Author response:

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

Reviewer #1 (Public review):

Summary:

The manuscript proposes that 5mC modifications to DNA, despite being ancient and widespread throughout life, represent a vulnerability, making cells more susceptible to both chemical alkylation and, of more general importance, reactive oxygen species. Sarkies et al take the innovative approach of introducing enzymatic genome-wide cytosine methylation system (DNA methyltransferases, DNMTs) into E. coli, which normally lacks such a system. They provide compelling evidence that the introduction of DNMTs increases the sensitivity of E. coli to chemical alkylation damage. Surprisingly they also show DNMTs increase the sensitivity to reactive oxygen species and propose that the DNMT generated 5mC presents a target for the reactive oxygen species that is especially damaging to cells. Evidence is presented that DNMT activity directly or indirectly produces reactive oxygen species in vivo, which is an important discovery if correct, though the mechanism for this remains obscure.

Strengths:

This work is based on an interesting initial premise, it is well-motivated in the introduction and the manuscript is clearly written. The results themselves are compelling.

We thank the reviewer for their positive response to our study.  We also really appreciate the thoughtful comments raised.  We have addressed the comments raised as detailed below. 

Weaknesses:

I am not currently convinced by the principal interpretations and think that other explanations based on known phenomena could account for key results. Specific points below.

(1) As noted in the manuscript, AlkB repairs alkylation damage by direct reversal (DNA strands are not cut). In the absence of AlkB, repair of alklylation damage/modification is likely through BER or other processes involving strand excision and resulting in single stranded DNA. It has previously been shown that 3mC modification from MMS exposure is highly specific to single stranded DNA (PMID:20663718) occurring at ~20,000 times the rate as double stranded DNA. Consequently, the introduction of DNMTs is expected to introduce many methylation adducts genome-wide that will generate single stranded DNA tracts when repaired in an AlkB deficient background (but not in an AlkB WT background), which are then hyper-susceptible to attack by MMS. Such ssDNA tracts are also vulnerable to generating double strand breaks, especially when they contain DNA polymerase stalling adducts such as 3mC. The generation of ssDNA during repair is similarly expected follow the H2O2 or TET based conversion of 5mC to 5hmC or 5fC neither of which can be directly repaired and depend on single strand excision for their removal. The potential importance of ssDNA generation in the experiments has not been considered.

We thank the reviewer for this interesting and insightful suggestion.  Our interpretation of our findings is that a subset of MMS-induced DNA damage, specifically 3mC, overlaps with the damage introduced by DNMTs and this accounts for increased sensitivity to MMS when DNMTs are expressed.  However, the idea that the introduction of 3mC by DNMT actually makes the DNA more liable to damage by MMS, potentially through increasing the level of ssDNA, is also a potential explanation, which could operate in addition to the mechanism that we propose.

(2) The authors emphasise the non-additivity of the MMS + DNMT + alkB experiment but the interpretation of the result is essentially an additive one: that both MMS and DNMT are introducing similar/same damage and AlkB acts to remove it. The non-additivity noted would seem to be more consistent with the ssDNA model proposed in #1. More generally non-additivity would also be seen if the survival to DNA methylation rate is non-linear over the range of the experiment, for example if there is a threshold effect where some repair process is overwhelmed. The linearity of MMS (and H2O2) exposure to survival could be directly tested with a dilution series of MMS (H2O2).

We thank the reviewer for this point.  As in the response to point #1, the reviewer’s hypothesis of increased potency of MMS, potentially through increased ssDNA, downstream of 3mC induction by DNMT, is a good one.  We have added a dose-response curve for DNMT-expressing cells to MMS to the revised version of the manuscript.  This shows that there is a non-linear response to MMS in the WT background.  Sensitivity is exacerbated by expression of DNMT and alkB mutation individually but there is also a strong non-additive effect that is particularly marked at low MMS concentrations where sensitivity is much higher in the double mutant than predicted from the two single mutants.  This is consistent with induction of DNA damage by DNMT that is repaired by alkB because alkB can be ‘overwhelmed’ even in WT backgrounds as the reviewer suggests.  However, it is also perfectly possible that the effect is due to increased levels of DNA damage induction in DNMT-expressing cells.  Both these results are compatible with our central hypothesis, namely that DNMT expression induces 3mC.  We have included these results along with discussion of them in the revised text in the results section:

In order to investigate the non-additivity between DNMT expression and alkB mutation further, we investigated the effect of MMS over a range of concentrations for the different strains (Supplemental Figure 1A).  We quantified the non-additivity by comparing between the survival of alkB expressing DNMT to the predicted combined effect of either alkB mutation alone or DNMT expression alone(Supplemental Figure 1B).  Significantly reduced survival than expected was observed, most notably at low concentrations of MMS, which could be due to the saturation of the effect at high concentrations of MMS for alkB mutants expressing DNMT, where extremely high levels of sensitivity were observed.  The non-linear shape of the graph observed for WT cells expressing DNMTs further suggests that the ability of AlkB to repair the DNA is overwhelmed at high MMS concentrations even in the WT background.  These results are consistent with the idea that AlkB repairs a form of DNA damage from MMS that is more prevalent when DNMT is expressed.  This could be because DNMT induces 3mC, repaired by AlkB, and further 3mC is induced by MMS leading to much higher 3mC levels in the absence of AlkB activity.  Alternatively, 3mC induction by DNMT may lead to increased levels of ssDNA, particularly in alkB mutants, which could increase the risk of further DNA damage by MMS exposure and heighten sensitivity.  Either of these mechanisms are consistent with induction of 3mC by DNMT, and  indicate that the induction of DNA damage by DNMT expression has a fitness cost for cells when exposed to genotoxic stress in their environment. 

(3) The substantial transcriptional changes induced by DNMT expression (Supplemental Figure 4) are a cause for concern and highlight that the ectopic introduction of methylation into a complex system is potentially more confounded than it may at first seem. Though the expression analysis shows bulk transcription properties, my concern is that the disruptive influence of methylation in a system not evolved with it adds not just consistent transcriptional changes but transcriptional heterogeneity between cells which could influence net survival in a stressed environment. In practice I don't think this can be controlled for, possibly quantified by single-cell RNA-seq but that is beyond the reasonable scope of this paper.

We fully agree with the reviewer and, indeed, we are very interested in what is driving the transcriptional changes that we observed.  Work is currently underway in the lab to investigate this further but, as the reviewer suggests, is beyond the scope of this paper.  Importantly, we have used the transcriptional data to determine that the effect of DNMTs on ROS is unlikely to be due to failure of ROS-induced detoxification mechanisms by investigating the expression of oxyR regulated genes.  Nevertheless we have explicitly mentioned the concern raised by the reviewer in the revised manuscript as follows:

“The substantial transcriptional responses could potentially affect how individual cells respond to genotoxic stress and thus could be contributing to some of the excess sensitivity to MMS and H2O2 in cells expressing DNMTs. However, the induction of oxyR regulated genes such as catalase was unaffected by 5mC (Supplementary Figure 4B).  Thus, the increased sensitivity to H2O2 is unlikely to be caused by failure of detoxification gene induction by DNMT expression.”

(4) Figure 4 represents a striking result. From its current presentation it could be inferred that DNMTs are actively promoting ROS generation from H2O2 and also to a lesser extent in the absence of exogenous H2O2. That would be very surprising and a major finding with far-reaching implications. It would need to be further validated, for example by in vitro reconstitution of the reaction and monitoring ROS production. Rather, I think the authors are proposing that some currently undefined, indirect consequence of DNMT activity promotes ROS generation, especially when exogenous H2O2 is available. It would help if this were clarified.

We thank the reviewer for picking this up.  In the discussion, we raise two possible explanations for why DNMT (even without H2O2) increases the ROS levels.  One idea is direct activity of DNMT, and one is through the product of DNMT activity (5mC) acting as a platform to generate more ROS from endogenous or exogenous sources.  Whilst we attempted to measure ROS from mSSSI activity in vitro, this experiment gave inconsistent results and therefore we cannot distinguish between these two possibilities.  However, we argued that direct activity is less likely, exactly as the reviewer points out.  We have clarified our discussion in the revised version, rewriting the entire section titled

Oxidative stress as a new source of DNA damage induction by DNMT expression to more clearly set out these possibilities. 

Reviewer #2 (Public review):

5-methylcytosine (5mC) is a key epigenetic mark in DNA and plays a crucial role in regulating gene expression in many eukaryotes including humans. The DNA methyltransferases (DNMTs) that establish and maintain 5mC, are conserved in many species across eukaryotes, including animals, plants, and fungi, mainly in a CpG context. Interestingly, 5mC levels and distributions are quite variable across phylogenies with some species even appearing to have no such DNA methylation.

This interesting and well-written paper discusses the continuation of some of the authors' work published several years ago. In that previous paper, the laboratory demonstrated that DNA methylation pathways coevolved with DNA repair mechanisms, specifically with the alkylation repair system. Specifically, they discovered that DNMTs can introduce alkylation damage into DNA, specifically in the form of 3-methylcytosine (3mC). (This appears to be an error in the DNMT enzymatic mechanism where the generation 3mC as opposed to its preferred product 5-methylcytosine (5mC), is caused by the flipped target cytosine binding to the active site pocket of the DNMT in an inverted orientation.) The presence of 3mC is potentially toxic and can cause replication stress, which this paper suggests may explain the loss of DNA methylation in different species. They further showed that the ALKB2 enzyme plays a crucial role in repairing this alkylation damage, further emphasizing the link between DNA methylation and DNA repair.

The co-evolution of DNMTs with DNA repair mechanisms suggests there can be distinct advantages and disadvantages of DNA methylation to different species which might depend on their environmental niche. In environments that expose species to high levels of DNA damage, high levels of 5mC in their genome may be disadvantageous. This present paper sets out to examine the sensitivity of an organism to genotoxic stresses such as alkylation and oxidation agents as the consequence of DNMT activity. Since such a study in eukaryotes would be complicated by DNA methylation controlling gene regulation, these authors cleverly utilize Escherichia coli (E.coli) and incorporate into it the DNMTs from other bacteria that methylate the cytosines of DNA in a CpG context like that observed in eukaryotes; the active sites of these enzymes are very similar to eukaryotic DNMTs and basically utilize the same catalytic mechanism (also this strain of E.coli does not specifically degrade this methylated DNA) .

The experiments in this paper more than adequately show that E. coli expression of these DNMTs (comparing to the same strain without the DNMTS) do indeed show increased sensitivity to alkylating agents and this sensitivity was even greater than expected when a DNA repair mechanism was inactivated. Moreover, they show that this E. coli expressing this DNMT is more sensitive to oxidizing agents such as H2O2 and has exacerbated sensitivity when a DNA repair glycosylase is inactivated. Both propensities suggest that DNMT activity itself may generate additional genotoxic stress. Intrigued that DNMT expression itself might induce sensitivity to oxidative stress, the experimenters used a fluorescent sensor to show that H2O2 induced reactive oxygen species (ROS) are markedly enhanced with DNMT expression. Importantly, they show that DNMT expression alone gave rise to increased ROS amounts and both H2O2 addition and DNMT expression has greater effect that the linear combination of the two separately. They also carefully checked that the increased sensitivity to H2O2 was not potentially caused by some effect on gene expression of detoxification genes by DNMT expression and activity. Finally, by using mass spectroscopy, they show that DNMT expression led to production of the 5mC oxidation derivatives 5-hydroxymethylcytosine (5hmC) and 5-formylcytosine (5fC) in DNA. 5fC is a substrate for base excision repair while 5hmC is not; more 5fC was observed. Introduction of non-bacterial enzymes that produce 5hmC and 5fC into the DNMT expressing bacteria again showed a greater sensitivity than expected. Remarkedly, in their assay with addition of H2O2, bacteria showed no growth with this dual expression of DNMT and these enzymes.

Overall, the authors conduct well thought-out and simple experiments to show that a disadvantageous consequence of DNMT expression leading to 5mC in DNA is increased sensitivity to oxidative stress as well as alkylating agents.

Again, the paper is well-written and organized. The hypotheses are well-examined by simple experiments. The results are interesting and can impact many scientific areas such as our understanding of evolutionary pressures on an organism by environment to impacting our understanding about how environment of a malignant cell in the human body may lead to cancer.

We thank the reviewer for their response to our study, and value the time taken to produce a public review that will aid readers in understanding the key results of our study. 

Reviewer #3 (Public review):

Summary:

Krwawicz et al., present evidence that expression of DNMTs in E. coli results in (1) introduction of alkylation damage that is repaired by AlkB; (2) confers hypersensitivity to alkylating agents such as MMS (and exacerbated by loss of AlkB); (3) confers hypersensitivity to oxidative stress (H2O2 exposure); (4) results in a modest increase in ROS in the absence of exogenous H2O2 exposure; and (5) results in the production of oxidation products of 5mC, namely 5hmC and 5fC, leading to cellular toxicity. The findings reported here have interesting implications for the concept that such genotoxic and potentially mutagenic consequences of DNMT expression (resulting in 5mC) could be selectively disadvantageous for certain organisms. The other aspect of this work which is important for understanding the biological endpoints of genotoxic stress is the notion that DNA damage per se somehow induces elevated levels of ROS.

Strengths:

The manuscript is well-written, and the experiments have been carefully executed providing data that support the authors' proposed model presented in Fig. 7 (Discussion, sources of DNA damage due to DNMT expression).

Weaknesses:

(1) The authors have established an informative system relying on expression of DNMTs to gauge the effects of such expression and subsequent induction of 3mC and 5mC on cell survival and sensitivity to an alkylating agent (MMS) and exogenous oxidative stress (H2O2 exposure). The authors state (p4) that Fig. 2 shows that "Cells expressing either M.SssI or M.MpeI showed increased sensitivity to MMS treatment compared to WT C2523, supporting the conclusion that the expression of DNMTs increased the levels of alkylation damage." This is a confusing statement and requires revision as Fig. 2 does ALL cells shown in Fig. 2 are expressing DNMTs and have been treated with MMS. It is the absence of AlkB and the expression of DNMTs that that causes the MMS sensitivity.

We thank the reviewer for this and agree that this needs to be clarified with regards to the figure presented and will do so in the revised manuscript. The key comparison is between the active and inactive mSSSI which shows increased sensitivity when active methyltransferases are expressed.  We have clarified this in the revised version of the manuscript as follows:

“Cells expressing either M.SssI or M.MpeI showed increased sensitivity to MMS treatment compared to cells expressing inactive M.SssI”

(2) It would be important to know whether the increased sensitivity (toxicity) to DNMT expression and MMS is also accompanied by substantial increases in mutagenicity. The authors should explain in the text why mutation frequencies were not also measured in these experiments.

This is an important point because it is not immediately obvious that increased sensitivity would be associated with increased mutagenicity (if, for example, 3mC was never a cause of innacurate DNA repair even in the absence of AlkB).  We have now added a Rif resistance assay which demonstrates increased mutagenesis in the presence of DNMT, and that this is exacerbated by loss of AlkB. This is now added as supplemental figure 2 and described in the manuscript as follows:

“One potential consequence of DNMT activity in inducing DNA damage might be increased mutagenesis.  To test this we performed a rifampicin resistance mutagenesis assay, in the absence of MMS, to test whether DNMT induced damage was sufficient to lead to mutation rate increase.  Mutation rate was increased by DNMT expression (p=1.6e-12; two way anova; Supplemental Figure 2) and alkB mutation (two way anova) separately (p<1e-16).  Moreover, there was a significant interaction such that combined alkB mutation and DNMT expression led to a further increased mutation rate compared to the expectation from alkB mutation and DNMT expression separately (p = 7.9e-10; Supplemental Figure 2).  Importantly, DNMT induction alone would be expected to lead to increased mutations due to cytosine deamination(Sarkies, 2022a); however, there is a synergistic effect on mutations when this is combined with loss of AlkB function in alkB mutants. This is consistent with 3mC induction by DNMTs which is repaired by AlkB in WT cells but leads to mutations in alkB mutant cells.

(3) Materials and Methods. ROS production monitoring. The "Total Reactive Oxygen Species (ROS) Assay Kit" has not been adequately described. Who is the Vendor? What is the nature of the ROS probes employed in this assay? Which specific ROS correspond to "total ROS"?

The ROS measurement was with a kit from ThermoFisher: https://www.thermofisher.com/order/catalog/product/88-5930-74.  The probe is DCFH-DA.  This is a general ROS sensor that is oxidised by a large number of cellular reactive oxygen species hence we cannot attribute the signal to a single species.  Use of a technique with the potential to more precisely identify the species involved is something we plan to do in future, but is beyond what we can do as part of this study.  We have added a comment as to the specificity of the ROS sensor in the revised version as follows:

“The ROS detection reagent in this system is DCFH-DA, a generalised ROS sensor that is not specific to any particular ROS molecule.”     

(4) The demonstration (Fig. 4) that DNMT expression results in elevated ROS and its further synergistic increase when cells are also exposed to H2O2 is the basis for the authors' discussion of DNA damage-induced increases in cellular ROS. S. cerevisiae does not possess DNMTs/5mC, yet exposure to MMS also results in substantial increases in intracellular ROS (Rowe et al, (2008) Free Rad. Biol. Med. 45:1167-1177. PMC2643028). The authors should be aware of previous studies that have linked DNA damage to intracellular increases in ROS in other organisms and should comment on this in the text.

We thank the reviewer for this point.  We note that the increased ROS that we observed occur in the presence of DNMTs alone and in the presence of H2O2, not in the presence of MMS; however, the point that DNA damage in general can promote increased ROS in some circumstances is well taken.  We have included a comment on this in the revised version as follows:

“We believe this is a plausible mechanism to explain both increased ROS and increased sensitivity to oxidative stress when DNMT is expressed.  However, other explanations are possible, and it is notable that DNA damaging agents such as MMS can lead to ROS generation(Rowe et al., 2008).  A more detailed chemical and kinetic study of the ROS formation in DNMT-expressing cells would be needed to resolve these questions.”

eLife Assessment

This study provides novel and convincing evidence that both dopamine D1 and D2 expressing neurons in the nucleus accumbens shell are crucial for the expression of cue-guided action selection, a fundamental component of decision-making. The research is systematic and rigorous in using optogenetic inhibition of either D1- or D2-expressing medium spiny neurons in the NAc shell to reveal attenuation of sensory-specific Pavlovian-Instrumental transfer, while largely sparing value-based decision on an instrumental task. Findings in this report build on prior research and resolve some conflicts in the literature regarding decision making.

