggregation propensity of the TrmD-Tm1570 protein appears to hinder other types of experiments. This is likely the reason why a key aspect, such as whether a ribosome or molecular chaperones are essential for the folding of TrmD-Tm1570, has not been experimentally clarified, even though it should be possible in principle.

We appreciate the suggestion that clarifying the requirement for molecular chaperones or the ribosome in TrmD-Tm1570 folding is crucial. We are pleased to report that the experiment investigating the role of molecular chaperones in the folding of TrmD-Tm1570 is currently under investigation in our laboratory. These results will provide the clarification on this aspect and will be incorporated into a future manuscript.

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors combined coarse-grained structure-based model simulation, optical tweezer experiments, and AI-based analysis to assess the knotting behavior of the TrmD-Tm1570 protein. Interestingly, they found that while the structure-based model can fold the single knot from TrmD and Tm1570, the double-knot protein TrmD-Tm1570 cannot form a knot itself, suggesting the need for chaperone proteins to facilitate this knotting process. This study has strong potential to understand the molecular mechanism of knotted proteins, supported by much experimental and simulation evidence. However, there are a few places that appear to lack sufficient details, and more clarification in the presentation is needed.

Strengths:

A combination of both experimental and computational studies.

We appreciate and we thank the reviewer for reading our manuscript.

Weaknesses:

There is a lack of detail to support some statements.

(1) The use of the AI-based method, SOM, can be emphasized further, especially in its analysis of the simulated unfolding trajectories and discovery of the four unfolding/folding pathways. This will strengthen the statistical robustness of the discovery.

We thank the reviewer for this observation. However, the AI-based method, SOM, was applied to obtain the main representative trajectories for the mechanical unfolding MD simulations. Specifically, for the TrmD, Tm1570, and fusion protein (TrmD-Tm1570) we extracted the representative conformational states by selecting the most highly populated SOM clusters shown in SI Figure 5 - figure supplement 3. Then, by identifying the cluster centroid, we selected the nearest point (simulations). These correspond to the clusters number 1 for Tm1570, number 11 for TrmD, and number 7 for TrmD-Tm1570. A sentence was added in the main manuscript to clarify how the main representative confirmation was obtained.

On the other hand, no AI‑based methods were applied to the thermal unfolding simulations. The four thermal unfolding trajectories shown in Figure 3 were obtained as follows: (i) trajectories where TrmD unfolds first and its knot unties before Tm1570 unfolds, corresponding to pathway 1 (Figure 3A and E); (ii) trajectories where Tm1570 unfolds and unties first, followed by TrmD, corresponding to pathway 3 (Figure 3C and G); and (iii) trajectories where TrmD unfolds first, then Tm1570, after which the TrmD knot unties and finally the Tm1570 knot unties—this corresponds to pathway 2. Pathway 4 follows the same sequence but in the reverse order.

(2) The manuscript would benefit from a clearer description of the correlation between the simulation and experimental results. The current correlation, presented in the paragraph starting from Line 250, focuses on measured distances. The authors could consider providing additional evidence on the order of events observed experimentally and computationally. More statistical analyses on the experimental curves presented in Figure 4 supplement would be helpful.

We thank the reviewer for this suggestion. In response, we prepared additional statistical analyses in a table format reporting the average length‑change increments together with their standard deviations, and we clarified in the revised text that the ± values correspond to standard deviations. In addition, we quantified the percentage of TrmD, Tm1570, and TrmD-Tm1570 unfold completely, providing a clearer comparison of the order of events observed experimentally and computationally. These analyses have been incorporated into the revised manuscript, Tables 1 and 2.

(3) How did the authors calibrate the timescale between simulation and experiment? Specifically, what is the value \tau used in Line 270, and how was it calculated? Relevant information would strengthen the connection between simulation and experiment.

In our model time unit is defined by a relation , where m is the reduced mass unit, is an average average mass of an amino acid, m = 110 Da = 1.66 x 10^-27 kg, 𝜀 is the reduced energy unit, an average interaction energy between amino acids. We may assume that ε is around 2-3 kcal/mol = 2-3 x 6.95 x 10^-21 J, is a distance unit and is equal to 1 nm.

After plugging this values into the equation defining 𝜏 , we get: 𝜏 = 3.2 ps.

The definition of the time unit comes from the fact that this is how one can combine units of mass, distance and energy into an expression that has an unit of time.

The pulling speeds used in the simulations (0.05–0.15 Å/) correspond to approximately 1.6 -4.7 m/s in real units. These speeds are necessarily much higher than the experimental pulling The pulling speeds used in the simulations (0.05–0.15 Å/ ) correspond to approximately 1.6 - speed (20 nm/s), which is a well‑known limitation of steered molecular dynamics. However, our coarse‑grained model is run in an implicit solvent regime and does not explicitly include hydrodynamic friction. As a consequence, the simulated dynamics do not reproduce absolute real time kinetics. Instead, the comparison between simulation and experiment is made through relative unfolding pathways, force extension behavior, and contour length changes, which remain robust across the range of simulated pulling speeds.

Thus, 𝜏 = 3.2 ps is derived directly from the coarse‑grained model parameters rather than calibratedτ to experiment, and the connection between simulation and experiment is established through mechanistic agreement rather than matching absolute timescales.

We have now added a clarifying sentence to the manuscript (Methods and Materials - Mechanical unfolding simulations) explaining how the timescale was defined and how the value of  was obtained.

Reference: 

Szymczak, P., and Marek Cieplak. "Stretching of proteins in a uniform flow." The Journal of chemical physics 125.16 (2006).

(4) In Line 342, the authors comment that whether using native contacts or not, they cannot fold double-knotted TrmD-Tm1570. Could the authors provide more details on how non-native interactions were analyzed?

To analyze the role of non‑native interactions, we calculated two non‑native contact maps, first using a distance cutoff criterion and second by identifying the highly frustrated contacts based on the frustration index using Frustratometer (http://frustratometer.qb.fcen.uba.ar/) - figure below. From this procedure, the non‑native interactions were incorporated in the SBM C-alpha model to potentially assist refolding or knot formation. However, in neither case we observe successful refolding or the formation of the double‑knotted native topology. These results indicate that the addition of these non‑native contacts are insufficient to drive the refolding of the TrmD–Tm1570 protein. This result may suggest that the protein needs the support of chaperones or the active role of ribosomes to tie the two knots. We have now clarified this point more explicitly in the revised manuscript .

Author response image 1.

Native and non‑native contact maps for TrmD–Tm1570. The upper triangle (blue dots) corresponds to the cutoff‑based contact map and shows only unique contacts not present in the native contact map. The lower triangle (red dots) represents highly frustrated contacts, again showing only unique contacts absent from the native map. Black dots indicate the native contacts derived from the structure, and the contact map was generated using the Shadow Contact Map software. The blue and orange shadows correspond to the knot position for TrmD and Tm1570 proteins, respectively. 

(5) It appears that the manuscript lacks simulation or experimental evidence to support the statement at Line 343: While each domain can self-tie into its native knot, this process inhibits the knotting of the other domain. Specifically, more clarification on this inhibition is needed.

Explaining this phenomenon remains challenging, and several contributing factors are likely.

(1) The folding success rates of the individual TrmD and Tm1570 domains are low (<3%); folding of the double-knotted protein is therefore expected to be even less efficient. 

(2) While formation of a single knot is observed when the two domains are examined, the folded domain adopts a native-like but not fully native conformation, regardless of whether it is TrmD or Tm1570. (2A) Fluctuations of the unfolded second domain may impose a destabilizing load, promoting unfolding of the folded domain. (2B) Conversely, folding of one domain restricts the conformational space available to the other. Such restriction may have either stabilizing or destabilizing effects: although reduced conformational space (crowding) is generally thought to increase the probability of knot formation in polymers, in this system the constraint is localized rather than global.

(3) It is possible that extending the simulations to much longer timescales would allow formation of the second knot; however, within the timescales accessible here, unfolding of the first knot is observed instead.

(4) The TrmD–Tm1570 protein forms a dimer with a well-defined interface, whereas our simulations were performed on a monomeric unit. Consequently, both domains are solvent-exposed, forming an open two-domain system with tRNA-binding elements that are not stabilized by intermolecular interactions.

Taken together, these factors preclude a quantitative assessment of the dominant contribution. Our results suggest that efficient folding may require assistance from molecular chaperones or an active role of the ribosome in coordinating formation of the two knots.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) The paper notes at the beginning of its results section that simulations aiming to fully fold the TrmD-Tm1570 protein from a denatured state were unsuccessful. While the failure to achieve complete folding is itself an instructive and important result, there is room for improvement in how it's presented. The authors provide no specific details on what actually occurred during these simulations. It is plausible that some intermediate state was reached, and one can imagine that the knotting of the C-terminal part, Tm1570, was partially completed. A more detailed description of these outcomes would have been beneficial.

In the main manuscript (Figure 3), we reported the folding trajectories and the probability of native contact formation for the TrmD–Tm1570 protein, focusing on the four main observed unfolding pathways from our simulations. In addition to these common pathways, we also examined a small number of trajectories which one or both domains may refold. These are presented in Figure 3 - figure supplements 1 and 2, where we highlight a set of trajectories that we classify as rare events. In these rare trajectories, partial refolding and the formation of intermediate states can indeed be observed. However, as described in the main text, successful refolding of the fusion protein only occurs when the knot remains close to its native position and does not undergo large fluctuations along the chain. When the knot drifts significantly, refolding is not completed.

Figure 3 - figure supplement 1 shows six representative examples of intermediate states sampled during these simulations. As the reviewer suggested, some intermediate conformations were reached, including partial reformation of structural elements. However, only the trajectory which maintains the knot sufficiently close to its native location is able to do substantial refolding. We have now clarified this point more explicitly in the revised manuscript to better explain why full folding was not achieved and how the knot dynamics constrain the refolding process.

(2) Is it not possible to plot the degree of knot formation as a function of time or Q in Figure 3A-H? Doing so would make the verbally described results much clearer.

We thank the reviewer for the suggestion. Based on your observation, we have added a new figure in the SI manuscript (Figure 3 - figure supplement 3) showing the knot translocation as a function of the frames with their respective structure representations from the transitions, from folded to unfolded state and knot untied processes.

(3) Placement of a paragraph starting from line 250 looks odd to me. The paragraph describes simulation results of the mechanical unfolding, which is fully described in the following section. Specifically, the simulation result is discussed before describing its method/outline, which is to be avoided as far as possible.

According to the standard journal style, the Method section is described after the Discussion section. However, in the simulation's results, a sentence addressing the methods was included to guide the reader through the text. 

(4) This is only an optional request. It is highly desired to examine the in vitro folding of TrmD-Tm1570 with and without molecular chaperones. At least, authors can envision/discuss this direction.

We agree that examining the in vitro folding of TrmD–Tm1570 with and without molecular chaperones would provide important mechanistic insights into the role of the fold of knotted proteins. We are planning to perform these experiments as part of our ongoing work, and in the revised manuscript we will add a discussion on this direction and its potential impact.

Reviewer #2 (Recommendations for the authors):

(1) Figure 6C was not referenced or discussed in the manuscript.

We thank the reviewer for pointing this out. Figure 6C is indeed referenced and discussed in the manuscript.

(2) Several places refer to figures in the Supporting Information, and should be updated to refer to the supplement figures associated with the main figures. 

In the revised version we ensure that all references are updated and clearly labeled.

eLife Assessment

This important study provides a comprehensive comparison of the mechanisms through which different inhibitors affect the SARS-CoV-2 main protease, a pivotal antiviral drug target, and suggests a potentially broad-spectrum strategy to inhibit this critical viral enzyme by disrupting its dimerization states. However, whereas the biophysical analyses of the dimer stability are convincing, evidence supporting this new mode of mechanism to inhibit the main protease is incomplete and would benefit from a correlation of the biophysical observations with functional activity. With the functional validation part strengthened, this work would be of interest to biochemists and virologists working on anti-coronavirus drug discovery.

Reviewer #1 (Public review):

Summary:

Since dimerization is essential for SARS-CoV-2 Mpro enzymatic activity, the authors investigated how different classes of inhibitors, including peptidomimetic inhibitors (PF-07321332, PF-00835231, GC376, boceprevir), non-peptidomimetic inhibitors (carmofur, ebselen, and its analog MR6-31-2), and allosteric inhibitors (AT7519 and pelitinib), influence the Mpro monomer-dimer equilibrium using native mass spectrometry. Further analyses with isotope labeling, HDX-MS, and MD simulations examined subunit exchange and conformational dynamics. Distinct inhibitory mechanisms were identified: peptidomimetic inhibitors stabilized dimerization and suppressed subunit exchange and structural flexibility, whereas ebselen covalently bound to a newly identified site at C300, disrupting dimerization and increasing conformational dynamics. This study provides detailed mechanistic evidence of how Mpro inhibitors modulate dimerization and structural dynamics. The newly identified covalently binding site C300 represents novelty as a druggable allosteric hotspot.

Strengths:

This manuscript investigates how different classes of inhibitors modulate SARS-CoV-2 main protease dimerization and structural dynamics, and identifies a newly observed covalent binding site for ebselen.

Weaknesses:

The major concern is the absence of mutagenesis data to support the proposed inhibitory mechanisms, particularly regarding the role of the inhibitor binding site.

Reviewer #2 (Public review):

Summary:

This is a mechanistic study that provides new insights into the inhibition of SARS-CoV-2 Mpro.

Strengths:

The identification of dimer interface stabilization/destabilization as distinct inhibitory mechanisms and the discovery of C300 as a potential allosteric site for ebselen are important contributions to the field. The experimental approach is modern, multi-faceted, and generally well-executed.

Weaknesses:

The primary weaknesses relate to linking the biophysical observations more directly to functional enzymatic outcomes and providing more quantitative rigor in some analyses. While the study is overall strong, addressing its weaknesses and limitations would elevate the impact and translational relevance of the current manuscript.

(1) Correlation with Functional Activity:

The most significant gap is the lack of direct enzymatic activity assays under the exact conditions used for MS and HDX. While EC50 values are listed from literature, demonstrating how the observed dimer stabilization (by peptidomimetics) or dimer disruption (by ebselen) directly correlates with inhibition of proteolytic activity in the same experimental setup would solidify the functional relevance of the biophysical observations. For instance, does the fraction of monomer measured by native MS quantitatively predict the loss of activity? Also, the single inhibitor concentration used in each MS experiment needs to be specified in the main text and legends. A discussion on whether the inhibitor concentrations required to observe these dimerization effects (in native MS) or structural dynamics (in HDX-MS) align with EC50 values would be helpful for contextualizing the findings.

(2) For the two Cys residues found to be targeted by ebselen, what are their respective modification stoichiometry related to the ebselen concentration? Especially for the covalent binding site C300, which is proposed in this study to represent a novel allosteric inhibition mechanism of ebselen, more direct experimental evidence is needed to support this major hypothesis. Does mutation or modification of C300 affect the Mpro dimerization/monomer equilibrium and alter the enzymatic activity? If ebselen acts as a covalent inhibitor linked to multiple Cys, why is its activity only in the uM range?

(3) For the allosteric inhibitor pelitinib with low-uM activity, no significant differences in deuterium uptake of Mpro were observed. In terms of the binding affinity, what is the difference between pelitinib and ebselen? Some explanations could be provided about the different HDX-MS results between the two non-peptidomimetic inhibitors with similar activities.

(4) Native MS Quantification:

The analysis of monomer-dimer ratios from native MS spectra appears qualitative or semi-quantitative. A more rigorous and quantified analysis of the percentage of dimer/monomer species under each condition, with statistical replicates, would strengthen the equilibrium shift claims. For native MS analysis of each inhibitor, the representative spectrum can be shown in the main figure together with quantified dimer/monomer fractions from replicates to show significance by statistical tests.

(5) Changes of HDX rates in certain regions seem very subtle. For example, as it states 'residues 296-304 in the C-terminal region of M pro were more flexible upon ebselen binding (Figure 4c)', the difference is barely observable. The percentage of HDX rate changes between two conditions (with p values) can be specified in the text for each fragment discussed, and any change below 5% or 10% is negligible.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

Since dimerization is essential for SARS-CoV-2 Mpro enzymatic activity, the authors investigated how different classes of inhibitors, including peptidomimetic inhibitors (PF-07321332, PF-00835231, GC376, boceprevir), non-peptidomimetic inhibitors (carmofur, ebselen, and its analog MR6-31-2), and allosteric inhibitors (AT7519 and pelitinib), influence the Mpro monomer-dimer equilibrium using native mass spectrometry. Further analyses with isotope labeling, HDX-MS, and MD simulations examined subunit exchange and conformational dynamics. Distinct inhibitory mechanisms were identified: peptidomimetic inhibitors stabilized dimerization and suppressed subunit exchange and structural flexibility, whereas ebselen covalently bound to a newly identified site at C300, disrupting dimerization and increasing conformational dynamics. This study provides detailed mechanistic evidence of how Mpro inhibitors modulate dimerization and structural dynamics. The newly identified covalently binding site C300 represents novelty as a druggable allosteric hotspot.

Strengths:

This manuscript investigates how different classes of inhibitors modulate SARS-CoV-2 main protease dimerization and structural dynamics, and identifies a newly observed covalent binding site for ebselen.

Weaknesses:

The major concern is the absence of mutagenesis data to support the proposed inhibitory mechanisms, particularly regarding the role of the inhibitor binding site.

We thank the reviewer for the comments and recognition of our study. We agree that mutagenesis experiments are very helpful to validate the proposed mechanisms. We will perform site-directed mutagenesis of the key residue C300 and assess the effects of those C300 mutants on dimerization and enzymatic activity of Mpro, and integrate the results and discussion into the revised manuscript.

Reviewer #2 (Public review):

Summary:

This is a mechanistic study that provides new insights into the inhibition of SARS-CoV-2 Mpro.

Strengths:

The identification of dimer interface stabilization/destabilization as distinct inhibitory mechanisms and the discovery of C300 as a potential allosteric site for ebselen are important contributions to the field. The experimental approach is modern, multi-faceted, and generally well-executed.

We thank the reviewer for the positive comments and recognition of our study.

Weaknesses:

The primary weaknesses relate to linking the biophysical observations more directly to functional enzymatic outcomes and providing more quantitative rigor in some analyses. While the study is overall strong, addressing its weaknesses and limitations would elevate the impact and translational relevance of the current manuscript.

We thank the reviewer for the comments that are very helpful for improving the quality and impact of our manuscript.

(1) Correlation with Functional Activity:

The most significant gap is the lack of direct enzymatic activity assays under the exact conditions used for MS and HDX. While EC50 values are listed from literature, demonstrating how the observed dimer stabilization (by peptidomimetics) or dimer disruption (by ebselen) directly correlates with inhibition of proteolytic activity in the same experimental setup would solidify the functional relevance of the biophysical observations. For instance, does the fraction of monomer measured by native MS quantitatively predict the loss of activity? Also, the single inhibitor concentration used in each MS experiment needs to be specified in the main text and legends. A discussion on whether the inhibitor concentrations required to observe these dimerization effects (in native MS) or structural dynamics (in HDX-MS) align with EC50 values would be helpful for contextualizing the findings.

We thank the reviewer for the points and agree that directly linking our biophysical observations to functional outcomes under identical conditions would be more meaningful. We will perform enzymatic activity assays to investigate whether the fraction of monomer measured by native MS can predict the loss of activity. The inhibitor concentrations used in each MS experiment will be explicitly stated in the main text and figure legends, and we will also discuss how these concentrations relate to the EC50/IC50 values, providing content for the biophysical observations.

(2) For the two Cys residues found to be targeted by ebselen, what are their respective modification stoichiometry related to the ebselen concentration? Especially for the covalent binding site C300, which is proposed in this study to represent a novel allosteric inhibition mechanism of ebselen, more direct experimental evidence is needed to support this major hypothesis. Does mutation or modification of C300 affect the Mpro dimerization/monomer equilibrium and alter the enzymatic activity? If ebselen acts as a covalent inhibitor linked to multiple Cys, why is its activity only in the uM range?

We thank the reviewer for the insightful comments. To address the stoichiometry of ebselen modification, we will further analyze the data and discuss accordingly. To display more direct evidence of C300 as a novel allosteric inhibition site of ebselen, we will perform site-directed mutagenesis and investigate whether these C300 mutants affect the Mpro dimerization and enzymatic activity. Regarding the modification of C300, several independent studies have been cited in this manuscript and showed that oxidation (by glutathione, Davis et., 2021) or chemical modification of C300 (by glutathione bismuth drugs, Tao et al., 2021, and Tixocortol, Davis et., 2024) leads to Mpro inactivation and promotes monomer formation. We will cite and further discuss these studies in the Discussion. The µM-range activity of ebselen can be explained by its multi-target covalent binding to multiple cysteines. The variable efficacy of cysteine modification may account for ebselen's moderate potency, as not all modifications equally inhibit their targets.

(3) For the allosteric inhibitor pelitinib with low-uM activity, no significant differences in deuterium uptake of Mpro were observed. In terms of the binding affinity, what is the difference between pelitinib and ebselen? Some explanations could be provided about the different HDX-MS results between the two non-peptidomimetic inhibitors with similar activities.

Pelitinib has non-covalent binding with Mpro, while the binding between ebselen and Mpro is covalent. We will add some explanations and discussion about their different HDX-MS results in the revised version.

(4) Native MS Quantification:

The analysis of monomer-dimer ratios from native MS spectra appears qualitative or semi-quantitative. A more rigorous and quantified analysis of the percentage of dimer/monomer species under each condition, with statistical replicates, would strengthen the equilibrium shift claims. For native MS analysis of each inhibitor, the representative spectrum can be shown in the main figure together with quantified dimer/monomer fractions from replicates to show significance by statistical tests.

We thank the reviewer for the suggestion, and we will perform a more rigorous and quantitative analysis of the monomer-dimer equilibrium. For each condition (unbound Mpro and Mpro bound to each inhibitor), native MS experiments will be shown in triplicate. As suggested, we will include a representative native MS spectrum for each condition. The quantified monomer/dimer ratios from replicates will be added. The results with statistical analysis will be provided to show significance.

(5) Changes of HDX rates in certain regions seem very subtle. For example, as it states 'residues 296-304 in the C-terminal region of M pro were more flexible upon ebselen binding (Figure 4c)', the difference is barely observable. The percentage of HDX rate changes between two conditions (with p values) can be specified in the text for each fragment discussed, and any change below 5% or 10% is negligible.

We agree with the reviewer about the need for quantitative rigor in reporting HDX changes. We will calculate the fractional deuterium uptake difference for each peptide fragment discussed in the text between the inhibitor-bound and unbound states. These values, along with their statistical significance (p-values from a two-tailed t-test), will be provided in the revised figures.

eLife Assessment

This work presents a brain-wide atlas of vasopressin (Avp) and vasopressin receptor 1A (Avpr1a) mRNA expression in mouse brains using high-resolution RNAscope in situ hybridization. The single-transcript approach provides precise localization and identifies additional brain regions expressing Avpr1a, creating a valuable resource for the field. The revised manuscript is clearer and more impactful, with improved figures, stronger data organization, and enhanced scholarship through added context and citations. Overall, the evidence is compelling, and the atlas should be broadly of use to researchers studying vasopressin signaling and related neural circuits.

Reviewer #1 (Public review):

Summary:

Despite accumulating prior studies on the expressions of AVP and AVPR1a in the brain, a detailed, gender-specific mapping of AVP/AVPR1a neuronal nodes has been lacking. Using RNAscope, a cutting-edge technology that detects single RNA transcripts, the authors created a comprehensive neuroanatomical atlas of Avp and Avpr1a in male and female brains.

Strengths:

This well-executed study provides valuable new insights into gender differences in the distribution of Avp and Avpr1a. The atlas is an important resource for the neuroscience community.

The authors have previously adequately addressed all of my concerns. I have no further questions or concerns.

Reviewer #2 (Public review):

Summary:

The authors conducted a brain-wide survey of Avp (arginine vasopressin) and its Avpr1a gene expression in the mouse brain using RNAscope, a high-resolution in situ hybridization method. Overall, the findings are useful and important because they identify brain regions that express the Avpr1a transcript. A comprehensive overview of Avpr1a expression in the mouse brain could be highly informative and impactful. The authors used RNAscope (a proprietary in situ hybridization method) to assess transcript abundance of Avp and one of its receptors, Avpr1a. The finding of Avp-expressing cells outside the hypothalamus and the extended amygdala is novel and is nicely demonstrated by new photomicrographs in the revised manuscript. The Avpr1a data suggest expression in numerous brain regions. In the revised manuscript, reworked figures make the data easier to interpret.

Strengths:

A survey of Avpr1a expression in the mouse brain is an important tool for exploring vasopressin function in the mammalian brain and for developing hypotheses about cell- and circuit-level function.

[Editors' note: The authors have substantially addressed all the reviewers' concerns and comments.]

Author response:

The following is the authors’ response to the previous reviews

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The authors have adequately addressed all of my concerns. I have no further questions or concerns.

We thank the Reviewer #1. 

Reviewer #2 (Recommendations for the authors):

We thank the Reviewer #2 for thoughtful recommendations.

(1) Figure 1A, 1B, 2B, 2C, etc.: The Y-axis label is confusing. I assume the intention was to make big numbers small by dividing by 1000. The comma makes the label confusing. Perhaps, make the label more "mathematical" as in "Avp density ((transcript/µm2) * 10-3)" or rearrange the math to be clearer as in "Avp density (transcript/1000 per µm2)".

Great suggestion and done exactly as suggested in Figures 1, 2 and 4.

(2) Figure 1B and 1C: The figure and legend do not match up. Either switch the figures or the legends. Currently, legend 1B describes image 1C.

Agreed and done as suggested.

(3) Figure 2A is broken up into separate pages/panels. It could be integrated better or separated to make A and B, then shift B and C to C and D.

Great suggestion and we have done exactly as suggested.

(4) Figure 2 legend: I recommend putting the scale bar info with (A) rather than at the end. The stars used in the figure are not explained in the legend.

Good points. We have made all necessary changes as suggested.

(5) Supplementary Figure 1B: The legend states that the data are the number of transcript-containing cells, but the figure states transcript number.

We thank the Reviewer for pointing out this typo. We corrected all graph legends in the Supplementary Figure 1.

eLife Assessment

Recent studies have shown that mRNA can be acetylated (ac4c), altering mRNA stability and translation efficiency; however, the role of mRNA acetylation in the brain remains unexplored. In this important study, the authors demonstrate that ac4c occurs in synaptically localised mRNAs, mediated by NAT10. Conditional reduction of NAT10 protein levels led to decreases in ac4c of mRNAs and deficits in synaptic plasticity and memory. These solid results suggest that mRNA acetylation may play a role in memory consolidation.

Reviewer #1 (Public review):

Summary:

RNA modification has emerged as an important modulator of protein synthesis. Recent studies found that mRNA can be acetylated (ac4c), which can alter mRNA stability and translation efficiency. The role of ac4c mRNA in the brain has not been studied. In this paper, the authors convincingly show that ac4c occurs selectively on mRNAs localized at synapses, but not cell wide. The ac4c "writer" NAT10 is highly expressed in hippocampal excitatory neurons. Using NAT10 conditional KO mice, decreasing levels of NAT10 resulted in decreases in ac4c of mRNAs and also showed deficits in LTP and spatial memory. These results reveal a potential role for ac4c mRNA in memory consolidation.

This is a new type of mRNA regulation that seems to act specifically at synapses, which may help elucidate the mechanisms of local protein synthesis in memory consolidation. Overall, the studies are well carried out and presented. The precise mRNAs that require ac4c to carry out memory consolidation is not clear, but is an important focus of future work. The specificity of changes occurring only at the end of training, rather than after each day of training is interesting and also warrants further investigation. This timeframe is puzzling because the authors show that ac4c can dynamically increase within 1hr after cLTP.

Strengths:

(1) The studies show that mRNA acetylation (ac4c) occurs selectively at mRNAs localized to synaptic compartments (using synaptoneurosome preps).

(2) The authors identify a few key mRNAs acetylated involved in plasticity and memory - eg Arc.

(3) The authors show that Ac4c is induced by learning and neuronal activity (cLTP).

(4) The studies show that the ac4c "writer" NAT10 is expressed in hippocampal excitatory neurons and may relocated to synapses after cLTP/learning induction.

(5) The authors used floxed NAT10 mice injected with AAV-Cre in the hippocampus (NAT10 cKO) to show that NAT10 may play a role in LTP maintenance and memory consolidation (using the Morris Water Maze).

Weaknesses:

(1) The NAT10 cKO mice are useful to test the causal role of NAT10 in ac4a and plasticity/memory but all the experiments used AAV-CRE injections in the dorsal hippocampus that showed somewhat modest decreases in total NAT10 protein levels. For these experiments, it would be better to cross the NAT10 floxed animals to CRE lines where better knock down of NAT10 can be achieved postnatally in specific neurons, with less variability.

(2) Because knock down is only modest (~50%), it is not clear if the remaining ac4c on mRNAs is due to remaining NAT10 protein or due to alternative writer (as the authors pose).

Reviewer #2 (Public review):

This is an interesting study that shows that mRNA acetylation at synapses is dynamically regulated at synapses by spatial memory in the mouse hippocampus. The dynamic changes of ac4C-mRNAs regulated by memory were validated by methods including ac4C dot-blot and liquid 13 chromatography-tandem mass spectrometry (LC-MS/MS).

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

(1) The authors use a confusing timeline for their behavioral experiments, i.e., day 1 is the first day of training in the MWM, and day 6 is the probe trial, but in reality, day 6 is the first day after the last training day. So this is really day 1 post-training, and day 20 is 14 days post-training.

We have revised the timeline accordingly. Briefly, mice were trained in the Morris water maze (MWM) with a hidden platform for five consecutive days (training days 1–5). Probe tests were then conducted on day 6 and day 20, which correspond to post-training day 1 and post-training day 15, respectively. We clearly stated as such in the revised manuscript (see results, line 108 – 113) and figure S1 (see figure legend, line 1747 – 1749).

(2) The authors inaccurately use memory as a term. During the training period in the MWM, the animals are learning, while memory is only probed on day 6 (after learning). Thus, day 6 reflects memory consolidation processes after learning has taken place.

We have revised the manuscript to distinguish between "learning" and "memory". We refer to the performance during the 5-day training period as "spatial learning" and restrict the term "memory" to the probe tests on day 6, which reflect memory consolidation after learning has taken place.

(3) The NAT10 cKO mice are useful... but all the experiments used AAV-CRE injections in the dorsal hippocampus that showed somewhat modest decreases... For these experiments, it would be better to cross the NAT10 floxed animals to CRE lines where a better knockdown of NAT10 can be achieved, with less variability.

We want to clarify the reason for using AAV-Cre injection rather than Cre lines. Indeed, we attempted to generate Nat10 conditional knockouts by crossing Nat10^flox/flox mice with several CNS-specific Cre lines. Crossing with Nestin-Cre and Emx1-Cre resulted in embryonic and premature lethality, respectively, consistent with the essential housekeeping function of NAT10 during neurodevelopment. We will use the Camk2α-Cre line which starts to express Cre after postnatal 3 weeks specifically in hippocampal pyramidal neurons (Tsien et al., 1996).

(4) Because knockdown is only modest (~50%), it is not clear if the remaining ac4c on mRNAs is due to remaining NAT10 protein or due to an alternative writer (as the authors pose).

Our results suggest the existence of alternative writers. As shown in Figure 6D, we identified a population of "NAT10-independent" MISA mRNAs (present in MISA but not downregulated in NASA). Remarkably, these mRNAs possess a consensus motif (RGGGCACTAACY) that is fundamentally different from the canonical NAT10 motif (AGCAGCTG). This distinct motif usage suggests that the residual ac4C signals are not merely due to incomplete knockdown of NAT10, but reflect the activity of other, as-yet-unidentified ac4C writers. We will perform ac4C immunostaining in Nat10-reporter mice which express red fluorescent proteins in Nat10-positive cells. The results that ac4C is expressed in both Nat10-positive and negative cells will support the presence of as-yet-unidentified ac4C writers.

Reviewer #2 (Public review):

(1) It is known that synaptosomes are contaminated with glial tissue... So the candidate mRNAs identified by acRIP-seq might also be mixed with glial mRNAs. Are the GO BP terms shown in Figure 3A specifically chosen, or unbiasedly listed for all top ones?

This reviewer is correct that some ac4C-mRNAs identified by acRIP-seq from the synaptosomes are highly expressed in astrocytes, such as Aldh1l1, ApoE, Sox9 and Aqp4 (see list of ac4C-mRNAs in the synaptosomes, Table S3). In agreement, we found that NAT10 was also expressed in astrocyte in addition to neurons. We have provided a representative image showing NAT10-Cre expression in astrocytes in the revised manuscript (Figure 4F and H). In the figure 3A of original submission, we showed 10 out of 16 top BP items for MISA mRNAs. In the figure 3A of revised manuscript, we showed all the top 16 BP items for MISA mRNAs, which are unbiasedly chosen (also see Table S4).

(2) Where does NAT10-mediated mRNA acetylation take place within cells generally? Is there evidence that NAT10 can catalyze mRNA acetylation in the cytoplasm?

The previous studies from non-neuronal cells showed that NAT10 can catalyze mRNA acetylation in the cytoplasm and enhance translational efficiency (Arango et al., 2018; Arango et al., 2022). In this study, we showed that mRNA acetylation occurred both in the homogenates and synapses (see ac4C-mRNA lists in Table S2 and S3). However, spatial memory upregulated mRNA acetylation mainly in the synapses rather than in the homogenates (Fig. 2 and Fig. S2).

(3) "The NAT10 proteins were significantly reduced in the cytoplasm (S2 fraction) but increased in the PSD fraction..." The small increase in synaptic NAT10 might not be enough to cause a decrease in soma NAT10 protein level.

We showed that the NAT10 protein levels were increased by one-fold in the PSD fraction, but were reduced by about 50% in the cytoplasm after memory formation (Fig. 5J and K). The protein levels of NAT10 in the homogenates and nucleus were not altered after memory formation (Fig. 5F and I). Due to these facts, we hypothesized that NAT10 proteins may have a relocation from cytoplasm to synapses after memory formation, which was also supported by the immunofluorescent results from cultured neurons (Fig. S4). However, we agree with this reviewer that drawing such a conclusion may require the time-lapse imaging of NAT10 protein trafficking in living animals, which is technically challenging at this moment.

(4) It is difficult to separate the effect on mRNA acetylation and protein mRNA acetylation when doing the loss of function of NAT10.

This is a good point. We agree with this reviewer that NAT10 may acetylate both mRNA and proteins. We examined the acetylation levels of a-tubulin and histone H3, two substrate proteins of NAT10 in the hippocampus of Nat10 cKO mice. As shown in Fig S5C, E, and F, the acetylation levels of a-tubulin and histone H3 remained unchanged in the Nat10 cKO mice, likely due to the compensation by other protein acetyltransferases. In contrast, mRNA ac4C levels were significantly decreased in the Nat10 cKO mice (Figure S5G–H). These results suggest that the memory deficits seen in Nat10 cKO mice may be largely due to the impaired mRNA acetylation. Nonetheless, we believe that developing a new technology which enables selective erasure of mRNA acetylation would be helpful to address the function of mRNA acetylation. We discussed these points in the MS (see discussion, line 582-589).

Reference

Arango, D., Sturgill, D., Alhusaini, N., Dillman, A. A., Sweet, T. J., Hanson, G., Hosogane, M., Sinclair, W. R., Nanan, K. K., & Mandler, M. D. (2018). Acetylation of cytidine in mRNA promotes translation efficiency. Cell, 175(7), 1872-1886. e1824.

Arango, D., Sturgill, D., Yang, R., Kanai, T., Bauer, P., Roy, J., Wang, Z., Hosogane, M., Schiffers, S., & Oberdoerffer, S. (2022). Direct epitranscriptomic regulation of mammalian translation initiation through N4-acetylcytidine. Molecular cell, 82(15), 2797-2814. e2711.

Tsien, J. Z., Chen, D. F., Gerber, D., Tom, C., Mercer, E. H., Anderson, D. J., Mayford, M., Kandel, E. R., & Tonegawa, S. (1996). Subregion-and cell type–restricted gene knockout in mouse brain. Cell, 87(7), 1317-1326.

eLife Assessment

This valuable study examines the role of E2 ubiquitin enzyme, Uev1a in tissue resistance to oncogenic RasV12 in Drosophila melanogaster polyploid germline cells and human cancer cell lines. The solid evidence suggests that Uev1a works with the E3 ligase APC/C to degrade Cyclin A. This work would be of interest to researchers in germline biology and cancer.

Reviewer #1 (Public review):

Summary:

This study uncovers a protective role of the ubiquitin-conjugating enzyme variant Uev1A in mitigating cell death caused by over-expressed oncogenic Ras in polyploid Drosophila nurse cells and by RasK12 in diploid human tumor cell lines. The authors previously showed that over-expression of oncogenic Ras induces death in nurse cells, and now they perform a deficiency- screen for modifiers. They identified Uev1A as a suppressor of this Ras-induced cell death. Using genetics and biochemistry, the authors found that Uev1A collaborates with the APC/C E3 ubiquitin ligase complex to promote proteasomal degradation of Cyclin A. This function of Uev1A appears to extend to diploid cells, where its human homologs UBE2V1 and UBE2V2 suppress oncogenic Ras-dependent phenotypes in human colorectal cancer cells in vitro and in xenografts in mice.

Strengths:

(1) Most of the data is supported by sufficient sample size and appropriate statistics.

(2) Good mix of genetics and biochemistry.

(3) Generation of new transgenes and Drosophila alleles that will be beneficial for the community.

Comments on revisions:

The authors have greatly improved the manuscript and satisfactorily addressed all of my concerns.

Reviewer #2 (Public review):

Summary:

The authors performed a genetic screen using deficiency lines and identified Uev1a as a factor that protects nurse cells from RasG12V-induced cell death. According to a previous study from the same lab, this cell death is caused by aberrant mitotic stress due to CycA upregulation (Zhang et al.). This paper further reveals that Uev1a forms a complex with APC/C to promote proteasome-mediated degradation of CycA.

In addition to polyploid nurse cells, the authors also examined the effect of RasG12V-overexpression in diploid germline cells, where RasG12V-overexpression triggers active proliferation not cell death. Uev1a was found to suppress its overgrowth as well.

Finally, the authors show that the overexpression of the human homolog, UBE2V1 and UBE2V2, suppresses tumor growth in human colorectal cancer xenografts and cell lines. Notably, these genes' expression correlates with the survival of colorectal cancer patients carrying Ras mutation.

Strength:

This paper presents a significant finding that UBE2V1/2 may serve as a potential therapy for cancers harboring Ras mutations. The authors propose a fascinating mechanism in which Uev1a forms a complex with APC/C to inhibit aberrant cell cycle progression.

Comments on revisions:

The authors have addressed several of the major concerns, including the addition of new data and improved figure presentation. However, some issues remain insufficiently resolved, particularly regarding control reuse (Major Comment 3) and experimental interpretation (Major Comments 5 and 8).

Regarding Major Comment 5, the authors state that UAS copy number affects the frequency of egg chamber degradation in Fig. 2D, and thus explains the reduced phenotype in RasG12V + GFP-RNAi compared to RasG12V alone. However, this explanation is not consistent with other data in the manuscript. UAS-RasG12V combined with UAS-lacZ in Fig. 2G shows a phenotype comparable to UAS-RasV12 alone, despite also increasing the UAS copy number. This suggests that the effect is not simply due to copy number.

I understand that the authors used UAS-RasG12V + GFP-RNAi as a control for the RNAi experiments and UAS-RasG12V + lacZ for the overexpression experiments. I suggest examining the phenotype frequency of UAS-RasG12V + UAS-GFP, to figure the reason out. Overall, these results indicate that there is a spectrum of phenotype frequencies, and therefore appropriate controls should be included for each experiment rather than reusing the same dataset across different experiments, as also noted in Major Comment 3.

Author response:

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

eLife Assessment

This valuable study examines the role of E2 ubiquitin enzyme, Uev1a in tissue resistance to oncogenic RasV12 in Drosophila melanogaster polyploid germline cells and human cancer cell lines. The incomplete evidence suggests that Uev1a works with the E3 ligase APC/C to degrade Cyclin A, and the strength of evidence could be increased by addressing the expression of CycA in the ovaries and the uev1a loss of function in human cancer cells. This work would be of interest to researchers in germline biology and cancer.

Thank you for your valuable assessment. The requested data on CycA expression (Figure 4E-G) and uev1a loss-of-function in human cancer cells (Figure 8 and Figure 8-figure supplement 2) have been added to the revised manuscript.

Public Reviews:

Reviewer #1 (Public review):

Summary:

This study uncovers a protective role of the ubiquitin-conjugating enzyme variant Uev1A in mitigating cell death caused by over-expressed oncogenic Ras in polyploid Drosophila nurse cells and by RasK12 in diploid human tumor cell lines. The authors previously showed that overexpression of oncogenic Ras induces death in nurse cells, and now they perform a deficiency screen for modifiers. They identified Uev1A as a suppressor of this Ras-induced cell death. Using genetics and biochemistry, the authors found that Uev1A collaborates with the APC/C E3 ubiquitin ligase complex to promote proteasomal degradation of Cyclin A. This function of Uev1A appears to extend to diploid cells, where its human homologs UBE2V1 and UBE2V2 suppress oncogenic Ras-dependent phenotypes in human colorectal cancer cells in vitro and in xenografts in mice.

Strengths:

(1) Most of the data is supported by a sufficient sample size and appropriate statistics.

(2) Good mix of genetics and biochemistry.

(3) Generation of new transgenes and Drosophila alleles that will be beneficial for the community.

We greatly appreciate your comments.

Weaknesses:

(1) Phenotypes are based on artificial overexpression. It is not clear whether these results are relevant to normal physiology.

Downregulation of Uev1A, Ben, and Cdc27 together significantly increased the incidence of dying nurse cells in normal ovaries (Figure 5-figure supplement 2), indicating that the mechanism we uncovered also protects nurse cells from death during normal oogenesis.

(2) The phenotype of "degenerating ovaries" is very broad, and the study is not focused on phenotypes at the cellular level. Furthermore, no information is provided in the Materials and Methods on how degenerating ovaries are scored, despite this being the most important assay in the study.

Thank you for pointing out this issue. We quantified the phenotype of nurse cell death using “degrading/total egg chambers per ovary”, not “degenerating ovaries”. Normal nurse cell nuclei exhibit a large, round morphology in DAPI staining (see the first panel in Figure 1D). During early death, they become disorganized and begin to condense and fragment (see the second panel in Figure 1D). In late-stage death, they are completely fragmented into small, spherical structures (see the third panel in Figure 1D), making cellular-level phenotypic quantification impossible. Since all nurse cells within the same egg chamber are interconnected, their death process is synchronous. Thus, quantifying the phenotype at the egg-chamber level is more practical than at the cellular level. We have added the description of this death phenotype and its quantification to the main text (Lines 104-108).

(3) In Figure 5, the authors want to conclude that uev1a is a tumor-suppressor, and so they over-express ubev1/2 in human cancer cell lines that have RasK12 and find reduced proliferation, colony formation, and xenograft size. However, genes that act as tumor suppressors have loss-of-function phenotypes that allow for increased cell division. The Drosophila uev1a mutant is viable and fertile, suggesting that it is not a tumor suppressor in flies. Additionally, they do not deplete human ubev1/2 from human cancer cell lines and assess whether this increases cell division, colony formation, and xenograph growth.

We apologize for any misleading description. We aimed to demonstrate that UBE2V1/2, like Uev1A in Drosophila “nos>Ras^G12V+bam-RNAi” germline tumors, suppress oncogenic KRAS-driven overgrowth in diploid human cancer cells. Importantly, this function of Uev1A and UBE2V1/2 is dependent on Ras-driven tumors; there is no evidence that they act as broad tumor suppressors in the absence of oncogenic Ras. Drosophila uev1a mutants were lethal, not viable (see Lines 135-137), and germline-specific knockdown of uev1a (nos>uev1a-RNAi) caused female sterility without inducing tumors. These findings suggest that Uev1A lacks tumor-suppressive activity in the Drosophila female germline in the absence of Ras-driven tumors. We have revised the manuscript to prevent misinterpretation. Furthermore, we have added data demonstrating that the combined knockdown of UBE2V1 and UBE2V2 significantly promotes the growth of KRAS-mutant human cancer cells, as suggested (Figure 8 and Figure 8-figure supplement 2).

(4) A critical part of the model does not make sense. CycA is a key part of their model, but they do not show CycA protein expression in WT egg chambers or in their over-expression models (nos.RasV12 or bam>RasV12). Based on Lilly and Spradling 1996, Cyclin A is not expressed in germ cells in region 2-3 of the germarium; whether CycA is expressed in nurse cells in later egg chambers is not shown but is critical to document comprehensively.

We appreciate your critical comment. CycA is a key cyclin that partners with Cdk1 to promote cell division (Edgar and Lehner, 1996). Notably, nurse cells are post-mitotic endocycling cells (Hammond and Laird, 1985) and typically do not express CycA (Lilly and Spradling, 1996) (see the last sentence, page 2518, paragraph 3 in this 1996 paper). However, their death induced by oncogenic Ras^G12V is significantly suppressed by monoallelic deletion of either cycA or cdk1 (Zhang et al., 2024). Conversely, ectopic CycA expression in nurse cells triggers their death (Figure 4C, D). These findings suggest that polyploid nurse cells exhibit high sensitivity to aberrant division-promoting stress, which may represent a distinct form of cellular stress unique to polyploid cells. In the revised manuscript, we have provided the CycA-staining data, comparing its expression in normal nurse cells versus cells undergoing oncogenic Ras^G12V-induced death (Figure 4E-G).

(5) The authors should provide more information about the knowledge base of uev1a and its homologs in the introduction.

Thank you for your suggestion. In the revised introduction, we have provided a more detailed description of Uev1A (Lines 72-79). Additionally, we have introduced its human homologs, UBE2V1 and UBE2V2, in the main text (Lines 143-145).

Reviewer #2 (Public review):

Summary:

The authors performed a genetic screen using deficiency lines and identified Uev1a as a factor that protects nurse cells from RasG12V-induced cell death. According to a previous study from the same lab, this cell death is caused by aberrant mitotic stress due to CycA upregulation (Zhang et al.). This paper further reveals that Uev1a forms a complex with APC/C to promote proteasome-mediated degradation of CycA.

In addition to polyploid nurse cells, the authors also examined the effect of RasG12V-overexpression in diploid germline cells, where RasG12V-overexpression triggers active proliferation, not cell death. Uev1a was found to suppress its overgrowth as well.

Finally, the authors show that the overexpression of the human homologs, UBE2V1 and UBE2V2, suppresses tumor growth in human colorectal cancer xenografts and cell lines. Notably, the expression of these genes correlates with the survival of colorectal cancer patients carrying the Ras mutation.

Strength:

This paper presents a significant finding that UBE2V1/2 may serve as a potential therapy for cancers harboring Ras mutations. The authors propose a fascinating mechanism in which Uev1a forms a complex with APC/C to inhibit aberrant cell cycle progression.

We greatly appreciate your comments.

Weakness:

The quantification of some crucial experiments lacks sufficient clarity.

Thank you for highlighting this issue. We have provided more details regarding the quantification data in the revised manuscript.

References

Edgar, B.A., and Lehner, C.F. (1996). Developmental control of cell cycle regulators: a fly's perspective. Science 274, 1646-1652.

Hammond, M.P., and Laird, C.D. (1985). Chromosome structure and DNA replication in nurse and follicle cells of Drosophila melanogaster. Chromosoma 91, 267-278.

Lilly, M.A., and Spradling, A.C. (1996). The Drosophila endocycle is controlled by Cyclin E and lacks a checkpoint ensuring S-phase completion. Genes Dev 10, 2514-2526.

Zhang, Q., Wang, Y., Bu, Z., Zhang, Y., Zhang, Q., Li, L., Yan, L., Wang, Y., and Zhao, S. (2024). Ras promotes germline stem cell division in Drosophila ovaries. Stem Cell Reports 19, 1205-1216.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) The figure legends insufficiently describe the figures. One example is Figure 3, where there are no details in the figure legend about what conditions apply to each panel and each lane of the gels.

For clarity and brevity, detailed experimental conditions are described in the Materials and Methods section. Figure legends therefore focus on summarizing the key findings. Thank you for your understanding!

(2) The font size on the figure is too small.

Thank you for your constructive suggestion. In response, we have enlarged all font sizes to improve readability.

(3) There are places where the authors overstate their results, and there are issues with the clarity of the text:

(3a) Lines 170: "excessive" is not appropriate. Their prior study showed a mild increase in proliferation.

“Excessive” has been removed in the revised manuscript (Lines 215-216).

(3b) Line 187-8: The authors should restate this sentence. Here's a possibility. Over-expression of Uev1a suppressed the phenotypes caused by CycA over-expression.

This sentence has been restated as “Notably, this cell death was suppressed by co-overexpression of CycA and Uev1A, indicating a genetic interaction between them”. (Lines 229-231).

(3c) Lines 266-7: The properties of Uev1a (ie, lacking a conserved Cys) should be in the introduction.

This information has been added to the revised introduction (Lines 74-76).

(3d) Line 318: "markedly" is an overstatement of the prior results.

Our quantification data revealed that “nos>Ras^G12V; bam^-/-” ovaries are three times larger than “nos>GFP; bam^-/-” control ovaries (see Figure 4A-C in Zhang et al., Stem Cell Reports 19, 1205-1216). Given this substantial difference, we think that using "markedly" is not an overstatement.

(4) Data not shown occurs in a few places in the text. Given the ability to supply supplemental information in eLife preprints, these data should be shown.

Thanks for your suggestion. All “not shown” data have been added to the revised manuscript.

Reviewer #2 (Recommendations for the authors):

Major Comments

(1) Cyclin A (CycA) is a key player in this study, but the authors do not provide evidence showing the upregulation of CycA following Ras overexpression in either polyploid or diploid cells. Data on CycA expression should be included.

Thank you for your constructive suggestion. These data have been added to the revised manuscript (Figure 4E-G).

(2) DNA replication stress, cellular senescence, and cell death should be assessed under Ras overexpression (RasOE) and RasOE + Uev1A RNAi conditions to support the model proposed in Figure 4F.

We apologize for any confusion caused by our initial model. We do not have evidence that DNA replication stress and cellular senescence occur under these conditions. Cell death can be readily detected through the presence of fragmented nuclei and condensed DNA (see Figure 1D). The model has been updated accordingly (Figure 9E).

(3) Appropriate controls should be performed alongside the experimental sets. The same nos>Ras+GFPi data set was repeatedly used in Figures 1I, 2B, 2H, and Figures 2, S2B, which is not ideal.

All these experiments were performed under identical conditions. Therefore, we deem it appropriate to use the same control data across these analyses.

(4) Overall, the microscopic images are too small and hard to see.

Thank you for raising this important point. In the revised manuscript, all images and the font size on figures have been enlarged for improved clarity.

(5) Figure 1H

Why is the frequency of egg chamber degradation quite less in nos>RasG12V+GFP-RNAi (about 40%) than nos > RasG12V (about 80%)? And the authors do not show that there is a significant difference between those two conditions, although it should be there. We will need the explanation from the authors on why there is a difference here.

These overexpression experiments were conducted using the GAL4/UAS system. While both “nos>Ras^G12V+GFP-RNAi” and “nos>Ras^G12V” contain a single nos-GAL4 driver, they differ in UAS copy number: the former incorporates two UAS elements compared to only one in the latter (see the detailed genotypes in Source data 2). These results demonstrate that UAS copy number impacts experimental outcomes in our system.

In the previous paper (Zhang et al. (2024), Figure 7H shows that the frequency of egg chambers in nos>RasG12V is 33%, although this paper shows it as about 80%. There seems to be a difference in flies' age (previous paper: 7d, this paper: 3d), but this data raises the question of why nos>RasG12V shows more egg chamber degradation this time.

We greatly appreciate your careful observation. The nurse-cell-death phenotype exhibits a spectrum from mild to severe manifestations [see Figure 1D and our response to weekness (2) in Reviewer #1’s public reviews]. While our 2024 paper exclusively quantified egg chambers with severe phenotypes as degrading, the current study included both mild and severe cases in this classification. We do not think fly age could account for this substantial phenotypic difference. A detailed description of the nurse-cell-death phenotype and its quantification have been added to the revised manuscript (Lines 104-108).

In the following experiments, only nos>RasG12V+GFP-RNAi is used as a control (Figures 2B, H, S2B). I wonder if these results would give us a different conclusion if nos>RasG12V were used as a control.

As explained above, the UAS copy number does matter in our analyses, so it is important to keep them identical for comparison.

(6) In the abstract, the authors mention that uev1a is an intrinsic factor to protect cells from RasG12V-induced cell death. RasG12V does not induce much cell death of cystocytes with bam-gal4, whereas it induces a lot of nurse cells' death. Does it mean the intrinsic expression level of uev1a is low in nurse cells (or polyploid cells) compared to cystocytes (or diploid cells)?

Overexpression of Ras^G12V driven by bam-GAL4 exhibited only minimal nurse cell death (Figure 1D, E). Additionally, Uev1A exhibited low intrinsic expression levels in both cystocytes and nurse cells (Figure 3E and Figure 5-figure supplement 1).

(7) Is uev1a-RNAi alone sufficient to induce egg chamber degradation? Or does it have any effect on ovarian development? (Related to question #1 in minor comments)

While nos>uev1a-RNAi resulted in female sterility, it alone was insufficient to induce egg chamber degradation. However, simultaneous downregulation of Uev1A, Ben, and Cdc27 triggered significant egg chamber degradation (Figure 5-figure supplement 2).

(8) Which stages of egg chambers get degraded with RasG12V induction?

This is a good question. In our analyses, we noted that degrading egg chambers exhibited considerable size variability (Figure 1D). Because degradation disrupts normal morphological cues, precise staging of these egg chambers is nearly impossible.

(9) I suggest testing the cellular senescence marker as well if the authors mention that CycA-degradation by Uev1a-APC/C complex prevents cellular senescence induced by RasG12V in a schematic image of Figure 4 (e.g., Dap/p21, SA-β-gal).

As addressed in our response to your Major Comment (2), we lacked experimental evidence to support cellular senescence in this context. We have therefore revised the model accordingly (Figure 9E). While this study focuses specifically on cell death, investigating potential roles of cellular senescence remains an important direction for future research. Thank you for your suggestion!

Minor Comments

(1) Figure 1D: Df#7584

It seems that the late-stage egg chamber is missing in this condition. Why does this occur without egg chamber degradation? Is there a possibility that we do not see egg chamber degradation because this deficiency line does not have a properly developed egg chamber that can have a degradation?

While this image represents only a single sample, we have confirmed the presence of late-stage egg chambers in other samples. If “Df#7584/+” females were unable to support late-stage egg chamber development, complete sterility would be expected due to the lack of mature eggs. However, as shown in this image (Figure 1D), the ovary contains mature eggs, and the “Df#7584/+” fly strain remains fertile.

(2) Based on the results that DDR signaling functions as keeping egg chambers from degradation, the authors may be better to check the DNA-damage markers in nos>RasG12V, nos>RasG12V +uev1a. (e.g. γ-H2AX)

Thank you for your constructive recommendation. These data have been added to the revised manuscript (Figure 3C).

eLife Assessment

This study presents valuable findings on the role of KLF6 in in vitro endothelial cells exposed to altered (high or low) shear stress with a customized microfluidic device to investigate mechanisms of atherosclerosis. The finding that altered shear stress results in endothelial cell ferroptosis through reduced expression of KLF6 is compelling and adds a new layer of complexity to the pathogenesis of atherosclerotic plaques. However, more detailed characterization of ferroptosis is needed.

Reviewer #1 (Public review):

Summary:

The authors used an in vitro microfluidic system where HUVECs are exposed to high, low or physiologic (normal) shear stress to demonstrate that both high and low shear stress for 24 hours resulted in decreased KLF6 expression, decreased lipid peroxidation and increased cell death which was reversible upon treatment with Fer-1, the ferroptosis inhibitor. RNA sequencing (LSS vs normal SS) revealed decreased steroid synthesis and UPR signaling in low shear stress conditions, which they confirmed by showing reduced expression of proteins that mitigate ER stress under both LSS and HSS. Decreased KLF6 expression after exposure to HSS/LSS was associated with decreased expression of regulators of ER stress (PERK, BiP, MVD) which was restored with KLF6 overexpression. Overexpression of KLF6 also restored SLC7A11 expression, Coq10 and reduced c11 bodipy oxidation state- all markers of lipid peroxidation and ferroptosis. The authors then used vascular smooth muscle cells (atherosclerotic model) with HUVECs and monocytes to show that KLF6 overexpression reduces the adhesion of monocytes and lipid accumulation in conditions of low shear stress.