Reviewer #1 (Public review):

In the current article, Octavia Soegyono and colleagues study "The influence of nucleus accumbens shell D1 and D2 neurons on outcome-specific Pavlovian instrumental transfer", building on extensive findings from the same lab. While there is a consensus about the specific involvement of the Shell part of the Nucleus Accumbens (NAc) in specific stimulus-based actions in choice settings (and not in General Pavlovian instrumental transfer - gPIT, as opposed to the Core part of the NAc), mechanisms at the cellular and circuitry levels remain to be explored. In the present work, using sophisticated methods (rat Cre-transgenic lines from both sexes, optogenetics, and the well-established behavioral paradigm outcome-specific PIT-sPIT), Octavia Soegyono and colleagues decipher the differential contribution of dopamine receptors D1 and D2 expressing spiny projection neurons (SPNs).

After validating the viral strategy and the specificity of the targeting (immunochemistry and electrophysiology), the authors demonstrate that while both NAc Shell D1- and D2-SPNs participate in mediating sPIT, NAc Shell D1-SPNs projections to the Ventral Pallidum (VP, previously demonstrated as crucial for sPIT), but not D2-SPNs, mediates sPIT. They also show that these effects were specific to stimulus-based actions, as value-based choices were left intact in all manipulations.

This is a well-designed study, and the results are well supported by the experimental evidence. The paper is extremely pleasant to read and adds to the current literature.

Reviewer #2 (Public review):

Summary:

This manuscript by Soegyono et al. describes a series of experiments designed to probe the involvement of dopamine D1 and D2 neurons within the nucleus accumbens shell in outcome-specific Pavlovian-instrumental transfer (osPIT), a well-controlled assay of cue-guided action selection based on congruent outcome associations. They used an optogenetic approach to phasically silence NAc shell D1 (D1-Cre mice) or D2 (A2a-Cre mice) neurons during a subset of osPIT trials. Both manipulations disrupted cue-guided action selection but had no effects on negative control measures/tasks (concomitant approach behavior, separate valued guided choice task), nor were any osPIT impairments found in reporter-only control groups. Separate experiments revealed that selective inhibition of NAc shell D1 but not D2 inputs to ventral pallidum was required for osPIT expression, thereby advancing understanding of the basal ganglia circuitry underpinning this important aspect of decision making.

Strengths:

The combinatorial viral and optogenetic approaches used here were convincingly validated through anatomical tract-tracing and ex vivo electrophysiology. The behavioral assays are sophisticated and well-controlled to parse cue and value-guided action selection. The inclusion of reporter-only control groups is rigorous and rules out nonspecific effects of the light manipulation. The findings are novel and address a critical question in the literature. Prior work using less decisive methods had implicated NAc shell D1 neurons in osPIT but suggested that D2 neurons may not be involved. The optogenetic manipulations used in the current study provide a more direct test of their involvement and convincingly demonstrate that both populations play an important role. Prior work had also implicated NAc shell connections to ventral pallidum in osPIT, but the current study reveals the selective involvement of D1 but not D2 neurons in this circuit. The authors do a good job of discussing their findings, including their nuanced interpretation that NAc shell D2 neurons may contribute to osPIT through their local regulation of NAc shell microcircuitry.

Weaknesses:

The current study exclusively used an optogenetic approach to probe the function of D1 and D2 NAc shell neurons. Providing a complementary assessment with chemogenetics or other appropriate methods would strengthen conclusions, particularly the novel demonstration of D2 NAc shell involvement. Likewise, the null result of optically inhibiting D2 inputs to the ventral pallidum leaves open the possibility that a more complete or sustained disruption of this pathway may have impaired osPIT.

Reviewer #3 (Public review):

Summary:

The authors present data demonstrating that optogenetic inhibition of either D1- or D2-MSNs in the NAc Shell attenuates expression of sensory-specific PIT while largely sparing value-based decision on an instrumental task. They also provide evidence that SS-PIT depends on D1-MSN projections from the NAc-Shell to the VP, whereas projections from D2-MSNs to the VP do not contribute to SS-PIT.

Strengths:

This is clearly written. The evidence largely supports the authors' interpretations, and these effects are somewhat novel, so they help advance our understanding of PIT and NAc-Shell function.

Weaknesses:

I think the interpretation of some of the effects (specifically the claim that D1-MSNs do not contribute to value-based decision making) is not fully supported by the data presented.

Author response:

Reviewer #1 (Public review):

In the current article, Octavia Soegyono and colleagues study "The influence of nucleus accumbens shell D1 and D2 neurons on outcome-specific Pavlovian instrumental transfer", building on extensive findings from the same lab. While there is a consensus about the specific involvement of the Shell part of the Nucleus Accumbens (NAc) in specific stimulus-based actions in choice settings (and not in General Pavlovian instrumental transfer - gPIT, as opposed to the Core part of the NAc), mechanisms at the cellular and circuitry levels remain to be explored. In the present work, using sophisticated methods (rat Cre-transgenic lines from both sexes, optogenetics, and the well-established behavioral paradigm outcome-specific PIT-sPIT), Octavia Soegyono and colleagues decipher the differential contribution of dopamine receptors D1 and D2 expressing spiny projection neurons (SPNs).

After validating the viral strategy and the specificity of the targeting (immunochemistry and electrophysiology), the authors demonstrate that while both NAc Shell D1- and D2-SPNs participate in mediating sPIT, NAc Shell D1-SPNs projections to the Ventral Pallidum (VP, previously demonstrated as crucial for sPIT), but not D2-SPNs, mediates sPIT. They also show that these effects were specific to stimulus-based actions, as value-based choices were left intact in all manipulations.

This is a well-designed study, and the results are well supported by the experimental evidence. The paper is extremely pleasant to read and adds to the current literature.

We thank the Reviewer for their positive assessment.

Reviewer #2 (Public review):

Summary:

This manuscript by Soegyono et al. describes a series of experiments designed to probe the involvement of dopamine D1 and D2 neurons within the nucleus accumbens shell in outcome-specific Pavlovian-instrumental transfer (osPIT), a well-controlled assay of cue-guided action selection based on congruent outcome associations. They used an optogenetic approach to phasically silence NAc shell D1 (D1-Cre mice) or D2 (A2a-Cre mice) neurons during a subset of osPIT trials. Both manipulations disrupted cue-guided action selection but had no effects on negative control measures/tasks (concomitant approach behavior, separate valued guided choice task), nor were any osPIT impairments found in reporter-only control groups. Separate experiments revealed that selective inhibition of NAc shell D1 but not D2 inputs to ventral pallidum was required for osPIT expression, thereby advancing understanding of the basal ganglia circuitry underpinning this important aspect of decision making.

Strengths:

The combinatorial viral and optogenetic approaches used here were convincingly validated through anatomical tract-tracing and ex vivo electrophysiology. The behavioral assays are sophisticated and well-controlled to parse cue and value-guided action selection. The inclusion of reporter-only control groups is rigorous and rules out nonspecific effects of the light manipulation. The findings are novel and address a critical question in the literature. Prior work using less decisive methods had implicated NAc shell D1 neurons in osPIT but suggested that D2 neurons may not be involved. The optogenetic manipulations used in the current study provide a more direct test of their involvement and convincingly demonstrate that both populations play an important role. Prior work had also implicated NAc shell connections to ventral pallidum in osPIT, but the current study reveals the selective involvement of D1 but not D2 neurons in this circuit. The authors do a good job of discussing their findings, including their nuanced interpretation that NAc shell D2 neurons may contribute to osPIT through their local regulation of NAc shell microcircuitry.

We thank the Reviewer for their positive assessment.

Weaknesses:

The current study exclusively used an optogenetic approach to probe the function of D1 and D2 NAc shell neurons. Providing a complementary assessment with chemogenetics or other appropriate methods would strengthen conclusions, particularly the novel demonstration of D2 NAc shell involvement. Likewise, the null result of optically inhibiting D2 inputs to the ventral pallidum leaves open the possibility that a more complete or sustained disruption of this pathway may have impaired osPIT.

We acknowledge the reviewer's valuable suggestion that demonstrating NAc-S D1- and D2-SPN engagement in outcome-specific PIT through another technique would strengthen our optogenetic findings. Several approaches could provide this validation. Chemogenetic manipulation, as the reviewer suggested, represents one compelling option. Alternatively, immunohistochemical assessment of phosphorylated histone H3 at serine 10 (P-H3) offers another promising avenue, given its established utility in reporting striatal SPN plasticity in the dorsal striatum (Matamales et al., 2020). We hope to complete such an assessment in future work since it would address the limitations of previous work that relied solely on ERK1/2 phosphorylation measures in NAc-S SPNs (Laurent et al., 2014).

Regarding the null result from optical silencing of D2 terminals in the ventral pallidum, we agree with the reviewer's assessment. While we acknowledge this limitation in the current manuscript (see discussion), we aim to address this gap in future studies to provide a more complete mechanistic understanding of the circuit.

Reviewer #3 (Public review):

Summary:

The authors present data demonstrating that optogenetic inhibition of either D1- or D2-MSNs in the NAc Shell attenuates expression of sensory-specific PIT while largely sparing value-based decision on an instrumental task. They also provide evidence that SS-PIT depends on D1-MSN projections from the NAc-Shell to the VP, whereas projections from D2-MSNs to the VP do not contribute to SS-PIT.

Strengths:

This is clearly written. The evidence largely supports the authors' interpretations, and these effects are somewhat novel, so they help advance our understanding of PIT and NAc-Shell function.

We thank the Reviewer for their positive assessment.

Weaknesses:

I think the interpretation of some of the effects (specifically the claim that D1-MSNs do not contribute to value-based decision making) is not fully supported by the data presented.

We appreciate the reviewer's comment regarding the marginal attenuation of value-based choice observed following NAc-S D1-SPN silencing. While this manipulation did produce a slight reduction in choice performance, the behavior remained largely intact. We are hesitant to interpret this marginal effect as evidence for a direct role of NAc-S D1-SPNs in value-based decision-making, particularly given the substantial literature demonstrating that NAc-S manipulations typically preserve such choice behavior (Corbit & Balleine, 2011; Corbit et al., 2001; Laurent et al., 2012). Notably, previous work has shown that NAc-S D1 receptor blockade impairs outcome-specific PIT while leaving value-based choice unaffected (Laurent et al., 2014). We favor an alternative explanation for our observed marginal reduction. As documented in Supplemental Figure 1, viral transduction extended slightly into the nucleus accumbens core (NAc-C), a region established as critical for value-based decision-making (Corbit & Balleine, 2011; Corbit et al., 2001; Laurent et al., 2012). The marginal impairment may therefore reflect inadvertent silencing of a small NAc-C D1-SPN population rather than a functional contribution from NAc-S D1-SPNs. Future studies specifically targeting larger NAc-C D1-SPN populations would help clarify this possibility and provide definitive resolution of this question.

eLife Assessment

The findings are valuable, given that they highlight the flexible and future-oriented nature of working memory. However, the evidence for the claims about context/color generalization, behavioural relevance of context decoding, dimensionality reduction, neural geometry, the XOR representation, and the specific contribution of working memory is incomplete. The work could be reframed in terms of prospective remapping.

Reviewer #1 (Public review):

Wojcik et al. conducted a working memory (WM) experiment in which participants had to press the right or left button after being presented with a square (upright) or diamond stimulus. The response mapping ('context') depended on a colour cue presented at the start of each trial. This results in an XOR task, requiring participants to integrate colour and shape information. Importantly, multiple colours could map onto the same context, allowing the authors to disentangle the (neural) representations of context from those of colour.

The authors report that participants learn the appropriate context mappings quickly over the course of the experiment. Neural context representation is evident in the WM delay and emerges later in the experiment, unlike colour representation, which is present only during colour presentation and does not evolve over experimental time. There are furthermore results on neural geometry (averaged cross-generalized decoding) and neural dimensionality (averaged decoding after shattering all task dimensions), which are somewhat harder to interpret.

Overall, the findings are likely Important, as they highlight the flexible and future-oriented nature of WM. The strength of support at the moment is incomplete: there are some loose ends on the context/colour generalization, and the evidence for the XOR neural representation is not (yet) well-established.

I have one (major) concern and several suggestions for improvement.

(1a) As the authors also acknowledge in several places, the XOR dimension is strongly correlated with motor responses, in any case toward the end of the task (and by definition for all correct trials). This should be dealt with properly. Right now, e.g. Figures 2g/i, 2h/j, 3e/g, 3f/h are highly similar, respectively, because of this strong collinearity. I would remove the semi-duplicate graphs and/or deal with this explicitly through some partial regression, trial selection, or similar (and report these correlations).

(1b) Most worrisome in this respect is that one of the key results presented is that XOR decoding increases with learning. But also task accuracy increases, meaning that the proportion of correct trials increases with learning, meaning that the XOR and motor regressors become more similar over experimental time. This means that any classifier picking up on motor signals will be better able to do so later on in the task than earlier on. (In other words, the XOR regressor may be a noisy version of the motor regressor early on, and a more precise version of the motor regressor later on.) Therefore, the increase in XOR decoding over experimental time may be (entirely) due to an increase in similarity between the XOR and motor dimensions. The authors should either rule out this explanation, and/or remove/tone down the conclusions regarding the XOR coding increase. (Note that the takeaway regarding colour/context generalization does not depend on this analysis, fortunately.) The absence of a change in motor decoding with learning (as reported on page 11) does not affect this potential confound; in fact it is made more likely with it.

(2) Bayes factors would be valuable in several places, especially with null results (p. 5) or cases with borderline-significant p-values.

(3) The authors' interpretation of the key results implies that the abstract coding learned over the task should be relevant for behaviour. The current results do not show a particularly strong behavioural relevance of coding, to put it mildly. It might be worth exploring whether neural coding expresses itself in reaction times, rather than (in)correct responses, and reflecting on the (lack of) behavioural relevance in the Discussion.

(4) All data and experiment/analysis code should be made available, in public repositories (i.e., not "upon request").

Reviewer #2 (Public review):

This manuscript describes an experiment in which subjects learned to apply an XOR rule in a task in which an initial color cue conditioned the instruction ("press left" or "press right") conveyed by a subsequent shape.

This manuscript gives the impression of being written to address a sophisticated computational framework, but the experiment was not designed to test this framework. Stated differently, the memory-as-resource-for-computations framework may not be needed to account for the results presented here. Variants of this task have been used for decades, often in the context of prospective processing, and although the authors emphasize a dimensionality reduction operation, the task may actually only require the recoding of retrospectively relevant sensory information into the prospectively relevant rule that is needed to guide the response on that trial. Consequently, many of the claims are only partially supported.

The framework invoked by the authors is summarized in the second paragraph of the manuscript:

"Insights from machine learning and computational neuroscience further highlight the idea that memory processes can be viewed as a resource for computations rather than a passive mechanism for storage (Dasgupta & Gershman, 2021; Ehrlich & Murray, 2022). In this light, working memory adapts computations to the current task demands (Dasgupta & Gershman, 2021); pre-computed information can be stored in working memory, and thus reduce the computation time at the moment of the decision (Braver, 2012; Hunt et al., 2021). This perspective is further supported by computational modelling of neural circuits that contends that working memory will change neural geometry in a way that supports the temporal decomposition of computations (Ehrlich & Murray, 2022). This work suggests that the computational load at the moment of action can be thus alleviated by decomposing complex operations into several simple problems solved sequentially in time."

However, the relevance, certainly the necessity, of this framework leads to mischaracterizations of some elements of the task (including about a hypothesis), the emphasis of constructs that don't actually exist in the task, some logical inconsistencies, and the repeated invocation of operations like "dimensionality reduction" despite the fact that the authors find no evidence for them.

Beginning with the final point, the task presented here is a variant of a Badre-style hierarchical control task, one requiring solution at the second order of abstraction (i.e., the color conditions the interpretation of the shape [2nd order], which then determines the correct response [1st order]. These operations can be accomplished without dimensionality reduction by simply carrying out the remapping instructed by each element. For example, on a trial beginning with a blue color cue, the subject can use a lookup table to translate this into the rule "square = left; diamond = right". When the shape is subsequently presented, the subject responds according to this rule. This is really no different from any of the several studies that have shown prospective recoding of information in working memory, including the work from the 1990s in nonhuman primates, and several subsequent studies using fMRI in humans beginning in the 2000s. Importantly, this account does not involve dimensionality reduction in any overt way. If it were the case that the more recent computational work indicates that this operation of "prospective recoding" does, in fact, entail dimensionality reduction on this type of task, that would be interesting. However, I don't see evidence that this is the case. Although the authors carry out several analyses of shattering dimensionality, I do not find any that track this measure across epochs within the trial, an approach that would presumably capture epoch-to-epoch dimensionality reduction, if it occurred.

With regard to mischaracterization of a hypothesis, the authors state: "We hypothesised that working memory processes control the dimensionality of neural representations by selecting features for maintenance. We tested this prediction by exploring the learning dynamics of the colour representation." However, what is described here is not a test of a prediction about dimensionality reduction. Rather, it's a test of a prediction that color decoding would not persist after color offset. To describe this as "dimensionality reduction" misrepresents/mischaracterizes what's happening, which is the translation of color (on any trial, a low-dimensional variable) into the rule that was cued by that color. It is a translation of what kind of information is being represented, as opposed to a dimensionality reduction applied to a representation.

With regard to constructs that don't actually exist, it is unclear what the reality is in the study of a "color pair"? I.e., because colors are never presented together, nor associated in some way, this would seem to be a device that's helpful to the authors for thinking about how their task might be solved, rather than a fundamental aspect of the task that the reader needs to understand. Furthermore, the example given here wasn't helpful for this reader. (What WAS helpful was the description of the two possible strategies and accompanying references to Mayr & Kleigel and to Vandierendonck.)

With regard to logical inconsistencies, one is the notion that color is irrelevant. This is not true, in a literal sense, because if every color cue were rendered as the same monochromatic patch, one wouldn't be able to solve the task. What the authors could do to make their point is perhaps refer to Strategy 1, which corresponds to a less efficient way to solve the task.

Also inconsistent is the relation of the present work to a previous study carried out by this group in nonhuman primates. That task did not include a working memory delay, and so this is difficult to reconcile the comparison that the authors draw with this task with the many suggestions that they make that it's something about WM, per se, that allows for the efficient performance of this task.