Strengths:

(1) The use of a microfluidic device used to simulate shear stress while keeping the pressure constant when varying shear stress applied is improved and more physiologic compared to traditional cone and shearing devices. Similarly, the utilization of both low and high shear stress in most experiments is a strength.

(2) This study provides a link between disturbed shear stress and ferroptosis, which is novel, and fits nicely with existing knowledge that endothelial cell ferroptosis promote atherosclerosis. This concept was also recently reported Sept 2025 when a publication also demonstrated that LSS trigger ferroptosis in vascular endothelial cells (PMID: 40939914), which partly validates these findings.

Weaknesses:

(1) While HUVECs are commonly used in endothelial in vitro studies, it would be preferable to confirm the findings using an arterial cell line such as human coronary artery cells when studying mechanisms of early atherosclerosis. Furthermore, physiologic arterial shear stress is higher than venous shear stress, and different vascular beds have varying responses to altered shear stress and as such, the up and downregulated pathways in HUVECs should be confirmed in an arterial system.

(2) The authors provide convincing evidence of disturbances in shear stress inducing endothelial ferroptosis with assays for impaired lipid peroxidation and increased cell death that was reversed with a ferroptosis inhibitor. However more detailed characterization of ferroptosis with iron accumulation assays, as well as evaluating GPX4 activity as a consequence of the impaired mevalonate pathway, and testing for concomitant apoptosis in addition to ferroptosis would add to the data.

(3) The authors state that KLF2 and KLF4 are not amongst the differentially expressed genes downregulated by reduced shear stress, which is contrary to previous data, where both KLF2 and KLF4 are well studied to be upregulated by physiologic laminar shear stress. While this might be due to the added pressure in their microfluidic system, it also might be due to changes in gene expression over time. In this case, a time course experiment would be needed. It is possible that KLF2, KLF4 and KLF6 are all reduced in low (and high) shear stress and cooperatively regulate the endothelial cell phenotype. Both KLF2 and KLF4 have been shown to be protective against atherosclerosis.

Comments on revisions:

The authors have failed to respond to all the preceding critiques with supporting experimental data. Recommend a reassessment of the initial critiques.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #2 (Public review):

Points to be addressed:

(1) As a statistical test, the authors report having used unpaired t-tests; however, often three groups are compared for which t-tests are inadequate. This is faulty as, amongst other things, it does not take multiple comparison testing into account.

We have adopted the reviewers' suggestions and conducted a variance analysis (ANOVA) to reanalyze the experimental results with three or more different condition groups. At the same time, we have retained the t-test results for experiments with only two condition groups.

(2) Both B-Actin and GAPDH seem to have been used for protein-level normalization. Why? The Figure 2HL first panel reports B-actin, whereas the other three report GAPDH. The same applies to Figures 3E-F, where both are shown, and it is not mentioned which of the two has been used. Moreso, uncropped blots seem to be unavailable as supplementary data for proper review. These should be provided as supplementary data.

In Figures 2G and 3E-F, β-actin and GAPDH both have been used for protein level normalization. The main issue is the mixed use of these two housekeeping proteins, without taking consistency into account in advance. In addition, the expression levels of these two proteins show no significant differences in response to different fluid shear stresses. The uncropped blot images have been organized and provided in the supplementary data.

(3) LSS and MSS were compared based on transcriptomic analysis. Conversely, RNA sequencing was not reported for the HSS. Why is this data missing? It would be valuable to assess transcriptomics following HSS, and also to allow transcriptomic comparison of LSS and HSS.

In the current study, we have only conducted the transcriptomic comparative analysis between LSS and MSS conditions, mainly considering that most of current researches focuses on the endothelial dysfunction and atherosclerosis under LSS. Since our HSS condition is overall about 24 dyn/cm², which is also recognized within the normal physiological range in some reports. Moreover, the transcriptomic data are primarily used to identify the targets in our study. Interestingly, for these selected genes, they share the same trend involved in endothelial cell ferroptosis induced by LSS and HSS. At the same time, we strongly agree with the reviewer’s claim that the RNA sequencing results under HSS are also valuable. Therefore, in the future, we are planning to perform the transcriptomic sequencing analysis under the HSS or higher level of shear stress, aiming to discover new insights.

(4) Actual sample sizes should be reported rather than "three or more". Moreso, it would be beneficial to show individual datapoints in bar graphs rather than only mean with SD if sample sizes are below 10 (e.g., Figures 1B-H, Figure 2G, etc.).

After rechecking our original data, All analyzed results were from three biological replicates, so they are uniformly marked as 'n=3' in the article. According to the reviewer's suggestion, the position of each data point has been added in the chart of the statistical results along with the standard deviation bars.

(5) The authors claim that by modifying the thickness of the middle layer, shear stress could be modified, whilst claiming to keep on-site pressure within physiological ranges (approx. 70 mmHg) as a hallmark of their microfluidic devices. Has it been experimentally verified that pressures indeed remain around 70 mmHg.

It is a very interesting question. In this article, the cross-sectional areas of different tunnel-like channel is related to the thickness of the middle layer, resulting in different level of shear stress. Since all flow rates under three conditions keep same at 1.6 ml/min, the average pressure is calculated to be around 70 mmHg based on our previously reported formula (PMID: 37662690). To address the reviewer's question about the actual pressure values, we used a water-filled tube connected to a chip and measured the height of the water surface in the elevated end relative to the chip position, as shown in the Author response image 1. As expected, when the height of the middle layer bulging to the same value (0.7 mm) as under the LSS condition, the water level reaches to 900 mm, which is corresponding to about 70 mmHg.

Author response image 1.

Schematic diagram of on-chip pressure detection

(6) A coculture model (VSMC, EC, monocytes) is mentioned in the last part of the results section without any further information. Information on this model should be provided in the methods section (seeding, cell numbers, etc.). Moreover, comparison of LSS vs LSS+KLF6 OE and HSS vs HSS+KLF6 OE is shown. It would benefit the interpretation of the outcomes if MSS were also shown. It would also be beneficial to demonstrate differences between LSS, MSS, and HSS in this coculture model (without KLF6 OE).

The specific methods for constructing the co-culture models (vascular smooth muscle cells, endothelial cells, monocytes) mentioned in the results section have been introduced in our previous paper. For the convenience for reading this article, we have added a brief description in the section of “Methods and materials” in this paper, including cell seeding and numbers. In this study, the results of LSS vs LSS+KLF6 OE and HSS vs HSS+KLF6 OE are presented to verify the role of KLF6 in LSS- or HSS-induced promotion of early atherosclerotic events. In our previously published paper (PMID: 37662690), we have showed the effects of three different shear stresses on the atherosclerotic events (shown in Fig. 4 in that paper). Those results have demonstrated that both LSS and HSS significantly promote early atherosclerotic events compared with the MSS.

(7) The experiments were solely performed with a venous endothelial cell line (HUVECs). Was the use of an arterial endothelial cell line considered? It may translate better towards atherosclerosis, which occurs within arteries. HUVECs are not accustomed to the claimed near-physiological pressures.

The human umbilical vein endothelial cell (HUVEC) is a commonly used cell line for many in vitro studies of vascular endothelium under fluid shear stress conditions. Although human arterial endothelial cells (HAECs) may be more suitable than HUVECs for responding to physiologically relevant pressure, HUVECs are more easy to obtain and maintain. However, we are going to order HAECs and will use them to validate the conclusion for the potential translatability.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

(1) Information on seeding of the microfluidic device is absent in the methods section (i.e., seeding, cell density, passage number, confluence, etc.). Moreso, treatment with Fer-1 is not reported in the methods section.

We have described the cell seeding information in‘Preparation of cell culture in the microfluidic chip’ and the Fer-1 treatment in ‘Cell death assay’ in the Method section.

(2) Figure 3F has "MSS", "HSS", and "LSS+KLF6" as groups on the x-axis; the latter should probably be "HSS+KLF6".

Thank you for pointing out this error in Figure 3F. We have made the correction.

(3) Data should be made available in online repositories rather than "making it available upon reasonable request". As it was not provided, the sequencing data could not be reviewed. In addition, it was stated that a preprint was available on BioRxiv, but I could not find it.

Thank you for the suggestion. We have uploaded the RNA-seq data to the NCBI GEO database, which was publicly available on December 9, 2025.

eLife Assessment

Using genome databases, the authors performed solid bioinformatic analyses to trace the genomic history of the clinically relevant Staphylococcus aureus tetracycline resistance plasmid pT181 over the last seven decades. They discovered that this element has transitioned from a multicopy plasmid to a chromosomally integrated element, and the work represents a valuable demonstration of the use of publicly available data to investigate plasmid biology and inform clinical epidemiology. This work will appeal to researchers interested in staphylococcal evolution and plasmid biology.

Reviewer #1 (Public review):

The study provides a robust bioinformatic characterization of the evolution of pT181. My main criticism of the work is the lack of experimental validation for the hypotheses proposed by the authors.

Comments on the study:

(1) One potential reason for the decline in pT181 copy number over time may be a high cost associated with the multicopy state. In this sense, it would be interesting if the authors could use (or construct) isogenic strains differing only in the state of the plasmid (multicopy/integrated). With this system, the authors could measure the fitness of the strains in the presence and absence of tetracycline, and they could be able to understand the benefit associated with the plasmid transition. The authors discuss these ideas, but it would be nice to test them.

(2) It would be interesting to know the transfer frequencies of the multicopy mobilizable pT181 plasmid, compared to the transfer frequency of the plasmid integrated into the SSCmec element (which can be co-transferred, integrated in conjugative plasmids, or by transduction).

(3) One important limitation of the study that should be mentioned is that inferring pT181 PCN from whole genome data can be problematic. For example, some DNA extraction methods may underestimate the copy number of small plasmids because the small, circular plasmids are preferentially depleted during the process (see, for example, https://www.nature.com/articles/srep28063).

Reviewer #2 (Public review):

Summary:

The authors performed bioinformatic analyses to trace the genomic history of the clinically relevant pT181 plasmid. Specifically, they:

(1) tracked the presence of pT181 across different S. aureus strain backgrounds through time. It was first found in one, later multiple strains, though this may reflect changes in sampling over time.

(2) estimated the mutation rate of the chromosome and plasmid.

(3) estimated the plasmid copy number of pT181, and found that it decreased over time. The latter was supported by two sets of statistical analyses, first showing that the number of single-copy isolates increased over time, and second, that the multicopy isolates demonstrated a lower PCN over time.

(4) reported the different integration sites at which pT181 integrated into the genome.

As a caveat, they mentioned that identical plasmid sequences have variable plasmid copy numbers across different genomes in their dataset.

Strengths:

This is a very solid, well-considered bioinformatic study on publicly available data. I greatly appreciate the thoughtful approach the authors have taken to their subject matter, neither over- nor underselling their results. It is a strength that the authors focussed on a single plasmid in a single bacterial species, as it allowed them to take into account unique knowledge about the biology of this system and really dive deep into the evolution of this specific plasmid. It makes for a compelling case study. At the same time, I think the introduction and discussion can be strengthened to demonstrate what lessons might be drawn from this case study for other plasmids.

Weaknesses:

The finding that the pT181 copy number declined over time is the most interesting claim of the paper to me, and not something that I have seen done before. While the authors have looked at some confounders in this analysis, I think this could be strengthened further in a revision.

For the flow of the storyline, I also think the estimation of mutation rates (starting L181) and integration into the chromosome (starting L255) could be moved to the supplement or a later position in the main text.

Clearly, the use of publicly available data prevents the authors from controlling the growth and sequencing conditions of the isolates. It is striking that they observe a clear signal in spite of this, but I would have loved to see more discussion of the metadata that came with the publicly available sequences and even more use of that metadata to control for confounding.

Author response:

eLife Assessment

Using genome databases, the authors performed solid bioinformatic analyses to trace the genomic history of the clinically relevant Staphylococcus aureus tetracycline resistance plasmid pT181 over the last seven decades. They discovered that this element has transitioned from a multicopy plasmid to a chromosomally integrated element, and the work represents a valuable demonstration of the use of publicly available data to investigate plasmid biology and inform clinical epidemiology. This work will appeal to researchers interested in staphylococcal evolution and plasmid biology.

Thank you, we agree with this overview. We also think this work is interesting to people interested in antimicrobial resistance and bacterial genome structure.

Public Reviews:

Reviewer #1 (Public review):

The study provides a robust bioinformatic characterization of the evolution of pT181. My main criticism of the work is the lack of experimental validation for the hypotheses proposed by the authors.

Comments on the study:

(1) One potential reason for the decline in pT181 copy number over time may be a high cost associated with the multicopy state. In this sense, it would be interesting if the authors could use (or construct) isogenic strains differing only in the state of the plasmid (multicopy/integrated). With this system, the authors could measure the fitness of the strains in the presence and absence of tetracycline, and they could be able to understand the benefit associated with the plasmid transition. The authors discuss these ideas, but it would be nice to test them.

We agree that the relative fitness of integrated versus multicopy plasmids is interesting and a costly multicopy state could explain the transition of independent pT181 replicons to chromosomal integration. This is a project we are exploring for a future study. However, we think that this additional experimental work goes beyond the scope of the paper.

(2) It would be interesting to know the transfer frequencies of the multicopy mobilizable pT181 plasmid, compared to the transfer frequency of the plasmid integrated into the SSCmec element (which can be co-transferred, integrated in conjugative plasmids, or by transduction).

We agree with the reviewer that this is an interesting question. However, we think inferring these rates from natural sequence data is not feasible in this case given the low heterogeneity of the plasmid sequence. A laboratory-based experimental study could not address the real transfers we observe over the course of decades, as in vitro S. aureus transfer rates are often not good proxies for in vivo (McCarthy et al., 2014). In addition, we do not know what is moving the integrated plasmid. pT181 could be moved by a phage or plasmid, so we are uncertain what the correct experiment would be to explore this.

(3) One important limitation of the study that should be mentioned is that inferring pT181 PCN from whole genome data can be problematic. For example, some DNA extraction methods may underestimate the copy number of small plasmids because the small, circular plasmids are preferentially depleted during the process (see, for example, https://www.nature.com/articles/srep28063).

We will investigate this issue further in the revisions. The kits used to extract DNA for the earlier-collected samples may possibly yield more plasmid DNA relative to the chromosome compared to newer ones on average; however, we think this is not driving the decline that we observe in multicopy pT181 copy number. Multiple BioProjects find the same result, where earlier samples have higher copy number compared to later samples. We expect extraction methods to be consistent within a BioProject, suggesting that this decline is genuine and not technical. In revisions, we intend to evaluate the effect of date of sequencing and additional metadata on copy number.

Reviewer #2 (Public review):

Summary:

The authors performed bioinformatic analyses to trace the genomic history of the clinically relevant pT181 plasmid. Specifically, they:

(1) Tracked the presence of pT181 across different S. aureus strain backgrounds through time. It was first found in one, later multiple strains, though this may reflect changes in sampling over time.

(2) Estimated the mutation rate of the chromosome and plasmid.

(3) Estimated the plasmid copy number of pT181, and found that it decreased over time. The latter was supported by two sets of statistical analyses, first showing that the number of single-copy isolates increased over time, and second, that the multicopy isolates demonstrated a lower PCN over time.

(4) Reported the different integration sites at which pT181 integrated into the genome.

As a caveat, they mentioned that identical plasmid sequences have variable plasmid copy numbers across different genomes in their dataset.

Strengths:

This is a very solid, well-considered bioinformatic study on publicly available data. I greatly appreciate the thoughtful approach the authors have taken to their subject matter, neither over- nor underselling their results. It is a strength that the authors focused on a single plasmid in a single bacterial species, as it allowed them to take into account unique knowledge about the biology of this system and really dive deep into the evolution of this specific plasmid. It makes for a compelling case study. At the same time, I think the introduction and discussion can be strengthened to demonstrate what lessons might be drawn from this case study for other plasmids.

Weaknesses:

The finding that the pT181 copy number declined over time is the most interesting claim of the paper to me, and not something that I have seen done before. While the authors have looked at some confounders in this analysis, I think this could be strengthened further in a revision.

In the revisions, we will further explore the impact that technical variation could have in contributing to copy number variation and update our claims for the decline in copy number of the independent replicon over time and variation for the same plasmid sequence accordingly. Multiple BioProjects show earlier samples have higher copy number compared to later samples; we expect extraction methods to be consistent within a BioProject, supporting our initial findings that this decline over time is not due to technical variation.

For the flow of the storyline, I also think the estimation of mutation rates (starting L181) and integration into the chromosome (starting L255) could be moved to the supplement or a later position in the main text.

We will revisit the text organization for flow and clarity of storyline.

Clearly, the use of publicly available data prevents the authors from controlling the growth and sequencing conditions of the isolates. It is striking that they observe a clear signal in spite of this, but I would have loved to see more discussion of the metadata that came with the publicly available sequences and even more use of that metadata to control for confounding.

In revisions, we will further investigate possible contributors to the observed decline in copy number of multicopy pT181 over time. We have incorporated the date of sample collection and BioProject in our analysis, but not the date of sequencing or extraction technique.

References

McCarthy, A. J., Loeffler, A., Witney, A. A., Gould, K. A., Lloyd, D. H., & Lindsay, J. A. (2014). Extensive horizontal gene transfer during Staphylococcus aureus co-colonization in vivo. Genome Biology and Evolution, 6(10), 2697–2708. https://doi.org/10.1093/gbe/evu214

eLife Assessment

This valuable study describes significant differences in prey capture behavior between PSD-95 knock-out and wild-type mice, despite prior work by the same authors showing only modest visual deficits in the former. The data convincingly demonstrated prey capture performance in PSD-95 knock-out mice to improve under monocular viewing conditions. However, this finding alone was inadequate to support the interpretation of results as revealing a deficit in binocular visual integration, especially given the lack of eye and head tracking data or consideration of alternative explanations for the observed behavior.

Reviewer #1 (Public review):

Summary:

PSD95 has long been studied in detail to understand molecular mechanisms of synaptic plasticity as related to specific cell types (excitatory), circuits (visual cortex) and circuit development and function (ocular dominance plasticity ). While much was known about the molecular and cellular details of its function, it remained unclear whether and how it might contribute to the development of specific aspects of visual perception. While overall vision is preserved in PSD95 KO (Knockout) mice, studying natural, visually-guided prey capture behavior revealed robust, yet specific, perturbations to binocular processing during the behavior.

Strengths:

A major strength of the paper is being able to quantify precise measures of the visual aspects versus the motor aspects of prey pursuit. Comparing changes in behavior due to monocular occlusion was particularly revealing that mice indeed employ binocular summation to extract visual cues useful for prey pursuit. This result further suggested that in cases with poor binocular vision, monocular input can improve perceptual and behavioral processes as it does in human subjects with comparable challenges.

The study not only provided a useful finding regarding the function of PSD95, but also outlined a useful general approach toward identifying and quantifying specific deficits in binocular summation. This is likely to broadly impact studies of visual system development, behavior, and neural circuit function. The careful attention to details, observations, and openness about subject variance will also be helpful to those studying specific visual pursuit and natural prey capture behavior in the mouse.

Weaknesses:

Lack of eye movement monitoring and detailed head movement analysis preclude total certainty for the interpretation of observed behaviors.

Reviewer #2 (Public review):

Summary:

This manuscript studies the impacts of knocking out a protein known to be involved in synapse maturation in mice, measuring their ability to hunt prey items (and to discriminate simple visual patterns) under binocular and monocular viewing conditions. The main results are that the mice with this protein knocked out are impaired when performing visual tasks with binocular viewing, but are actually better when they perform monocularly. The interpretation is that the knocked-out protein has affected binocular visual integration.

Strengths:

Overall, the attempt to connect a protein to behavior/perception, via known mechanistic effects on synapse development and visual critical periods, is admirable.

The use of multiple visual conditions and behavioral paradigms (binocular/monocular, cricket hunting/orientation discrimination, light/dark) strengthens and enriches the results.

Weaknesses:

The primary interpretation - that binocular integration is affected in the PSD-95 knockouts- is not supported by the behavioral evidence. Using behavior to isolate a particular stage in visual processing (and further, to distinguish it from elements of generating the behavioral response and/or acquiring the visual information in the first place) is notoriously difficult. Such attempts are, of course, the domain of psychophysics. In fact, the most classical and loveliest success is in the domain of binocular integration- Bela Julesz's "psychoanatomy" that used random dot stereograms to isolate stereoscopic computations.

I mention this example because it is, in fact, directly relevant to my primary concern about the evidence used as support for the favored interpretation here. Julesz's stimuli were extremely clever in isolating binocular mechanisms (i.e., binocular mechanisms MUST be used to perform the task), and any perceptual/behavioral reports are very straightforward to interpret (i.e., a stereoscopically-defined shape can be identified, or not).

Now compare this to the work described in this manuscript. KO (knockout) mice are worse than wild types at chasing prey items or at moving towards a rewarded orientation, but they get better when performing this task monocularly. No argument that that is an interesting bit of scientific phenomenology to characterize. However, the behaviors do not require binocular integration, the freely-moving paradigms involve a variety of gaze and body-movement strategies, and the metrics used to quantify performance are similarly high-dimensional. Bottom line, it is not possible to glean whether the KO's intriguing binocular-vs-monocular differences are due to binocular integration per se, or something better thought of as fundamentally sensorimotor in origin. The tasks do not isolate visual from sensorimotor processing, and the behaviors and associated metrics cannot definitely adjudicate between a multitude of possible specific interpretations.

More specifically, the KO mice may have abnormal patterns of binocular coordination. Eye movements were not tracked in these studies, despite the availability of such instrumentation and their successful application in many preceding studies of mouse prey capture. If the KO mice do not coordinate their eye movements (in task-specific/task-relevant ways), they might receive binocular input that is abnormal. Under monocular conditions, that mismatched or inappropriately coordinated binocular input is absent, which would relieve them of the confusing visual information. That is rather different than having an impairment of binocular integration, as it is basically a question of whether the visual system is impaired, or whether the inputs to the visual system are abnormal due to differences in binocular coordination.

It is also possible that the binocular deficit, as measured in behavior,r occurs in a distinct part of the sensorimotor loop. Even if the binocular eye movements are normal, and binocular visual integration is normal, PSD-95 KO mice may be confused or distracted by the larger visual field that comes from binocular viewing (quite profound in species with mostly lateralized eyes). Such a "post-sensory" interpretation related to target selection (from what could be a totally normal visual representation) is difficult to rule out as well.

In summary, this reviewer appreciates the value of trying to connect this molecular mechanism to sensory processing and behavior. The use of naturalistic tasks and freely-moving paradigms is also something to commend. However, the sorts of visual stimuli and behavioral paradigms used here are not well-suited to supporting the rather specific interpretation that has been put forth in this manuscript.

Reviewer #3 (Public review):

Summary:

Bhattacharya et al. describe significant differences in prey capture behaviour in PSD-95 KO (Knockout) and wild-type (WT) mice. This work develops logically from their previous findings that KO of PSD-95 inhibits the maturation in the primary visual cortex. However, their previous work revealed that the visual deficits in the KO mice were relatively modest. Here, by employing an ethologically-relevant behavioural task, they show that several aspects of prey capture are impaired in the KO. Importantly, the deficits in predatory behavior in the KO mouse improved with monocular deprivation, consistent with deficits in binocular vision.

Strengths:

Overall, the data presented are convincing and valuable, and support the idea that PSD-95 expression is important for the maturation of visual responses.

Weaknesses:

The manuscript could be strengthened by consideration of the following points:

(1) The deficits in predatory behavior are interpreted to reveal several possible visual defects, including the absence of binocularity, binocular summation, or binocular mismatch in V1 neurons. Yet this is done with insufficient detail about each possible mechanism and without direct neuronal evidence.

(2) The observation that binocular visual field bias is intact in the PSD-95 KO mice is interesting but appears to contradict other data suggesting the absence of binocularity in the KO visual system, and this is not discussed in sufficient detail.

(3) No consideration of previous work using constitutive PSD-95 KOs that documented a learning deficit.

(4) Throughout the manuscript, including the first paragraph of the discussion, the authors state that "This study explored whether the maturation of CP closure, inhibited by PSD-95 influences binocular visual behaviour". However, if this were the case, the current experiments would have compared cricket capture behavior at two ages across the two genotypes: pre- and post-CP closure in WTs and at matching chronological ages in KOs.

(5) Freeman and others have shown that the influence of binocular summation on orientation discrimination is highest at low stimulus contrast and short duration stimuli. How does this impact the interpretation of predatory behavior and discrimination in the VWT?

Author response:

We thank the reviewers for their thorough and constructive evaluation of our manuscript titled “PSD-95 drives binocular vision maturation critical for predation”. The reviewers raised several important conceptual and technical points. Here, we address and provide additional context on the major themes and outline our planned revisions.

We acknowledge that the current prey capture task cannot directly adjudicate between PSD-95 binocular vision impairments or sensorimotor processing deficits. However, we did not observe any major impairment supporting a sensorimotor processing deficit, in contrast to a major impairment in line with binocular vision impairment. Evidence from Huang et al. (2015) [1], Favaro et al. (2018) [2] and our data with the visual water task (VWT) — thus requiring identical sensorimotor but differential visual processing—clearly demonstrated intact visual acuity but impaired orientation discrimination in PSD-95 KO mice. Therefore, we believe that a binocular integration deficit is the most likely explanation of PSD-95 KO binocular impairments. In line with this, it is unlikely that aberrations in binocular eye movements account for the observations. We appreciate that alternative explanations remain possible and merit explicit discussion. Accordingly, we intend to expand the discussion of these alternatives.

Importantly, we will provide additional experimental data demonstrating that knock-down of PSD-95 in V1 but not in superior colliculus, significantly decreases orientation discrimination analyzed with the VWT, as we had shown for PSD-95 KO mice (while control knock-down does not have this effect). We believe that this new evidence better delineates the potential neuroanatomical locus of the PSD-95-associated deficits.

Furthermore, we will provide additional head movement analyses, as suggested by Reviewer 1. Specifically, we will investigate the head angle in relation to the cricket (azimuth) in time (±1 second) around prey contact under light and dark conditions.

We will also address the potential impact of PSD-95 KO learning deficits. We agree that there are more impairments in the PSD-95 KO brain, as has been published previously. But strikingly, the binocular impairment was dominating the sensory processing. This cannot be convincingly explained by learning deficits. In fact, we have observed improved learning of PSD-95 KO mice with some tasks (e.g. cocaine conditioned place preference) [3], but no significant differences in the VWT [1,2]. Learning differences were described for another PSD-95 mouse line, expressing the N-terminus with two PDZ domains [4]. To avoid potential learning dependent confounds, we have chosen salient stimuli, like water aversion, and prey capture to reduce impacts of potential learning defects.

We agree on the strength of the random dot stereograms to isolate stereoscopic computations. However, it requires special filters in front of either eye, which renders it unsuitable for the VWT. The lengthy training with less silent stimuli of water reward, could potentially add additional confounds of PSD-95 KO deficits. Thus, we think that this would be something for future experiments to allow for integration of different visual inputs. However, the combined improved performance of WT mice with binocular vision for prey capture (depth percept) and orientation discrimination (summation) is already supporting the importance of binocular vision in mice and the dominant defect in PSD-95 KO mice.

Finally, we will address the other points raised by the reviewers through clearer exposition and reorganization of the manuscript.

Once again, we would like to thank the reviewers for their thoughtful and constructive feedback, which we believe will substantially strengthen the manuscript.

(1) Huang, X., Stodieck, S. K., Goetze, B., Cui, L., Wong, M. H., Wenzel, C., Hosang, L., Dong, Y., Löwel, S., and Schlüter, O. M. (2015). Progressive maturation of silent synapses governs the duration of a critical period. Proc. Natl. Acad. Sci. 112, E3131–E3140. https://doi.org/10.1073/pnas.1506488112.

(2) Favaro, P.D., Huang, X., Hosang, L., Stodieck, S., Cui, L., Liu, Y., Engelhardt, K.-A., Schmitz, F., Dong, Y., Löwel, S., et al. (2018). An opposing function of paralogs in balancing developmental synapse maturation. PLOS Biol. 16, e2006838. https://doi.org/10.1371/journal.pbio.2006838.

(3) Shukla, A., Beroun, A., Panopoulou, M., Neumann, P.A., Grant, S.G., Olive, M.F., Dong, Y., and Schlüter, O.M. (2017). Calcium‐permeable AMPA receptors and silent synapses in cocaine‐conditioned place preference. EMBO J. 36, 458–474. https://doi.org/10.15252/embj.201695465.

(4) Migaud, M., Charlesworth, P., Dempster, M., Webster, L.C., Watabe, A.M., Makhinson, M., He, Y., Ramsay, M.F., Morris, R.G.M., Morrison, J.H., et al. (1998). Enhanced long-term potentiation and impaired learning in mice with mutant postsynaptic density-95 protein. Nature 396, 433–439. https://doi.org/10.1038/24790.

eLife Assessment

In this valuable study, the authors present traces of bone modification on ~1.8 million-year-old proboscidean remains from Tanzania, which they infer to be the earliest evidence for stone-tool-assisted megafaunal consumption by hominins. Challenging published claims, the authors argue that persistent megafaunal exploitation roughly coincided with the earliest Acheulean tools. Notwithstanding the rich descriptive and spatial data, the behavioral inferences about hominin agency rely on traces (such as bone fracture patterns and spatial overlap) that are not unequivocal; the evidence presented to support the inferences thus remains incomplete. Given the implications of the timing and extent of hominin consumption of nutritious and energy-dense food resources, as well as of bone toolmaking, the findings of this study will be of interest to paleoanthropologists and other evolutionary biologists.

Reviewer #2 (Public review):

The revised manuscript does a good job of using less definitive language, particularly by adding "possible" qualifiers to several interpretations. This addresses the concern about overstatement.

The main issue raised in the original review, however, remains unresolved. Only two elephant bone specimens at EAK show green-bone breakage interpreted as anthropogenic, and the diagnostic basis for that interpretation is not demonstrated clearly on the EAK material itself. The manuscript discusses a suite of fracture attributes described as diagnostic of dynamic percussive breakage, but these attributes are not explicitly documented on the EAK specimens. Instead, the diagnostic traits are illustrated using material from other Olduvai contexts, and that behavior is then extrapolated to make similar claims at EAK. For a paper making a potentially important behavioral argument, the key diagnostic evidence is not clearly demonstrated at the focal assemblage.

This problem is evident in the presentation of the EAK specimens. In their response, the authors state that one EAK specimen shows "overlapping scars" and constitutes a "long bone flake"; however, these features are not clearly identifiable in the figures or captions as currently presented. The authors state that Figures S21-S23 clearly indicate human agency, including a long bone flake with overlapping scars and a view of the medullary surface, but it is unclear which specimens or surfaces these descriptions refer to. Figure S21 does appear to show green fracture and is described only as an "elephant-sized flat bone fragment with green-bone curvilinear break." Figure S22 shows the same bone and cortical surface in a different orientation, providing no additional information. In Figure S23, I cannot clearly identify a medullary surface or evidence of green-bone fracture from this image. None of these images clearly demonstrates overlapping scars, and the figures would be substantially improved by explicitly identifying the features described in the text. Even if both EAK specimens are accepted as green-broken, they do not demonstrate the co-occurrence of multiple diagnostic fracture traits such as multiple green breaks, large step fractures, hackle marks, and overlapping scars that the authors state is required to attribute dynamic percussive activity to hominins and address equifinality.

I appreciate that the authors are careful to state that spatial association between stone tools and fossils alone does not demonstrate hominin behavior, and that they treat the spatial analyses as supportive rather than decisive. While the association is intriguing, the problem is downstream: spatial association is used to strengthen an interpretation of butchery at EAK that still depends on fracture evidence that is not clearly documented at the assemblage level.

The critique concerning Nyayanga is not addressed in the revision. The manuscript proposes alternative explanations for the Nyayanga material but does not demonstrate why these are more plausible than the interpretation advanced by Plummer et al. (2023). I am not arguing that the Nyayanga material should be accepted as butchery; rather, showing that trampling is possible does not establish it as more probable than cut marks. In contrast, the EAK material is treated as evidence of butchery on the basis of evidence that, in my opinion, is more limited and less clearly demonstrated. Even if this is not the authors' intention, the uneven treatment removes an earlier megafaunal case from the comparison and strengthens the case for interpreting EAK as marking a behavioral shift toward megafaunal butchery by excluding other early cases.

While I remain concerned about how the EAK evidence is documented and interpreted, I think the manuscript is appropriate for publication and will generate useful discussion. Readers can then assess for themselves whether the available evidence supports the strength of the behavioral claims.

Author response:

The following is the authors’ response to the previous reviews

Reviewer #1 (Public review):

I am happy with the revisions the authors made, and believe that the manuscript is now stronger, representing an important contribution.

We are truly thankful to this reviewer for the very constructive comments

Reviewer #2 (Public review):

In their response, the authors state that they do not treat the EAK evidence as decisive, yet the manuscript repeatedly characterizes the assemblage in very definitive terms. For example, EAK is described as "the oldest unambiguous proboscidean butchery site at Olduvai" and as "the oldest secure proboscidean butchery evidence." These phrases communicate a high level of confidence that does not align with the more qualified position articulated in the rebuttal and extends beyond what the documented evidence securely supports.

We decided to sound less dogmatic and remove the emphasis by adding “potentially” the oldest…. We emphasize that even if we had documented cut marks, we would be on the same epistemological ground, since there is no 100% certainty that the marks identified as cut marks could be cut marks.

I appreciate the authors' clarification regarding the fracture features, and I agree that these are well-established outcomes of dynamic hammerstone percussion. At the same time, several of these traits have been documented in non-anthropogenic contexts, including helicoidal spiral fractures resulting from trampling and carnivore activity (Haynes 1983), adjacent or flake-like scars created by carnivore gnawing (Villa and Bartram 1996), hackled break surfaces produced by heavy passive breakage such as trampling or sediment pressure (Haynes 1983), and impact-related bone flakes observed in carnivore-modified assemblages (Coil et al. 2020).

We added this explanation to the final version of the article:

“This interpretation is epistemologically problematic because it does not satisfy the fundamental criteria for valid analogy as outlined by Bunge (1981), namely substantial, structural, and environmental affinity. Specifically, the cited examples involve agents, materials, and contexts that differ markedly in composition, mechanical properties, and loading regimes from those considered here. Experimental and actualistic studies demonstrate that carnivores—rather than trampling—are also capable of producing spiral fractures and overlapping bone scarring, but these observations are restricted to faunal remains of substantially smaller body size than elephants, which they can gnaw (Haynes 1983; see also Figures S30–S36). To date, no carnivore has been documented as producing comparable fracture morphologies or surface damage on elephant bones. Consequently, the proposed analogy is not supported. Moreover, Haynes (1983) provides no empirical evidence that sediment pressure or trampling can generate hackled fracture surfaces. Such features are instead associated with dynamic loading conditions, whereas passive breakage processes have not been shown to produce these types of modifications. This reasoning also applies to impact flakes on elephant bones, which can only be produced by the sole modern agent documented to dynamically fracture green proboscidean long bones: humans.”

One of the biggest issues is that there is no quantitative data or images of the bone fracture features that the authors refer to as the main diagnostic criteria at EAK. The only figures that show EAK specimens (S21, S22, S23) illustrate general green-bone fracture morphology but none of the specific traits listed in the text. In contrast, clear examples of similar features come from other Olduvai assemblages, which may be misleading to readers if they mistakenly interpret those as images from EAK. The manuscript also states that these traits "co-occur," but it is not defined whether this refers to multiple features on the same fragment or within the broader assemblage. Without images or counts that document these traits on EAK fossils, readers cannot evaluate the strength of the interpretation. Including that information would substantially strengthen the manuscript.

The arguments were addressed in the general criteria criticized by the reviewer in his/her previous review encompassing all green broken elephant bones documented. If we restrict the arguments now to EAK, then suffice to rescue the arguments from the previous reply. Images (Figs S21-23) show the EAK broken specimens and clearly indicate their human agency by two factors: a) at least one of them is a long bone flake with overlapping scars (FS 23 is showing its medullary side), and b) elephant bones impacted by carnivores (namely, hyenas) have always shown intensive gnawing and tooth-marking; lack thereof in both EAK specimens refutes a non-human carnivore agency. The former argument is interpreted as human agency because carnivores have not documented to produce such features on elephant bones.

Regarding the statement that "natural elephant long limb breaks have been documented only in pre or peri-mortem stages when an elephant breaks a leg, and only in femora (Haynes et al., 2021)," it is not entirely clear what this example is intended to illustrate in relation to the EAK assemblage. My understanding is that the authors are suggesting that naturally produced green bone fractures in elephants are very limited, perhaps occurring only in pre or peri-mortem broken leg cases, and that fractures on other elements should therefore be attributed to hominin activity. If that is not the intended argument, I would encourage clarifying this point. This appears to conflate pre-mortem injury with the broader issue of equifinality. My original comment was not referring to pre-mortem breaks but to the range of natural (i.e., non-hominin) and post-mortem processes that can generate spiral or green bone fractures similar to those described by the authors.

We elaborated such argument addressing exclusively the reviewer´s previous argument that natural limb breaking produced spiral breaks on elephant long bones, which is correctly, as Haynes describes it, the only way not involving human agency that can generate a helicoidal spiral fracture on an elephant long bone. Non-human post-mortem processes on fresh bone do not generate these features. Neither have extant carnivores documented to produce these features on elephant bones.

Finally, in considering the authors' response on the Nyayanga material, I still find the basis for their dismissal of that evidence difficult to follow and the contrasting treatment of the Nyayanga and EAK evidence raises concerns about interpretive consistency. Plummer et al. (2023) specify that bone surface modifications were examined using low-power magnification (10×-40×) and strong light sources to identify modifications and that they attributed agency (e.g., hominin, carnivore) to modifications only after excluding possible alternatives. The rebuttal does not engage with the procedures reported. The existence of newer analytical techniques does not diminish the validity of long-standing methods that have been applied across many studies. It is also unclear why abrasion is presented as a more likely explanation than stone tool cutmarks. The authors dismiss the Nyayanga images as "blurry," but this is irrelevant to the interpretation, since the analysis was based on the fossils, not the photographs. The Nyayanga dataset is dismissed without a thorough engagement, while the EAK material, despite similar uncertainties and potential for alternative explanations, is treated as definitive.

We believe the rebuttal engages with these arguments. The protocol “bone surface modifications were examined using low-power magnification (10×-40×) and strong light sources to identify modifications and that they attributed agency (e.g., hominin, carnivore) to modifications only after excluding possible alternatives” does not guarantee that any derived interpretation is correct. These methods have consistently been used for decades now in contexts in which different researchers draw different conclusions on the same marks. The underlying variables used are subjectively interpreted and tallied, and equifinal when not considering overlapping factors, such as sediment abrasion and trampling. As an example, the same marks on the Nyayanga hippo bones interpreted by the original authors as cut marks, we see them undifferentiable from trampling marks from the image evidence published.

It is clear in the final version of our article that the EAK evidence is not treated as definitive, since that would be dogmatic, and thus, non-scientific. We thank this reviewer for having given us the chance to reconsider our original phrasing.

eLife Assessment

This is an important study that identifies the developmental time window during which re-expression of TCF4 mutated in Pitt-Hopkins syndrome, can rescue phenotypic features of brain function in a TCF4 knockout mouse. The study presents compelling data using a viral transgenic intersection approach to show that TCF4 expression is required early in perinatal life. These findings have implications for the timing of possible gene therapy in people with Pitt-Hopkins-associated TCF4 mutations.

Reviewer #1 (Public review):

Summary:

This manuscript follows up previous work from this group using a conditional TCF4 mouse where Cre-expression turns "on" expression of TCF4 to investigate whether postnatal re-expression of TCF4 is effective to correct phenotypes related to Pitt-Hopkins Syndrome (PTHS) in humans. Results may inform gene therapy human PTHS gene therapy efforts on effective developmental windows for gene therapy. The authors demonstrate that re-expression of TCF4, induced by retro-orbital (RO) AAV-PHP.eB-Cre, during 2-4th postnatal week, does not rescue brain or body weight, anxiety-like or nest-building behaviors, but rescues an object location memory task, a measure of cognition. These results are novel and interesting in that they reveal distinct developmental roles for TCF4 in distinct behaviors and suggest that TCF4 plays a role in the mature brain in hippocampal and memory-related plasticity. Results may inform gene therapy design in PTHS.

Strengths:

The results are rigorous and high quality. Multiple methods are used to assess AAV-mediated re-expression of Cre, reactivation of TCF4, and the developmental time course of expression. Multiple behavioral phenotypes and molecular rescue are assessed. Most behavioral phenotypes are reproducible and robust, and it is clear whether a rescue was observed.

Weaknesses:

(1) Although the authors demonstrate the time course and spatial extent of Cre and a Cre-reporter (TdTom) in the brain with the AAV-Cre, it is unclear how many cells are transduced. Similarly, the authors do not measure TCF4 levels with immunohistochemistry or western blot. So the level of protein reactivation is unknown. A possible reason the rescue is incomplete is that the TCF4 protein is not induced in a large % of neurons in specific brain regions that mediate specific behaviors, such as the hippocampus vs. the striatum.

(2) The authors perform bulk qPCR to demonstrate a 20% increase in TCF4 RNA with Cre-mediated activation. It is unclear why the full gene reactivation is not observed. An alternative interpretation of the incomplete rescue of the phenotypes is that full TCF4 expression is required at later developmental time points.

Reviewer #2 (Public review):

Summary:

The basic helix-loop-helix transcription factor TCF4 (also known, as ITF2, SEF2, or E2-2) is a protein involved in the development and functioning of many different cell types. TCF4 plays important roles in the nervous system, both in health and disease. Its importance in the nervous system is underlined by its association with common and rare cognitive disorders. Specifically, variants of the TCF4 gene are implicated in increased susceptibility to schizophrenia, and mutations in the TCF4 gene cause Pitt-Hopkins syndrome (PTHS) or mild to moderate non-syndromic intellectual disability.

In this manuscript, the authors have studied whether reinstating TCF4 later in postnatal development in juvenile PTHS model mice could reverse behavioral phenotypes, thereby simulating gene therapy. Previous research by the same group has demonstrated that restoring TCF4 during embryonic or neonatal stages, corresponding to prenatal or neonatal periods in humans, improved phenotypes in a PTHS mouse model. In the current study, a conditional TCF4 reinstatement mouse model, Tcf4-lox-stop-lox (Tcf4-LSL), previously developed and characterized by their lab, where Cre-mediated recombination removes a floxed transcriptional stop cassette downstream of exon 17, leading to reinstatement of all TCF4 isoforms at appropriate levels in neurons, was used. The study showed that this later intervention failed to correct most phenotypes, suggesting that perinatal reinstatement of TCF4 holds the greatest potential to treat behavioral symptoms of PTHS. However, the study also suggests that some cognitive behaviors may still be responsive to TCF4 reinstatement later in life.

Strengths:

This is a very important study aimed at developing gene therapy for PTHS. The study is technically very well performed and written.

Weaknesses:

The only weakness is that a human disease is modelled in a mouse, which is evolutionarily not the closest mammal to humans. Hopefully, in the future, similar studies will also be performed in a nonhuman primate model, for example rhesus macaque.

eLife Assessment

This study proposes a cross-species transcriptomic framework to predict vaccine reactogenicity, with implications for preclinical vaccine safety assessment. The findings show that mouse muscle transcriptomic signatures capture conserved inflammatory programs and can identify highly reactogenic formulations, with supportive but limited evidence for finer discrimination among licensed human vaccines. Overall, the work establishes a valuable foundation for translational biomarkers of reactogenicity, although the strength of evidence for broad cross-species predictive performance remains incomplete and would benefit from further validation.

Reviewer #1 (Public review):

Summary:

The authors aimed to develop a translational framework for predicting vaccine reactogenicity by training a penalized ordinal regression model on mouse muscle transcriptomics and applying it across tissues and species to rank human vaccines by their inflammatory potential.

Strengths:

The study addresses an important gap in preclinical vaccine safety assessment. The identification of IL6/JAK/STAT3 signaling as a key pathway implicated in reactogenicity is biologically plausible, and the observation of coordinated changes between muscle and blood compartments supports the biological relevance of the signature. The model achieves near-perfect classification in mouse muscle tissue and successfully identifies Fluad (MF59-adjuvanted) as the most reactogenic among licensed human vaccines, consistent with clinical safety data.

Weaknesses:

The methodological foundation has several concerns. The reactogenicity class definitions rely on PC1 scores with modest variance explained, yet no sensitivity analyses demonstrate robustness to different normalization strategies, feature selection approaches, or dimensionality reduction methods. I suggest performing sensitivity analyses demonstrating that reactogenicity class definitions are robust to alternative normalization methods, feature selection criteria, and dimensionality reduction approaches.

The combined mouse analysis reveals that tissue effects dominate over vaccine-induced variation, and no explicit batch or compartment correction was reported. The authors can apply batch/compartment correction (e.g., SVA) when analyzing combined mouse muscle and blood data, then recompute PCA and downstream analyses.

The central claim regarding cross-species ranking capability is not fully supported. In human blood, the model largely distinguishes Fluad from other vaccines but shows limited separation among non-Fluad formulations, with many pairwise comparisons yielding non-significant adjusted p-values. This pattern suggests the model may be tuned to detect large inflammatory magnitudes-likely a consequence of training on extreme stimuli such as LPS and whole-cell pertussis-rather than capturing the finer gradations relevant for distinguishing licensed vaccines with moderate reactogenicity profiles. I highly suggest retraining the model, excluding extreme stimuli (LPS, Pentavac), to evaluate whether mid-range separations among licensed vaccines can be recovered.

Impact:

While the conceptual framework is promising, the current evidence does not convincingly demonstrate that the model can rank vaccines beyond identifying highly inflammatory outliers. The utility for preclinical assessment of novel vaccine candidates with moderate reactogenicity profiles remains uncertain.

Reviewer #2 (Public review):

Summary:

The authors derived a time-specific signature of reactogenicity from mouse muscle following exposure to vaccines /TLRs for capturing the reactogenicity patterns. They tested this reactogenicity signature in mouse blood, and then they applied the reactogenicity signature to human blood from subjects having received different vaccines. They identified biomarkers in mouse muscle which are also observed in mouse and human blood and could be used as a reactogenicity signature in mice, instead of CRP.

Strengths:

(1) The authors used transcriptomic response following vaccination and used common genes to human and mice for defining a reactogenic signature.

(2) As the authors used different formulations in mice, the model was trained across a broad reactogenicity spectrum, which has the advantage of being used for evaluating new vaccines/vaccine platforms.

Weaknesses:

(1) The muscle gene signature reflects local reactogenicity. Systemic reactogenicity is not specifically addressed, except where overlapping gene signatures are observed for both local and systemic reactogenicity.

(2) In the same logic, could we find additional genes in the blood which are not captured in the muscle?

(3) The peak of the reactogenicity is usually 24h; it is not certain that additional TPs have helped the findings. If they have, the authors should explain.

eLife Assessment

The study presents a valuable finding on the ubiquitin-dependent regulatory loop in which proapoptotic Bim is targeted to the E3 ubiquitin ligase Cul5-Wsb2-mediated degradation through its sequestration by BCL2 proteins. The conclusions are supported by incomplete evidence and would benefit from additional experiments addressing both the mechanistic understanding and the physiological/cancer-related significance of the study.

Reviewer #1 (Public review):

This manuscript by Toczyski and colleagues explores the role of ubiquitin-dependent degradation in the co-regulation between pro- and anti-apoptotic proteins. The binding of the pro-apoptotic sensor Bim to BCL2 anti-apoptotic proteins sequesters it into inactive complexes, inhibiting BCL2 members but also preventing Bim from activating the apoptotic executors BAX and BAK. The authors now suggest that the E3 ubiquitin ligase Cul5-Wsb2 targets Bim turnover while in complex with BLC2 members. The authors reveal the importance of WSB2 in apoptosis of neuroblastoma cell lines, highlighting the importance of Wsb2 as a cancer biomarker. In sum, this study identifies Bim as a novel Wsb2 target and suggests a novel co-receptor mechanism using BCL-2 members as bridging factors, thus adding a novel mechanistic layer to the apoptosis repressor role of Wsb2. Their experimental approach is sound, and in most cases, the conclusions are justified. However, whether Cul5-Wsb2 targets Bim via BLC2 anti-apoptotic members would require further analysis.

Major comments:

(1) They find that Wsb2 or Cul5 downregulation increases the levels of Puma and Bim isoforms, and that Wsb2 strongly interacts with all Bim isoforms. Moreover, Wsb2 regulates Bim turnover, especially visible for Bim-EL, and controls Bim-L ubiquitylation. Finally, Figure 2E suggests that Wsb2-Bim interaction is bridged by Bcl-xL, and they identify the domain in Bcl-xL/Wsb2 responsible for their binding in Figure 4A-E. However, Figure 4F shows only a mild decrease between Bim-EL and HA-Wsb2EEE, which is inconsistent with their model. This important gap should be backed up by further experimental evidence. For example, by performing (a) coIP studies between Bim and Wsb2 in the presence of Bcl-xlAAA and (b) Bim stability and ubiquitylation analysis in the presence of either Bcl-xlAAA or Wsb2EEE.

(2) The manuscript lacks quantifications and statistical analysis in most figures, which are particularly important for Figure 1D - especially regarding the upregulation of Puma and Bim isoforms upon downregulation of Cul5 and Wsb2, for Fig 3A - also including statistical analyses of Bim1 stability in presence or absence of proteasomal inhibitors, and for Figure 4D, F, especially regarding the interaction of Bim-EL- with WT and mutant Bcl-xL in 4D and with WT and mutant Wsb2 in 4F.

(3) The localization of BCL2 family members at the mitochondrial outer membrane is a crucial step in the implementation of apoptosis, and BCL2 members recruit Bim to the OM. Despite their finding suggesting that Bim insertion into the OM might be dispensable for interaction with Bim, the interaction was abolished by BH3-mimetics that disrupt Bcl-xL interaction with BIM. This suggests that Wsb2 interacts with Bim at the mitochondrial surface. Therefore, it would be interesting to investigate the sub-cellular localization Bim and WSB2 with and without ABT-263.

(4) Wsb2 mildly interacts with Bcl-xL and with Mcl1, but does not interact with Bcl-w or Bcl2. However, they show that Wsb2 recognizes Bcl-xl through a motif conserved between Bcl-xl, Bcl-w and Bcl2. Therefore, it would be helpful to precipitate Bcl-w or Bcl2 and check interaction with Wsb2.

Reviewer #2 (Public review):

Summary

This manuscript proposes an original and conceptually interesting model in which anti-apoptotic BCL-2 family proteins, particularly BCL-XL and MCL-1, not only sequester BIM but also act as adaptor "co-receptors" that recruit BIM to the CUL5-WSB2 ubiquitin ligase complex for degradation. The authors present a mechanistic framework supported by structure-guided mutagenesis, BH3 mimetic perturbations and co-immunoprecipitation assays performed in RPE1 cells. In parallel, the study shows that neuroblastoma cell lines are highly dependent on WSB2 for survival. These observations give the work both conceptual and translational relevance.

Strengths

The principal strength of the study lies in its conceptual novelty. Reframing BCL-XL and MCL-1 not only as sequestration factors but also as adaptors that facilitate substrate engagement by an E3 ligase substantially extends current models of apoptotic regulation. The mechanistic narrative developed in RPE1 cells is clear and internally consistent: the combination of AlphaFold-guided motif identification with complementary mutagenesis provides a persuasive framework for how WSB2 associates with anti-apoptotic BCL-2 family members and promotes BIM turnover. The definition of a BCL-XL/MCL-1 co-receptor mechanism for WSB2-mediated BIM degradation is therefore both intuitive and mechanistically appealing. In parallel, the authors present a distinct experimental series showing that neuroblastoma cells exhibit pronounced sensitivity to WSB2 loss, undergo apoptosis upon its depletion and display reduced competitiveness in mixed-culture assays. Although the mechanistic connection between these observations requires further clarification, the convergence of a well-defined biochemical model with a clear cancer-relevant phenotype enhances the potential biological significance of WSB2 and raises the possibility that its regulation may hold therapeutic relevance.

Weaknesses

There are several limitations that readers should consider when interpreting the study. The most fundamental issue is the disconnect between the mechanistic model established in RPE1 cells and the apoptotic phenotype observed in neuroblastoma. Although the manuscript convincingly demonstrates the WSB2-BCL-XL/MCL-1-BIM axis in RPE1 cells and independently shows that WSB2 loss compromises neuroblastoma viability, it does not examine whether BIM levels are elevated upon WSB2 depletion in neuroblastoma, nor whether apoptosis in these cells requires BIM. Without demonstrating WSB2-BCL-2-BIM complex formation or BIM dependence in the disease-relevant context, it remains unclear whether the co-receptor mechanism characterised in RPE1 cells explains the phenotype. This gap is compounded by the observation that PUMA, another potent pro-apoptotic factor, also increases following WSB2 loss, raising the possibility that multiple death pathways contribute to the outcome. The absence of a genetic rescue experiment, such as re-expression of an shRNA-resistant WSB2 restoring viability and suppressing apoptosis, further limits causal inference regarding WSB2's role in neuroblastoma.

Many central claims rely on single Western blots and pulldown assays without quantification or assessment of reproducibility. This complicates the interpretation of CHX chase experiments (where initial steady-state levels differ between samples) and limits confidence in BH3 mimetic experiments, which use a single concentration and short exposure time. Without dose-response curves, time-course analyses, caspase inhibition, or orthogonal genetic perturbation of BCL-XL or MCL-1, indirect or off-target drug effects cannot be excluded. Reduced co-IP signals in these assays could therefore reflect early apoptotic events or compound instability rather than specific disruption of protein-protein interactions.

A further limitation concerns the inference of a direct WSB2-BCL-XL interaction. The mutagenesis analyses are performed in lysates that contain endogenous or overexpressed BIM, and BH3 mimetics disrupt the WSB2 interaction only when the BCL-XL-BIM heterodimer is dismantled. The study thus cannot distinguish whether the mapped WSB2 motifs mediate direct contact with BCL-XL or whether they influence the architecture or stability of the BCL-XL-BIM complex. Because no purified protein reconstitution or biophysical binding assays are presented, the evidence for direct binding remains suggestive rather than conclusive.

The ubiquitination data also remain incomplete. Although the WSB2 mutation reduces the ubiquitin smear on BIM, the assay does not demonstrate dependence on CUL5, RBX2 or ARIH2, leaving open which ligase components are directly responsible. MLN4924 implicates CRLs more broadly, but the ubiquitination assay itself does not assign activity to the CUL5-WSB2 module.

Finally, several methodological details are insufficiently described, including the generation and validation of the doxycycline-inducible WSB2 and HA-WSB2 lines and the suitability of the WSB2-overexpressing control line used in immunoprecipitations.

Collectively, these issues do not undermine the conceptual interest of the proposed co-receptor model, but they do limit the strength of the mechanistic claims and weaken the connection between the defined mechanism and the neuroblastoma phenotype.

eLife Assessment

This important work substantially advances our understanding of the role of synaptotagmin-7 (Syt7) in short-term plasticity at cortical glutamatergic synapses. The evidence supporting the conclusions is convincing, with rigorous and elegant quantal-level iGluSnFR imaging and failure-based analyses at single boutons. The work will be of broad interest to synaptic physiologists and molecular biologists.

Reviewer #1 (Public review):

Kotzadimitriou et al. investigate how synaptotagmin-7 (syt7) contributes to short-term plasticity at cortical glutamatergic synapses. Using quantal-level iGluSnFR imaging and failure-based analyses at single boutons, the authors distinguish between synchronous and asynchronous glutamate release across boutons with differing baseline efficacy. They show that knocking out syt7 abolishes facilitation of synchronous release while leaving asynchronous facilitation largely intact, although reduced in magnitude. Furthermore, they argue that synchronous and asynchronous events arise from functionally distinct vesicle pools. The manuscript concludes that syt7 is essential for the facilitation of synchronous release, while other calcium sensors govern asynchronous release.

Strengths:

(1) The use of iGluSnFR provides a robust readout of single-synapse activity. Unlike traditional ephys methods that average the activity of thousands of synapses (which may mask the facilitation of low Pr synapses), the authors employ quantal imaging to analyze thousands of individual boutons and stratify them by efficacy. The representative images and traces in Figure 1 are of high quality, and the quantal analysis demonstrating multiple quantal peaks aligns well with previously published work (Mendonca et al., 2022; Wang et al., 2022).

(2) The failure-based analysis is thoughtfully implemented. By isolating trials in which no release occurred, the authors effectively separate facilitation from depletion, strengthening their central argument that syt7 is required for facilitation independent of vesicle depletion.