"Crucially, the irrelevant feature was only discarded during the delay after it entered working memory." This statement is in direct contradiction with the authors' own reporting of the results: "Decoding analyses demonstrated that colour information peaked in the early colour locked period of the trial and then rapidly declined over time to reach chance levels before the delay-locked period, 𝑐𝑙𝑢𝑠𝑡𝑒𝑟 1: 0.082 − 0.484 𝑚𝑠, 𝑝 = 0.006 (Fig. 2c)."

Other areas where I had difficulties include:

(1) "These results suggest that participants rapidly discarded irrelevant colour information. Only information relevant for performance (context) entered working memory and was maintained."<br /> Although this may be the case, each of the four colors also instructed a rule, and so what's being documented in this study is the translation of a cue into a rule, not the transformation of a "meaningless color" into a "meaningful context." It is very possible that if the authors only used two colors, one for each rule (i.e., one for each "context"), they'd get the same decoding results.

(2) "A defining characteristic of low-dimensional task representations is that they can be easily cross-generalised to different sensory instances of the same task."<br /> This result is difficult to reconcile with the loss of color decoding with color offset. Must it not mean that the rule is being represented differently when cued, e.g., by blue vs. by pink, or by green vs. by khaki? If this is true, then this would also argue against the idea of dimensionality reduction during the delay period, because subjects will, in effect, have swapped needing to represent one of four colors with needing to represent one of four rules.

(3) The authors assert that "cross-colour generalisation of context in the delay period is already implied by the significant context decoding combined with the absence of irrelevant colour coding."<br /> This is contradicted, however, by the failure of the direct test of cross-color decoding!

(4) "Taken together, these findings imply that participants constructed abstract representations of task features but that the mechanism responsible for this transformation relied heavily on discarding colour information early in trial time."

This statement does not follow from the data because no mechanism is being directly measured. Rather, it's simply the case that after translating the color to a rule, the color is no longer needed and so is no longer kept in an active state. There is certainly no evidence for "heavy reliance".

Reviewer #3 (Public review):

Summary:

Wójcik and colleagues investigated how the maintenance of task information in working memory influences the dimensionality of task representations. The task required an exclusive-or (XOR) mapping as the output by combining stimulus features separated by a delay period. The authors found that context information invariant to input features (i.e., color) is maintained and enhanced over the course of learning the task.

The significance of this study lies in its demonstration of how learning selectively changes the geometry of task representations. The clear-cut results emphasize that learning promotes the abstraction of task representations for context-dependent computations. It is also important to investigate how working memory mechanisms contribute to the geometry and optimization of task representations, as such studies in humans are scarce.

Strengths:

(1) The task design and analyses are clear.

(2) The theoretical motivation to study low-dimensional representations and temporal decomposition is strong. Understanding how learning changes these qualities is a novel and important question.

Weaknesses:

(1) The specific contribution of working memory maintenance to the dimensionality and abstraction of representations is unclear. While the task likely recruits working memory, there are no direct assessments linking the observed results to particular qualities or mechanisms of working memory. In other words, neural representations observed during the delay period are interpreted as working memory.

(2) The dissociation between XOR and motor representations is ambiguous, as they only become distinguishable during error trials. Additionally, they show similar time courses and learning-related changes.

Author Response:

Reviewer #1( Public review):

The reviewer raised two main concerns: the potential confound between XOR and motor coding, and the relationship between neural coding and behaviour.

First, we appreciate the consideration of the collinearity between the XOR and motor dimensions. We fully agree that this confound may have contributed to the observed increase in XOR decoding over the course of learning. In response, we will merge the XOR and motor features in the main figures, tone down our interpretation of the XOR learning effect, and clarify how motor signals may obscure or mimic XOR-related changes. As the reviewer noted, this confound does not affect the colour/context cross-generalisation analyses, which remain central to our conclusions regarding flexible and prospective working memory coding.

We also thank the reviewer for the suggestion to examine the behavioural relevance of the neural representations more directly. We agree entirely, and will incorporate new analyses relating coding strength to reaction times, as well as reflect on the implications of these results in the revised Discussion.

Reviewer #2 (Public Review):

The reviewer rightly noted that our manuscript overlooks the established concept of retrospective/prospective coding in working memory, giving the impression that we attempted to reframe it using newer machine learning terminology. We thank the reviewer for catching this important omission. Our intention was not to override this well-established conceptual framework with a newer machine learning term, but rather to build upon it. In fact, prospective coding and the idea of working memory as a resource for computation are closely related—one helps define the functions (prospective and retrospective coding) and the other explains the computational rationale behind applying them. For example, prospective codes specify what is being stored (future-relevant information), while the “memory-as-computation” view addresses why such representation is useful: to enable temporal decomposition of complex tasks and reduce computational load at decision time. We will revise the relevant paragraphs to explicitly reference this cognitive framework and clarify how it relates to — and is complemented by — the newer computational perspective we introduce. Thank you again for highlighting this.

Reviewer 2 also argues that the evidence presented does not support dimensionality reduction, noting that participants likely transition from processing the sensory cue (e.g., blue) to a rule-based representation (e.g., context 1 vs context 2) later in the trial, and that this remapping does not inherently require dimensionality reduction. We agree that our results are consistent with such a transformation into an abstract rule representation during the delay period, as supported by the observed cross- colour context generalisation (Figure 3b) and that this process does not require dimensionality reduction per se. However, we would like to clarify that a shared decision boundary between two colour pairs (e.g., context 1 vs context 2) can manifest in two types of neural geometries. In one case — observed in our data — the irrelevant colour dimension is not maintained after the presentation period, such that blue and pink are maintained as context 1 but variance along the blues vs pink dimension is not represented in neural activity. In the other case, it is possible for the same abstract rule (context 1) to be constructed while maintaining the sensory representation of colour (e.g., “blue” or “pink”), resulting in a change in representational geometry without a reduction in dimensionality. Our data do not support the latter scenario: irrelevant colour information is not maintained in the delay period, suggesting that the abstraction is accompanied by a loss of variance along irrelevant sensory dimensions—i.e., a form of dimensionality reduction. We will clarify this point in the revised manuscript and include a new analysis that explicitly tests whether shattering dimensionality changes as a function of trial time.

The reviewer also raised concerns about inconsistencies in our terminology, particularly the use of “colour pair” and “irrelevant colour.” We agree with the reviewer that the term “colour pair” was a conceptual device rather than a literal aspect of the task, and we will revise the text to make this clear. We recognise that our wording around “irrelevant colour” might have caused confusion. We did not mean “colour” in the broad sense of all colour processing, but rather referred to specific colour dimensions that are not relevant for task performance—for example, when context 1 is cued by both pink and blue, the dimension carrying variance between blue and pink can be considered irrelevant. We will clarify this point in the revised manuscript, using the reviewer’s suggestion to incorporate the description we had already provided in the Methods section.

While we respectfully disagree with the reviewer’s interpretation of our findings—particularly regarding the absence of dimensionality reduction, which they associate with the failure of the direct test of cross-colour context decoding (see Fig. 3b, which shows a significant effect)—we appreciate the opportunity to clarify our position and will revise the manuscript to ensure our reasoning is as transparent and rigorous as possible.

Reviewer #3 (PublIc review):

The reviewer values the study’s demonstration that learning promotes abstraction in task representations, but raises concerns about the lack of direct evidence linking delay-period activity to specific working memory mechanisms and the ambiguous dissociation between XOR and motor representations. We thank the reviewer for their careful reading of the manuscript and will address both concerns in the revised version. As mentioned in our response to Reviewer #1, we will merge the motor and XOR analyses, tone down our interpretations, and clarify why these signals are entangled. Additionally, we will link delay-period neural activity to behavioural performance to establish a more direct connection to working memory processes. Notably, in Figure 4f, we show that early in learning, participants who exhibit stronger cross-generalisation of context during the delay are also more likely to exhibit decreased shattering dimensionality at decision time — providing an early link between the preparation of a contextual signal and the subsequent reduction in computational complexity at decision time. We will include additional analyses to further strengthen this link in the revised manuscript.

eLife Assessment

This study provides potentially important findings on the understanding of circannual timing in mammals, for which iodothyronine deiodinases (DIOs) have been suggested to be of critical importance, yet functional genetic evidence has been missing. The authors aim to implicate dio3, the major inactivator of the biologically active thyroid hormone T3, in circannual timing in Djungarian hamsters, using a combination of correlative and gene knock-out experiments. Currently, several questions have been raised concerning either the methodological description and/or the design of the experiments, and so the experimental evidence is considered incomplete.

Reviewer #1 (Public review):

Circannual timing is a phylogenetically widespread phenomenon in long-lived organisms and is central to the seasonal regulation of reproduction, hibernation, migration, fur color changes, body weight, and fat deposition in response to photoperiodic changes. Photoperiodic control of thyroid hormone T3 levels in the hypothalamus dictates this timing. However, the mechanisms that regulate these changes are not fully understood. The study by Stewart et al. reports that hypothalamic iodothyronine deiodinase 3 (Dio3), the major inactivator of the biologically active thyroid hormone T3, plays a critical role in circannual timing in the Djungarian hamster. Overall, the study yields important results for the field and is well-conducted, with the exception of the CRISPR/Cas9 manipulation.

Figure 1 lays the foundation for examining circannual timing by establishing the timing of induction, maintenance, and recovery phases of the circannual timer upon exposure of hamsters to short photoperiod (SP) by monitoring morphological and physiological markers. Measures of pelage color, torpor, body mass, plasma glucose, etc, established that the initiation phase occurred by weeks 4-8 in SP, the maintenance by weeks 12-20, and the recovery after week 20, where all morphological and physiological changes started to reverse back to long photoperiod phenotypes. The statistical analyses look fine, and the results are unambiguous. Their representation could, however, be improved. In Figures 1d and 1e, two different measures are plotted on each graph and differentiated by dots and upward or downward arrowheads. The plots are so small, though, that distinguishing between the direction of the arrows is difficult. Some color coding would make it more reader-friendly. The same comment applies to Figure S4. The authors went on to profile the transcriptome of the mediobasal and dorsomedial hypothalamus, paraventricular nucleus, and pituitary gland (all known to be involved in seasonal timing) every 4 weeks over the different phases of the circannual interval timer. A number of transcripts displaying seasonal rhythms in expression levels in each of the investigated structures were identified, including transcripts whose expression peaks during each phase. This included two genes of particular interest due to their known modulation of expression in response to photoperiod, Dio3 and Sst, found among the transcripts upregulated during the induction and maintenance phases, respectively. The experiments are technically sound and properly analyzed, revealing interesting candidates. Again, my main issues lie with the representation in the figure. In particular, the authors should clarify what the heatmaps on the right of Figures 1f and 1g represent. I suspect they are simply heatmaps of averaged expression of all genes within a defined category, but a description is missing in the legend, as well as a scale for color coding near the figure.

Figure 2 reveals that SP-programmed body mass loss is correlated to increased Dio3-dependent somatostatin (Sst) expression. First, to distinguish whether the body mass loss was controlled by rheostatic mechanisms and not just acute homeostatic changes in energy balance, experiments from hamsters fed ad lib or experiencing an acute food restriction in both LP and SP were tested. Unlike plasma insulin, food restriction had no additional effect on SP-driven epididymal fat mass loss (Figure S7). This clearly establishes a rheostatic control of body mass loss across weeks in SP conditions. Importantly, Sst expression in the mediobasal hypothalamus increased in both ad lib fed or restriction fed SP hamsters and this increase in expression could be reduced by a single subcutaneous injection of active T3, clearly suggesting that increase in Sst expression in SP is due to a decrease of active T3 likely via Dio3 increase in expression in the hypothalamus. The results are unambiguous.

Figure 3 provides a functional test of Dio3's role in the circannual timer. Mediobasal hypothalamic injections of CRISPR-Cas9 lentiviral vectors expressing two guide RNAs targeting the hamster Dio3 led to a significant reduction in the interval between induction and recovery phases seen in SP as measured by body mass, and diminished the extent of pelage color change by weeks 15-20. In addition, hamsters that failed to respond to SP exposure by decreasing their body mass also had undetectable Dio3 expression in the mediobasal hypothalamus. Together, these data provide strong evidence that Dio3 functions in the circannual timer. I noted, however, a few problems in the way the CRISPR modification of Dio3 in the mediobasal hypothalamus was reported in Figure S8. One is in Figure S8b, where the PAM sites are reported to be 9bp and 11bp downstream of sgRNA1 and sgRNA2, respectively. Is this really the case? If so, I would have expected the experiment to fail to show any effect as PAM sites need to immediately follow the target genomic sequence recognized by the sgRNA for Cas9 to induce a DNA double-stranded break. It seems that each guide contains a 3' NGG sequence that is currently underlined as part of sgRNAs in both Fig S8b and in the method section. If this is not a mistake in reporting the experimental design, I believe that the design is less than optimal and the efficiencies of sgRNAs are rather low, if at all functional. The authors report efficiencies around 60% (line 325), but how these were obtained is not specified. Another unclear point is the degree to which the mediobasal hypothalamus was actually mutated. Only one mutated (truncated) sequence in Figure S8c is reported, but I would have expected a range of mutations in different cells of the tissue of interest. Although the authors clearly find a phenotypic effect with their CRISPR manipulation, I suspect that they may have uncovered greater effects with better sgRNA design. These points need some clarification. I would also argue that repeating this experiment with properly designed sgRNAs would provide much stronger support for causally linking Dio3 in circannual timing.

A proposed schematic model for mechanisms of circannual interval timing is presented in Figure S9. I think this represents a nice summary of the findings put in a broader context and should be presented as a main figure in the manuscript itself rather than being relayed in supplementary materials.

Reviewer #2 (Public review):

Summary:

Several animals and plants adjust their physiology and behavior to seasons. These changes are timed to precede the seasonal transitions, maximizing chances of survival and reproduction. The molecular mechanisms used for this process are still unclear. Studies in mammals and birds have shown that the expression of deiodinase type-1, 2, and 3 (Dio1, 2, 3) in the hypothalamus spikes right before the transition to winter phenotypes. Yet, whether this change is required or an unrelated product of the seasonal changes has not been shown, particularly because of the genetic intractability of the animal models used to study seasonality. Here, the authors show for the first time a direct link between Dio3 expression and the modulation of circannual rhythms.

Strengths:

The work is concise and presents the data in a clear manner. The data is, for the most part, solid and supports the author's main claims. The use of CRISPR is a clear advancement in the field. This is, to my knowledge, the first study showing a clear (i.e., causal) role of Dio3 in the circannual rhythms in mammals. Having established a clear component of the circannual timing and a clean approach to address causality, this study could serve as a blueprint to decipher other components of the timing mechanism. It could also help to enlighten the elusive nature of the upstream regulators, in particular, on how the integration of day length takes place, maybe within the components in the Pars tuberalis, and the regulation of tanycytes.

Weaknesses:

Due to the nature of the CRISPR manipulation, the low N number is a clear weakness. This is compensated by the fact that the phenotypes shown here are strong enough. Also, this is the only causal evidence of Dio3's role; thus, additional evidence would have significantly strengthened the author's claims. The use of the non-responsive population of hamsters also helps, but it falls within the realm of correlations. Additionally, the consequences of the mutations generated by CRISPR are not detailed; it is not clear if the mutations affect the expression of Dio3 or generate a truncation or deletion, resulting in a shorter protein.

Reviewer #3 (Public review):

The authors investigated SP-induced physiological and molecular changes in Djungarian hamsters and the endogenous recovery from it after circa half a year. The study aimed to elucidate the intrinsic mechanism and included nice experiments to distinguish between rheostatic effects on energy state and homeostatic cues driven by an interval timer. It also aimed to elucidate the role of Dio3 by introducing a targeted mutation in the MBH by ICV. The experiments and analyses are sound, and the amount of work is impressive. The impact of this study on the field of seasonal chronobiology is probably high.

Even though the general conclusions are well-founded, I have fundamental criticism concerning 3 points, which I recommend revising:

(1) The authors talk about a circannual interval timer, but this is no circannual timer. This is a circa-semiannual timer. It is important that the authors use precise wording throughout the manuscript.

(2) The authors put their results in the context of clocks. For example, line 180/181 seasonal clock. But they have described and investigated an interval timer. A clock must be able to complete a full cycle endogenously (and ideally repeatedly) and not only half of it. In contrast, a timer steers a duration. Thus, it is well possible that a circannual clock mechanism and this circa-semiannual timer of photoperiodic species are 2 completely different mechanisms. The argumentation should be changed accordingly.

(3) The authors chose as animal model the Djungarian hamster, which is a predominantly photoperiodic species and not a circannual species. A photoperiodic species has no circannual clock. That is another reason why it is difficult to draw conclusions from the experiment for circannual clocks. However, the Djungarian hamster is kind of "indifferent" concerning its seasonal timing, since a small fraction of them are indeed able to cycle (Anchordoquy HC, Lynch GR (2000), Evidence of an annual rhythm in a small proportion of Siberian hamsters exposed to chronic short days. J Biol Rhythms 15:122-125.). Nevertheless, the proportion is too small to suggest that the findings in the current study might reflect part of the circannual timing.

Therefore, the authors should make a clear distinction between timers and clocks, as well as between circa-annual and circa-semiannual durations/periods.

eLife Assessment

Avoidance of UV and blue light by the nematode C. elegans is mediated by the unusual transmembrane protein LITE-1, a non-canonical photoreceptor. In this valuable work, the authors provide convincing evidence that LITE-1 function is also required for avoidance of very high concentrations of the food-associated cue diacetyl, suggesting that it may also function as a diacetyl chemoreceptor. While the evidence for this idea is incomplete, these intriguing findings suggest an unexpected complexity in the function of this unusual photoreceptor.

Reviewer #1 (Public review):

Summary:

This paper describes an interesting phenotype of C. elegans lite-1 mutants. Previous work showed that lite-1 mutants lose a violet/blue light avoidance response. The authors show here that lite-1 mutants also show a defect in negative diacetyl chemotaxis. While wild-type worms avoid diacetyl at high concentrations, lite-1 mutants are instead *attracted* to it. The authors go on to perform Ca2+ imaging in sensory neurons and find that ADL and ASK neurons show altered Ca2+ responses to diacetyl in lite-1 mutants, suggesting LITE-1 is required for these responses. As unc-13 mutants with defective synaptic transmission show similar diacetyl Ca2+ responses as wild-type, this suggests these neurons respond cell autonomously to diacetyl. However, whether lite-1 also acts cell-autonomously is not discussed. Indeed, because unc-13 and lite-1 mutants show different ADL and ASK Ca2+ responses, it seems the diacetyl response regulated by LITE-1 is likely acting outside of those cells. An interesting result that is not commented on is the switching of the valence of the ASK Ca2+ response in lite-1 mutants. ASK neurons still respond to diacetyl, but instead of a strong increase in Ca2+, diacetyl appears to drive it strongly lower. This may be consistent with the switch in valence in the diacetyl chemotaxis assay. It also argues against the idea that LITE-1 is a low-affinity diacetyl receptor that drives avoidance or the Ca2+ responses in ASK, since it is still present in lite-1 mutants. The authors then use a strain that expresses LITE-1 in the body wall muscles and show this expression is sufficient to engender them with sensitivity to diacetyl, as measured through altered swimming and hypercontractility. The authors interpret this result as LITE-1 may act as a diacetyl receptor. The authors test whether a structurally similar molecule, 2,3-pentanedione, shows similar effects, and they find it does. Alpha-fold modeling and molecular docking analysis show where diacetyl might bind to the LITE-1 protein. They then test whether lite-1 mutants show chemotaxis defects to other molecules, as seen with diacetyl. Generally, they find that the observed diacetyl responses are unique, although lite-1 mutants do lose their avoidance response to 2,3-pentanedione. However, unlike the acquisition of diacetyl attraction in lite-1 mutants, 2,3 pentanedione avoidance is *lost*; it is not switched to attraction. Overall, I felt the description of the results and their implications could have been more in-depth. Further, the evidence that LITE-1 is a chemoreceptor itself, rather than acting in some way to shape chemoreceptor responses (via light or otherwise), remains unclear, as conceded by the authors.

Strengths:

Overall, the study follows up on an interesting and useful result. The experiments as presented are generally well-conceived and performed. The authors use a variety of behavioral and imaging approaches to test how LITE-1 mediates diacetyl avoidance.

Weaknesses:

The study is missing experiments needed to resolve whether LITE-1 is doing what they propose. The evidence that LITE-1 is a diacetyl receptor is lacking support since lite-1 mutants have their avoidance and calcium responses flipped, which would not be expected if it were acting solely as an avoidance receptor. Presumably, the authors are concluding that the attractive response that is left in the lite-1 mutant is mediated by ODR-10, but that experiment is not shown. Similarly, the authors concede that "the use of lite-1 point mutants that affect specific LITE-1 function, such as light sensing, channel gating, or binding pocket, could further elucidate LITE-1 mechanisms." This reviewer agrees, and such experiments designed to localize diacetyl binding site(s) would be necessary to conclude definitively that LITE-1 is a diacetyl receptor. The body wall muscle assay used or some other heterologous experimental system could work for such a structure-function analysis. A concern is whether the extensive number of LITE-1 point mutants described in the literature affect cell surface expression vs. receptor function, which might complicate the interpretation of a result showing loss of diacetyl responses.

Reviewer #2 (Public review):

Summary:

Koh and colleagues investigate the broader sensory role of LITE-1, a gustatory receptor previously linked to UV light detection in C. elegans. Their study explores whether LITE-1 also mediates avoidance of specific chemical stimuli-namely, high concentrations of diacetyl and 2,3-pentanedione. They show that LITE-1 is required in the ADL and ASK neurons for calcium responses to diacetyl, and that its expression in body-wall muscles is sufficient to trigger hypercontraction upon odorant exposure. Molecular docking suggests both odorants may directly bind to LITE-1 with micromolar affinity. These findings suggest LITE-1 may act as a multimodal receptor for both light and chemical stimuli.

Strengths:

(1) Methodological Precision: The study is technically strong, with well-executed calcium imaging and quantitative behavioral assays that clearly show neural and muscular responses to chemical stimuli.

(2) Novelty and Scope: The work presents a compelling case for LITE-1 functioning as a multimodal sensor, which is an intriguing expansion of its known role.

(3) Potential Impact: If validated, the findings could significantly advance the understanding of sensory integration in C. elegans, and the tools developed may be broadly useful to the research community.

(4) Relevance to the Field: The study adds to evidence that C. elegans uses non-canonical sensory pathways and may inspire further exploration of multimodal receptor functions in other systems.

Weaknesses:

(1) Lack of Rescue Experiments: The absence of rescue experiments makes it difficult to definitively link the observed phenotypes to loss of lite-1.

(2) Single Loss-of-Function Approach: The reliance on a single genetic mutant limits interpretability. Additional strategies such as RNAi (e.g., neuron-specific knockdown) would provide stronger evidence.

(3) Unclear Neuronal Contribution: While calcium responses in ADL and ASK are reduced, it's unclear which neuron(s) are necessary for behavioral avoidance. Cell-specific rescue or knockdown experiments are needed.

(4) Unvalidated Docking Data: The molecular docking predictions lack experimental validation. Site-directed mutagenesis would be needed to support claims of direct interaction.

(5) Limited Odorant Specificity Testing: Docking analysis does not include non-binding odorants, making it difficult to assess binding specificity.

(6) Incomplete Quantification: Some calcium imaging results (e.g., in AWA neurons of unc-13 mutants) lack statistical comparisons, which limits their interpretive value.

Reviewer #3 (Public review):

In this work, Brown and colleagues report that the photosensor protein LITE-1 of the nematode C. elegans may also be a chemosensor that can be activated by high concentrations of the compound diacetyl. LITE-1 was described as a putative ion channel of the gustatory receptor family, which is mainly constituted by insect odorant receptors. These form tetrameric ion channels that can be activated by odorants. Specificity is achieved by forming heteromeric channels from three copies of the odorant receptor co-receptor (ORCO) and another subunit that resembles ORCO in the pore-forming C-terminus, but brings in a binding site for the respective odorant. LITE-1 has a very similar structure, according to Alphafold3 predictions, and also carries a binding pocket. In LITE-1, this was proposed to be occupied by a light-absorbing molecule that activates the channel when a photon is absorbed. Alternatively, compounds generated by absorption of high-energy photons may be formed in vivo and bound by the LITE-1 binding pocket. Koh et al. now demonstrate that another, non-light-activated compound, diacetyl, at high concentrations, can activate cells expressing LITE-1. Such (chemosensory) cells are also responsible for the avoidance of high concentrations of diacetyl. LITE-1 activation in excitable cells, i.e, muscles, causes strong body contraction and paralysis, and the authors show that this is also the case when diacetyl is presented. The authors further present molecular docking studies showing that diacetyl could occupy the binding pocket of LITE-1. Last, they show that another compound chemically resembling diacetyl, i.e., 2,3-pentanedione, can also induce avoidance in a LITE-1 dependent manner, though not as potently.

The data are intriguing, and the demonstration of LITE-1 being a diacetyl chemosensor is interesting. Yet, there are a few questions arising that the authors should address.

The authors identified mutants lacking diacetyl responses. In their chemotaxis assay (Figures 1A, B), they show that lite-1 mutants do not avoid high concentrations of diacetyl. However, the animals actually showed attraction, as the chemotaxis index was positive. If the lite-1 animals were insensitive, they should be indifferent, and the chemotaxis index should be close to zero. This means, other neurons contribute to the diacetyl response, and the result of these neurons being activated means/remains attraction? If so, the authors need to rule out any effects of these neurons on the effects they attribute to LITE-1 in the other assays.

The effect of diacetyl on muscle cells (Figure 3C) is pretty rapid, i.e., already during 1 minute after application, the animals are almost maximally contracted. How fast is it really? Can the authors provide a time course with more time points during the first minute? This is a relevant question, as the compound would have to either pass the worm cuticle or enter through the gut and diffuse through the body to reach the muscle cells. Can one expect this to occur within (less than) a minute?

In this context, the authors need to rule out that other mechanisms may be at play. E.g., diacetyl may be immediately sensed by ciliated chemosensory neurons that might release a signaling molecule that leads to activation of LITE-1 in muscles, or that sensitizes it somehow, responding to light used for filming animals. The authors should repeat this assay in a lite-1 mutant background. Furthermore, the authors tested unc-13 mutants to rule out indirect effects on the neurons recorded. Likewise, they should eliminate neuropeptide signaling via unc-31 mutants (a recent paper cited by the authors showed involvement of neuropeptide signaling in LITE-1-mediated light avoidance behavior). Last, to demonstrate that effects are not indirect in response to chemosensory neurons, the authors should repeat the contraction or swimming assay in a tax-4 mutant, which largely lacks chemosensation. This also applies to the chemotaxis assay. Animals should exhibit a chemotaxis index to diacetyl of zero, then.

Does diacetyl activate other neurons expressing LITE-1? A number of cells express LITE-1 at high levels, which the authors have not tested (they restricted their analyses to chemosensory neurons). This is important to address because it leaves the possibility that LITE-1 requires a specific partner only present in these chemosensory neurons to detect diacetyl. This partner would have to be present also in muscles, where diacetyl could activate ectopically expressed LITE-1. According to CeNGEN scRNAseq data, cells expressing LITE-1 can be identified. The ADL and ASH neurons actually come up only at the lowest threshold, so some of the other cells showing much higher levels of LITE-1 mRNAs, i.e., AVG, ALM, PLM, ASG, PHA, PHB, AVM, RIF, or some pharyngeal neurons, should be tested. ASG was among the cells the authors recorded from, but this neuron did not show a response.

The authors need to show that diacetyl responses of ADL and/or ASK can be rescued by expressing LITE-1 specifically in these neurons in a lite-1 mutant background.

Molecular docking studies are not described in detail. How was this done? Diacetyl is a very small molecule. How well can docking algorithms assess this at all? Did the authors preselect the binding pocket, or did the algorithm sample the entire molecular surface of the LITE-1 model and end up with the binding pocket? The latter would be very convincing. The authors should provide control docking experiments with other molecules that caused avoidance in their hands (i.e. benzaldehyde, 2,4,5,trimethlythiazole, isoamyl alcohol, nonanone, octanone), but did not activate LITE-1. Also, they should try docking molecules related to diacetyl, and if there are some that do not dock under the same conditions, such molecules should be used in a behavioral experiment. Ideally, they should also not activate LITE-1. Examples could be, e.g., diacetyl monoxime or 2,4-pentanedione.

Last, the authors should provide a PDB file with the docked diacetyl to allow readers to assess the binding for themselves. Since a large number of mutations of LITE-1 have been reported, it may be that amino acids shown to be essential for LITE-1 function are also required for diacetyl binding. If so, this could be backed up with an experiment.

eLife Assessment

This study examines how the neuronal cytoskeleton contributes to the formation of the axonal membrane-associated periodic skeleton (MPS) in embryonic dorsal root ganglia (DRG) neurons, using STED imaging. Conclusions are supported by convincing methods, data, and analyses. This useful work confirms previous data and improves our understanding of the roles of microtubules and actin dynamics in the chronological recruitment of MPS components.

Reviewer #1 (Public review):

The axonal membrane periodic skeleton (MPS) comprises axially aligned tetramers of α and β spectrins that are attached to evenly distributed radial F-actin rings, which maintain a<br /> typical spacing of 180 - 190 nm. The exact molecular mechanisms underlying the early organization have been unclear. The focus of this study is on those mechanisms.

This is a comprehensive and professionally carried out study. It brings convincing evidence that intact actin and microtubules are required for normal development of MPS and that the actin-binding and lipid-interacting domains of βII-spectrin are critical for its subplasmalemmal confinement and, subsequently, MPS maturation. However, whilst the study does bring new insights, we are still missing the overall understanding of how everything comes together.

The study describes, using spectrin mutations, that the membrane and actin binding of spectrin are required for the proper organization of MPS. However, it is unclear how everything could come together mechanistically.

The authors follow how the MPS is organized by looking at spectrin. Latrunculin affects actin polymerization, as well as CK666 and formin inhibition, but it remains unclear which actin structures are affected. The same is true for microtubules; while they are affected, we don't know how they are affected.

Reviewer #2 (Public review):

Summary:

In their manuscript, Bodas et al present a chronological analysis of the development of the axonal MPS in embryonic DRG neurons, using a series of biochemical assays coupled with STED nanoscopy. Several interesting conclusions, well supported by the data presented, are drawn that further our understanding of bII-spectrin axonal recruitment and on the role of microtubules and actin dynamics during the early MPS formation and at the latter stages of neuronal maturation.

Strengths:

The assays presented are well-designed, and the results obtained clearly support the main conclusions drawn by the authors. Their findings highlight important aspects of cytoskeleton regulation and dynamics required for MPS formation/maintenance, i.e, during different stages of neuronal development, that remained undocumented.

Weaknesses:

The study is mostly limited to biochemical assays followed by STED microscopy to analyse MPS periodicity and (in certain cases) axonal diameter. Functional implications of the manipulations done are lacking, as well as analyses of axonal integrity/degeneration. This is a relevant aspect, as some of the effects observed may be a secondary effect of decreased neuronal/axonal viability.

Reviewer #3 (Public review):

Summary:

In this study, Shivani Bodas et al. investigate the role of actin, actin-binding proteins, and microtubules in regulating the membrane-associated periodic skeleton (MPS) in neuronal axons. The MPS, first reported by Ke Xu et al. in 2013 (Science), has since been implicated in various neuronal functions, including mechanical support, axonal diameter control, axonal degeneration regulation, and spatial organization of signaling molecules. Given its biological importance, further elucidation of MPS assembly mechanisms is of considerable interest. However, I have concerns regarding the novelty and strength of the conclusions presented in this work. Many of the findings largely reiterate previously published observations, and the most novel conclusions are not fully substantiated by the data.

Strengths:

(1) The MPS represents a structurally and functionally important cytoskeletal system in neurons. Studies aimed at understanding its developmental mechanisms are biologically meaningful and potentially impactful.

(2) The authors attempt to dissect MPS assembly during early neuronal development, a process that could offer mechanistic insight into how the MPS is established and maintained.

Weaknesses:

(1) Limited Novelty Across Results Sections:

Of the seven Results sections, only one (Figure 6) and part of another (Figure 9) present data leading to relatively novel interpretations, specifically, the authors' claim that βII-spectrin is recruited to the axonal cortex via F-actin interactions as early as DIV1, followed by rearrangement into a periodic structure by DIV4. However, this conclusion is not fully supported (see below). The remaining results (Figures 1-5, 7, and 8) largely recapitulate findings reported in earlier studies and thus add limited new knowledge.

(2) Insufficient Evidence for Early Recruitment and Rearrangement of βII-spectrin:

The claim that βII-spectrin is recruited to the axonal cortex via F-actin interactions as early as at DIV 1 and subsequently reorganized into a periodic structure during DIV1-4 is central to the manuscript but lacks robust experimental support.

On Page 17, Line 526, the authors the authors state that " To exclude cytoplasmic spectrin resulting from overexpression, only axons with low expression of βII spectrin-GFP were selected for the analysis". However, selecting for low expression alone does not guarantee the absence of cytoplasmic signal. Without volumetric imaging (e.g., 3D super-resolution imaging to see the cross section of axons), it is difficult to definitively conclude that the FRAP data (Figures 6 and 9) reflect cortical rather than cytoplasmic localization.

Prior FRAP studies (Zhong et al., eLife 2014) observed minimal fluorescence recovery over 1800 seconds in axons expressing βII-spectrin-GFP at low levels, with faster recovery (~200-300 seconds) only evident under high expression conditions. The fast recovery kinetics (tens of seconds) reported in this manuscript could plausibly result from free diffusion of cytoplasmic βII-spectrin-GFP rather than cortical turnover.

Furthermore, on Page 10, Line 310, the authors assert that endogenous βII-spectrin "is recruited early to the axonal cortex, followed by progressive establishment of periodic order". However, the STED images shown in Figure 1 do not convincingly distinguish between cortical and cytoplasmic pools.

As such, the observed disordered βII-spectrin molecules, whether overexpressed or endogenous, could still represent a diffuse cytoplasmic population. An alternative and perhaps more parsimonious interpretation is that βII-spectrin is initially cytoplasmic and only later recruited and arranged into periodic structures at the cortex.

(3) Use of Pharmacological Perturbations:

Like many earlier studies, this manuscript relies heavily on pharmacological perturbation (e.g., cytoskeletal drugs) to assess the roles of actin, actin-binding proteins, and microtubules in MPS assembly. While this approach is widely used, it is important to acknowledge that such agents may have off-target effects. The manuscript would benefit from greater caution in interpreting these results, or better yet, the inclusion of genetic or optogenetic approaches to independently validate these findings.

eLife Assessment

These findings are among some of the first to identify a behavioral and neurobiological substrate that disentangles nonassociative from associative fear responses following stress, providing a fundamental push forward in the field. The evidence supporting this is convincing and uses a variety of conceptual and technological approaches. This investigation will be of interest to neuroscientists and behaviourists broadly, as well as clinicians for its relevance to post-traumatic stress disorder.

Reviewer #1 (Public review):

Summary:

This study delineates a highly specific role for the pPVT in unconditioned defensive responses. The authors use a novel, combined SEFL and SEFR paradigm to test both conditioned and unconditioned responses in the same animal. Next, a c-fos mapping experiment showed enhanced PVT activity in the stress group when exposed to the novel tone. No other regions showed differences. Fiber photometry measurements in pPVT showed enhancement in response to the novel tone in the stressed but not non-stressed groups. Importantly, there were also no effects when calcium measurements were taken during conditioning. Using DREADDS to bidirectionally manipulate global pPVT activity, inhibition of the PVT reduced tone freezing in stressed mice while stimulation increased tone freezing in non-stressed mice.

Strengths:

A major strength of this research is the use of a multi-dimensional behavioral assay that delineates behavior related to both learned and non-learned defensive responses. The research also incorporates high-resolution approaches to measure neuronal activity and provide causal evidence for a role for PVT in a very narrow band of defensive behavior. The data are compelling, and the manuscript is well-written overall.

Weaknesses:

Figure 1 shows a small, but looks to be, statistically significant, increase in freezing in response to the novel tone in the no-stress group relative to baseline freezing. This observation was also noticed in Figures 2 and 7. The tone presented is relatively high frequency (9 kHz) and high dB (90), making it a high-intensity stimulus. Is it possible that this stimulus is acting as an unconditioned stimulus? In addition, in the final experiment, the tone intensity was increased to 115 dB, and the freezing % in the non-stressed group was nearly identical (~20%) to the non-stressed groups in Figures 1-2 and Figure 7. It seems this manipulation was meant as a startle assay (Pantoni et al., 2020). Because the auditory perception of mice is better at high frequencies (best at ~16 kHz), would the effect seen be evident at a lower dB (50-55) at 9 kHz? If the tone was indeed perceived as "neutral," there should be no freezing in response to the tone. This complicates the interpretation of the results somewhat because while the authors do admit the stimulus is loud, would a less loud stimulus result in the same effect? Could the interaction observed in this set of studies require not a novel tone, but rather a high-intensity tone that elicits an unconditioned response? Along these same lines, it appears there may be an elevation in c-fos in the PVT in the non-stress tone test group versus the no-stress home cage control, and overall it appears that tone increases c-fos relative to homecage. Could PVT be sensitive to the tone outside of stress? Would there be the same results with a less intense stimulus? I would also be curious to know what mice in the non-stressed group were doing upon presentation of the tone besides freezing. Were any startle or orienting responses noticed?