(3) The proposed model (depicted in Figure 7) is interesting and may reconcile the contradictory roles attributed to syt7, as described by others in the field. Specifically, the authors provide data to address syt7's potential function in facilitation, asynchronous release, and replenishment. However, to further support their model, which argues that "multiple Ca2+ sensors have both unique and overlapping roles in regulating synaptic plasticity," additional experiments are needed (see point 2 below).

Weaknesses:

(1) While the authors use cultures from syt7 knockout mice (and wild-type controls), there are no acute rescue experiments (e.g., syt7 viral transduction in KO cultures) or checks for compensatory changes in other proteins. Previous studies (Bacaj et al., 2013; Jackman et al., 2016) have utilized viral rescues to confirm specificity. Without such experiments, it remains theoretically possible that the chronic loss of syt7 leads to downregulation of another protein essential for facilitation. At a minimum, the authors should perform rescue experiments for at least some of their findings. Additionally, western blots for syt1 and syt7 should be conducted to confirm that their knockout is specific to syt7.

(2) The manuscript acknowledges the possible roles of Doc2a and syt3 but fails to address them experimentally. Recent work (Wu et al., 2024; Weingarten et al., 2024) has identified Doc2a as the primary sensor for asynchronous release. Even if its expression in cortical cultures remains unconfirmed (as claimed by the authors), they should, at the very least, perform Western blots for Doc2a and syt3 in both wild-type (to determine basal expression levels) and syt7 knockout cultures. Without analyzing the levels of these proteins, the mechanism/model behind the "remaining" asynchronous release remains speculative. Is it possible that these other calcium sensors are upregulated in their syt7 KO cultures and could instead explain their results?

Reviewer #2 (Public review):

Summary:

In this elegant study, the authors employ live iGluSnFR-based imaging of glutamate release from cortical boutons to dissect the distinct roles of the Ca²⁺ sensor synaptotagmin-7 (Syt7) in synaptic transmission. Although multiple functions have been attributed to Syt7 over the years, the field remains conflicted. The authors argue that one major obstacle for resolving some of these discrepancies lies in a fundamental limitation of electrophysiological recordings, which aggregate signals across all synapses to yield averaged readouts, dominated by strong, high-release-probability synapses. By using a live glutamate imaging approach combined with sensitive detection of action potential-evoked activity across different stimulation regimes, and a dedicated analysis pipeline, the authors confirm a role for Syt7 in facilitating synchronous release and in regulating the magnitude of asynchronous release. In contrast, they find no evidence that Syt7 contributes to the facilitation of asynchronous release, do not find evidence for a role for Syt7 in synaptic vesicle replenishment during AP trains, and provide evidence suggesting that the maintenance of facilitation by Syt7 may occur independently of vesicle depletion.

Strengths:

This study offers a fresh perspective on a debated issue, using a new experimental approach that the authors previously explored in the context of Synaptotagmin 1 (Mendonca et al. 2022). The authors record the response to a series of pair-pulse stimulations, followed by an AP train. By carefully quantifying individual events and by sorting events based on their efficacy, the authors extract quantitative information that they assign to different properties of synaptic function. They also devised an interesting approach for monitoring aspects of facilitation, in which they isolate PPR events where the first response did not elicit detectable release (thus regarding the release in response to the second AP as facilitating), and compare them with successful events. Together, the authors provide semi-quantitative descriptions of synchronous and asynchronous release during single, paired, and AP trains, yielding a weighted estimate of Syt7's contribution to distinct features of synaptic vesicle release that are independent of postsynaptic readouts. A major strength of the study is the confirmation of two principal proposed functions of Syt7: facilitation of synchronous release and regulation of the magnitude of asynchronous release.

Weaknesses:

The experimental approach presented here is elegant and well-executed. However, a principal limitation lies in translating electrophysiological terminology to imaging-based measurements. For instance, interpreting signals persisting beyond 10 ms as a proxy for asynchronous release relies on assumptions that would be good to experimentally justify. Could such signals arise from iGluSnFR saturation, or be affected by desensitization?. Moreover, the quantification of asynchronous release is based on very small signals that represent only a fraction of the already small synchronous release component, raising concerns about signal-to-noise limitations. A key issue is that failures to evoke glutamate release may arise from AP failures, such that the second response in a PPR does not necessarily represent facilitation. Given that many of the findings largely confirm existing literature, the study might have benefited from a different framing, for example, as an additional validation of the correspondence between electrophysiological measures and the authors' imaging-based readouts. Another point concerns the analysis of synaptic vesicle replenishment following depletion, which would ideally be addressed using alternative stimulation protocols, such as quantifying the response/success rate to single APs at varying time points after a train. Although the authors are appropriately cautious in their conclusions (e.g., with respect to Figure 5b), this limitation remains. Finally, the use of heterogeneous cortical neuronal cultures is likely to introduce substantial variability, as the authors themselves acknowledge, which may arise from the co-expression of multiple Ca²⁺ sensors across diverse cell types.

In summary, the authors were able to confirm previously-described changes in neurotransmission properties upon the loss of Syt7 using live imaging of glutamate release at the level of single boutons. They also present preliminary evidence for the interdependence of Syt7 function, synaptic vesicle replenishment, and the facilitation of asynchronous release, although these results will need to be substantiated in future studies using alternative stimulation protocols and complementary methodologies. Taken together with the group's prior work on synaptotagmin-1, this study illustrates that live imaging of glutamate release offers an alternative approach that recapitulates some elements detectable via electrophysiological analysis, while possibly revealing new insights into the function of synaptic proteins. As a whole, taking a live imaging approach may be a broadly accessible way forward to analyze synaptic function. The potential of studying synaptic proteins in diverse cell types that are difficult to access with patch-clamp electrophysiology is particularly compelling.

Reviewer #3 (Public review):

In this manuscript, the authors examine the role of Syt7 in the plasticity of synchronous and asynchronous release in cultured neurons. The experimental approach is the imaging of SF-iGluSnFR.A184V expressed in cultured neurons while delivering stimulation through whole-cell patch clamping of single neurons in the culture. In this manner, they could examine the optical signature of glutamate release in single presynaptic terminals, while separating the release events into synchronous (<10ms) and asynchronous (>10ms) while delivering both paired pulses or trains of stimuli (at 20 Hz, 50 ms between stimuli).

This manuscript employs techniques previously reported by the research group in their Mendoca et al., Nat Comms 2022 paper. This paper uses this approach to specifically examine the role of Syt7. The use of iGluSnFR in this manner provides significant rigor to the paper. The most significant weakness is that some of the events the authors discuss in this manuscript are rare, and the strength of the conclusions regarding those is somewhat unclear.

The main novel contribution of this manuscript is that single-bouton high-frequency imaging allowed them to examine paired-pulse plasticity in boutons that had not released neurotransmitter during the first pulse (failure-based analysis), thus separating between the effects of vesicle depletion and facilitation of the release machinery. This approach also allowed them to segregate their observations according to bouton-specific release efficacy. Both examinations are unavailable when performing cell-level analysis of neurotransmitter release, as is reported by most electrophysiological approaches.

The authors conclude that Syt7 contributes specifically to facilitation of synchronous release, not asynchronous release, while reducing the magnitude of the asynchronous component. Finally, the authors suggest segregation of synchronous and asynchronous release, either by differential use of calcium sensors or spatial segregation of the vesicles contributing to both modes of release.

This report contributes significantly to the discussion of the control of synaptic plasticity by different molecular players. It is not the first to examine Syt7, but its contribution to the examination of this protein is significant.

I find this report to be well executed and reasoned. In my opinion, the authors could improve the manuscript by clarifying the description of several methodological and experimental sections. Furthermore, in my opinion, some of the conclusions are overstated.

The authors state: "Because boutons along a single axon originate from the same presynaptic neuron, they are expected to share broadly similar molecular components of the vesicular release machinery and experience comparable presynaptic action potential waveforms." The authors should address the idea that presynaptic terminals from the same neuron on different postsynaptic targets can differ in the molecular components, as well as in the presynaptic side. There is ample evidence for differences between synapses onto glutamatergic and GABAergic neurons of the same neuron.

The authors used 4ms-long frames, but the stimuli are delivered at 20Hz (50ms apart). Therefore, in paired pulse stimulation, isn't there going to be a difference between the first and second stimuli regarding the timing of the frames relative to the stimulus? Isn't the deconvolution sensitive to such an offset?

A 10ms threshold for defining synchronous vs. asynchronous release full in-between frames. Doesn't this increase the chance of assigning borderline events to the wrong category?

On page 11 of the conclusion, the authors state that "Our data indicate that in our conditions during paired-pulse protocol Syt7 primarily enhances release probability rather than increasing the RRP size." While I understand the reasoning behind this statement, it should be toned down. The authors did not directly address the RRP size.

In failure-based analysis, the number of failure events in high-efficiency boutons is expected to be low. How does this affect the conclusions of the authors concerning the effects of Syt7 deletion on facilitation in high-efficiency boutons?<br /> SourceData.xlsx was not available to me, as far as I could tell.

How can the conclusions of the authors on the differential molecular composition of vesicles contributing to synchronous and asynchronous release be related to the reported effect of strontium on the nature of release? (see 10.1523/JNEUROSCI.20-12-04414.2000)

Is this the first use of failure-based analysis? If not, the authors should cite precedents. In 10.1016/s0896-6273(00)80338-4, failure of release during the 1st AP was presented, with facilitation during the 2nd, although no formal analysis was performed.

eLife Assessment

This study presents useful findings on the molecular mechanisms driving female-to-male sex reversal in the ricefield eel (Monopterus albus) during aging, which would be of interest to biologists studying sex determination. The manuscript describes an interesting mechanism potentially underlying sex differentiation in M. albus. However, the current data are incomplete and would benefit from more rigorous experimental approaches.

Reviewer #1 (Public review):

Summary:

This preprint investigates the molecular mechanism by which warm temperature induces female-to-male sex reversal in the ricefield eel (Monopterus albus), a protogynous hermaphroditic fish of significant aquacultural value in China. The study identifies Trpv4 - a temperature-sensitive Ca²⁺ channel - as a putative thermosensor linking environmental temperature to sex determination. The authors propose that Trpv4 causes Ca²⁺ influx, leading to activation of Stat3 (pStat3). pStat3 then transcriptionally upregulates the histone demethylase Kdm6b (aka Jmjd3), leading to increased dmrt1 gene expression and ovo-testes development. This work aims to bridge ecological cues with molecular and epigenetic regulators of sex change and has potential implications for sex control in aquaculture.

Strengths:

(1) This study proposes the first mechanistic pathway linking thermal cues to natural sex reversal in adult ricefield eel, extending the temperature-dependent sex determination paradigm beyond embryonic reptiles and saltwater fish

(2) The findings could have applications for aquaculture, where skewed sex ratios apparently limit breeding efficiency

Weaknesses:

Although the revised manuscript represents an improvement over the original version, substantial weaknesses remain.

Scientific Concerns

(1) Western blot normalization and exposure: The loading controls (GAPDH) in Fig. S3C appear overexposed, as do several Foxl2 blots. Because these signals are likely outside the linear range, I am not convinced that normalization is reliable. This raises concerns about the validity of the quantified results.

(2) Antibody validation and referencing (Line 776): The authors need to refer explicitly to figures demonstrating antibody validation. At present, these data are provided only as a supplementary file that is not cited in the manuscript. In addition, the Sox9a antibody appears to yield indistinguishable signals in control and RNAi conditions, suggesting that it may not recognize eel Sox9a. This issue is not addressed by the authors. Furthermore, antibody validation Western blots should be quantified.

(3) Unclear sample sizes (N values): Sample sizes remain unclear for several figures:

(a) Fig. 3F - No N value is provided. Each graph shows three data points; does this indicate that only three samples were quantified? If ten samples were collected, why were all not quantified?

(b) Fig. 4 - No N values are reported.

(c) Fig. 5A - Again, only three data points are shown per group, despite the apparent availability of twelve samples. The rationale for this discrepancy is not explained.

(4) qRT-PCR normalization: The manuscript does not specify the reference gene(s) used for qRT-PCR normalization. Although expression levels are reported as "relative," neither the identity of the reference gene(s) nor the justification for their selection is provided.

(5) Specificity of key antibodies: While the authors have made some effort to validate anti-Amh, anti-Sox9, and anti-Dmrt antibodies, the results remain incomplete. The Amh and Dmrt antibodies detect reduced protein levels following knockdown of their respective targets, which is encouraging. However, the Sox9a antibody shows no difference between control and RNAi conditions, suggesting it does not recognize eel Sox9. This is not acknowledged in the manuscript. In addition, no validation data are presented for Foxl2. Antibody validation data must be clearly referenced in the main text and presented in an interpretable and quantitative manner.

(6) Immunofluorescence data quality: The immunofluorescence images remain difficult to interpret. I strongly encourage the authors to enlarge the image panels and to present monochrome images (white signal on black background). The current presentation severely limits interpretability.

(7) Unreferenced supplementary figure: Fig. S4 is included in the submission but is not referenced anywhere in the manuscript text.

(8) Fig. 5B image resolution: The micrographs in Fig. 5B are too small to allow meaningful evaluation of the data.

(9) Unexplained data inclusion (Fig. 5E): Fig. 5E includes a pERK blot that is not mentioned in the Results section. The rationale for including these data is unclear.

(10) Poor blot quality (Fig. S3C): The blots in Fig. S3C exhibit high background and overexposure. I am concerned about the reliability of the quantification shown in panel D.

(11) Poor blot quality (Fig. S5G): The Stat3 blots in Fig. S5G contain numerous white artifacts, raising concerns about their suitability for normalization in panel H.

(12) Missing controls (Fig. 6E): Fig. 6E lacks controls for HO-3867 and Colivelin treatments alone. Without these controls, it is not possible to determine whether the reported effects are meaningful.

(13) Graphical presentation: The use of a light blue-to-pink gradient in bar graphs throughout the manuscript does not aid interpretation. I recommend using more distinct colors (e.g., red, orange, green, blue, purple, gray, black) to improve clarity. In summary, the interpretation of the study remains limited by persistent issues related to data presentation, image quality, and reagent specificity.

Author response:

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

Public Reviews: 

Reviewer #1 (Public review): 

Summary:

This study investigates the molecular mechanism by which warm temperature induces female-to-male sex reversal in the ricefield eel (Monopterus albus), a protogynous hermaphroditic fish of significant aquacultural value in China. The study identifies Trpv4 - a temperature-sensitive Ca²⁺ channel - as a putative thermosensor linking environmental temperature to sex determination. The authors propose that Trpv4 causes Ca²⁺ influx, leading to activation of Stat3 (pStat3).pStat3 then transcriptionally upregulates the histone demethylase Kdm6b (aka Jmjd3), leading to increased dmrt1 gene expression and ovo-testes development. This work aims to bridge ecological cues with molecular and epigenetic regulators of sex change and has potential implications for sex control in aquaculture.

Strengths:

(1) This study proposes the first mechanistic pathway linking thermal cues to natural sex reversal in adult ricefield eel, extending the temperature-dependent sex determination paradigm beyond embryonic reptiles and saltwater fish.

(2) The findings could have applications for aquaculture, where skewed sex ratios apparently limit breeding efficiency.

We thank you for the encouraging comments of our work, and answering your questions has greatly improved the quality of the manuscript.

Weaknesses:

(A) Scientific Concerns:

(1) There is insufficient replication and data transparency. First, the qPCR data are presented as bar graphs without individual data points, making it impossible to assess variability or replication. Please show all individual data points and clarify n (sample size) per group. Second, the Western blotting is only shown as single replicates. If repeated 2-3 times as stated, quantification and normalization (e.g., pStat3/Stat3, GAPDH loading control) are essential. The full, uncropped blots should be included in the supplementary data.

We thank you for the critical comments. Now we have remade the bar graphs with individual data points, and added the sample size per group if possible. Quantification and/or normalization of the WB data based on at least two replicates were included. The representative uncropped blots have also been loaded as the supplementary data.

(2) The biological significance of the results is not clear. Many reported fold changes (e.g., kdm6b modulation by Stat3 inhibition, sox9a in S3A) are modest (<2-fold), raising concerns about biological relevance. Can the authors define thresholds of functional relevance or confirm phenotypic outcomes in these animals?

We thank you for the inspiring comments. Most of the experiments were transient in nature, for instance, warm temperature treatment of fish for 3-4 days, the fold change of gene expression were modest.

We admit that there are some shortcomings in this work. The major one is lacking of data showing that Trpv4 inhibition/activation,or pStat3 inhibition/activation can cause a gonadal phenotype change, for instance, from ovary to ovotestis or causing females to intersex fish. We only showed that pharmacological or RNAi can lead to change in sex-biased gene expression or affect temperature-induced gene expression, but not gonadal transformation.

In natural population, the sex change of ricefield eel may take several months to one year or even longer. We propose that the magnitude and duration of temperature exposure promote sex change of ricefield eel by driving the accumulation of testicular differentiation genes in sufficient quantities. In experimental condition, to realize the gonadal phenotype change, animals may need to be under repeated pharmaceutical treatment (3 day interval treatment) for longer time to reach a threshold. However, long term treatment significantly increases the death rate of the animals, caused by stress or frequent manipulation.

Inspired by your comment, we are optimizing the experimental conditions in order to cause some phenotypic outcomes, thanks.

(3) The specificity of key antibodies is not validated. Key antibodies (Stat3, pStat3, Foxl2, Amh) were raised against mammalian proteins. Their specificity for ricefield eel proteins is unverified. Validation should include siRNA-mediated knockdown with immunoblot quantification with 3 replicates. Homemade antibodies (Sox9a, Dmrt1) also require rigorous validation.

We thank you for the comments about the specificity of the antibodies. First,when choosing the commercial antibodies, we have compared the immunogen of the animal with the corresponding amino acids of ricefield eel, making sure that it was conserved to some extent (at least> 85% similarity). Second, we have referred the published work, where the antibodies have been proven to work in zebrafish, frogs, and turtles et al. This was true for pStat3 and Stat3 antibodies (Weber et al. 2020; Ge et al., 2024). Third, the specificity for each antibody was assessed using WB, based on the predicted size of the protein and the correct control setting.

For instance, we are very confident for the specificity for Dmrt1 antibody. First, Dmrt1 protein was readily detected in testes of males but barely detected in ovaries of females (Author response image 1). Second, Dmrt1 protein was not detected in ovary of fish at cool temperature, but clearly detected in nuclei of follicles in warm temperature-treated fish (Figure 3C, 4B), in line with our qPCR results. Third, by performing IF, Dmrt1 was not detected in females reared at lower temperature. By contrast, after warm temperature treatment or Trpv4 activation, it was detected in the nuclei in specific cell types but not everywhere (Figure 3E, 6C).

Author response image 1.

Although we have carefully evaluated the antibodies before experiments as described above, in response to your concerns, we went on to validate Amh, Dmrt1, Sox9a, and Stat3 antibodies using the corresponding siRNAs (Author response image 2). The results indicated that the antibodies, although not perfect, can be used in this work, as the expected band was gone or reduced in intensity. The experiments were repeated two times, and shown were representative.

Author response image 2.

(4) Most of the imaging data (immunofluorescence) is inconclusive. Immunofluorescence panels are small and lack monochrome channels, which severely limits interpretability. Larger, better-contrasted images (showing the merge and the monochrome of important channels) and quantification would enhance the clarity of these findings.

We apologize for the poor quality of the IF images. At your suggestion, we have repeated the majority of the IF experiments, and imaging data with better quality were presented in the revised manuscript. Quantification of WB and IF was also included to enhance the clarity. Please see the revised manuscript, Thanks.

(B) Other comments about the science: 

(1) In S3A, sox9a expression is not dose-responsive to Trpv4 modulation, weakening the causal inference.

We have repeated the experiments, and new data was included for the replacement of the old one in the revised manuscript.

(2) An antibody against Kdm6b (if available) should be used to confirm protein-level changes.

We thank you for the nice suggestion. Unfortunately, current commercial antibody for Kdm6b is for mammals, which was not working in ricefield eel. At your suggestion, we are going to make one in future.

In sum, the interpretations are limited by the above concerns regarding data presentation and reagent specificity.

Reviewer #2 (Public review):

Summary:

This study presents valuable findings on the molecular mechanisms driving the female-to-male transformation in the ricefield eel (Monopterus albus) during aging. The authors explore the role of temperature-activated TRPV4 signaling in promoting testicular differentiation, proposing a TRPV4-Ca²⁺-pSTAT3-Kdm6b axis that facilitates this gonadal shift.

We thank you for the encouraging comments. Answering your questions has greatly improved our understanding of Trpv4 function in ricefield eel, and the quality of the manuscript.

Strengths:

The manuscript describes an interesting mechanism potentially underlying sex differentiation in M. albus.

Weaknesses:

The current data are insufficient to fully support the central claims, and the study would benefit from more rigorous experimental approaches.

(1) Overstated Title and Claims:

The title "TRPV4 mediates temperature-induced sex change" overstates the evidence. No histological confirmation of gonadal transformation (e.g., formation of testicular structures) is presented. Conclusions are based solely on molecular markers such as dmrt1 and sox9a, which, although suggestive, are not definitive indicators of functional sex reversal.

We thank you for pointing out this. The title has been changed to “Trpv4 links environmental temperature to testicular differentiation in hermaphroditic ricefield eel.”

(2) Temperature vs Growth Rate Confounding (Figure 1E):<br /> The conclusion that warm temperature directly induces gonadal transformation is confounded by potential growth rate effects. The authors state that body size was "comparable" between 25C and 33C groups, but fail to provide supporting data. In ectotherms, growth is intrinsically temperature-dependent. Given the known correlation between size and sex change in M. albus, growth rate-rather than temperature per se-may underlie the observed sex ratio shifts. Controlled growth-matched comparisons or inclusion of growth rate metrics are needed.

We thank you for the critical comments. We have repeated the experiments, and have carefully compared the body length and weight, and results showed that there is no big difference between 25 and 33 degree groups. Please see Figure S1D-E, and the text in the last paragraph of “Warm temperature promotes gonadal transformation” section in the Results part.

(3) TRPV4 as a Thermosensor-Insufficient Evidence:<br /> The characterisation of TRPV4 as a direct thermosensor lacks biophysical validation. The observed transcriptional upregulation of Trpv4 under heat (Figure 2) reflects downstream responses rather than primary sensor function. Functional thermosensors, including TRPV4, respond to heat via immediate ion channel activity-typically measurable within seconds-not mRNA expression over hours. No patch-clamp or electrophysiological data are provided to confirm TRPV4 activation thresholds in eel gonadal cells.

We thank you for the critical comments. The patch-clamp or electrophysiological experiments require special equipment and well-trained expert, unfortunately, our lab members and nearby collaborators have no experience in performing the kind of experiments. The Trpv4 is a well-known cation channel protein that is activated by moderate heat (> 27 degree). And a body of published work has demonstrated its role in the regulation of Ca²⁺ signals via change its configuration in response to temperature (J Physiol. 2017 Oct 25;595(22):6869–6885. doi: 10.1113/JP275052; Cell Death Dis 11, 1009 (2020). https://doi.org/10.1038/s41419-020-03181-7; Cell Death Dis 10, 497 (2019). https://doi.org/10.1038/s41419-019-1708-9; Cell calcium, https://doi.org/10.1016/j.ceca.2026.103108).

Consistently, warm temperature increased calcium influx within an hour, similar to the Trpv4 agonist treatment (Figure 2E, 5D), and addition of ion channel Trpv4 inhibitor prevents the calcium signals by war temperature treatment. Moreover, calcium signaling activity is closely linked with pStat3 activity and expression of sex-biased genes (Figures 5G, 6F). Although we did not show biophysical data, these results implied that Trpv4 is a thermosensor, and regulate the downstream pathway via the regulation of calcium signals, in line with it functions as an ion channel.

Additionally, the Ca²⁺ imaging assay (Figure 2F) lacks essential details: the timing of GSK1016790A/RN1734 administration relative to imaging is unclear, making it difficult to distinguish direct channel activity from indirect transcriptional effects.

We have added more information for Ca²⁺ imaging assay (now Figure 2E and the corresponding text in Figure 2 legend, in the revised manuscript). In particular, we added the timing of treatment to better show that it was a direct effect.

(4) Cellular Context of TRPV4 Activity Is Unclear:<br /> In situ hybridisation suggests TRPV4 expression shifts from interstitial to somatic domains under heat (Figures. 2H, S2C), implying potential cell-type-specific roles. However, the study does not clarify: (i) whether TRPV4 plays the same role across these cell types, (ii) why somatic cells show stronger signal amplification, or (iii) the cellular composition of explants used in in vitro assays. Without this resolution, conclusions from pharmacological manipulation (e.g., GSK1016790A effects) cannot be definitively linked to specific cell populations.

We thank you for the inspiring comments. We have performed IF experiments using Trpv4 specific antibodies (antibody specificity was confirmed). It was clearly shown that Trpv4 was expressed in a portion of follicle cells. To explore the identity of Trpv4-expressing somatic cells, we have performed double IF experiments using Trpv4 and Foxl2, a granulosa cell marker. The results (Figure 2H) clearly showed that Trpv4-expressing cells are a portion of Foxl2-positive granulosa cells. We propose that Trpv4-expressing granulosa cells may play an important role in sensing the temperature, and that Trpv4-expressing granulosa cells transdifferentiate into Sertoli cells by warm temperature exposure, because Dmrt1, a Sertoli cell marker, started within follicles in a typical granulosa cell location. Unfortunately, current Dmrt1/Trpv4 antibodies are both produced from rabbit. To overcome this, we are ordering mouse Dmrt1 antibodies, and in future we will perform Trpv4/Dmrt1 double IF to show if Dmrt1 positive cells co-localize with Trpv4 expressing cells. We would like to update the results to you once the antibody was available.

As our animal experiments (Figure 2H) have clearly shown the identify of Trpv4 expressing somatic cells, we did not repeat the experiments using explants, to explore the cellular composition of explants used in in vitro assays.

(5) Rapid Trpv4 mRNA Elevation and Channel Function:<br /> The authors report a dramatic increase in Trpv4 mRNA within one day of heat exposure (Figures 4D, S2B). Given that TRPV4 is a membrane channel, not a transcription factor, its rapid transcriptional sensitivity to temperature raises mechanistic questions. This finding, while intriguing, seems more correlational than functional. A clearer explanation of how TRPV4 senses temperature at the molecular level is needed.

We appreciate you for your inspiring comments. Actually, we are also wondering about how trpv4 mRNA was regulated by warm temperature. First of all, the up-regulation of trpv4 mRNA is true, as evidenced by multiple pieces of data using qPCR and ISH experiments. It appears that ovarian cells respond to the temperature changes by increasing calcium influx via Trpv4 ion channel,as well as by increasing trpv4 mRNA expression levels.

Then, how trpv4 mRNA is regulated by heat? It is well-known that gene expression can be regulated by subtle temperature change via some direct temperature sensing genes (Haltenhof et al., 2020). We hypothesized that trpv4 is a downstream target of these thermosensors, displaying a mechanism similar to mammals. Actually, we have performed some experiments, and the preliminary data were obtained, which support our hypothesis.

Because the mechanistic explanation study is undergoing and not published, we chose not to discuss it in detail in the revised manuscript. We wish to report it by the end of this year, and by then are pleased to update you with the progress.

(6) Inconclusive Evidence for the Ca²⁺-pSTAT3-Kdm6b Axis: Although the authors propose a TRPV4-Ca²⁺-pSTAT3-Kdm6b-dmrt1 pathway, intermediate steps remain poorly supported. For example, western blot data (Figures 3C, 4B) do not convincingly demonstrate significant pSTAT3 elevation at 34C. Higher-resolution and properly quantified blots are essential. The inferred signalling cascade is based largely on temporal correlation and pharmacological inhibition, which are insufficient to establish direct regulatory relationships.

We thank you for the critical comments. In response to your concerns, we have repeated experiments, and better resolution WB data with proper quantification were included in the revised manuscript. In particular, we convincingly demonstrate that 34 degree caused significant pStat3 elevation.

To directly establish regulatory relationship of the members, at your suggestion, we provided some genetic and molecular biology data to support our conclusion in the revised manuscript. For instance, we have knockdown the stat3 gene by using siRNAs, and as shown in Figure 6F, we further showed that pStat3 is functionally downstream of Trpv4. Moreover, ChIP and luciferase assays were performed to show that pStat3 directly binds and activate kdm6b (Figure 7B-C). We have also performed various pharmacological inhibition to further strength our conclusion (Figures 6B-E).