Reviewer #2 (Public review):

Summary:

Nishimura and colleagues present findings of a behavioral and neurobiological dissociation of associative and nonassociative components of Stress Enhanced Fear Responding (SEFR).

Strengths:

This is a strong paper that identifies the PVT as a critical brain region for SEFR responses using a variety of approaches, including immunohistochemistry, fiber photometry, and bidirectional chemogenetics. In addition, there is a great deal of conceptual innovation. The authors identify a dissociable behavior to distinguish the effects of PVT function (among other brain regions).

Weaknesses:

(1) The authors find a lack of difference between the Stress and No Stress groups in pPVT activity during SEFL conditioning with fiber photometry but an increase in freezing with Gq DREADD stimulation. How do authors reconcile this difference in activity vs function?

(2) Because the PVT plays a role in defensive behaviors, it would be beneficial to show fiber photometry data during freezing bouts vs exclusively presented during tone a shock cue presentations.

(3) Similar to the above point, were other defensive behaviors expressed as a result of footshock stress or PVT manipulations?

(4) Tone attenuation in Figure 8 seems to be largely a result of minimal freezing to a 115-dB tone. While not a major point of the paper, a more robust fear response would be convincing.

(5) In the open field test, the authors measure total distance. It would be beneficial to also show defensive behavioral (escape, freezing, etc) bouts expressed.

(6) The authors, along with others, show a behavioral and neural dissociation of footshock stress on nonassociative vs associative components of stress; however, the nonassociative components as a direct consequence of the stress seem to be necessary for enhancement of associative aspects of fear. Can authors elaborate on how these systems converge to enhance or potentiate fear?

(7) In the discussion, authors should elaborate on/clarify the cell population heterogeneity of the PVT since authors later describe PVT neurons as exclusively glutamatergic.

Reviewer #3 (Public review):

Summary:

The manuscript by Nishimura et al. examines the behavioural and neural mechanisms of stress-enhanced fear responding (SEFR) and stress-enhanced fear learning (SEFL). Groups of stressed (4 x shock exposure in a context) vs non-stressed (context exposure only) animals are compared for their fear of an unconditioned tone, and context, as well as their learning of new context fear associations. Shock of higher intensity led to higher levels of unlearned stress-enhanced fear expression. Immediate early gene analysis uncovered the PVT as a critical neural locus, and this was confirmed using fiber photometry, with stressed animals showing an elevated neural signal to an unconditioned tone. Using a gain and loss of function DREADDs methodology, the authors provide convincing evidence for a causal role of the PVT in SEFR.

Strengths:

(1) The manuscript uses critical behavioural controls (no stress vs stress) and behavioural parameters (0.25mA, 0.5mA, 1mA shock). Findings are replicated across experiments.

(2) Dissociating the SEFR and SEFL is a critical distinction that has not been made previously. Moreover, this dissociation is essential in understanding the behavioural (and neural) processes that can go awry in fear.

(3) Neural methods use a multifaceted approach to convincingly link the PVT to SEFR: from Fos, fiber photometry, gain and loss of function using DREADDs.

Weaknesses:

No weaknesses were identified by this reviewer; however, I have the following comments:

A closer examination of the Test data across time would help determine if differences may be present early or later in the session that could otherwise be washed out when the data are averaged across time. If none are seen, then it may be worth noting this in the manuscript.

Given the sex/gender differences in PTSD in the human population, having the male and female data points distinguished in the figures would be helpful. I assume sex was run as a variable in the statistics, and nothing came as significant. Noting this would also be of value to other readers who may wonder about the presence of sex differences in the data.

eLife Assessment

The authors show that innate defensive behavior in mice is shaped by threat intensity, reward value, and social hierarchy, highlighting how value and social context influence instinctive decisions. The authors provide useful behavioural findings supported by strong data, yet the evidence is incomplete due to ambiguities about methodology and the computational model that remains largely descriptive.

Reviewer #1 (Public review):

Summary:

This study investigates how mice make defensive decisions when exposed to visual threats and how those decisions are influenced by reward value and social hierarchy. Using a naturalistic foraging setup and looming stimuli, the authors show that higher threat leads to faster escape, while lower threat allows mice to weigh reward value. Dominant mice behave more cautiously, showing higher vigilance. The behavioral findings are further supported by a computational model aimed at capturing how different factors shape decisions.

Strengths:

(1) The behavioral paradigm is well-designed and ethologically relevant, capturing instinctive responses in a controlled setting.

(2) The paper addresses an important question: how defensive behaviors are influenced by social and value-based factors.

(3) The classification of behavioral responses using machine learning is a solid methodological choice that improves reproducibility.

Weaknesses:

(1) Key parts of the methods are hard to follow, especially how trials are selected and whether learning across trials is fully controlled for. For example, it is unclear whether animals are in the nest during the looming stimulus presentations. The main text and methods should clarify whether multiple mice are in the nest simultaneously and whether only one mouse is in the arena during looming exposure. From the description, it seems that all mice may be freely exploring during some phases, but only one is allowed in the arena at a time during stimulus presentation. This point is important for understanding the social context and potential interactions, and should be clearly explained in both the main text and methods.

(2) It is often unclear whether the data shown (especially in the main summary figures) come from the first trial or are averages across several exposures. When is the cut-off for trials of each animal? How do we know how many trial presentations were considered, and how learning at different rates between individuals is taken into account when plotting all animals together? This is important because the looming stimulus is learned to be harmless very quickly, so the trial number strongly affects interpretation.

(3) The reward-related effects are difficult to interpret without a clearer separation of learning vs first responses.

(4) The model reproduces observed patterns but adds limited explanatory or predictive power. It does not integrate major findings like social hierarchy. Its impact would be greatly improved if the authors used it to predict outcomes under novel or intermediate conditions.

(5) Some conclusions (e.g., about vigilance increasing with reward) are counterintuitive and need stronger support or alternative explanations. Regarding the interpretation of social differences in area coverage, it's also possible that the observed behavioral differences reflect access to the nesting space. Dominant mice may control the nest, forcing subordinates to remain in the open arena even during or after looming stimuli. In this case, subordinates may be choosing between the threat of the dominant mouse and the external visual threat. The current data do not distinguish between these possibilities, and the authors do not provide evidence to support one interpretation over the other. Including this alternative explanation or providing data that addresses it would strengthen the conclusions.

(6) While potential neural circuits are mentioned in the discussion, an earlier introduction of candidate brain regions and their relevance to threat and value processing would help ground the study in existing systems neuroscience.

(7) Some figures are difficult to interpret without clearer trial/mouse labeling, and a few claims in the text are stronger than what the data fully support. Figure 3H is done for low contrast, but the interesting findings will be to do this experiment with high contrast. Figure 4H - I don't understand this part. If the amount of time in the center after the loom changes for subordinate mice, how does this lead to the conclusion that they spend most of their time in the reward zone?. Figure 3A - The example shown does not seem representative of the claim that high contrast stimuli are more likely to trigger escape. In particular, the 10% sucrose condition appears to show more arena visits under low contrast than high contrast, which seems to contradict that interpretation. Also, the plot currently uses trials on the Y-axis, but it would be more informative to show one line per animal, using only the first trial for each. This would help separate initial threat responses from learning effects and clarify individual variability.

(8) The analysis does not explore individual variability in behavior, which could be an important source of structure in the data. Without this, it is difficult to know whether social hierarchy alone explains behavioral differences or if other stable traits (e.g., anxiety level, prior experiences) also contribute.

(9) The study shows robust looming responses in group-housed animals, which contrasts with other studies that often require single housing to elicit reliable defensive responses. It would be valuable for the authors to discuss why their results differ in this regard and whether housing conditions might interact with social rank or habituation.

Reviewer #2 (Public review):

Zhe Li and colleagues investigate how mice exposed to visual threats and rewards balance their decisions in favour of consuming rewards or engaging in defensive actions. By varying threat intensity and reward value, they first confirm previous findings showing that defensive responses increase with threat intensity and that there is habituation to the threat stimulus. They then find that water-deprived mice have a reduced probability of escaping from low contrast visual looming stimuli when water or sucrose are offered in the environment, but that when the stimulus contrast is high, the presence of sucrose or water increases the probability of escape. By analysing behaviour metrics such as the latency to flee from the threat stimulus, they suggest that this increase in threat sensitivity is due to increased vigilance. Analysis of this behaviour as a function of social hierarchy shows that dominant mice have higher threat sensitivity, which is also interpreted as being due to increased vigilance. These results are captured by a drift diffusion model variant that incorporates threat intensity and reward value.

The main contribution of this work is to quantify how the presence of water or sucrose in water-deprived mice affects escape behaviour. The differential effects of reward between the low and high contrast conditions are intriguing, but I find the interpretation that vigilance plays a major role in this process is not supported by the data. The idea that reward value exerts some form of graded modulation of the escape response is also not supported by the data. In addition, there is very limited methodological information, which makes assessing the quality of some of the analyses difficult, and there is no quantification of the quality of the model fits.

(1) The main measure of vigilance in this work is reaction time. While reaction time can indeed be affected by vigilance, reaction times can vary as a function of many variables, and be different for the same level of vigilance. For example, a primate performing the random dot motion task exhibits differences in reaction times that can be explained entirely by the stimulus strength. Reaction time is therefore not a sound measure of vigilance, and if a goal of this work is to investigate this parameter, then it should be measured. There is some attempt at doing this for a subset of the data in Figure 3H, by looking at differences in the action of monitoring the visual field (presumably a rearing motion, though this is not described) between the first and second trials in the presence of sucrose. I find this an extremely contrived measure. What is the rationale for analysing only the difference between the first and second trials? Also, the results are only statistically significant because the first trial in the sucrose condition happens to have zero up action bouts, in contrast to all other conditions. I am afraid that the statistics are not solid here. When analysing the effects of dominance, a vigilance metric is the time spent in the reward zone. Why is this a measure of vigilance? More generally, measuring vigilance of threats in mice requires monitoring the position of the eyes, which previous work has shown is biased to the upper visual field, consistent with the threat ecology of rodents.

(2) In both low and high contrast conditions, there are differences in escape behaviour between no reward and water or sucrose presence, but no statistically significant differences between water and sucrose (eg, Figure 3B). I therefore find that statements about reward value are not supported by the data, which only show differences between the presence or absence of reward. Furthermore, there is a confound in these experiments, because according to the methods, mice in the no-reward condition were not water deprived. It is thus possible that the differences in behaviour arise from differences in the underlying state.

(3) There is very little methodological information on behavioural quantification. For example, what is hiding latency? Is this the same are reaction time? Time to reach the safe zone? What exactly is distance fled? I don't understand how this can vary between 20 and 100cm. Presumably, the 20cm flights don't reach the safe place, since the threat is roughly at the same location for each trial? How is the end of a flight determined? How is duration measured in reward zone measures, e.g., from when to when? How is fleeing onset determined?

(4) There is little methodological information on how the model was fit (for example, it is surprising that in the no reward condition, the r parameter is exactly 0. What this constrained in any way), and none of the fit parameters have uncertainty measures so it is not possible to assess whether there are actually any differences in parameters that are statistically significant.

Reviewer #3 (Public review):

Male mice were tested in a classic behavioral "flee the looming stimulus" paradigm. This is a purely behavioral study; no neural analyses were done. Mice were housed socially, but faced the looming stimulus individually. Drift-diffusion modeling found that reward-level interacted with threat level such that at low-threat levels, reward contrasted with threat as classically expected (high reward overwhelms low threat, low threat overwhelms low reward), but that reward aligned with threat at higher threat levels.

Note that they define threat level by the darkness of the looming stimulus. I am not sure that darker stimuli are more threatening to mice. But maybe. Figure 3 shows that mice react more quickly to high contrast looming stimuli, but can the authors distinguish between the ability to detect the visual signal from considering it a more dangerous threat? (The fact that vigilance makes a difference in the high contrast condition, not the low contrast condition, actually supports the author's hypotheses here.)

The drift-diffusion model (DDM) is fine. I note that the authors included a "leakage rate", which is not a standard DDM parameter (although I like including it). I would have liked to see more about the parameters. What were the distributions? What did the parameters correlate with behaviorally? I would have liked to see distributions of the parameters under the different conditions and different animals. Figure 2C shows the progression of learning. How do the fit parameters change over time as mice shift from choice to choice? How do the parameters change over mice? How do the parameters change over distance to the threat/distance to safety (as per Fanselow and Lester 1988)? They did a supplemental experiment where the threat arrived halfway along the corridor - we could get a lot more detail about that experiment - how did it change the modeling?

Overall, this is a reasonable study showing mostly unsurprising results. I think the authors could do more to connect the vigilance question to their results (which seems somewhat new to me).

Although the data appear generally fine and the modeling reasonable, the authors do not do the necessary work to set themselves within the extensive literature on decision-making in mice retreating from threats.

First of all, this is not a new paradigm; variants of this paradigm have been used since at least the 1980s. There is an *extensive* literature on this, including extensive theoretical work on the relation of fear and other motivational factors. I recommend starting with the classic Fanselow and Lester 1988 paper (which they cite, but only in passing), and the reviews by Dean Mobbs and Jeansok Kim, and by Denis Paré and Greg Quirk, which have explicit theoretical proposals that the authors can compare their results to. I would also recommend that the authors look into the "active avoidance" literature. Moreover, to talk about a mouse running from a looming stimulus without addressing the other "flee the predator" tasks is to miss a huge space for understanding their results. Again, I would start with the reviews above, but also strongly urge the authors to look at the Robogator task (work by June-Seek Choi and Jeansok Kim, work by Denis Paré, and others).

Similarly, in their anatomical review, they do not mention the amygdala. Given the extensive literature on the role of the amygdala in retreating from danger, both in terms of active avoidance and in terms of encoding the danger itself, it would surprise me greatly if this behavior does not involve amygdala processing. (If there is evidence that the amygdala does not play a role here, but that the superior colliculus does, then that would be a *very* important result that needs to be folded into our understanding of decision-making systems and neural computational processing.)

Second, there is an extensive economic literature on non-human animals in general and on rodents in particular. Again, the authors seem unaware of this work, which would provide them with important data and theories to broaden the impact of their results (by placing them within the literature). First, there are explicit economic literatures in terms of positively-valenced conflicts (e.g., neuroeconomics within the primate literature, sequential foraging and delay-discounting tasks within the rodent literature), but also there is a long history within the rodent conditioning world, such as the classic work by Len Green and Peter Shizgal. I would strongly urge the authors to explore the motivational conflict literature by people like Gavin McNally, Greg Quirk, and Mark Andermann. Again, putting their results into this literature will increase the impact of their experiment and modeling.

eLife Assessment

This is a methodologically rich manuscript that is important for elucidating the neural mechanisms of expectation in perception. The analyses are convincing in extending analogous findings in attention and working memory. With further clarification, the findings will be of broad interest to vision researchers.

Reviewer #1 (Public review):

Summary:

The authors tested two competing mechanisms of expectation: (1) a sharpening model that suppresses unexpected information via center-surround inhibition; (2) a cancelation model that predicts a monotonic gradient response profile. Using two psychophysical experiments manipulating feature space distance between expected and unexpected stimuli, the results consistently supported the sharpening model. Computational modeling further showed that expectation effects were explained by either sharpened tuning curves or tuning shifts. Finally, convolutional neural network simulations revealed that feedback connections critically mediate the observed center-surround inhibition.

Strengths:

The manuscript provides compelling and convergent evidence from both psychophysical experiments and computational modeling to robustly support the sharpening model of expectation, demonstrating clear center-surround inhibition of unexpected information.

Weaknesses:

The manuscript could directly validate the experimental manipulations and address how these results reconcile with existing literature on expectation effects.

Reviewer #2 (Public review):

Summary:

This is a compelling and methodologically rich manuscript. The authors used a variety of methods, including psychophysics, computational modeling, and artificial neural networks, to reveal a non-monotonic, center-surround "Mexican-hat" profile of expectation in orientation space. Their data convincingly extend analogous findings in attention and working memory, and the modeling nicely teases apart sharpening vs. shift mechanisms.

Strengths:

The findings are novel and important in elucidating the potential neural mechanisms by which expectation shapes perception. The authors conducted a series of well-designed psychophysical experiments to careful examination of the profile of expectation's modulation. Computational modeling also provides further insights, linking the neural mechanisms of expectation to behavioral results.

Weaknesses:

There are several aspects that could be strengthened or clarified.

(1) The sharpening model of expectation can predict surround suppression. The authors could further clarify how the cancellation model predicts a monotonic profile of expectation (Figure 1C) with the highest response at the expected orientation, while the cancellation model suggests a suppression of neurons tuned toward the expected stimulus.

(2) I'm a bit concerned about whether the profile solely arises from modulation of expectation. The two auditory cues are each associated with a fixed orientation, which may be confounded by other cognitive processes like visual working memory or attention (which I think the authors also discussed). Although the authors tried to use SFD task to render orientation task-irrelevant, luminance edges (i.e., orientation) and spatial frequency in gratings are highly intertwined and orientation of the gratings may help recall the first grating's SF (fixed at 0.9 c/{degree sign}), especially given the first and second grating's orientations are not very different (4.8{degree sign}).

(3) For each of the expected orientations (20{degree sign} or 70{degree sign}), the unexpected ones are linearly separable (i.e., all unexpected ones lie on one side of the expected angle). This might further encourage people to shift their attended or expected orientation, according to the optimal tuning hypothesis. Would this provide an alternative explanation to the tuning shift that the authors found?