(7) Species-Specific STAT3-Kdm6b Regulation Is Unresolved:<br /> The proposed activation of Kdm6b by pSTAT3 contrasts with findings in the red-eared slider turtle (Trachemys scripta), where pSTAT3 represses Kdm6b. This divergence in regulatory direction between the two TSD species is surprising and demands further justification. Cross-species differences in binding motifs or epigenetic context should be explored. Additional evidence, such as luciferase reporter assays (using wild-type and mutant pSTAT3 binding motifs in the Kdm6b promoter) is needed to confirm direct activation.

We thank you for the inspiring comments. At your suggestion, we have performed luciferase assay using kdm6b promotor that is intact or mutated. The results were in favor of our statement. Please see Figure 7C and the related text.

A rescue experiment-testing whether Kdm6b overexpression can compensate for pSTAT3 inhibition-would also greatly strengthen the model.

We thank you for the nice suggestion. It is technically challenging to perform kdm6b overexpression or any Kdm6b gain of function experiments (we have tried to make lentivirus, however, it was not working). There is no Kdm6b-specific agonists.

Inspired by you, we are establishing constitutive kdm6b transgenic ricefield eel. Although it require at least a year to allow the fish to grow up for functional experiments, once it was established, we can directly answer some important questions.

(8) Immunofluorescence-Lack of Structural Markers: <br /> All immunofluorescence images should include structural markers to delineate gonadal boundaries. Furthermore, image descriptions in the figure legends and main text lack detail and should be significantly expanded for clarity.

We thank you for the critical comments. At your comments, we have first performed IF using beta-catenin as structural marker. However, the results were not good for some unknown reasons. Then, we used Vimentin as a structural maker, as it can label all the cells in gonads. Foxl2 was used as granulosa cell marker. Dmrt1 was used as Sertoli cell marker.

Some essential description was added in the figure legend as requested. Please see detail in the revised manuscript.

(9) Pharmacological Reagents-Mechanisms and References: <br /> The manuscript lacks proper references and mechanistic descriptions for the pharmacological agents used (e.g., GSK1016790A, RN1734, Stattic). Established literature on their specificity and usage context should be cited to support their application and interpretation in this study.

These pharmacological agents have been used by others (Ge et al., 2017; Liu et al., 2021; Weber et al., 2020; Wu et al.,2024), and they are properly cited in the manuscript.

(10) Efficiency of Experimental Interventions: <br /> The percentage of gonads exhibiting sex reversal following pharmacological or RNAi treatments should be reported in the Results. This is critical for evaluating the strength and reproducibility of the interventions.

We thank you for the critical and important comments. Actually another reviewer has asked the same question. We admit that this was the big shortcoming of the work, as we did not provide data demonstrating that Trpv4 inhibition/activation, or pStat3 inhibition/activation can cause a gonadal phenotype change, for instance, from ovary to ovotestis or causing sex reversal of fish. We only showed that pharmacological or RNAi can lead to alteration of sex-biased gene expression or affect temperature induced gene expression.

In wild population, the entire sex change of ricefield eel may take months to one year or even longer. We propose that the magnitude and duration of temperature exposure promote sex change of ricefield eel by driving the accumulation of testicular differentiation genes in sufficient quantities. In experimental condition, to realize the gonadal phenotype change, animals may need to be under repeated pharmaceutical treatment (3 day interval treatment) for longer time to reach a threshold, however, long term treatment significantly increases the death rate of the animals, caused by stress or frequent manipulation. Actually, my students have tried the experiments, unfortunately, either the number of sex-versing animals were small or the experiments lacked of repeat. So no percentage of gonadal transformation after treatment can be provided at this time, but we have indicated the number of samples when performing molecular experiments (showing expression of sex-biased genes).

Inspired by your important comment, we are optimizing the experimental conditions in order to cause some phenotypic outcomes. By then, the percentage of gonads exhibiting sex reversal following pharmacological or RNAi treatments can be calculated, showing the biological significance.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Editorial Concerns: 

(1) The term "sex reversal" should be clearly defined upfront as female-to-male, and the developmental consequences (e.g., increase in body size post-transition) should be explicitly stated early in the introduction.

We thank our editorial for pointing out this. We have added those in the introduction Part. It reads “The species begins life as a female and then develops into a male through an intersex stage, thus displaying a female-to-male sex reversal during aging. Females are small in size (< 25 cm), and during and after sex change, there is a gradual increase in body size (> 55 cm for the majority of males).”

Additional information was shown in the first and second paragraph in the results Part.

(2) The manuscript references skewed sex ratios in cultured ricefield eel but fails to specify the direction (e.g., too many males or females). This should be clarified to contextualize the biological and commercial problem. 

According to your suggestion, we now added additional information, and it reads “The reproductive mode of ricefield eel, which leads to much more females than males in spawning season, severely affects the sex ratio, and decreases the productivity of broodstock. Moreover, adult females lay limited eggs (~200) due to its small size.”

(3) Define TSD (temperature-dependent sex determination) upon first use, not at the second mention.

We have checked this, and make sure it was properly done.

(4) The phrase "quality fries for aquaculture" should be reworded or defined; it is unclear to non-specialists.

We thank you for pointing out this. Now it reads “adult females lay limited eggs (~200) due to its small size, which is a limiting factor for massive production of seedling for aquaculture industry”.

(5) Several in-text citations (e.g., Weber 2020, Wu 2024) are absent from the bibliography. ]

We have double checked the reference, thanks.

(6) The inclusion of page and line numbers would facilitate peer review.

We have now shown the page and line.

(7) The discussion is written vaguely. Clarify species names when discussing comparative biology and consider breaking down complex sentences to aid comprehension for a broad audience, such as that of eLife. 

We have added the species name, and try our best to use concise expression. Thanks.

eLife Assessment

This manuscript details important findings that DNA polymerase kappa shows age-related changes in subcellular localization within different cell types in the brains of mice, from the nucleus in young cells to the cytoplasm in old cells. The authors' findings suggest that age-related alterations in POLK localization could drive mechanistic and functional changes in the aging brain. The authors provide solid evidence for their study, with data broadly supporting their claims with minor weaknesses.

Reviewer #1 (Public review):

Summary:

Abdelmageed et al. investigate age-related changes in the subcellular localization of DNA polymerase kappa (POLK) in the brains of mice. POLK has been actively investigated for its role in translesion DNA synthesis and involvement in other DNA repair pathways in proliferating cells, very little is known about POLK in a tissue-specific context or let alone in post-mitotic cells. The authors investigated POLK subcellular distribution in the brains of young, middle-aged, and old mice via immunoblotting of fractioned tissue extracts and immunofluorescence (IF). Immunoblotting revealed a progressive decrease in the abundance of nuclear POLK, while cytoplasmic POLK levels concomitantly increased. Similar findings were present when IF was performed on brain sections. Further IF studies of cingulate cortex (Cg1), motor cortex (M1, M2), and somatosensory (S1) cortical regions all showed an age-related decline in nuclear POLK. Nuclear speckles of POLK decrease in each region, meanwhile the number of cytoplasmic POLK granules decreases in all four regions, but granule size is increasing. The authors report similar findings for REV1, another Y-family DNA polymerase.

The authors then investigate the colocalization of POLK with other DNA damage response (DDR) proteins in either pyramidal neurons or inhibitory interneurons. At 18 months of age, DNA damage marker gH2AX demonstrated colocalization with nuclear POLK, while strong colocalization of POLK and 8-oxo-dG was present in geriatric mice. The authors find that cytoplasmic POLK granules colocalize with stress granule marker G3BP1, suggesting that the accumulated POLK ends up in the lysosome.

Brain regions were further stained to identify POLK patterns in NeuN+ neurons, GABAergic neurons, and other non-neuronal cell types present in the cortex. Microglia associated with pyramidal neurons or inhibitory interneurons were found to have higher abundance of cytoplasmic POLK. The authors also report that POLK localization can be regulated by neuronal activity induced by Kainic acid treatment. Lastly, the authors suggest that POLK could serve as an aging clock for brain tissue, but POLK deserves further characterization and correlation to functional changes before being considered for a biomarker.

Strengths:

Investigation of TLS polymerases in specific tissues and in post-mitotic cells is largely understudied. The potential changes in sub cellular localization of POLK and potentially other TLS polymerases opens up many questions about DNA repair and damage tolerance in the brain and how it can change with age.

Weaknesses:

The work is quite novel and interesting, and the authors do suggest some potentially interesting roles for POLK in the brain, but these are in of themselves a bit speculative. The majority of the findings of this paper draw upon findings from POLK antibody and its presumed specificity for POLK. However, this antibody has not been fully validated and would benefit from further validation of the different band sizes. More mechanistic investigation is needed before POLK could be considered as a brain aging clock but does not preclude the potential for using POLK as a biological "dating" system for the brain.

Comments on revisions:

The revised manuscript is suitably improved and addresses reviewer comments.

Reviewer #2 (Public review):

Summary:

Abdelmageed et al., demonstrate POLK expression in nervous tissue and focus mainly on neurons. Here, they describe an exciting age-dependent change in POLK subcellular localization, from the nucleus in young tissue to the cytoplasm in old tissue. They argue that the cytosolic POLK associates with stress granules. They also investigate cell-type specific expression of POLK, and quantitate expression changes induced by cell autonomous (activity) and cell nonautonomous (microglia) factors.

Comments on revisions:

Do the authors have any explanation or reason for why they weren't able to achieve a higher knockdown of POLK using siRNA in Figure 1A2? It does not seem statistically different by eye, as all values in the KD overlap with the control. This does not seem like strong evidence that their antibody works.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

Abdelmageed et al. investigate age-related changes in the subcellular localization of DNA polymerase kappa (POLK) in the brains of mice. POLK has been actively investigated for its role in translesion DNA synthesis and involvement in other DNA repair pathways in proliferating cells, very little is known about POLK in a tissue-specific context, let alone in post-mitotic cells. The authors investigated POLK subcellular distribution in the brains of young, middle-aged, and old mice via immunoblotting of fractioned tissue extracts and immunofluorescence (IF). Immunoblotting revealed a progressive decrease in the abundance of nuclear POLK, while cytoplasmic POLK levels concomitantly increased. Similar findings were present when IF was performed on brain sections. Further, IF studies of the cingulate cortex (Cg1), the motor cortex (M1, M2), and the somatosensory (S1) cortical regions all showed an age-related decline in nuclear POLK. Nuclear speckles of POLK decrease in each region, meanwhile, the number of cytoplasmic POLK granules decreases in all four regions, but granule size is increasing. The authors report similar findings for REV1, another Y-family DNA polymerase.

The authors then investigate the colocalization of POLK with other DNA damage response (DDR) proteins in either pyramidal neurons or inhibitory interneurons. At 18 months of age, DNA damage marker gH2AX demonstrated colocalization with nuclear POLK, while strong colocalization of POLK and 8-oxo-dG was present in geriatric mice. The authors find that cytoplasmic POLK granules colocalize with stress granule marker G3BP1, suggesting that the accumulated POLK ends up in the lysosome.

Brain regions were further stained to identify POLK patterns in NeuN+ neurons, GABAergic neurons, and other non-neuronal cell types present in the cortex. Microglia associated with pyramidal neurons or inhibitory interneurons were found to have a higher abundance of cytoplasmic POLK. The authors also report that POLK localization can be regulated by neuronal activity induced by Kainic acid treatment. Lastly, the authors suggest that POLK could serve as an aging clock for brain tissue, but POLK deserves further characterization and correlation to functional changes before being considered as a biomarker.

Strengths:

Investigation of TLS polymerases in specific tissues and in post-mitotic cells is largely understudied. The potential changes in sub-cellular localization of POLK and potentially other TLS polymerases open up many questions about DNA repair and damage tolerance in the brain and how it can change with age.

Weaknesses:

The work is quite novel and interesting, and the authors do suggest some potentially interesting roles for POLK in the brain, but these are in and of themselves a bit speculative. The majority of the findings of this paper draw upon findings from POLK antibody and its presumed specificity for POLK. However, this antibody has not been fully validated and needs further work. Further validation experiments using Polk-deficient or knocked-down cells to investigate antibody specificity for both immunoblotting and immunofluorescence should be performed. More mechanistic investigation is needed before POLK could be considered as a brain aging clock.

We are thankful for the overall enthusiasm and positive comments.

(a) Concern over POLK antibody characterization in mouse:

We performed siRNA and shRNA knock downs in mouse primary cortical neurons as well as efficiently transfectable murine lines like 4T1 and Neuro-2A showing knock down of 99kDa and 120kDa bands recognized by sc-166667 anti-POLK antibody (exact figure number Figure 1 and S1). We show that in IF sc-166667 and A12052 (Figure S1G) shows similar immunostaining patterns and we used sc-166667 in all reported figures and western blots.

(b) More mechanistic investigation is needed before POLK could be considered as a brain aging clock:

We sincerely appreciate the valuable suggestion. We agree as a terminal assay POLK nucleo-cytoplasmic status is not practical for longitudinal studies. However, we believe it may serve an investigative/correlative endogenous signal for determining tissue age, that may be useful to "date" brain sections, since not many such cell biological markers exist. We have added clarification texts to address this.

Reviewer #2 (Public review):

Summary:

Abdelmageed et al., demonstrate POLK expression in nervous tissue and focus mainly on neurons. Here they describe an exciting age-dependent change in POLK subcellular localization, from the nucleus in young tissue to the cytoplasm in old tissue. They argue that the cytosolic POLK is associated with stress granules. They also investigate the cell-type specific expression of POLK, and quantitate expression changes induced by cell-autonomous (activity) and cell nonautonomous (microglia) factors.

I think it is an interesting report but requires a few more experiments to support their findings in the latter half of the paper. Additionally, a more mechanistic understanding of the pathways regulating POLK dynamics between the nucleus and cytosol, what is POLK doing in the cytosol, and what is it interacting with; would greatly increase the impact of this report. However, additional mechanistic experiments are mostly not needed to support much of the currently presented results, again, it would simply increase the impact.

(a) Concern on more mechanistic understanding of the pathways regulating POLK dynamics between the nucleus and cytosol:

We sincerely appreciate the reviewer’s enthusiasm and valuable guidance in helping us better understand the mechanism of nuclear-cytoplasmic POLK dynamics. Previously, we developed a modified aniPOND (accelerated native isolation of proteins on nascent DNA) protocol, which we termed iPoKD-MS (isolation of proteins on Pol kappa synthesized DNA followed by mass spectrometry), to capture proteins bound to nascent DNA synthesized by POLK in human cell lines (bioRxiv https://www.biorxiv.org/content/10.1101/2022.10.27.513845v3). In this dataset, we identified potential candidates that may regulate nuclear/cytoplasmic POLK dynamics. These candidates are currently undergoing validation in human cell lines, and we are preparing a manuscript on these findings. Among these, some candidates, including previously identified proteins such as exportin and importin (Temprine et al., 2020, PMID: 32345725), are being explored further as potential POLK nuclear/cytoplasmic shuttles. We are also conducting tests on these candidates in mouse cortical primary neurons to assess their role in POLK dynamics. In the revised version of the manuscript, we have included a discussion of our current understanding.

(b) Question on “… what is POLK doing in the cytosol, and what is it interacting with …”: Our data so far indicate that POLK accumulates in stress granules and lysosomes. We are very grateful for the reviewer’s insightful suggestions and will make every effort to incorporate them in the revised manuscript. We characterized POLK accumulation in the cytoplasm using six additional endo-lysosomal markers, as recommended by the reviewer. This data is now part of entirely new Figure 3.

Reviewer #3 (Public review):

Summary:

In this study, the authors show that DNA polymerase kappa POLK relocalizes in the cytoplasm as granules with age in mice. The reduction of nuclear POLK in old brains is congruent with an increase in DNA damage markers. The cytoplasmic granules colocalize with stress granules and endo-lysosome. The study proposes that protein localization of POLK could be used to determine the biological age of brain tissue sections.

Strengths:

Very few studies focus on the POLK protein in the peripheral nervous system (PNS). The microscopy approach used here is also very relevant: it allows the authors to highlight a radical change in POLK localization (nuclear versus cytoplasmic) depending on the age of the neurons. 

The conclusions of the study are strong. Several types of neurons are compared, the colocalization with several proteins from the NHEJ and BER repair pathways is tested, and microscopy images are systematically quantified.

Weaknesses:

The authors do not discuss the physical nature of POLK granules. There is a large field of research dedicated to the nature and function of condensates: in particular numerous studies have shown that some condensates but not all exhibit liquid-like properties (https://www.nature.com/articles/nrm.2017.7, https://pubmed.ncbi.nlm.nih.gov/33510441/ https://www.mdpi.com/2073-4425/13/10/1846). The change of physical properties of condensates is particularly important in cells undergoing stress and during aging. The authors should discuss this literature.

We highly appreciate the reviewer bringing up the context of biomolecular condensates. Our iPoKD-MS data referenced above suggests candidates from various biomolecular condensates that we are currently investigating. We appreciate the reviewer providing important literature cited these articles in text and potential biomolecular condensates are discussed in the revised version. 

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The work is quite novel and interesting, and the authors do suggest some potentially interesting roles for POLK in the brain, but these are in of themselves a bit speculative. The majority of the findings of this paper rely upon the POLK antibody and its specificity for POLK, which is not fully characterized and needs further work (validation of antibodies using immunoblots of Polk KO cells or siRNA KD of POLK in murine cells) to provide confidence in the authors' findings. 

Points

siRNA knockdown of Polk in primary neurons showed a dramatic reduction in signal by IF even though qPCR analysis showed a reduction of only ~35% at the transcript level. Typically many DNA repair genes need to be knocked down by 80% or more to see discernable differences at the protein level. siRNA knockdown in a murine cell line (MEFs, neurons, or some other easily transfectable cell type) needs to be performed with immunoblotting with whole cell and fractionated (nuclear/cytoplasmic) lysates in order to better validate the anti-POLK antibodies and which bands that are visualized during immunoblotting are specific to POLK.

We performed siRNA and shRNA knock downs in mouse primary cortical neurons as well as efficiently transfectable murine lines like 4T1 and Neuro-2A showing knock down of 99kDa and 120kDa bands recognized by sc-166667 anti-POLK antibody (exact figure number Figure 1 and S1). We show that in IF sc-166667 and A12052 (Figure S1G) shows similar immunostaining patterns and we used sc-166667 in all reported figures and western blots.

Figure 1B and C, it is not clear which antibody(ies) are used for the immunoblotting of nuclear and cytoplasmic fractions and for a blot with whole tissue lysates. Please place the antibody vendor or clone next to the corresponding blot or describe it in the figure legend. Bands of varying sizes are present in 1B (and Figure S1) but only a band at 99 kDa was shown in 1C. Because there are no bands of equivalent size present in the nuclear and cytoplasmic fractions in Figure 1B, please describe or denote which bands were used for quantification purposes for nuclear and cytoplasmic POLK.

This has been clarified by using only one antibody throughout the manuscript sc-166667. We observed in whole cell lysate an intense ~99kDa and a faint ~120kDa band, which gets intense in nuclear fraction and is absent in cytoplasmic fraction. We have noted this in multiple human cell lines and hiPSC-derived neurons, which is our ongoing work. We do not know yet if the ~120kDa is a modification or isoform of POLK. We have hints from our proteomics data that it may be SUMOylated or ubiquitinylated or other post translational modifications. We added this in the discussion section.

Figure 1I, is there a quantification beyond just the representative image? There is no green staining pattern outside the cytoplasm in the 1-month-old M1 images that is present in all the other images in the panel.

Fig 1I is now Fig S1G in the revised manuscript. Since REV1 and POLH were not central to the study that focused on POLK, they were meant to be exploratory data panels and as such we did not quantify beyond the qualitative evaluation, which broadly resembled POLK’s disposition with age. We have noted there are some sample to sample variability in the background signal. In general, outside the cytoplasm as subcellularly segmented by fluorescent nissl expression, tends to be variable by brain areas but also higher in older brains

"Association with PRKDC further suggests POLK's role in the "gap-filling" step in the NHEJ repair pathway in neurons." There is no strong evidence in the literature for mammalian POLK playing a role in NHEJ. Some description of a role in HR has been described, however. The reference regarding the iPoKD-MS data set that provides evidence of POLK associating with BER and NHEJ factors is listed as Paul, 2022 but is in the reference list as Shilpi Paul 2022.

We removed this speculative statement and citation fixed.

Figure 4A, what is the age of the mouse for the representative images?

19 months and now mentioned in the figure legend

Figure 4C, Could the data from the different ages be plotted side by side to better evaluate the differences for each cell type/region?

Data is plotted side by side

Why was the one-month time point chosen as this could still represent the developing and not mature murine brain? 

Reviewer correctly noted that a 1 month brain is still developing, but mostly from the behavioral and circuit maturation standpoint. However, from cell division and neurogenesis perspective, that is considered to be complete by first postnatal month, with neuron production thereafter largely restricted to specialized adult niches in the dentate gyrus and subventricular zone–olfactory bulb pathway; these adult neurogenic stem cells are embryonically derived and are regulated in ways that are distinct from the early, expansionary developmental waves of neurogenesis. In our study we performed our measurements in the cortical areas only. (Caviness et al., 1995, PMID: 7482802; Ansorg et al., 2012, PMID: 22564330; Ming & Song, 2011, PMID: 21609825; Bond et al., 2015, PMID: 26431181; Bond et al., 2021, PMID: 33706926; Bartkowska et al., 2022, PMID: 36078144). Also, in Figure 6A it was incorrectly mentioned to be just 1month, we rechecked our metadata and noted that young brains were comprised of 1 and 2 month old brains and now it has been corrected.

Furthermore, can the authors describe which sex of mice was used in these experiments and the justification if a single sex was used? If both sexes were used, were there any dimorphic differences in POLK localization patterns?

This is an important aspect, but in the beginning to keep mice numbers within manageable limits, we were focusing more on the age component. While both males and female brains were assayed but due to uneven sample distribution between sexes, we could not estimate if there were any statistically significant sexual dimorphic differences in IN, PN and NNs. Future studies will investigate the sex component as a function of age.

The suggestion of POLK as a brain aging clock may be a bit premature as the functional and behavioral consequences of cytoplasmic POLK sequestration are not fully known. Furthermore, investigation of POLK levels in other genetic models of neurodegeneration or with gerotherapeutics would be needed to establish if the POLK brain clock is responsive to changes that shift brain aging. Lastly, this clock may be impractical and not useful for longitudinal studies due to the terminal nature of assessing POLK levels.

We agree as a terminal assay POLK nucleo-cytoplasmic status is not practical for longitudinal studies. However, we believe it may serve an investigative/correlative endogenous signal for determining tissue age, that may be useful to "date" brain sections, since not many such cell biological markers exist. We have added clarification text.

Some discussion of the Polk-null mice is warranted, as they only have a slightly shortened lifespan, and any disease phenotypes were not reported. This stands in contrast to other DNA repair-deficient mice that mimic premature aging and show behavioral and motor deficits. This calls into question the role of POLK in brain aging.

Discussion statements on Polk-null mice has been added.

Please correct the catalog number for the SCBT anti-POLK antibody to sc-166667

Typographical error has been corrected

Reviewer #2 (Recommendations for the authors):

Results:

Figure by figure 

(1) A progressive age-associated shift in subcellular localization of POLK The authors state that POLK has not been studied in nervous tissue before and they want to see if it is expressed, and if it changes subcellular location as a function of age. The authors argue age = stress like that seen in previous models using genotoxic agents and cancer cells. Indeed, POLK seems to convincingly change subcellular location from the nucleus to larger cytosolic puncta. 

(2) Nuclear POLK co-localizes with DNA damage response and repair proteins This was a difficult dataset for me to decipher. To me, it appears as though POLK colocalizes with these examined proteins in the CYTOSOL, not the nucleus. Especially, in the oldest mice.

We added in the discussion that DNA repair proteins were observed to be present in the cytoplasm and biomolecular condensates citing relevant reviews and primary references.

(3) POLK in the cytoplasm is associated with stress granules and lysosomes in old brains LAMP1 has some issues as a lysosome marker. The authors even state it can be on endosomes. It would be nice to use a marker for mature lysosomes, some fluorescent reporter that is activated only by lysosomal proteases or pH. It is also of interest if POLK is localized to the membrane or the inside of these structures. The authors have access to an airyscan which is sufficient to examine luminal vs membrane localization on larger organelles like lysosomes.

We thank the reviewer for pushing us to investigate the nature of cytoplasmic POLK in endo-lysosomal compartments. We have now added a full-page figure on the cell biological results from six different markers, subset (Cathepsin B and D) are known to present in the lumens of endo-lysosomes, in Figure 3. Further high-resolution membrane vs lumen was not pursued, which is perhaps better suited in cultured neurons rather than thick fixed tissues.

(4) Differentially altered POLK subcellular expression amongst excitatory, inhibitory, and nonneuronal cells in the cortex.

This seems fine. I don't see anything wrong with the author's statement that there is more POLK in neurons vs non-neuronal cells. 

(5) Microglia associated with IN and PN have significantly higher levels of cytoplasmic POLK I don't see really any convincing evidence of the author's claim here. They find a difference at early-old age, but not at old-old, or other ages. This is explained by "However, this effect is lost in late-old age (Figure 5D), likely due to the MG-mediated removal of the INs.". But no trend being observed, no experiment to show sufficiency, and no experiment to uncover a directional relationship; this is a tough claim to stand by.

Changes made in text to reflect speculative nature of this observation

(6) Subcellular localization of POLK is regulated by neuronal activity

Interesting and fairly difficult experiment. Can the authors talk more about what these values mean? I am confused as to why there is a decline in nuclear puncta at 80 min. Also, why are POLK counts in 6c similar at baseline between young and early-old? In Figures 5 and 6 I also worry about statistical analysis. Are all assumptions checked to use t-tests? Why not always use a test that has fewer assumptions?

We have explained in the text the artificial nature of few hour long acute slice preparations is very different and inherently a stressful environment, especially for the old brains, compared to the vascular perfused PFA fixed brain tissues tested between young and old ages.

We don’t have a proper explanation for the initial dip in nuclear puncta in both young and old brains at 80min of very similar magnitude. It could be a separate biological phenomenon that occurs at much shorter time scales that would not otherwise be captured in a fixed tissue assay and needs careful investigation using live tissue fluorescence imaging that is beyond the scope of this manuscript.

We apologize for the typographical error in the figure legend. We rechecked our R code and the tests were all Wilcoxon rank-sum (Mann–Whitney U) two-sided nonparametric.

Figure 6B & E had absurdly small p values due to large sample numbers. So, we implemented random sampling of 100 cells repeating for 200 times and presented the distribution of p values and Cohen’s d in the supplement and reported the median p value and Cohen’s in the main plot.

(7) POLK as an endogenous "aging clock" for brain tissue

Trainable model. What are the criteria for the model, and how does it work? The cutoffs it uses to classify each age group might be interesting in that the model may have identified a trait the researchers were unaware of. Otherwise, it is not especially useful. Maybe as an independent 'blind' analysis of the data?

We have added a better description of the models, assumptions and how two different unsupervised approaches converge on the same set of features with high AUROCs.

Minor questions:

The cartoons (1a, 2a-b, 5a, 6a) help a lot. However, I still had to work a bit to understand some of the graphs (e.g., 5d, 6b-e, fig 7). Is there a simpler way to present them? Maybe simply additional labelling? I'm not sure.

A more thorough discussion of statistical tests is warranted I think. I am not very clear why some were chosen (t-test vs nonparametric with fewer assumptions). Infinitesimally small p values also make me think maybe incorrect tests were done or no power analysis was performed beforehand. A fix for this is just discussing what went into the testing methods and why they were chosen.

Statistical analysis for Fig2 (using Generalized Estimating Equations), and Fig6 (with random repeated subsampling; method explained in text, figure legend updated and supplementary data on the distribution of p values and cohen’s d are added) to address the very small p values. Descriptions rewritten in relevant text.

In the absence of further mechanistic experiments, it would still be interesting to hear what the authors think is going on and what the significance of this altered subcellular location means. How do the authors think this is occurring? I think they are arguing that cytosolic localization of POLK is 100% detrimental to the neuron. ("The reduction of nuclear POLK in old brains is congruent with an increase in DNA damage markers") Do they have any idea what the 'bug' is in the POLK system then?

Statements in the discussion has been added.

Reviewer #3 (Recommendations for the authors):

POLK is detected as small " as small "speckles" inside the nucleus at a young age (1-2 months) and larger "granules" can be seen in the cytoplasm at progressively older time points (>9 months). In the nucleus, is POLK bound to DNA? In the cytoplasm, how are the POLK molecules organized: are they bound to a substrate or are they just organized as a proteins condensate without DNA?