(4) It is great that the authors conducted computational modeling to elucidate the potential neuronal mechanisms of expectation. But I think the sharpening hypothesis (e.g., reviewed in de Lange, Heilbron & Kok, 2018) focuses on the neural population level, i.e., narrowing of population tuning profile, while the authors conducted the sharpening at the neuronal tuning level. However, the sharpening of population does not necessarily rely on the sharpening of individual neuronal tuning. For example, neuronal gain modulation can also account for such population sharpening. I think similar logic applies to the orientation adjustment experiment. The behavioral level shift does not necessarily suggest a similar shift at the neuronal level. I would recommend that the authors comment on this.

(5) If the orientation adjustment experiment suggests that both sharpening and shifting are present at the same time, have the authors tried combining both in their computational model?

eLife Assessment

This valuable study presents a theoretical framework for building continuous attractor networks that integrate with a wide range of topologies, which are of increasing relevance to neuroscientists. While the work offers solid evidence for most claims, the evidence supporting biological plausibility and key claims - such as the existence of a continuum of stable states and robustness across geometries - is currently incomplete and would benefit from further analysis or discussion. The study will be of interest to computational and systems neuroscientists working on neural dynamics and network models of cognition.

Reviewer #1 (Public review):

This is a theoretical study addressing the problem of constructing integrator networks for which the activity state and integrated variables display non-trivial topologies. Historically, researchers in theoretical neuroscience have focused on models with simple underlying geometries (e.g., circle, torus), for which analytical models could be more easily constructed. How these models can be generalised to complex scenarios is, however, a non-trivial question. This is furthermore a time-sensitive issue, as population recordings from the brain in complex tasks and environments increasingly require the ability to construct such models.

I believe the authors do a good job of explaining the challenges related to this problem. They also propose a class of models that, although not fully general, overcome many of these difficulties while appearing solid and well-functioning. This requires some non-trivial mathematics, which is nevertheless conveyed in a reasonably accessible form. The manuscript is well written, and both the methodology and the code are well documented.

That said, I believe the manuscript has two major limitations, which could be addressed in a revision. First, some of the assumptions underlying this class of models are somewhat restrictive but are not sufficiently discussed. Second, although the stated goal of the manuscript is to provide practical recipes for constructing integrator networks, the methods section is not very explicit about the specific steps required for different geometries. I elaborate on these limitations below.


(1) The authors repeatedly describe MADE as a technique for constructing integrators of specified "topologies and geometries." What do they mean by "geometries"? Intuitively, I would associate geometry with properties beyond topology, such as embedding dimensionality or curvature. However, it is unclear to me to what extent these aspects are explicitly specified or controlled in MADE. It seems that geometry is only indirectly defined via the connectivity kernel, which itself obeys certain constraints (e.g., limited spatial scale; see below). I believe it is important for the authors to clarify what they mean by "geometry." They should also specify which aspects are under their control, and whether, in fact, all geometries can be realized.


(2) The authors make two key assumptions: that connectivity is purely inhibitory and that the connectivity kernel has a small spatial scale. They state that under these conditions, the homogeneous fixed point becomes unstable, leading to a non-periodic state. However, it seems to me that they do not demonstrate that this emergent state is necessarily a bump localized in all manifold dimensions -- although this is assumed throughout the manuscript. Are other solutions possible or observed? For example, might the network converge to states that are localized in one dimension but extended in another, yielding e.g., stripe-like activity in the plane rather than bumps? In other words, does the proposed recipe guarantee convergence to bumps? This is a critical point and should be clarified.


(3) Related to the question above: What are the failure modes when these two assumptions are violated? Does the network always exhibit runaway activity (as suggested in the text), or can other types of solutions emerge? It would be useful if the authors could briefly discuss this.


(4) Again, related to the question above: can this formalism be extended to activity profiles beyond bumps? For example, periodic fields as seen in grid cells, or irregular fields as observed in many biological datasets -- particularly in naturalistic environments? These activity profiles are of key importance to neuroscientists, so I believe this is an important point that should at least be addressed in the Discussion. Can MADE be naturally extended to these scenarios? What are the challenges involved?


(5) Line 119: "Since σ is the only spatial scale being introduced in the dynamics, we qualitatively expect that a localized bump state within the ball will have a spatial scale of O(σ)."
Is this statement always true? I understand that the spatial scale of the synaptic inputs exchanged via recurrent interactions (i.e., the argument of the function f in Equation 1) is characterised by the spatial scale σ. But the non-linear function f could modify that spatial scale -- for example, by "cutting" the bump close to its tip. Where am I wrong? Could the authors clarify?


(6) The authors provide beautiful intuition about the problem of constructing integrators on non-trivial topologies and propose a mathematically grounded solution using Killing vectors. Of course, solutions based on Killing vectors are more complex than those with constant offsets, which raises the question: Is the brain capable of learning and handling such complex structures? Perhaps the authors could speculate in the Discussion about the biological plausibility of these mechanisms.


(7) A great merit of this paper is that it provides mathematical tools for neuroscience researchers to build integrators on non-trivial geometries. I found that, although all the necessary information is present in the Methods, the authors could improve the presentation by schematizing the steps required to build each type of model. It would be extremely useful if, for each considered geometry, the authors provided a short list of required components: the manifold P, the choice of distance, and the connectivity offsets defined by the Killing vectors. Currently, this information is presented, but scattered (not grouped by geometry).

Reviewer #2 (Public review):

Summary:

The work by Claudi et al. presents a framework for constructing continuous attractor neural networks (CANs) with user-defined topologies and integration capabilities. The framework unifies and generalizes classical attractor models and includes simulations across a range of topologies, including ring, torus, sphere, Möbius band, and Klein bottle. A key contribution of the paper is the introduction of Killing vectors to enable integration on non-parallelizable manifolds. However, the need for Killing vectors currently appears hypothetical, as biologically discovered manifolds-such as rings and tori-do not require them.

Moreover, throughout the manuscript, the authors claim to be addressing "biologically plausible" attractor networks, yet the constraints required by their construction - such as exact symmetry, fine-tuning of weights, and idealized geometry-seem incompatible with biological variability. It appears that "biologically plausible" is effectively used to mean "capable of integration." While these issues do not diminish the contributions of the work, they should be acknowledged and addressed more explicitly in the text. I applaud the authors for their interesting work. Below are my major and minor concerns.

Strengths:

(1) Theoretical framework for integrating CANs<br /> The paper introduces a systematic method for constructing continuous attractor networks (CANs) with arbitrary topologies. This goes beyond classical models and includes novel topologies such as the Möbius band, sphere, and Klein bottle. The approach generalizes well-known ring and torus attractor models and provides a unified view of their construction, dynamics, and integration capabilities.

(2) Novel use of killing vector fields<br /> A key theoretical innovation is the introduction of Killing vectors to support velocity integration on non-parallelizable manifolds. This is mathematically elegant and extends the domain of tractable attractor models.

(3) Insightful simulations across manifolds<br /> The paper includes detailed simulations demonstrating bump attractor dynamics across a range of topologies.

Weaknesses:

(1) Biological plausibility is overstated<br /> Despite frequent use of the term "biologically plausible," the models rely on assumptions (e.g., symmetric connectivity, perfect geometries, fine-tuning) that are not consistent with known biological networks, and the authors do not incorporate heterogeneity, noise, or constraints like Dale's law.

(2) Continuum of states not directly demonstrated<br /> The authors claim to generate a continuum of stable states but do not provide direct evidence (e.g., Jacobian analysis with zero eigenvalues along the manifold). This weakens the central claim about the nature of the attractor.

(3) Lack of clarity around assumptions<br /> Several assumptions and analyses (e.g., symmetry breaking, linearity, stability conditions) are introduced without justification or overstated. The analytical rigor in discussing alternative solutions and bifurcation behavior is limited.

(4) Scalability to high dimensions<br /> The authors claim their method scales better than learning-based approaches. This should be better discussed.

Major Concerns

(1) Biological plausibility

The claim that the proposed framework is "biologically plausible" is misleading, as it is unclear what the authors mean by this term. Biological plausibility could include features such as heterogeneity in synaptic weights, randomness in tuning curves, irregular geometries, or connectivity constraints consistent with known biological architectures (e.g., Dale's law, multiple cell types). None of these elements is implemented in the current framework. Furthermore, it is not clear whether the framework can be extended to include such features-for example, CANs with heterogeneous connections or tuning curves. The connectivity matrix is symmetric to allow an energy-based description and analytical tractability, which is fine, but not a biologically realistic constraint. I recommend removing or significantly qualifying the use of the term "biologically plausible."

(2) Continuum of stable states<br /> While the authors claim their model generates a continuum of stable states, this is not demonstrated directly in their simulations or in a stability analysis (though there are some indirect hints). One way to provide evidence would be to compute the Jacobian at various points along the manifold and show that it possesses (approximately) zero eigenvalues in the tangent/on-manifold directions at each point (e.g., see Ságodi et al. 2024 and others). It would be especially valuable to provide such analysis for the more complex topologies illustrated in the paper.

(3) Assumptions, limitations, and analytical rigor<br /> Some assumptions and derivations lack justification or are presented without sufficient detail. Examples include:

• Line 126: "If the homogeneous state (all neurons equally active) were unstable, there must exist some other stable state, with broken symmetry." Is this guaranteed? In the ring model with ReLU activation, there could also be unbounded solutions-not just bump solutions-and, in principle, there could also be oscillatory or other solutions. In general, multiple states can co-exist, with differing stability. It appears the authors only analyze the homogeneous case and do not study the stability or bifurcations of other solutions, limiting their theoretical work.

• Line 122: "The conditions for the formation..." What are these conditions, precisely? A citation or elaboration would be helpful. Why is the assumption σ≪L necessary, and how does it impact the construction or conclusions?

• The theory relies heavily on exact symmetries and fine-tuned parameters. Indeed, in line 106, the authors write: "We seek interaction weights consistent with the formation, through symmetry breaking." Is this symmetry-breaking necessary for all CANs? Or is it a limitation specific to hand-crafted models (see also below)? There is insufficient discussion of such limitations. For example, it is difficult to envision how the authors' framework might form attractor manifolds with different geometries or heterogeneous tuning curves.

(4) Comparison with models of learned attractors<br /> While the connectivity patterns of learned attractors often resemble classical hand-crafted models (e.g., see also Vafidis et al. 2022), this is not always the case. If initial conditions include randomness or if the geometry of the attractor deviates from standard forms, the solutions can diverge significantly from hand-designed architectures. Such biologically realistic conditions highlight the limitations the hand-crafted CANs like those proposed here. I suggest updating the discussion accordingly.

(5) High-Dimensional Manifolds<br /> The authors argue that their method scales better than training-based approaches in high dimensions and that it is straightforward to extend their framework to generate high-dimensional CANs. It would be useful for the authors to elaborate further. First, it is unclear what k refers to in the expression k^M used in the introduction. Second, trained neural networks seem to exhibit inductive bias (e.g., Cantar et al. 2021; Bordelon & Pehlevan 2022; Darshan & Rivkind 2022), which may mitigate such scaling issues. To support their claim, the authors could also provide an example of a high-dimensional manifold and show that their framework efficiently supports a (semi-)continuum of stable states.

eLife Assessment

This study provides valuable insights into humans' ability to generalize knowledge of learned graph structures to new experiences that share the same structure but are built from different stimuli. However, the evidence for the authors' claims is incomplete, with the main claims of structural generalization and compositionality only partially supported by MEG and behavioral data. This study will be of interest to cognitive neuroscientists studying structure learning and generalization.

Reviewer #1 (Public review):

Summary of the paper:

The paper presents an elegant task designed to investigate humans' ability to generalize knowledge of learned graph structures to new experiences that share the same structure but are built from different stimuli. Using behavior and MEG recordings, the authors test evidence for neural representation and application of structural knowledge.

Review overview:

While the task design is elegant, it isn't clear to me that the data support all the claims made in the paper. I have detailed my concerns below.

Major concerns

(1) The authors claim that their findings reveal "striking learning and generalization abilities based on factorization of complex experiences into underlying structural elements, parsing these into distinct subprocesses derived from past experience, and forming a representation of the dynamical roles these features play within distinct subprocesses." And "neural dynamics that support compositional generalisation, consistent with a structural scaffolding mechanism that facilitates efficient adaption within new contexts".

a. First, terms used in these example quotes (but also throughout the paper) do not seem to be well supported by data or the task design. For example, terms such as 'compositional generalisation' and 'building blocks' have important relevance in other papers by (some of) the same authors (e.g., Schwartenbeck et al., 2023), but in the context of this experiment, what is 'composition'? Can the authors demonstrate clear behavioural or neural evidence for compositional use of multiple graph structures, or alternatively remove reference to these terms? In the current paper, it seems to me that the authors are investigating abstract knowledge for singular graph structures (together with the influence of prior learning), as opposed to knowledge for the compound, more complex graph formed from the product of two simpler graphs.

b. While I would like to be convinced that this data provides evidence for the transfer of abstract, structural knowledge, I think the authors either need to provide more convincing evidence or tone down their claims.

Specifically:

(i) Can the increase in neural similarity between stimuli mapping to the same abstract structural sub-process not be explained by temporal proximity in experiencing the transitions (e.g., Cai et al., 2016)? Indeed, behavior seems to be dominated by direct experience of the structure as opposed to applying abstract knowledge of equivalent structures (and, as a result, there is little difference in behavioural performance between experience and inference probes).

(ii) The strongest evidence for neural representation of abstract task structures seems to be the increase in similarity by transition type. But this common code for 'transition type' is only observed for 6-bridge graphs and only for experienced transitions. There was no significant effect in inference probes. Therefore, there doesn't seem to be evidence for the application of a knowledge scaffold to facilitate transfer learning. Instead, the data reflects learning from direct experience and not generalisation.

(iii) The authors frequently suggest that they are providing insight into temporal dynamics, but there is no mention of particular oscillations or particular temporal sequences of neural representation that support task performance.

(2) Regardless of point (b), can the authors provide more convincing evidence for a graph structure being represented per se (regardless of whether this representation is directly experienced or inferred)? From Figure 3C, it seems that the model RDM doesn't account for relative distance within the graph. Do they see evidence for distance coding? Can they reconstruct the graph from representational patterns using MDS?

(3) In general, the figures are not very clear, and the outcome from statistical tests is not graphically shown. The paper would be easier to digest if, for example, Figures 1-2 were made clearer and statistical significance relative to chance were indicated throughout. To give two examples: (i) Figure 1 should clearly indicate what is meant by observed and held-out transitions and whether it is just the transition or also the compound that is new to the participant. (ii) Figure 2D-E could be shown with relevant comparisons and simpler statistical comparisons. Currently, it is hard to follow without carefully reading the legend.

Reviewer #2 (Public review):

Summary:

The authors aimed to investigate the temporal dynamics of how prior experiences shape learning in new complex environments by examining whether the brain reuses abstract structural components from those experiences. They employed a sequence learning task based on graph factorization and recorded neural activity using magnetoencephalography (MEG) to investigate how the underlying graph factors are reused to support learning and inference in a new graph. MEG data was derived from passive stimulus presentation trials, and behavior was assessed through a small number of probe trials testing either experienced or inferred successions in the graph. Representational similarity analysis of the MEG data was performed at a quite aggregated level (the principal components explaining 80% of the variance). The authors report (1) enhanced neural similarity among stimuli that belong to the same graph-factor as well as (2) a correlation between abstract role representations, corresponding to particular positions in the graph, and performance in experience-probes but not in inference-probes.

Strengths & Weaknesses:

(1) The first finding is considered evidence for representational alignment of the graph factors. However, alignment seems to be just one possible arrangement underlying the increased similarity between stimuli of the same vs different graph factors. For instance, a simple categorical grouping of stimuli belonging to the same graph, rather than their structural alignment, could also underlie the reported effect. The wording should be adjusted to avoid overinterpretation.

(2) The second finding of abstract role representations is indeed expected for structural generalisation. While the data presents an interesting indication, its interpretability is constrained by a lack of testing for generalization of the effect to other graph structures (e.g., to rule out graph-specific strategies) as well as the absence of a link to transfer performance in inference-probes. The authors argue that the experienced transitions the classifier was trained on might be more similar in process to the experience-probes than the inference-probes. However, as inference-probes are the key measure of transfer, one could argue that if abstract role representations truly underlie transfer learning, they should be evident in the common neural signal.

(3) The authors write, "we observed a qualitative pattern indicative of increased neural similarity between stimuli that adhered to the same underlying subprocess across task phases. (...) There was a statistically significant interaction effect of condition x graph factor spanning approximately 300 - 680 ms post-stimulus onset". I conclude there was no significant main effect of graph factor, but the relevant statistics are not reported. The authors should report and discuss the complete statistics.

(4) The RSA is performed on highly aggregated data (the PCs that explained 80% of the variance). Could the authors include their rationale for this choice (e.g. over-analysis of sensor-level data)? In case sensor-level analyses have been conducted as well, maybe there are comparisons or implications of the chosen approach that are useful to mention in the discussion. The authors should provide the average and distribution of the number of PCs underlying their analyses.

(5) While the paper is well-written overall, it would benefit from more explicitly identifying the concrete research question and advancing through the results. The authors state their aim as understanding the "temporal dynamics of compositional generalisation", revealing "at which moment during neural information processing are they assembled". They conclude with "providing evidence for temporally resolved neural dynamics that support compositional generalization" and "we show the neural dynamics (...) presented across different task phases...". It remains somewhat vague what specific insight about the process is provided through the temporal resolution (e.g., is the time window itself meaningful, if so, it should be contextualized; is the temporal resolution critical to dissociate subprocesses). The different task phases -initial learning and transfer- are the necessary conditions to investigate transfer learning, but do not by themselves offer a particularly resolved depiction of the process.

Overall, the findings are congruent with prior research on neural correlates of structural abstraction. They offer an elegant, well-suited task design to study compositional representations, replicating the authors' earlier finding and providing temporal information on structural generalisation in a sequence learning task.

Reviewer #3 (Public review):

Summary

This study investigates how task components can be learned and transferred across different task contexts. The authors designed two consecutive sequence learning tasks, in which complex image sequences were generated from the combination of two graph-based structural "building blocks". One of these components was shared between the prior and transfer task environments, allowing the authors to test compositional transfer. Behavioral analyses using generalized linear models (GLMs) assessed participants' sensitivity to the underlying structure. MEG data were recorded and analyzed using classifications and feature representational similarity analysis (RSA) to examine whether neural similarity increased for stimuli sharing the same relational structure. The paper aims to uncover the neural dynamics that support compositional transfer during learning.