In human U2OS cell line Dnase1 treatment leads to loss of POLK from the nucleus as well as its activity as reported in Fig5 of Paul, S. et. al. 2023 bioRxiv. While we haven’t reproduced these results in mouse primary neurons, we anticipate a similar situation which will be tested in the future. We have addressed limited aspects of the POLK in the cytoplasm in all new Fig3 with six endo-lysosomal markers, and added text.

When POLK proteins accumulate in the cytoplasm in aging cells, do they also repair condensates in the cytoplasm? What is the function of cytoplasmic POLK granules? More generally, is it known if other granules or foci, such as repair foci are found in the cytoplasms in aging cells, or in cells under stress?

Six markers for endo-lysosomes were tested to characterize the cytoplasmic granules now shown in Fig3.

While the authors quantify the number and sizes of the POLK signal, they don't discuss their physical nature. Some membrane-less condensates exhibit liquid-like properties, such as stress granules, P-bodies, or in the nucleus some repair condensates. In some diseased tissues, some condensates lose their liquid properties and become solid-like. Is it known if POLK condensates behave like liquid condensates or they are simply formed by bound molecules on DNA? Since they are larger and fewer in the cytoplasm, is it because several small puncta fused together to form a larger one? It would be worthwhile to discuss these points.

Discussion statements on the nature of condensates in context of the POLK cytoplasmic signal has been added.

eLife Assessment

This structural biology study provides insights into the assembly of the GID/CTLH E3 ligase complex. The multi-subunit complex forms unique, ring shaped assemblies and the findings presented here describe a "specificity code" regulates formation of subunit interfaces. The data supporting the conclusions are convincing, both in thoroughness and rigor. This study will be valuable to biochemists, structural biologists, and could lay foundation for novel designed protein assemblies.

Reviewer #1 (Public review):

Summary:

GID/CTLH-type RING ligases are huge multi-protein complexes that play an important role in protein ubiquitylation. The subunits of its core complex are distinct and form a defined structural arrangement, but there can be variations in subunit composition, such as exchange of RanBP9 and RanBP10. In this study, van gen Hassend and Schindelin provide new crystal structures of (parts of) key subunits and use those structures to elucidate the molecular details of the pairwise binding between those subunits. They identify key residues that mediate binding partner specificity. Using in vitro binding assays with purified protein, they show that altering those residues can switch specificity to a different binding partner.

Strengths:

This is a technically demanding study that sheds light on an interesting structural biology problem in residue-level detail. The combination of crystallization, structural modeling, and binding assays with purified mutant proteins is elegant and, in my eyes, convincing.

Weaknesses:

I mainly have some suggestions for further clarification, especially for a broad audience beyond the structural biology community.

(1) The authors establish what they call an 'engineering toolkit' for the controlled assembly of alternative compositions of the GID complex. The mutagenesis results are great for the specific questions asked in this manuscript. It would be great if they could elaborate on the more general significance of this 'toolkit' - is there anything from a technical point of view that can be generalized? Is there a biological interest in altering the ring composition for functional studies?

(2) Along the same lines, the mutagenesis required to rewire Twa1 binding was very complex (8 mutations). While this is impressive work, the 'big picture conclusion' from this part is not as clear as for the simpler RanBP9/10. It would be great if the authors could provide more context as to what this is useful for (e.g., potential for in vivo or in vitro functional studies, maybe even with clinical significance?)

(3) For many new crystal structures, the authors used truncated, fused, or otherwise modified versions of the proteins for technical reasons. It would be helpful if the authors could provide reasoning why those modifications are unlikely to change the conclusions of those experiments compared to the full-length proteins (which are challenging to work with for technical reasons). For instance, could the authors use folding prediction (AlphaFold) that incorporates information of their resolved structures and predicts the impact of the omitted parts of the proteins? The authors used AlphaFold for some aspects of the study, which could be expanded.

Reviewer #2 (Public review):

Summary:

This is a very interesting study focusing on a remarkable oligomerization domain, the LisH-CTLH-CRA module. The module is found in a diverse set of proteins across evolution. The present manuscript focuses on the extraordinary elaboration of this domain in GID/CTLH RING E3 ubiquitin ligases, which assemble into a gigantic, highly ordered, oval-shaped megadalton complex with strict subunit specificity. The arrangement of LisH-CTLH-CRA modules from several distinct subunits is required to form the oval on the outside of the assembly, allowing functional entities to recruit and modify substrates in the center. Although previous structures had shown that data revealed that CTLH-CRA dimerization interfaces share a conserved helical architecture, the molecular rules that govern subunit pairing have not been explored. This was a daunting task in protein biochemistry that was achieved in the present study, which defines this "assembly specificity code" at the structural and residue-specific level.

The authors used X-ray crystallography to solve high-resolution structures of mammalian CTLH-CRA domains, including RANBP9, RANBP10, TWA1, MAEA, and the heterodimeric complex between RANBP9 and MKLN. They further examined and characterized assemblies by quantitative methods (ITC and SEC-MALS) and qualitatively using nondenaturing gels. Some of their ITC measurements were particularly clever and involved competitive titrations and titrations of varying partners depending on protein behavior. The experiments allowed the authors to discover that affinities for interactions between partners is exceptionally tight, in the pM-nM range, and to distill the basis for specificity while also inferring that additional interactions beyond the LisH-CTLH-CRA modules likely also contribute to stability. Beyond discovering how the native pairings are achieved, the authors were able to use this new structural knowledge to reengineer interfaces to achieve different preferred partnerings.

Strengths:

Nearly everything about this work is exceptionally strong.

(1) The question is interesting for the native complexes, and even beyond that, has potential implications for the design of novel molecular machines.

(2) The experimental data and analyses are quantitative, rigorous, and thorough.

(3) The paper is a great read - scholarly and really interesting.

(4) The figures are exceptional in every possible way. They present very complex and intricate interactions with exquisite clarity. The authors are to be commended for outstanding use of color and color-coding throughout the study, including in cartoons to help track what was studied in what experiments. And the figures are also outstanding aesthetically.

Weaknesses:

There are no major weaknesses of note, but I can make a few recommendations for editing the text.

Reviewer #3 (Public review):

Summary:

Protein complexes, like the GID/CTLH-type E3 ligase, adopt a complex three-dimensional structure, which is of functional importance. Several domains are known to be involved in shaping the complexes. Structural information based on cryo-EM is available, but its resolution does not always provide detailed information on protein-protein interactions. The work by van gen Hassend and Schindelin provides additional structural data based on crystal structures.

Strengths:

The work is solid and very carefully performed. It provides high-resolution insights into the domain architecture, which helps to understand the protein-protein interactions on a detailed molecular level. They also include mutant data and can thereby draw conclusions on the specificity of the domain interactions. These data are probably very helpful for others who work on a functional level with protein complexes containing these domains.

Weaknesses:

The manuscript contains a lot of useful, very detailed information. This information is likely very helpful to investigate functional and regulatory aspects of the protein complexes, whose assembly relies on the LisH-CTLH-CRA modules. However, this goes beyond the scope of this manuscript.

eLife Assessment

This important study provides mechanistic evidence that tea-adapted two-spotted spider mite overcomes green tea catechin defenses via the horizontally transferred dioxygenase TkDOG15, supporting a two-step adaptation model, combining enzyme refinement and inducible upregulation. The evidence is convincing because multi-omics signals converge with functional validation (RNAi knockdown and recombinant enzyme assays) and well-controlled behavioral/toxicity assays to link TkDOG15 activity and expression to survival and feeding on tea.

Reviewer #1 (Public review):

Summary:

This study investigates the molecular mechanisms allowing the KSM mite to infest tea plants, a host that is toxic to the closely related TSSM mite due to high concentrations of phenolic catechins. The authors utilize a comparative approach involving tea-adapted KSM, non-adapted KSM, and TSSM to assess behavioral avoidance and physiological tolerance to catechins. The main finding is that tea-adapted KSM possesses a specific detoxification mechanism mediated by an enzyme, TkDOG15, which was acquired via horizontal gene transfer. The study demonstrates that adaptation is a two-step process: (1) structural refinement of the TkDOG15 enzyme through amino acid substitutions that enhance enzymatic efficiency against catechins, and (2) significant transcriptional upregulation of this gene in response to tea feeding. This enzymatic adaptation allows the mites to cleave and detoxify tea catechins, enabling survival on a toxic host plant.

Strengths:

A multiomics approach (transcriptomics and proteomics) provided a compelling cross-validation of its findings. Functional bioassays, such as RNAi and recombinant enzyme assays, demonstrated that the adapted mite has higher activity against catechins via TkDOG15. Other methodologies, like feeding assay using a parafilm-covered leaf disc, were effective in avoiding contact chemosensation.

Weaknesses:

Although TkDOG15 is assumed to "detoxify" catechins by ring cleavage, the study doesn't identify or characterize the breakdown metabolic products. If the metabolites are indeed non-toxic compared to the parent catechins, that would strengthen the detoxification hypothesis. Also, the transcriptomic and proteomic analyses identified other potential detoxification enzymes, such as CCEs, UGTs, and ABC (Supplementary Tables 3-1 & 3-2), which were also upregulated. The manuscript focuses almost exclusively on TkDOG15, potentially overlooking a multigenic adaptation mechanism, where these other enzymes might play synergistic roles, although it was mentioned in the discussion section.

Reviewer #2 (Public review):

Summary:

The fascinating topic of the host range of arthropods, including insects, and the detoxification of host secondary metabolites has been elucidated through studies of the host specificity of two closely related species. The discovery that key genes were acquired from fungi through horizontal gene transfer (HGT) is particularly significant.

Strengths:

(1) The discovery that the TkDOG15 enzyme, acquired through HGT from fungi, plays a key role in the detoxification of green tea catechins in the Kanzawa mite, revealing a new mechanism of plant-herbivore interactions, is highly encouraging.

(2) The verification of this finding through various experiments, including behavioral, toxicological, transcriptomic, and proteomic analyses, RNAi-based gene function analysis, and recombinant enzyme activity assays, is also highly commendable.

(3) By proposing a two-step model in which amino acid substitutions and expression regulation of a specific enzyme gene (TkDOG15) enable host adaptive evolution, this study contributes significantly to our understanding of the evolutionary mechanisms of speciation and plant defense overcoming.

Weaknesses:

While transcriptome/proteome analyses reported changes in the expression of other detoxification-related enzymes, including CCEs, UGTs, ABC transporters, DOG1, DOG4, and DOG7, it is regrettable that the contribution of each enzyme, including its interaction with TkDOG15 and the functional analysis of each enzyme within the overall catechin detoxification system, was not investigated.

eLife Assessment

This convincing study examines a novel interaction of RAB5 with VPS34 complex II. Structural data are combined with site-directed mutagenesis, sequence analysis, biochemistry, yeast mutant analysis, and prior data on RAB1-VPS34 and RAB5-VPS34 interactions to provide a new perspective on how RAB GTPases recruit related but distinct VPS34 complexes to different organelles. Although minor revisions are recommended, the judgment is that this work represents a fundamental advance in our understanding of VPS34 localization and regulation.

Reviewer #1 (Public review):

Summary:

This manuscript presents high-resolution cryoEM structures of VPS34-complex II bound to Rab5A at 3.2A resolution. The Williams group previously reported the structure of VPS34 complex II bound to Rab5A on liposomes using tomography, and therefore, the previous structure, although very informative, was at lower resolution.

The first new structure they present is of the 'REIE>AAAA' mutant complex bound to RAB5A. The structure resembles the previously determined one, except that an additional molecule of RAB5A was observed bound to the complex in a new position, interacting with the solenoid of VPS15.

Although this second binding site exhibited reduced occupancy of RAB5A in the structure, the authors determined an additional structure in which the primary binding site was mutated to prevent RAB5A binding ('REIE>ERIR'). In this structure, there is no RAB5A bound to the primary binding site on VPS34, but the RAB5A bound to VPS15 now has strong density. The authors note that the way in which RAB5A interacts with each site is distinct, though both interfaces involve the switch regions. The authors confirm the location of this additional binding site using HDX-MS.

The authors then determine multiple structures of the wild-type complex bound to RAB5A from a single sample, as they use 3D classifications to separate out versions of the complex bound to 0, 1, or 2 copies of RAB5A. Overall, the structure of VPS34-Complex II does not change between the different states, and the data indicate that both RAB5A binding sites can be occupied at the same time.

The authors then design a new mutant form of the complex (SHMIT>DDMIE) that is expected to disrupt the interaction at the secondary site between VPS15 and RAB5A. This mutation had a minor impact on the Kd for RAB5A binding, but when combined with the REIE>ERIR mutation of the primary binding site, RAB5A binding to the complex was abolished.

Comparison of sequences across species indicated that the RAB5A binding site on VPS15 was conserved in yeast, while the RAB5A binding site on VPS34 is not.

The authors tested the impact of a corresponding yeast Vps15 mutation (SHLITY>DDLIEY) predicted to disrupt interaction with yeast Rab5/Vps21, and found that this mutant Vps15 protein was mislocalized and caused defective CPY processing.

The authors then compare these structures of the RAB5A-class II complex to recently published structures from the Hurley group of the RAB1A-class I complex, and find that in both complexes the Rab protein is bound to the VPS34 binding site in a somewhat similar manner. However, a key difference is that the position of VPS34 is slightly different in the two complexes because of the unique ATL14L and UVRAG subunits in the class I and class II complexes, respectively. This difference creates a different RAB binding pocket that explains the difference in RAB specificity between the two complexes.

Finally, the higher resolution structures enable the authors to now model portions of BECLIN1 and UVRAG that were not previously modeled in the cryoET structure.

Strengths:

Overall, I found this to be an interesting and comprehensive study of the structural basis for the interaction of RAB5A with VPS34-complex II. The authors have performed experiments to validate their structural interpretations, and they present a clear and thorough comparative analysis of the Rab binding sites in the two different VPS34 complexes. The result is a much better understanding of how two different Rab GTPases specifically recruit two different, but highly similar complexes to the membrane surface.

Weaknesses:

No significant weaknesses were noted.

Reviewer #2 (Public review):

The work by Spokaite et al describes the discovery of a novel Rab5 binding site present in complex II of class III PI3K using a combination of HDX and Cryo EM. Extensive mutational and sequence analysis define this as the primordial Rab5 interface. The data presented are convincing that this is indeed a biologically relevant interface, and is important in defining mechanistically how VPS34 complexes are regulated.

This paper is a very nice expansion of their previous cryo-ET work from 2021, and is an excellent companion piece on high-resolution cryo-EM of the complex I class III complex bound to Rab1 from the Hurley lab in 2025. Overall, this work is of excellent technical quality and answers important unexplained observations on some unexpected mutational analysis from the previous work.

They used their increased affinity VPS34 mutant to determine the 3.2 ang structure of Rab5 bound to VPS34-CII. Clear density was seen for the original Rab5 interface, but an additional site was observed. Based on this structure, they mutated out the VPS34 interface, allowing for a high-resolution structure of the Rab5 bound at the VPS15 interface.

They extensively validated the VPS15 interface in the yeast variant of VPS34, showing that the Vp215-Rab5 (VPS21) interface identified is critical in controlling complex II VPS34 recruitment.

The major strengths of this paper are that the experiments appear to be done carefully and rigorously, and I have very few experimental suggestions.

Here is what I recommend based on some very minor weaknesses I observed

(1) My main concern has to do a little bit with presentation. My main issue is how the authors use mutant description. They clearly indicate the mutant sequence in the human isoform (for example, see Figure 2A, VPS15 described as 579-SHMIT-583>DDMIE); however, when they shift to the yeast version, they shift to saying VPS15 mutant, but don't define the mutant, Figure 2G). I would recommend they just include the same sequence numbering and WT to mutant replacement every time a new mutant (or species) is described. It is always easier to interpret what is being shown when the authors are jumping between species, when the exact mutant is included. This is particularly important in this paper, where we are jumping between different subunits and different species, so a clear description in the figure/figure legends makes it much easier to read for non-specialists.

(2) The HDX data very clearly shows that Rab5 is likely able to bind at both sites, which back ups the cryo EM data nicely. I am slightly confused by some of the HDX statements described in the methods.

(3) The authors state, "Only statistically significant peptides showing a difference greater than 0.25 Da and greater than 5% for at least two timepoints were kept." This seems to be confusing as to why they required multiple timepoints, and before they also describe that they required a p-value of less than 0.05. It might be clearer to state that significant differences required a 0.25 Da, 5%, and p-value of <0.05 (n=3). Also, what do they mean by kept? Does this mean that they only fully processed the peptides with differences?

(4) They show peptide traces for a selection in the supplement, but it would be ideal to include the full set of HDX data as an Excel file, including peptides with no differences, as there is a lot of additional information (deuteration levels for everything) that would be useful to share, as recommended from the Masson et al 2019 recommendations paper. This may be attached, but this reviewer could not see an example of it in the shared data dropbox folder.

Reviewer #3 (Public review):

Summary:

The manuscript of Spokaite et al. focuses on the Vps34 complex involved in PI3P production. This complex exists in two variants, one (class I) specific for autophagy, and a second one (class II) specific for the endocytic system. Both differ only in one subunit. The authors previously showed that the Vps34 complexes interact with Rab GTPases, Rab1 or Rab5 (for class II), and the identified site was found at Vps34. Now, the authors identify a conserved and overlooked Rab5 binding site in Vps15, which is required for the function of the Class II complex. In support of this, they show cryo-EM data with a second Rab5 bound to Vps15, identify the corresponding residues, and show by mutant analysis that impaired Rab5 binding also results in defects using yeast as a model system.

Overall, this is a most complete study with little to criticize. The paper shows convincingly that the two Rab5 binding sites are required for Vps34 complex II function, with the Vps15 binding site being critical for endosomal localization. The structural data is very much complete. What I am missing are a few controls that show that the mutations in Vps15 do not affect autophagy. I also found the last paragraph of the results section a bit out of place, even though this is a nice observation that the N-terminal part of BECLIN has these domains. However, what does it add to the story?

eLife Assessment

Li et al. present an important and innovative study linking developmental changes in sleep to ecological context in Drosophila mojavensis, and propose that sleep at one stage of an animal's life might anticipate needs at a future stage. The results fit well with this model, but are correlative in nature. The work is convincing, scientifically rigorous, and effectively bridges sleep biology and evolutionary ecology, opening promising new directions for the field.

Joint Public review:

Summary

This interesting work by Shuhao Li and colleagues suggests that developmental sleep and feeding behavior in larval flies is genetically programmed to prepare the animal for adult contingencies, such as in the case of flies living in harsh ecological environments, such as deserts. Thus, the work proposes that desert-dwelling flies such as Drosophila mojavensis sleep less and feed more than D. melanogaster as larvae, which allows them to feed less and sleep more as adults in the harsh desert conditions where they live. The authors argue that this is evidence for developmental sleep reallocation, which helps the adult flies survive in the desert. In general, their results support this compelling hypothesis, so this work provides a new perspective on how sleep might be differentially programmed across developmental stages according to the requirements of an ecological niche. This work is particularly innovative for several reasons. First, it extends the Drosophila sleep field beyond D. melanogaster and directly addresses questions about the evolution of sleep that remain largely unexplored. Second, it investigates the possibility that changes in sleep across development may be adaptive, rather than sleep being a static trait. Overall, this work opens new avenues of research, effectively bridges the fields of sleep biology and evolutionary ecology, and should be of broad interest to a general readership. The manuscript is scientifically sound and clearly written for a generalist audience.

There are, however, two important weaknesses that should be addressed. The first is the implicit assumption that all observed behavioral differences are adaptive; this would benefit from a more cautious framing. Second, the manuscript would be strengthened by a more detailed discussion, and potentially additional data, regarding the ecological differences experienced by D. mojavensis and D. melanogaster at distinct life-cycle stages.

Strengths:

(1) The study astutely uses desert Drosophila species as models to understand how sleep is optimized in a challenging environment. The manuscript is rigorous, experiments are well controlled, the work is very clearly presented, and the results support the main conclusions, which are quite exciting.

(2) The manuscript examines previously unexplored sleep differences in a non-melanogaster species.

(3) The study provides evidence that selective pressure can be restricted to specific developmental stages.

(4) This work offers evolutionary insights into the trade-offs between sleep and feeding across development.

Weaknesses

(1) The authors should soften interpretations so that it is not assumed that any observed difference between mojavensis and melanogaster is necessarily adaptive, or evolved due to food availability or temperature stress.

(2) The study relies on comparisons and correlations. While it seems likely that the observed differences in sleep explain the increased food consumption and energy storage in the larvae of desert flies, demonstrating this through sleep manipulation would strengthen the authors' conclusions.

(3) The question arises regarding whether transiently quiescent larvae are always really sleeping, and whether it is appropriate to treat sleep as a stochastic population-level phenomenon rather than as an individual trait.

(4) The manuscript would benefit from comparative analysis beyond mojavensis and melanogaster.

(5) A deeper discussion of the ecological differences between the 2 Drosophila species would place the results in a broader context.

(6) The feeding parameters used in adults and larvae measure different aspects of feeding, confounding comparisons.

eLife Assessment

This work presents a brain-wide atlas of vasopressin (Avp) and vasopressin receptor 1A (Avpr1a) mRNA expression in mouse brains using high-resolution RNAscope in situ hybridization. The single-transcript approach provides precise localization and identifies additional brain regions expressing Avpr1a, creating a valuable resource for the field. The revised manuscript is clearer and more impactful, with improved figures, stronger data organization, and enhanced scholarship through added context and citations. Overall, the evidence is compelling, and the atlas should be broadly of use to researchers studying vasopressin signaling and related neural circuits.

Reviewer #1 (Public review):

Summary:

Despite accumulating prior studies on the expressions of AVP and AVPR1a in the brain, a detailed, gender-specific mapping of AVP/AVPR1a neuronal nodes has been lacking. Using RNAscope, a cutting-edge technology that detects single RNA transcripts, the authors created a comprehensive neuroanatomical atlas of Avp and Avpr1a in male and female brains.

Strengths:

This well-executed study provides valuable new insights into gender differences in the distribution of Avp and Avpr1a. The atlas is an important resource for the neuroscience community.

The authors have adequately addressed all of my concerns. I have no further questions or concerns.

Reviewer #2 (Public review):

Summary:

The authors conducted a brain-wide survey of Avp (arginine vasopressin) and its Avpr1a gene expression in the mouse brain using RNAscope, a high-resolution in situ hybridization method. Overall, the findings are useful and important because they identify brain regions that express the Avpr1a transcript. A comprehensive overview of Avpr1a expression in the mouse brain could be highly informative and impactful. The authors used RNAscope (a proprietary in situ hybridization method) to assess transcript abundance of Avp and one of its receptors, Avpr1a. The finding of Avp-expressing cells outside the hypothalamus and the extended amygdala is novel and is nicely demonstrated by new photomicrographs in the revised manuscript. The Avpr1a data suggest expression in numerous brain regions. In the revised manuscript, reworked figures make the data easier to interpret.

Strengths:

A survey of Avpr1a expression in the mouse brain is an important tool for exploring vasopressin function in the mammalian brain and for developing hypotheses about cell- and circuit-level function.

Future considerations:

The work contained in the manuscript is substantial and informative. Some questions remain and would be addressed in the current manuscript. How many cells are impacted? Are transcripts spread across many cells or only present in a few cells? Is density evenly distributed through a brain region or compacted into a subfield?

Author response:

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

Reviewer #1:

We thank the reviewer for great suggestions.

(1) The X-axis labels in some panels in Figure 2C and Supplementary Figure 2B overlap, making them difficult to read. Adjusting the label spacing or formatting would improve clarity.

We thank the reviewer for the comment. All panels including Figure 2C and Supplementary Figure 2B, have now been organized the way in which X-axis labels are easily read.

(2) In the scatter dot plot bar diagrams, it appears that n=3 for most of the data. Does this represent the number of mice used or the number of tissue sections per sample? This should be clarified in the figure legends for better transparency. 

Great suggestion. In Results (page 7, lines 135-136), we now clarified that quantification was performed on every tenth section of the brain from 3 female and 3 male mice. Additionally, in the legends for scatter dot plot bar diagrams we also mentioned that n=3 represents the number of mice used.

(3) In Supplemental Figure 2B, the positive signals are not clearly visible. Providing higher-magnification images is recommended.

Great suggestion. The revised Supplemental Figure 2B, but also Figure 2A, now provide higher magnification inset images with distinctive positive signals.

Reviewer #2:

We thank the reviewer for great and critical suggestions.

(1) Introduction:

Line 58: References should be provided for this statement as it is based on a robust field of research, not on a new concept.

We thank the reviewer for the comment. We have now included relevant references as suggested (page 4, line 58).

(2) Line 100-102: This sentence seems to make new, an idea that has been well-documented since the late 1970s. Posterior pituitary hormones oxytocin and vasopressin have long been known to have multiple peripheral targets, and at least a subset of vasopressin and oxytocin neurons have robust central projections. The central targets have been the focus of study for numerous labs. Reference 34 does not relate to posterior pituitary hormones and seems mis-cited.

We have changed this sentence, excluded the reference that does not relate to posterior pituitary hormones and added 4 further references reporting other non-traditional roles of vasopressin and oxytocin (page 6, lines 100-102).

(3) Lines 102-108: While the regulation of bone is an interesting example of an under-appreciated impact of vasopressin, the example does not build to the rationale for examining central Avp and Avpr1a expression.

We mean no disrespect here, but we have recently reported neural brain-bone connections using the SNS-specific PRV152 virus (Ryu et al., 2024; PMID: 38963696) and submitted Single Transcript Level Atlas of Oxytocin and the Oxytocin Receptor in the Mouse Brain (doi: https://doi.org/10.1101/2024.02.15.580498). Surprisingly, we detected Avpr1a and Oxtr expression in certain brain areas (for example, PVH and MPOM) that connect to both bone and adipose tissue through the SNS—raising an important question regarding a central role of Avpr1a and Oxtr in bodily mass and fat regulation. 

(4) Line 111: Avp expression and Avpr1a expression have both been studied using in situ hybridization. Thus, the overall concept is less novel than hinted at in the text. Avp expression has been studied quite extensively. Avpr1a expression has not been studied in an exhaustive fashion. 

We thank the reviewer for this comment and absolutely agree that brain AVP expression has been studied extensively. As with the Avpr, we believe that RNAscope probe design and signal amplification system employed in our study allow for more specific and sensitive detection of individual RNA targets at the single transcript level with much cleaner background noise comparing to in situ hybridization method. 

(5) Results:

Line 143: RNAscope is indeed a powerful method of detecting mRNA at the single transcript level. However, using that single transcript resolution only to provide transcript per brain region analysis, losing all of the nuance of the individual transcript expression, seems like a poor use of the method potential.

This is a good point and we did notice that Avpr1a transcript expression in several brain nuclei displayed individual pattern of expression versus more ubiquitous expression in most of the other brain areas. We noted this finding in Results (page 9, lines 164-168); however, because of the word limits in Discussion, we are not sure what would be dropped to make more room and whether this is truly necessary.

(6 &7) Line 135: Sections were coded from 3 males and 3 females. I would argue that there is not enough statistical power to make inferences regarding sex differences or regional differences. In fact, the authors did not provide any statistical analysis in the manuscript at all, even though they stated they had completed statistical tests on the methods.

150-157: All statements regarding sex differences in expression are made without statistical analyses, which, if conducted, would be underpowered. Given the limitations of performing and analyzing RNAscope data en masse a low n is understandable, but it requires a much more precise description of the data and a more careful look at how the results can be interpreted.

We thank the reviewer for these comments. We mean no disrespect here, but while statistical analysis for main brain regions is relevant, it is not meaningful as far as nuclei, sub-nuclei and regions are concerned. It is noteworthy to mention that RNAscope data analysis in the whole mouse brain is an extremely drawn-out process requiring almost 2 months to conduct exhaustive manual counting of single Avpr1a transcripts in a single mouse brain—authors analyzed 6 brains. That said, statistical tests have been performed and exact P values are now shown in graphs.

(8) Line 146: I am flagging this instance, but it should be corrected everywhere it occurs. Since we cannot know the gender of a given mouse, I would recommend referring to the mouse's "sex" rather than its "gender."

Good suggestion. We made adequate changes throughout the manuscript.

(9) Line 153: The authors switch to discussing cell numbers. Why is this data relegated to the supplemental material?

Main figures in the manuscript report Avp and Avpr1a transcript density which has more important biological significance in terms of signal efficiency and cellular response dynamics. Due to the graph abundancy in the main text, we included all graphs with Avp and Avpr1a transcript counts in the supplemental material.

(10) Methods:

Line 369: "For simplicity and clarity, exact test results and exact P values are not presented." Simplicity or clarity is not a scientific rationale not to provide accurate statistics.

We now provide exact P values in the graphs and the sentence in line 369 has been corrected accordingly (page 18, lines 379-380).

(11) Line 362: The description of how data were analyzed is inadequate. More detail is needed.

Agreed. We now included a detailed description on how data was analyzed (page 18, lines 365-374).

(12) Discussion:

Line 321: "This contrasts the rudimentary attribution of a single function per brain area." While brain function is often taught in such rudimentary terms to make the information palatable to students, I do not think the scientific literature on vasopressin function published over the past 50 years would suggest that we are so naïve in interpreting the functional role of vasopressin in the brain. Clearly, vasopressin is involved in numerous brain functions that likely cross behavioral modalities.

Agreed and we removed this sentence.

(13) Line 322: "The approach of direct mapping of receptor expression in the brain and periphery provides the groundwork." On its face, this statement is true, but the present data build on the groundwork laid by others (multiple papers from Ostrowski et al. in the early 1990s).

Agreed.

(14) Figures:

Figure 1: 1B, I do not know the purpose of creating graphs with single bars (3V, ic, pir-male, and pir-female); there are no comparisons made in the graph. In the graphs with many brain regions, very little data can be effectively represented with the scale as it is. I recommend using tables to provide the count/density data and making graphs of only the most robust areas. In addition, although there is no statistical comparison, combining males and females in the same graphs might be beneficial to make a visual comparison easier. Why were cell counts only included in the supplemental material? Is that data not relevant?

We thank the reviewer for this comment. Now all figures are presented in a more effective and aesthetically pleasing way.

(15) There is a real missed opportunity to highlight some of the findings. For example, cell counts and density measures are provided for regions in the hippocampus, thalamus, and cortex that are not typically reported to contain vasopressin-expressing cells. Photomicrographs of these locations showing the RNAscope staining would be far more impactful in reporting these data. Are there cells expressing Avp, or is the Avp mRNA in these areas contained in fibers projecting to these areas from hypothalamic and forebrain sources?

Great suggestion. We now see in Figure 1D showing novel Avp transcript expression in the hippocampus, thalamus and cortex. Based on counterstained hematoxylin staining, Avp mRNA transcripts were found in somata.

(16) Figure 1C legend suggests images of the hippocampus and cortex, but all images are from the hypothalamus. Abbreviations are not defined.

Thank you for the comment. We corrected Figure 1C legend and separately included Figure 1D showing novel Avp mRNA expression in the hippocampus and cortex.

(17) Figure 2: The analysis of Avpr1a suffers from some of the same issues as the Avp analysis. In Figure 2A, the photomicrographs do not do a very good job of illustrating representative staining. The central canal image does not appear to have any obvious puncta, but the density of Avpr1a puncta suggests something different. The sex difference in the arcuate is also not clearly apparent in representative images. There is minimal visualization of the data for a project that depends so heavily on the appearance of puncta in tissue, coupled with the lack of clarity in the images provided, greatly diminished the overall enthusiasm for the data presentation. The figures in 2C would be more useful as tables with graphs used to highlight specific regions; as is, most of the data points are lost against the graph axis. Photomicrographs would also provide a better understanding of the data than graphs.

Great suggestion. The revised Figure 2A but also Supplemental Figure 2B now provide higher magnification inset images with distinctive positive signals. As with Figures 2C, we arranged all graphs in a more effective and aesthetically pleasing manner.

(18) Figure 3: Given the low number of animals and, therefore, low statistical power, I do not think that illustrating the ratios of male to female is a statistically valid comparison.

Please see response to Point 6 & Point 7.

(19) Figure 4: Pituitary is an interesting choice to analyze. However, why was only the posterior pituitary analyzed? Were Avp transcripts contained in terminals of vasopressin neuron axons or other cells? Was Avpr1a transcript present in blood vessel cells where Avp is released? A different cell type? Why not examine the anterior pituitary, which also expresses Avp receptors (although the literature suggests largely Avpr1b)?

Thank you for the great comment. We included only posterior pituitary because there were no positive Avp/Avpr1a transcripts found in the anterior pituitary. Unfortunately, we have not performed cell type-specific staining, which would have enabled greater variation in AVP and its receptor expression across various cell types.

eLife Assessment

This study provides useful insights regarding the alterations of sleep architecture in a knock-in mouse model of Alzheimer's Disease (AD). These include age-related hyperactivity that is typically associated with increased arousal, a normal homeostatic response to sleep loss, and a stronger AD-like phenotype in females. Although the analyses are robust, evidence for the proposed mechanisms underlying abnormal sleep architecture is incomplete. Overall, the study may have a focused impact on the sleep and AD fields.

Reviewer #1 (Public review):

Summary:

The manuscript titled, "Sleep-Wake Transitions Are Impaired in the AppNL-G-F Mouse Model of Early Onset Alzheimer's Disease", is about a study of sleep/wake phenomena in a knockin mouse strain carrying "three mutations in the human App gene associated with elevated risk for early onset AD". Traditional, in-depth characterization of sleep/wake states, EEG parameters, and response to sleep loss are employed to provide evidence, "supporting the use of this strain as a model to investigate interventions that mitigate AD burden during early disease stages". The sleep/wake findings of earlier studies (especially Maezono et al., 2020, as noted by the authors) were extended by several important, genotype-related observations, including age-related hyperactivity onset that is typically associated with increased arousal, a normal response to loss of sleep and to multiple sleep latency testing, and a stronger AD-like phenotype in females. The authors conclude that the AppNL-G-F mice demonstrate many of the human AD prodromal symptoms and suggest that this strain may serve as a model for prodromal AD in humans, confirming the earlier results and conclusions of Maezono et al. Finally, based on state bout frequency and duration analyses, it is suggested that the AppNL-G-F mice may develop disruptions in mechanism(s) involved in state transition.

Strengths:

The study appears to have been, technically, rigorously conducted with high quality, in-depth traditional assessment of both state and EEG characteristics, with the concordant addition of activity and temperature. The major strengths of this study derive from observations that the AppNL-G-F mice: (1) are more hyperactive in association with decreased transitions between states; (2) maintain a normal response to sleep deprivation and have normal MSLT results; and (3) display a sex specific, "stronger" insomnia-like effect of the knockin in females.

Weaknesses:

The weaknesses stem from the study's impact being limited due to its being largely confirmatory of the Maezono et al. study, with advances of importance to a potentially more focused field. Further, the authors conclude that AppNL-G-F mice have disrupted mechanism(s) responsible for state transition; however, these were not directly examined. The rationale for this conclusion is stated by the authors as based on the observations that bouts of both W and NREM tend to be longer in duration and decreased in frequency in AppNL-G-F mice. Although altered mechanism(s) of state transition (it is not clear what mechanisms are referenced here) cannot be ruled out, other explanations might be considered. For example, increased arousal in association with hyperactivity would be expected to result in increased duration of W bouts during the active phase. This would also predictably result in greater sleep pressure that is typically associated with more consolidated NREM bouts, consistent with the observations of bout duration and frequency.

Reviewer #2 (Public review):

Summary:

The authors have used a knock-in mouse model to explore late-in-life amyloid effects on sleep. This is an excellent model as the mutated genes are regulated by the endogenous promoter system. The sleep study techniques and statistical analyses are also first-rate.

The group finds an age-dependent increase in motor activity in advanced age in the NLGF homozygous knock-in mice (NLGF), with a parallel age-dependent increase in body temperature, both effects predominate in the dark period. Interestingly, the sleep patterns do not quite follow the sleep changes. Wake time is increased in NLGF mice, and there is no progression in increased wake over time. NREMS and REM sleep are both reduced, and there is no progression. Sleep-wake effects, however, show a robust light:dark effect with larger effects in the dark period. These findings support distinct effects of this mutation on activity and temperature and on sleep. This is the first description of the temporal pattern of these effects. NLGF mice show wake stability (longer bout durations in the dark period (their active period) and fewer brief arousals from sleep. Sleep homeostasis across the lights-on period is normal. Wake power spectral density is unaffected in NLGF mice at either age. Only REM power spectra are affected, with NLGF mice showing less theta and more delta. There are interesting sex differences, with females showing no gene difference in wake bout number, while males show a gene effect. Similarly, gene effects on NREM bout number seem larger in males than in females. Although there was no difference in homeostatic response, there was normalization of sleep-wake activity after sleep deprivation.

Strengths:

Approach (model extent of sleep phenotyping), analysis.

Weaknesses:

The weaknesses are summarized below and are viewed as "addressable".

(1) The term insomnia. Insomnia is defined as a subjective dissatisfaction with sleep, which cannot be ascertained in a mouse model. The findings across baseline sleep in NLGF mice support increased wake consolidation in the active period. The predominant sleep period (lights on) is largely unaffected, and the active period (lights off) shows increased activity and increased wake with longer bouts. There is a fantastic clue where NLGF effects are consistent with increased hypocretinergic (orexinergic) neuron activity in the dark period, and/or increased drive to hypocretin neurons from PVH.

(2) Sleep-wake transitions are impaired: This should not be termed an impairment. It could actually be beneficial to have greater state stability, especially wake stability in the dark or active period. There is reduced sleep in the model that can be normalized by short-term sleep loss. It is fascinating that recovery sleep normalized sleep in the NLGF in the immediate lights-on and light-off period. This is a key finding.

Reviewer #3 (Public review):

Summary:

In this study, Tisdale et al. studied the sleep/wake patterns in the biological mouse model of Alzheimer's disease. The results in this study, together with the established literature on the relationship of sleep and Alzheimer's disease progression, guided the authors to propose this mouse model for the mechanistic understanding of sleep states that translates to Alzheimer's disease patients. However, the manuscript currently suffers from a disconnect between the physiological data and the mechanistic interpretations. Specifically, the claim of "impaired transitions" is logically at odds with the observed increase in wake-state stability or possible hyperactivity. Additionally, the description of the methods, the quantification, and the figure presentation could be substantially improved. I detail some of my concerns below.

Strengths:

The selection of the knock-in model is a notable strength as it avoids the artifacts associated with APP overexpression and more closely mimics human pathology. The study utilizes continuous 14-day EEG recordings, providing a unique dataset for assessing chronic changes in arousal states. The assessment of sex as a biological variable identifies a more severe "insomniac-like" phenotype in females, which aligns with the higher prevalence and severity of Alzheimer's disease in women.

Weaknesses:

The study seems to lack a clear hypothesis-driven approach and relies mostly on explorative investigations. Moreover, lack of quantitative analytical methods as well as shaky logical conclusions, possibly not supported by data in its current form, leaves room for major improvement.

Since this paper studied sleep states, the "Methods" section is quite unclear on what specific criteria were used to classify sleep states. There is no quantitative description of classifying sleep based on clear, reproducible procedures. There are many reasonably well-characterized sleep scoring systems used in rat electrophysiological literature, which could be useful here. The authors are generally expected to describe movement speed and/or EMG and/or EEG (theta/delta/gamma) criteria used to classify these epochs. The subjective (manual) nature of this procedure provides no verifiable validation of the accuracy and interpretability of the results.

One of the bigger claims is that "state transition mechanism(s)" are impaired. However, Figure 7 shows that model mice exhibit significantly more long wake bouts (>260s) and fewer short wake bouts (<60s). Logically, an "impaired switch" (the flip-flop model, Saper et al., 2010) results in state fragmentation. The data here show the opposite: the wake state has become too stable. This suggests the primary defect is not in the transition mechanism itself, but possibly in a pathological increase in arousal drive (hyper-arousal), likely linked to the dark-phase hyperactivity shown in Figures 4 and 5. Also, a point to note is that this finding is not new.

Figure 3 heatmaps lack color bars and units. Spectral power must be quantitatively defined and methods well-explained in the Methods section. Without these, the reader cannot discern if the "reduced power" in females is a global suppression of signal or a frequency-specific shift. Additionally, the representative example used to claim shorter sleep bouts lacks the statistical weight required for a major physiological conclusion. How does a cooler color (not clear what range and what the interpretation is) mean shorter sleep bout in female mice? The authors should clearly mark the frequency ranges that support their claims. In this figure, there is a question mark following the theta/delta range. The authors should avoid speculation and state their claims based on facts. They should also add the theta and delta ranges in the plot, such that readers can draw their own conclusions.

Figure 8 and the MSLT results show that model mice are "no sleepier than WT mice" and have a functional homeostatic rebound. This presents a logical flaw in the "insomnia" narrative. True insomnia in AD patients typically involves a failure of the homeostatic process or a debilitating accumulation of sleep debt. If these mice do not show increased sleepiness (shorter latency) despite ~19% less sleep, the authors might be describing a "reduced need" for sleep or a "hyper-aroused" state, possibly not a clinical insomnia phenotype.

In Figure 9, LFP power shown and compared in percentages is problematic, as LFP power distribution is known to be skewed (follows power law). This is particularly problematic here because all the frequencies above ~20 Hz seem to be totally flattened or nonexistent, which makes this comparison of power severely limited and biased towards the relative frequency in the highly skewed portion of the LFP power spectrum, i.e., very low frequency ranges like delta, theta, and possibly beta. This ignores low, mid, and high gamma as well as ripple band frequencies. NREM sleep is known to have relatively greater ripple band (100-250 Hz) power bursts in hippocampal regions, and REM sleep is known to have synchronous theta-gamma relationships.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

The manuscript titled, "Sleep-Wake Transitions Are Impaired in the AppNL-G-F Mouse Model of Early Onset Alzheimer's Disease", is about a study of sleep/wake phenomena in a knockin mouse strain carrying "three mutations in the human App gene associated with elevated risk for early onset AD". Traditional, in-depth characterization of sleep/wake states, EEG parameters, and response to sleep loss are employed to provide evidence, "supporting the use of this strain as a model to investigate interventions that mitigate AD burden during early disease stages". The sleep/wake findings of earlier studies (especially Maezono et al., 2020, as noted by the authors) were extended by several important, genotype-related observations, including age-related hyperactivity onset that is typically associated with increased arousal, a normal response to loss of sleep and to multiple sleep latency testing, and a stronger AD-like phenotype in females. The authors conclude that the AppNL-G-F mice demonstrate many of the human AD prodromal symptoms and suggest that this strain may serve as a model for prodromal AD in humans, confirming the earlier results and conclusions of Maezono et al. Finally, based on state bout frequency and duration analyses, it is suggested that the AppNL-G-F mice may develop disruptions in mechanism(s) involved in state transition.

Strengths:

The study appears to have been, technically, rigorously conducted with high quality, in-depth traditional assessment of both state and EEG characteristics, with the concordant addition of activity and temperature. The major strengths of this study derive from observations that the AppNL-G-F mice: (1) are more hyperactive in association with decreased transitions between states; (2) maintain a normal response to sleep deprivation and have normal MSLT results; and (3) display a sex specific, "stronger" insomnia-like effect of the knockin in females.

Weaknesses:

The weaknesses stem from the study's impact being limited due to its being largely confirmatory of the Maezono et al. study, with advances of importance to a potentially more focused field. Further, the authors conclude that AppNL-G-F mice have disrupted mechanism(s) responsible for state transition; however, these were not directly examined. The rationale for this conclusion is stated by the authors as based on the observations that bouts of both W and NREM tend to be longer in duration and decreased in frequency in AppNL-G-F mice. Although altered mechanism(s) of state transition (it is not clear what mechanisms are referenced here) cannot be ruled out, other explanations might be considered. For example, increased arousal in association with hyperactivity would be expected to result in increased duration of W bouts during the active phase. This would also predictably result in greater sleep pressure that is typically associated with more consolidated NREM bouts, consistent with the observations of bout duration and frequency.

Reviewer 1 succinctly summarizes the advances of this study beyond the ground-breaking Maezono et al (2020) study of this “humanized” mouse model exhibiting amyloid deposition. Whereas Maezono et al. conducted sleep/wake studies on male App^NL-G-F mice at 6 and 12 months of age, we had the unusual opportunity to study both sexes of homozygous App^NL-G-F mice and WT littermates at 14-18 months of age and to conduct a longitudinal assessment of many of the same individuals at 18-22 months. In addition to baseline sleep/wake and EEG spectral analyses, we (1) measured subcutaneous body temperature and activity to obtain a broader picture of the physiology and behavior of this strain at advanced ages; (2) assessed baseline sleepiness in this strain using the murine version of the clinically-relevant Multiple Sleep Latency Test (MSLT); (3) evaluated the response of App^NL-G-F mice and WT littermates to a perturbation of the sleep homeostat; (4) compared the sleep/wake characteristics of male vs. female App^NL-G-F mice at 18-22 months and, (5) to assess the stability of the phenotypes, analyzed these data over a continuous 14-d recording rather than the conventional 24h recordings typical of most sleep/wake studies including Maezono et al. We found that a long wake/short sleep phenotype was characteristic of homozygous App^NL-G-F mice at these advanced ages which is also evident in the Maezono et al. (2020) study at 12 months of age (but not at 6 months), although the authors do not comment on this phenotype and instead focus on the reduced REM sleep which is particularly evident in female App^NL-G-F mice in our study. Remarkably, despite being awake ~20% longer per day, we find that App^NL-G-F mice are no sleepier than WT mice as determined by the MSLT and that their sleep homeostat is intact when challenged by 6-h sleep deprivation. At both advanced ages, the long wake/short sleep phenotype is due primarily to longer Wake bouts and shorter bouts of both NREM and REM sleep during the dark phase. Moreover, hyperactivity develops in older in App^NL-G-F mice, particularly females, which contributes to this phenotype. We agree with Reviewer 1 that “hyperactivity would be expected to result in increased duration of W bouts during the active phase” and that this could result in more consolidated NREM bouts and we will modify the manuscript to discuss this alternative. However, the suggestion of greater sleep pressure is not borne out by the MSLT studies as we did not observe the shorter sleep latencies and increased sleep during the nap opportunities on the MSLT that we have observed in other mouse strains. Moreover, due to their short sleep phenotype, App^NL-G-F mice would be entering the sleep deprivation study with a greater sleep debt than WT mice, yet we did not observe greater EEG Slow Wave Activity in this strain during recovery from sleep deprivation. Thus, we have suggested that App^NL-G-F mice are unable to transition from Wake to sleep as readily as their WT littermates. Our observations summarized above set the stage for subsequent mechanistic studies in aged App^NL-G-F mice, although realistically, mice of this age and genotype are a rare commodity.

Reviewer #2 (Public review):

Summary:

The authors have used a knock-in mouse model to explore late-in-life amyloid effects on sleep. This is an excellent model as the mutated genes are regulated by the endogenous promoter system. The sleep study techniques and statistical analyses are also first-rate.

The group finds an age-dependent increase in motor activity in advanced age in the NLGF homozygous knock-in mice (NLGF), with a parallel age-dependent increase in body temperature, both effects predominate in the dark period. Interestingly, the sleep patterns do not quite follow the sleep changes. Wake time is increased in NLGF mice, and there is no progression in increased wake over time. NREMS and REM sleep are both reduced, and there is no progression. Sleep-wake effects, however, show a robust light:dark effect with larger effects in the dark period. These findings support distinct effects of this mutation on activity and temperature and on sleep. This is the first description of the temporal pattern of these effects. NLGF mice show wake stability (longer bout durations in the dark period (their active period) and fewer brief arousals from sleep. Sleep homeostasis across the lights-on period is normal. Wake power spectral density is unaffected in NLGF mice at either age. Only REM power spectra are affected, with NLGF mice showing less theta and more delta. There are interesting sex differences, with females showing no gene difference in wake bout number, while males show a gene effect. Similarly, gene effects on NREM bout number seem larger in males than in females. Although there was no difference in homeostatic response, there was normalization of sleep-wake activity after sleep deprivation.

Strengths:

Approach (model extent of sleep phenotyping), analysis.

Weaknesses:

The weaknesses are summarized below and are viewed as "addressable".

(1) The term insomnia. Insomnia is defined as a subjective dissatisfaction with sleep, which cannot be ascertained in a mouse model. The findings across baseline sleep in NLGF mice support increased wake consolidation in the active period. The predominant sleep period (lights on) is largely unaffected, and the active period (lights off) shows increased activity and increased wake with longer bouts. There is a fantastic clue where NLGF effects are consistent with increased hypocretinergic (orexinergic) neuron activity in the dark period, and/or increased drive to hypocretin neurons from PVH.

(2) Sleep-wake transitions are impaired: This should not be termed an impairment. It could actually be beneficial to have greater state stability, especially wake stability in the dark or active period. There is reduced sleep in the model that can be normalized by short-term sleep loss. It is fascinating that recovery sleep normalized sleep in the NLGF in the immediate lights-on and light-off period. This is a key finding.

Reviewer 2 suggests a provocative hypothesis to test. Curiously, although a recent Science paper suggests that hyperexcitable hypocretin/orexin neurons in aging mice results in greater sleep/wake fragmentation, hyperexcitability of this system could result in hyperactivity and longer wake bouts in aged App^NL-G-F mice.

Reviewer #3 (Public review):

Summary:

In this study, Tisdale et al. studied the sleep/wake patterns in the biological mouse model of Alzheimer's disease. The results in this study, together with the established literature on the relationship of sleep and Alzheimer's disease progression, guided the authors to propose this mouse model for the mechanistic understanding of sleep states that translates to Alzheimer's disease patients. However, the manuscript currently suffers from a disconnect between the physiological data and the mechanistic interpretations. Specifically, the claim of "impaired transitions" is logically at odds with the observed increase in wake-state stability or possible hyperactivity. Additionally, the description of the methods, the quantification, and the figure presentation could be substantially improved. I detail some of my concerns below.

Strengths:

The selection of the knock-in model is a notable strength as it avoids the artifacts associated with APP overexpression and more closely mimics human pathology. The study utilizes continuous 14-day EEG recordings, providing a unique dataset for assessing chronic changes in arousal states. The assessment of sex as a biological variable identifies a more severe "insomniac-like" phenotype in females, which aligns with the higher prevalence and severity of Alzheimer's disease in women.

Weaknesses:

The study seems to lack a clear hypothesis-driven approach and relies mostly on explorative investigations. Moreover, lack of quantitative analytical methods as well as shaky logical conclusions, possibly not supported by data in its current form, leaves room for major improvement.

Since this paper studied sleep states, the "Methods" section is quite unclear on what specific criteria were used to classify sleep states. There is no quantitative description of classifying sleep based on clear, reproducible procedures. There are many reasonably well-characterized sleep scoring systems used in rat electrophysiological literature, which could be useful here. The authors are generally expected to describe movement speed and/or EMG and/or EEG (theta/delta/gamma) criteria used to classify these epochs. The subjective (manual) nature of this procedure provides no verifiable validation of the accuracy and interpretability of the results.

One of the bigger claims is that "state transition mechanism(s)" are impaired. However, Figure 7 shows that model mice exhibit significantly more long wake bouts (>260s) and fewer short wake bouts (<60s). Logically, an "impaired switch" (the flip-flop model, Saper et al., 2010) results in state fragmentation. The data here show the opposite: the wake state has become too stable. This suggests the primary defect is not in the transition mechanism itself, but possibly in a pathological increase in arousal drive (hyper-arousal), likely linked to the dark-phase hyperactivity shown in Figures 4 and 5. Also, a point to note is that this finding is not new.

Figure 3 heatmaps lack color bars and units. Spectral power must be quantitatively defined and methods well-explained in the Methods section. Without these, the reader cannot discern if the "reduced power" in females is a global suppression of signal or a frequency-specific shift. Additionally, the representative example used to claim shorter sleep bouts lacks the statistical weight required for a major physiological conclusion. How does a cooler color (not clear what range and what the interpretation is) mean shorter sleep bout in female mice? The authors should clearly mark the frequency ranges that support their claims. In this figure, there is a question mark following the theta/delta range. The authors should avoid speculation and state their claims based on facts. They should also add the theta and delta ranges in the plot, such that readers can draw their own conclusions.

Figure 8 and the MSLT results show that model mice are "no sleepier than WT mice" and have a functional homeostatic rebound. This presents a logical flaw in the "insomnia" narrative. True insomnia in AD patients typically involves a failure of the homeostatic process or a debilitating accumulation of sleep debt. If these mice do not show increased sleepiness (shorter latency) despite ~19% less sleep, the authors might be describing a "reduced need" for sleep or a "hyper-aroused" state, possibly not a clinical insomnia phenotype.

In Figure 9, LFP power shown and compared in percentages is problematic, as LFP power distribution is known to be skewed (follows power law). This is particularly problematic here because all the frequencies above ~20 Hz seem to be totally flattened or nonexistent, which makes this comparison of power severely limited and biased towards the relative frequency in the highly skewed portion of the LFP power spectrum, i.e., very low frequency ranges like delta, theta, and possibly beta. This ignores low, mid, and high gamma as well as ripple band frequencies. NREM sleep is known to have relatively greater ripple band (100-250 Hz) power bursts in hippocampal regions, and REM sleep is known to have synchronous theta-gamma relationships.

We agree with the reviewer that the “Classification of arousal states” section was missing the key description of how we scored the recordings into arousal states based on EEG, EMG and locomotor activity; this was an oversight as the corresponding text exists in all our previous sleep/wake studies published over several decades. Reviewer 1 also points out the alternative interpretation that “the wake state has become too stable.” However, I think we are using different words to say the same thing: that the transition from wake to sleep is impaired whether it is due to hyperarousal or to a defect in the flip/flop switch that results in greater Wake stability. We will revise Fig 3 (Reviewer 2 suggests combining with Fig 14) but note that the X-axis is labelled 0-25 Hz and that this figure was intended to be descriptive -- illustrating how unusual the female App^NL-G-F mice are relative to WT -- rather than a quantitative analysis of spectral power as in Fig. 14. Both Reviewer 2 and 3 suggest that we are using “insomnia” incorrectly, which we have simply used to describe less sleep per 24h period. Reviewer 2 states that “Insomnia is defined as a subjective dissatisfaction with sleep” and Reviewer 3 suggests a narrow definition of insomnia as due only to “a failure of the homeostatic process or a debilitating accumulation of sleep debt.” In a revised manuscript, we will define “insomnia” as an operational term to succinctly mean “less sleep”. Regarding the problem of presenting spectral power in percentages, we completely agree with the reviewer. However, we intentionally presented spectral power density, a measure of relative power, as in Figure 3A and 3B of Maezono et al. (2020). At the risk of making Fig. 9 even more busy, we will revise Fig. 9 to add labels for all Y-axes.

In addition to a revised Fig. 9, in the revised manuscript, we will reformat Tables 1-3, Figs. S1 and S2 for legibility and correct an error in Fig. 7.

eLife Assessment

This important work employed a recent functional muscle network analysis to evaluate rehabilitation outcomes in post-stroke patients. While the research direction is relevant and suggests the need for further investigation, the strength of evidence supporting the claims is incomplete. Muscle interactions can serve as biomarkers, but improvements in function are not directly demonstrated, and the method's robustness is not benchmarked against existing approaches.

Reviewer #1 (Public review):

While the revised manuscript includes additional methodological details and a supplementary comparison with conventional NMF, it would be great if the authors could add the point below as limitations in the manuscript or change the title and abstract accordingly, since core issues remain:

(1) The study claims to evaluate rehabilitation outcomes without demonstrating that patients actually improved functionally

(2) The comparison with existing methods lacks the quantitative rigor needed to establish superiority

(3) The added value of this complex framework over much simpler alternatives has not been demonstrated

The strength of evidence supporting the main claims remains incomplete. I would encourage the authors to consider discussing these points

(1) including or adding a limitation section about functional outcome measures that go beyond clinical scale scores, (2) providing/discussing quantitative benchmarks showing their method outperforms alternatives on specific, predefined metrics, and (3) clarifying the clinical pathway by which these biomarkers would inform treatment decisions.

There are specific, relatively minor points, that require attention

The authors write: "we did not focus on such complementary evidence in this study." This is a weakness for a paper claiming to provide "biomarkers of therapeutic responsiveness." The FMA-UE threshold defines responders, but there's no independent validation that patients actually functioned better in daily life. Can you please clarify?

Maybe I missed the exact point about this, but with the added NMF plot, the authors list 'lower dimensionality' among their framework's advantages, but the basis for this claim is not clear because given that 12 network components were extracted compared to 11 "conventional" synergies. Can you please clarify, as it is not clear. You claim 'lower dimensionality' as an advantage of the proposed framework (in the Supplementary Materials), yet you extracted 12 components (5 redundant + 7 synergistic networks) compared to 11 synergies from the conventional NMF approach, which does not support a clinical / outcome advantage of this method. Please clarify.