Strengths and weaknesses

I found the methods and task design of this paper difficult to follow, particularly the way stimuli were constructed and how the experimental sequences were generated from the graph structures. These aspects would be hard to replicate without some clarification. I appreciate the integration of behavioral and neuroimaging data. The overall approach, especially the use of compositional graph structures in sequence learning, is interesting and could be used and revised in further studies in compositionality and transfer learning. I appreciated the authors' careful interpretation of their findings in the discussion. However, I would have liked a similar level of caution in the abstract, which currently overstates some claims.

Major Comments:

(1) While the introduction mentions brain areas implicated in the low-dimensional representation of task knowledge, the current study uses M/EEG and does not include source reconstruction. As a result, the focus is primarily on the temporal dynamics of the signal rather than its spatial origins. Although I am not suggesting that the authors should perform source reconstruction in this study, it would strengthen the paper to introduce the broader M/EEG literature on task-relevant representations and transfer. The same applies to behavioral studies looking at structural similarities and transfer learning. I encourage the authors to integrate relevant literature to better contextualize their results.

Duan, Y., Zhan, J., Gross, J., Ince, R. A. & Schyns, P. G. Pre-frontal cortex guides dimension-reducing transformations in the occipito-ventral pathway for categorization behaviors. Current Biology 34, 3392-3404 (2024).

Luyckx, F., Nili, H., Spitzer, B. & Summerfield, C. Neural structure mapping in human probabilistic reward learning. eLife 8, e42816 (2019). (This is in the references but not in the text).

Zhang, M. & Yu, Q. The representation of abstract goals in working memory is supported by task-congruent neural geometry. PLoS biology 22, e3002461 (2024).

L. Teichmann, T. Grootswagers, T. Carlson, A.N. Rich Decoding digits and dice with magnetoencephalography: evidence for a shared representation of magnitude Journal of cognitive neuroscience, 30 (7) (2018), pp. 999-1010

Garner, K., Lynch, C. R. & Dux, P. E. Transfer of training benefits requires rules we cannot see (or hear). Journal of Experimental Psychology: Human Perception and Performance 42, 1148 (2016).

Holton, E., Braun, L., Thompson, J., Grohn, J. & Summerfield, C. Humans and neural networks show similar patterns of transfer and interference during continual learning (2025).

(2) I found it interesting that the authors chose to perform PCA for dimensionality reduction prior to conducting RSA; however, I haven't seen such an approach in the literature before. It would be helpful to either cite prior studies that have employed a similar method or to include a comparison with more standard approaches, such as sensor-level RSA or sensor-searchlight analysis.

(3) Connected to the previous point, the choice to use absolute distance as a dissimilarity measure is not justified. How does it compare to standard metrics such as correlation distance or Mahalanobis distance? The same applies to the use of Kendall's tau.

(4) The analysis described in the "Abstract representation of dynamical roles in subprocesses" does not appear to convincingly test the stated prediction of a structural scaffolding account. The authors hypothesize that if structure and dynamics from prior experiences are repurposed, then stimuli occupying the same "dynamical roles" across different sequences should exhibit enhanced neural similarity. However, the analysis seems to focus on decoding transitions rather than directly assessing representational similarity. Rather, this approach may reflect shared temporal representation in the sequences without necessarily indicating that the neural system generalizes the abstract function or position of a stimulus within the graph. To truly demonstrate that the brain captures the dynamical role across different stimuli, it would be more appropriate to directly assess whether neural patterns evoked by stimuli, in the same temporal part of the sequence, with shared roles (but different visual identities) are more similar to each other than to those from different roles.

(5) In the following section, the authors correlate decoding accuracy with participants' behavioral performance across different conditions. However, out of the four reported correlations and the additional comparison of differences between conditions, only one correlation and one correlation difference reach significance, and only marginally so. The interpretation of this finding should therefore be more cautious, especially if it is used to support a link between neural representations and behavior. Additionally, it is possible that correlation with a more clearly defined or targeted neural signature, more directly tied to the hypothesized representational content, could yield stronger or more interpretable correlations.

Minor Comments:

During preprocessing, sensors were excluded based on an identified noise level. However, the authors do not specify the threshold used to define this noise level, nor do they report how many sensors were excluded per participant. It would be helpful to have these details. Additionally, it is unclear why the authors opted to exclude sensors rather than removing noise with MaxFiltering or interpolating bad sensors. Finally, the authors should report how many trials were discarded on average (and standard deviation) per participant.

eLife Assessment

This study introduces a valuable simulation-based inference (SBI) framework to identify degenerate compensatory mechanisms that stabilize network activity despite neuronal hyperexcitability, a feature common to many brain disorders. By estimating posterior distributions of network parameters, the authors highlight factors such as threshold potential and interneuron-to-principal cell connectivity as key compensators for increased intrinsic excitability and interneuron loss. While the approach is promising and could become a key tool for probing network degeneracy, the study is currently incomplete. To fully realize its potential, the framework requires improved scalability and more rigorous cross-validation.

Joint Public Review:

Summary:

This manuscript couples a 32-parameter model with simulation-based inference (SBI) to identify parameter changes that can compensate for three canonical hyperexcitability perturbations (interneuron loss, recurrent-excitatory sprouting, and intrinsic depolarisation). The study demonstrates a careful implementation of SBI and offers a practical ranking of "compensatory levers" that could, in principle, guide therapeutic strategies for epilepsy and related network disorders.

Strengths:

(1) By analysing three mechanistically distinct hyper-excitable regimes within the same modelling and inference framework, the work reveals how different perturbations require different compensatory interventions.

(2) The authors adopt posterior estimation to systematically rank the efficiency of different mechanisms in balancing hyperexcitability.

(3) Code and data are available.

Weaknesses:

(1) A highly dense presentation of the simulated models and undefined symbols makes it hard for readers outside the modelling community to follow the biological message. An illustration of the models, accompanied by some explanations and references to the main equations and parameters discussed in this paper, would make the first section much more straightforward.

(2) This methodology appears to be a brute-force approach, requiring millions of simulations to tune 32 parameters in a network of 500-700 cells. It isn't scalable. Moreover, the authors did not use cross-validation, which, with a relatively low increase in computational cost, would provide a quantitative measure as to how well it generalizes; this combination raises doubts about both scalability and reliability.

(3) Several parameters remain so broadly distributed after fitting that the model cannot say with confidence which specific changes matter. Therefore, presenting them as "compensatory levers" is somewhat questionable.

(4) Every conclusion is drawn from simulated data; without testing the predictions on recordings, we have no evidence that the proposed interventions would work in real neural tissue. Because today we cannot diagnose which of the three modelled pathological regimes is actually present in vivo, the paper's recommendations cannot yet be used to guide therapy.

eLife Assessment

This valuable short paper is an ingenious use of clinical patient data to address an issue in imaging neuroscience. The authors clarify the role of face-selectivity in human fusiform gyrus by measuring both BOLD fMRI and depth electrode recordings in the same individuals; furthermore, by comparing responses in different brain regions in the two patients, they suggested that the suppression of blood oxygenation is associated with a decrease in local neural activity. The methods are solid and provide a rare dataset of potentially general importance.

Reviewer #1 (Public review):

Summary:

Measurement of BOLD MR imaging has regularly found regions of the brain that show reliable suppression of BOLD responses during specific experimental testing conditions. These observations are to some degree unexplained, in comparison with more usual association between activation of the BOLD response and excitatory activation of the neurons (most tightly linked to synaptic activity) in the same brain location. This paper finds two patients whose brains were tested with both non-invasive functional MRI and with invasive insertion of electrodes, which allowed the direct recording of neuronal activity. The electrode insertions were made within the fusiform gyrus, which is known to process information abouit faces, in a clinical search for the sites of intractable epilepsy in each patient. The simple observation is that the electrode location in one patient showed activation of the BOLD response and activation of neuronal firing in response to face stimuli. This is the classical association. The other patient showed an informative and different pattern of responses. In this person, the electrode location showed a suppression of the BOLD response to face stimuli and, most interestingly, an associated suppression of neuronal activity at the electrode site.

Strengths:

Whilst these results are not by themselves definitive, they add an important piece of evidence to a long-standing discussion about the origins of the BOLD response. The observation of decreased neuronal activation associated with negative BOLD is interesting because, at various times, exactly the opposite association has been predicted. It has been previously argued that if synaptic mechanisms of neuronal inhibition are responsible for the suppression of neuronal firing, then it would be reasonable

Weaknesses:

The chief weakness of the paper is that the results may be unique in a slightly awkward way. The observation of positive BOLD and neuronal activation is made at one brain site in one patient, while the complementary observation of negative BOLD and neuronal suppression actually derives from the other patient. Showing both effects in both patients would make a much stronger paper.

Comments on revisions:

The material on lines 165-175 should not be left hidden away in the Methods section. This should be highlighted in the Discussion as a limitation of the current study and an issue that could be improved upon in future studies.

Reviewer #2 (Public review):

Summary:

This is a short and straightforward paper describing BOLD fMRI and depth electrode measurements from two regions of the fusiform gyrus that show either higher or lower BOLD responses to faces vs. objects (which I will call face-positive and face-negative regions). In these regions, which were studied separately in two patients undergoing epilepsy surgery, spiking activity increased for faces relative to objects in the face-positive region and decreased for faces relative to objects in the face-negative region. Interestingly, about 30% of neurons in the face-negative region did not respond to objects and decreased their responses below baseline in response to faces (absolute suppression).

Strengths:

These patient data are valuable, with many recording sessions and neurons from human face-selective regions, and the methods used for comparing face and object responses in both fMRI and electrode recordings were robust and well-established. The finding of absolute suppression could clarify the nature of face selectivity in human fusiform gyrus, since previous fMRI studies of the face-negative region could not distinguish whether face < object responses came from absolute suppression, or just relatively lower but still positive responses to faces vs. objects.

Weaknesses:

The authors claim that the results tell us about both 1) face-selectivity in the fusiform gyrus, and 2) the physiological basis of the BOLD signal. However, I would like to see more of the data that supports the first claim included in the paper.

The authors report that ~30% of neurons showed absolute suppression, but those data are not shown separately from the neurons that only show relative reductions. It is difficult to evaluate the absolute suppression claim from the short assertion in the text alone (lines 105-106), although this is a critical claim in the paper.

Comments on revisions:

The authors have provided a figure showing one example neuron that shows absolute suppression in their response to reviewers; I would recommend including a similar panel in one of the paper figures showing data averaged across all neurons classified as showing absolute suppression.

Reviewer #3 (Public review):

Summary:

In this paper the authors conduct two experiments an fMRI experiment and intracranial recordings of neurons in two patients P1 and P2. In both experiments, they employ a SSVEP paradigm in which they show images at a fast rate (e.g. 6Hz) and then they show face images at a slower rate (e.g. 1.2Hz), where the rest of the images are a variety of object images. In the first patient, they record from neurons over a region in the mid fusiform gyrus that is face-selective and in the second patient, they record neurons from a region more medially that is not face selective (it responds more strongly to objects than faces). Results find similar selectivity between the electrophysiology data and the fMRI data in that the location which shows higher fMRI to faces also finds face-selective neurons and the location which finds preference to non faces also shows non face preferring neurons.

Strengths:

The data is important in that it shows that there is a relationship between category selectivity measured from electrophysiology data and category-selective from fMRI. The data is unique as it contains a lot of single and multiunit recordings (245 units) from the human fusiform gyrus - which the authors point out - is a humanoid specific gyrus.

Weaknesses:

My major concerns are two-fold: (i) There is a paucity of data; Thus, more information (results and methods) is warranted; and in particular there is no comparison between the fMRI data and the SEEG data.

(ii) One main claim of the paper is that there is evidence for suppressed responses to faces in the non-face selective region. That is, the reduction in activation to faces in the non-face selective region is interpreted as a suppression in the neural response and consequently the reduction in fMRI signal is interpreted as suppression. However, the SSVEP paradigm has no baseline (it alternates between faces and objects) and therefore it cannot distinguish between lower firing rate to faces vs suppression of response to faces.

(1) Additional data: the paper has 2 figures: figure 1 which shows the experimental design and figure 2 which presents data, the latter shows one example neuron raster plot from each patient and group average neural data from each patient. In this reader's opinion this is insufficient data to support the conclusions of the paper. The paper will be more impactful if the researchers would report the data more comprehensively.

(a) There is no direct comparison between the fMRI data and the SEEG data, except for a comparison of the location of the electrodes relative to the statistical parametric map generated from a contrast (Fig 2a,d). It will be helpful to build a model linking between the neural responses to the voxel response in the same location - i.e., estimate from the electrophysiology data the fMRI data (e.g. Logothetis & Wandell, 2004)

(b) More comprehensive analyses of the SSVEP neural data: It will be helpful to show the results of the frequency analyses of the SSVEP data for all neurons to show that there are significant visual responses and significant face responses. It will be also useful to compare and quantify the magnitude of the face responses compared to the visual responses.

(c) The neuron shown in E shows cyclical responses tied to the onset of the stimuli, is this the visual response? If so, why is there an increase in the firing rate of the neuron before the face stimulus is shown in time 0? The neuron's data seems different than the average response across neurons; This raises a concern about interpreting the average response across neurons in panel F which seems different than the single neuron responses

(d) Related to (c) it would be useful to show raster plots of all neurons and quantify if the neural responses within a region are homogeneous or heterogeneous. This would add data relating the single neuron response to the population responses measured from fMRI. See also Nir 2009.

(e) When reporting group average data (e.g., Fig 2C,F) it is necessary to show standard deviation of the response across neurons.

(f) Is it possible to estimate the latency of the neural responses to face and object images from the phase data? If so, this will add important information on the timing of neural responses in the human fusiform gyrus to face and object images.

(g) Related to (e) In total the authors recorded data from 245 units (some single units and some multiunits) and they found that both in the face and nonface selective most of the recoded neurons exhibited face -selectivity, which this reader found confusing: They write " Among all visually responsive neurons, we 87 found a very high proportion of face-selective neurons (p < 0.05) in both activated 88 and deactivated MidFG regions (P1: 98.1%; N = 51/52; P2: 86.6%; N = 110/127)'. Is the face selectivity in P1 an increase in response to faces and P2 a reduction in response to faces or in both it's an increase in response to faces

(1) Additional methods (a) it is unclear if the SSVEP analyses of neural responses were done on the spikes or the raw electrical signal. If the former, how is the SSVEP frequency analysis done on discrete data like action potentials? (b) it is unclear why the onset time was shifted by 33ms; one can measure the phase of the response relative to the cycle onset and use that to estimate the delay between the onset of a stimulus and the onset of the response. Adding phase information will be useful.

(2) Interpretation of suppression:

The SSVEP paradigm alternates between 2 conditions: faces and objects and has no baseline; In other words, responses to faces are measured relative to the baseline response to objects so that any region that contains neurons that have a lower firing rate to faces than objects is bound to show a lower response in the SSVEP signal. Therefore, because the experiment does not have a true baseline (e.g. blank screen, with no visual stimulation) this experimental design cannot distinguish between lower firing rate to faces vs suppression of response to faces. The strongest evidence put forward for suppression is the response of non-visual neurons that was also reduced when patients looked at faces, but since these are non-visual neurons, it is unclear how to interpret the responses to faces.

Comments on revisions:

In the revision, the authors added information and answered several of the main questions. Several points remain unanswered because the authors would like to publish a short format paper here, and suggest that answering these questions is outside the scope of the paper. The authors would like to leave some of the more detailed analyses for a subsequent longer paper.

eLife Assessment

In their study, Diana et al. introduce a novel method for spike inference from calcium imaging data using a Monte Carlo-based approach, emphasizing the quantification of uncertainties in spike time estimates through a Bayesian framework. This method employs particle Gibbs sampling for estimating model parameter probabilities, offering accuracy comparable to existing methods with the added benefit of directly assessing uncertainties. The presentation of the underlying methods and its characterization is convincing and it presents a valuable advancement for neuroscientists interested in new approaches for parameter estimation from calcium imaging data.

Reviewer #1 (Public review):

Summary:

In this study, Diana et al. present a Monte Carlo-based method to perform spike inference from calcium imaging data. A particular strength of their approach is that they can estimate not only averages but also uncertainties of the modeled process. The authors focus on the quantification of spike time uncertainties in simulated data and in data recorded with high sampling rate in cebellar slices with GCaMP8f, and they demonstrate the high temporal precision that can be achieved with their method to estimate spike timing.

Strengths:

- The author provide a solid ground work for sequential Monte Carlo-based spike inference, which extends previous work of Pnevmatikakis et al., Greenberg et al. and others.

- The integration of two states (silence vs. burst firing) seems to improve the performance of the model.

- The acquisition of a GCaMP8f dataset in cerebellum is useful and helps make the point that high spike time inference precision is possible under certain conditions.

Weaknesses:

- Although the algorithm is compared (in the revised manuscript) to other models to infer individual spikes (e.g., MLSpike), these comparisons could be more comprehensive. Future work that benchmarks this and other algorithms under varying conditions (e.g., noise levels, temporal resolution, calcium indicators) would help assess and confirm robustness and useability of this algorithm.

- The mathematical complexity underlying the method may pose challenges for experimentalist who may want to use the methods for their analyses. While this is not a weakness of the approach itself, this highlights the need for further validation and benchmarking in future work, to build user confidence.

Reviewer #2 (Public review):

Summary:

Methods to infer action potentials from fluorescence-based measurements of intracellular calcium dynamics are important for optical measurements of activity across large populations of neurons. The variety of existing methods can be separated into two broad classes: a) model-independent approaches that are trained on ground truth datasets (e.g., deep networks), and b) approaches based on a model of the processes that link action potentials to calcium signals. Models usually contains parameters describing biophysical variables, such as rate constants of the calcium dynamics and features of the calcium indicator. The method presented here, PGBAR, is model-based and uses a Bayesian approach. A novelty of PGBAR is that static parameters and state variables are jointly estimated using particle Gibbs sampling, a sequential Monte Carlo technique that can efficiently sample the latent embedding space.

Strengths:

A main strength of PGBAR is that it provides probability distributions rather than point estimates of spike times. This is different from most other methods and may be an important feature in cases when estimates of uncertainty are desired. Another important feature of PGBAR is that it estimates not only the state variable representing spiking activity, but also other variables such as baseline fluctuations and stationary model variables, in a joint process. PGBAR can therefore provide more information than various other methods. The information in the github repository is well-organized.

Weaknesses:

On the other hand, the accuracy of spike train reconstructions is not higher than that of other model-based approaches, and clearly lower than the accuracy of a model-independent approach based on a deep network. The authors demonstrate convincingly that PGBAR can resolve inter-spike intervals in the range of 5 ms using fluorescence data obtained with a very fast genetically encoded calcium indicator at very high sampling rates (line scans at >= 1 kHz).

eLife Assessment

These useful findings assigned a novel functional implication of histone acylation, crotonylation. Mechanistic insights have been provided in great detail regarding the role of the YEATS2-GCDH axis in modulating epithelial-to-mesenchymal transition (EMT) in head and neck cancer, and overall the strength of evidence is solid.

Joint Public Review:

This manuscript investigates a mechanism between the histone reader protein YEATS2 and the metabolic enzyme GCDH, particularly in regulating epithelial-to-mesenchymal transition (EMT) in head and neck cancer (HNC).

The authors addressed most of the concerns of the reviewers. They have:

(1) Increased the patient cohort size from 10 to 23 for evaluating the levels of YEATS2 and H3K27cr.

(2) Checked the expression of major genes involved in the YEATS2-mediated histone crotonylation axis (YEATS2, GCDH, ECHS1, Twist1, along with H3K27cr levels) in head and neck cancer tissues using immunohistochemistry.

(3) Analyzed publicly available head and neck cancer patient datasets, which revealed a significant positive correlation between YEATS2 expression and increasing tumor grade.

(4) Performed GSEA on TCGA HNC patient samples stratified by high versus low YEATS2 expression. This analysis robustly demonstrated a positive enrichment of metastasis-related gene sets in the high YEATS2 expression group, compared to the low YEATS2 group.

(5) Performed extensive experiments to look into the role of p300 in assisting YEATS2 in regulating promoter histone crotonylation. The p300 was knocked down in BICR10 cells, followed by immunoblotting to assess SPARC protein levels.

(6) Performed co-immunoprecipitation assays to check for an interaction between endogenous YEATS2 and p300. The results clearly demonstrate the presence of YEATS2 in the p300-immunoprecipitate sample, indicating that YEATS2 and p300 physically interact and likely function together as a complex to drive the expression of target genes like SPARC.

(7) Performed RNA Polymerase II ChIP-qPCR on the SPARC promoter in YEATS2 knockdown cells.

(8) To confirm p300's specific role in crotonylation at this locus, they performed H3K27cr ChIP-qPCR after p300 knockdown.

(9) Performed SP1 knockdown (which reduces YEATS2 expression) followed by ectopic YEATS2 overexpression, and then assessed p300 occupancy and H3K27cr levels on the SPARC promoter.

eLife Assessment

In this work, the authors intend to assess the existence of a redox potential across germline stem cells and neighboring somatic stem cells in the Drosophila testis. Some aspects of the manuscript are solid, like the clear effect of SOD KD on cyst cell differentiation state. Other conclusions of the work, such as the non-autonomous effect of this KD in germ cells are not sufficiently supported by the data. The work is potentially useful if the critiques of the reviewers are fully addressed; the strength of the evidence of the manuscript as it stands is incomplete.

Reviewer #1 (Public review):

Mitochondrial staining difference is convincing, but the status of the mitos, fused vs fragmented, elongated vs spherical, does not seem convincing. Given the density of mito staining in CySC, it is difficult to tell what is an elongated or fused mito vs the overlap of several smaller mitos.

I'm afraid the quantification and conclusions about the gstD1 staining in CySC vs. GSCs is just not convincing-I cannot see how they were able to distinguish the relevant signals to quantify once cell type vs the other.

The overall increase in gstD1 staining with the CySC SOD KD looks nice, but again I can't distinguish different cel types. This experiment would have been more convincing if the SOD KD was mosaic, so that individual samples would show changes in only some of the cells. Still, it seems that KD of SOD in the CySC does have an effect on the germline, which is interesting.

The effect of SOD KD on the number of less differentiated somatic cells seems clear. However, the effect on the germline is less clear and is somewhat confusing. Normally, a tumor of CySC or less differentiated Cyst cells, such as with activated JAK/STAT, also leads to a large increase in undifferentiated germ cells, not a decrease in germline as they conclude they observe here. The images do not appear to show reduced number of GSCs, but if they counted GSCs at the niche, then that is the correct way to do it, but its odd that they chose images that do not show the phenotype. In addition, lower number of GSCs could also be caused by "too many CySCs" which can kick out GSCs from the niche, rather than any affect on GSC redox state. Further, their conclusion of reduced germline overall, e.g. by vasa staining, does not appear to be true in the images they present and their indication that lower vasa equals fewer GSCs is invalid since all the early germline expresses Vasa.

The effect of somatic SOD KD is perhaps most striking in the observation of Eya+ cyst cells closer to the niche. The combination of increased Zfh1+ cells with many also being Eya+ demonstrates a strong effect on cyst cell differentiation, but one that is also confusing because they observe increases in both early cyst cells (Zfh1+) as well as late cyst cells (Eya+) or perhaps just an increase in the Zfh1/Eya double-positive state that is not normally common. The effects on the RTK and Hh pathways may also reflect this disturbed state of the Cyst cells.

However, the effect on germline differentiation is less clear-the images shown do not really demonstrate any change in BAM expression that I can tell, which is even more confusing given the clear effect on cyst cell differentiation.

For the last figure, any effect of SOD OE in the germline on the germline itself is apparently very subtle and is within the range observed between different "wt" genetic backgrounds.

Reviewer #3 (Public review):

The authors want to prove that there is a redox potential between germline stem cells and somatic cyst stem cells in the Drosophila testis, with ROS being higher in the former compared to the latter. They also want to prove that ROS travels from CySCs to GSCs. Finally, they begin to characterize the phenotypes cause by loss of SOD (The function of SOD is to lower ROS levels, and depletion of SOD increases ROS levels) in the tj-Gal4 lineage and how this impacts the germline.

The authors fall short of accomplished their goals in the revised manuscript. There are issues with the concept of the paper (ROS gradient between cells that causes a transfer of ROS across membranes for homeostasis) as this is not supported by the data. In Fig. 1N (tj-SODi), one can see that all of gst-GFP resides within the differentiating somatic cells and none is in the germ cells. Furthermore, the information provided in the materials and methods about quantification of gst-GFP is not sufficient. Focusing on Dlg staining is not sufficient. They need to quantify the overlap of Vasa (a cytoplasmic protein in GSCs) with GFP. I interpret their results as the following: (1) depletion of SOD from somatic support cells leads to autonomous increases in ROS activity; (2) the increase somatic ROS is not transferred to the germline. Instead increase somatic ROS perturbs homeostasis of the somatic linage. As such, the entire premise of the paper is greatly weakened. Additionally, since tj-gal4 is active in hub cells, it is not clear whether the effects of SOD depletion also arise from perturbation of niche cells. These weaknesses negatively impact the conclusions put forward by the authors. As I wrote in my first critique, their data is not compelling: there is no evidence provide by the authors that ROS diffuses from CySCs to GSCs as most of the claims about stem cells is founded on data about differentiating germ and somatic cells.

There are still many issues about the paper apart from the weak premise. First, the authors are studying a developmental affect, rather than an adult phenotype. Second, the characterization of the somatic lineage is incomplete. It appears that high ROS in the somatic lineage autonomously decreases MAP kinase signaling and increases Hh signaling. They assume that the MAPK signaling is due to changes in Egfr activity but there are other tyrosine kinases active in CySCs, including PVR/VEGFR (PMID: 36400422), that impinge on MAPK. In any event, their results are puzzling because lower Egfr should reduce CySC self-renewal and CySC number (Amoyel, 2016) and the ability of cyst cells to encapsulate gonialblasts (Lenhart Dev Cell 2015). The increased Hh should increase CySC number and the ability of CySCs to outcompete GSCs. The fact that the average total number of GSCs declines in tj>SODi testes suggests that high ROS CySCs are indeed outcompeting GSCs. However, as I wrote in my first critique, the characterization of the high ROS soma is incomplete. And the role of high ROS in the hub cells is acknowledged but not investigated.

(1) Concept: The authors still do not describe why would it be important to have a redox gradient across adjacent cells. The paragraph in the introduction (lines 62-76) mentions autonomous ROS levels in stem cells, not the transfer of ROS from one cell to another. And this paragraph is confusing because it starts with the (inaccurate) statement all stem cells have low ROS and then they discuss ISCs, which have high ROS.

(2) Issues with scholarship of the testis. While there has been an improvement in the scholarship of the testis, there are still places where the correct paper is not cited.

a. Lines 80-82 - cite Roach and Lenhart Dev 2024.

b. Lines 86-88. They is no real evidence for concerted division of GSCs and CySCs. In fact, the Dinardo has shown that these stem cells do not divide synchronously (Lenhart and Dinardo, Dev Cell 2015).

(3) Issues with the text;

a. Lines 194-196 - The authors need to cite Tan 2017 (PMID: 28669604) who have already published a paper about what excess ROS does to the GSC lineage.

b. Lines 210-211 - STAT drives expression of ECad. Socs36E and Ptp61F do not drive Ecad. Please correct.

c. Line 225 "uncontrolled proliferation" is an overstatement and should be toned down.

d. Line 237 - Hh-RNAi does not reduce gene dosage (as the authors have written) but it presumably depletes hh mRNAs levels in hub cells and CySCs.

e. Line 147 - C587-Gal4 on its own should not cause a reduction in GSCs. This sentence should be corrected.

f. Lines 177 - why would the authors predict that increasing ROS in GSCs using nos-Gal4 would non-autonomously affect CySCs? The logic is not clear. Please explain.

g. Line 291-293 - this sentence make no sense. Please revise.

Author response:

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

Reviewer #1 (Public review):

In Figure 1, it is very difficult to identify where CySCs end and GSCs begin without using a cell surface marker for these different cell types. In addition, the methods for quantifying the mitochondrial distribution in GSCs vs. CySCs are very much unclear and appear to rely on colocalization with molecular markers that are not in the same cellular compartment (Tj-nuclear vs. Vasa-perinuclear and cytoplasmic) the reader has no way to determine the validity of the mitochondrial distribution. Similarly, the labelling with gstD1-GFP is also very much unclear - I see little to no GFP signal in either GSCs or CySCs in panels 1GK. Lastly, while the expression o SOD in CySCs does increase the gstD1-GFP signal in CySCs, the effects on GSCs claimed by the authors are not apparent.

We appreciate the reviewer’s detailed feedback on Figure 1 and the concerns raised regarding identifying CySCs and GSCs, as well as the methods used for quantifying mitochondrial distribution and gstD1-GFP labeling. Below, we address each point and describe the revisions made to improve clarity and rigor

Distinguishing CySCs and GSCs and Mitochondrial Distribution in GSCs vs. CySCs in Figure1

We acknowledge the difficulty in distinguishing CySCs from GSCs without the use of additional cell surface markers. To improve clarity, we have now included a membrane marker discslarge (Dlg) in our revised Figure 1 and S1 to delineate cell boundaries more clearly. Additionally, we provide higher-magnification images to indicate the mitochondria in CySCs and GSCs. We also agree that ing on mitochondrial distribution might be far-fetched. In the revised manuscript, we have limited our analysis to mitochondrial shape, which was found to be different in GSC and CySC (Fig. 1, D, F, G, and S1B). We have clarified our quantification methods in the revised Methods section, providing details on the image processing and analysis pipeline used to assess mitochondrial distribution. 

Clarity of gstD1-GFP Labelling:

We recognize the reviewer’s concern regarding the weak GFP signal in these panels. To improve visualization, we have included fresh set of images by optimizing the contrast and presenting additional monochrome images with higher exposure settings to better illustrate gstD1-GFP expression (Figure 1L,1Q, and S1C’’’-D’’’). Additionally, we have demarcated the cell boundaries using Dlg along with individual labelling of Vasa+ and Tj+ cells. Due to technical difficulty associated with acquisition of images, we could not co-stain Vasa, Tj and Dlg together. Therefore, quantified the gstD-GFP intensity separately for GSCs and CySCs under similar acquisition conditions (Figure 1R).   

Effects of SOD depletion on GSCs:

While our initial analysis suggested changes in gstD1-GFP expression in GSCs upon Sod1 depletion in CySCs, we acknowledge that the effects may not be as apparent in the provided images. In response, we have expanded our quantification, included a statistical analysis of gstD1-GFP intensity specifically in GSCs and CySCs (Figure 1S), and added more representative images in the revised figure panels (Figure S1C-D’’’) to support our claims.

In Figure 2, while the cell composition of the niche region does appear to be different from controls when SOD1 is knocked down in the CySCs, at least in the example images shown in Figures 2A and B, how cell type is quantified in figures 2E-G is very much unclear in the figure and methods. Are these counts of cells contacting the niche? If so, how was that defined? Or were additional regions away from the niche also counted and, if so, how were these regions defined?

Thank you for your  regarding the quantification of cell types in Figures 2E-G. We counted all cells that were Tj-positive and Zfh1-positive in individual testis, while for GSCs, only those in direct contact with the hub were included. This clarification has been incorporated into the revised figure legend and methods (line no.400-407). We have now provided a clearer description in the text to improve transparency in our analysis.

In Figure 3, it is quite interesting that there is an increase in Eya⁺, differentiating cyst cells in SOD1 knockdown animals, and that these Eya+ cells appear closer to the niche than in controls. However, this seems at odds with the proliferation data presented in Figure 2, since Eya⁺ somatic cells do not normally divide at all. Are they suggesting that now differentiating cyst cells are proliferative? In addition, it is important for them to show example images of the changes in Socs36E and ptp61F expression.

Thank you for your insightful observations. We acknowledge the apparent contradiction and appreciate the opportunity to clarify our interpretation.

Regarding the increase in Eya⁺ differentiating cyst cells in Sod1RNAi individuals and their proximity to the niche, we do not suggest that these differentiating cells are proliferative. Instead, we propose that the knockdown of Sod1 may alter the timing or regulation of cyst cell differentiation, leading to an accumulation of Eya⁺ cells near the niche. To clarify this point, we have revised the manuscript (line no. 186-189) to emphasize that our proliferation data specifically refers to early-stage somatic cells, not Eya⁺ differentiating cyst cells.

We also appreciate the reviewer's request for example images illustrating the changes in Socs36E and Ptp61F expression. We could not access the antibodies specific to Socs36E and Ptp61F. Hence, we had to rely on the measurements were obtained using real-time PCR from the tip region of testis. We have clarified the same in the figure legends (line 700). 

Overall, the various changes in signaling are quite puzzling-while Jak/Stat signaling from the niche is reduced, hh signaling appears to be increased. Similarly, while the authors conclude that premature differentiation occurs close to the niche, EGF signaling, which occurs from germ cells to cyst cells during differentiation, is decreased. Many times these, changes are contradictory, and the authors do not provide a suitable explanation to resolve these contradictions. 

We appreciate the reviewer’s thoughtful feedback on the signaling changes described in our study. We acknowledge that the observed alterations in Jak/Stat, Hedgehog (Hh), and EGF signaling may appear contradictory at first glance. However, our data suggest that these changes reflect a complex interplay between different signaling pathways that regulate cyst cell behavior in response to specific genetic perturbation.

Regarding Jak/Stat and Hh signaling, while Jak/Stat activity is reduced in the niche, the increase in Hh signaling may reflect a compensatory mechanism or a context-dependent response of cyst cells to reduced Jak/Stat input. Prior studies have suggested that Hh signaling can function in parallel and independently of Jak/Stat signaling (PMID: 23175633) and our findings align with this possibility. 

The reduction in EGFR signaling in this context appears contradictory to existing literature. One possible explanation is that, the altered GSC -CySC balance and loss of contact in Tj>Sod1i testes, leads to insufficient ligand response, thereby failing to activate EGFR signaling. (line no.222-224, 313-318). 

Reviewer #2 (Public review):

We sincerely appreciate the reviewer’s detailed feedback, which has helped refine our manuscript. In this study we have focussed on the role of ROS generated due to manipulation of Sod1 in the interplay between GSC and CySCs. In this regard, we have conducted additional experiments and incorporated quantitative data into the revised manuscript. Additionally, we have refined the text and provided further context to enhance the clarity. Key revisions include:

(1) Clarification of Quantification Methods – We have refined intensity measurements by incorporating a membrane marker (Dlg) to better delineate cell boundaries and have normalized Ptc and Ci expression per cell to improve clarity.

(2) Cell-Specific ROS Measurement – We separately measured ROS in germ cells and cyst cells and performed independent Sod1 depletion in GSCs to determine its direct effects.

(3) Mitochondrial Analysis – We revised our approach, focusing on mitochondrial shape rather than asymmetric distribution, and removed overreaching claims.

(4) Proliferation Analysis – We reanalyzed FUCCI data by normalizing to total cell count, supporting the conclusion that increased proliferation, rather than differentiation delay, underlies the observed phenotype.

(5) E-Cad Quantification – We specifically analyzed E-Cad levels at the GSC-hub interface to strengthen conclusions on GSC attachment.

(6) JAK/STAT Signaling – While we could not obtain a STAT92E antibody, we clarified the spatial limitations of our current analysis and revised the text accordingly.

(7) Rescue Experiments and Gal4 Titration Control – We performed additional control experiments to confirm that observed effects are not due to Gal4 dilution.

(8) Image Quality and Terminology Corrections – We enhanced figure resolution, corrected terminology (e.g., "cystic" to "cyst"), and revised ambiguous phrasing for clarity and accuracy.

As suggested, we have also changed the manuscript title to better align with our results:

Previous Manuscript Title: Non-autonomous cell redox-pairs dictate niche homeostasis in multi-lineage stem populations

Updated Manuscript Title: Superoxide Dismutases maintain niche homeostasis in stem cell populations

Specific responses to the reviewer’s: 

While the decrease in pERK in CySCs is clear from the image and matched in the quantification, the increase in cyst cells is not apparent from the fire LUT used. The change in fluorescence intensity therefore may be that more cells have active ERK, rather than an increase per cell (similar arguments apply to the quantifications for p4E-BP or Ptc). Therefore, it is hard to know whether Sod1 knockdownresults in increased or decreased signaling in individual cells.

Thank you for your insightful . To clarify, in the Fire LUT images, only pERK intensity is shown, not the cyst cell number. In our context, while there are more cells, the overall pERK intensity is lower, eliminating any ambiguity about whether the change is occurring per cell or due to an increased number of circulating cells. Moreover, for Ptc and Ci levels, we have normalized Ptc and Ci expression intensity per cell to enhance clarity and ensure an accurate interpretation of signaling changes.

There are several places in which the authors could strengthen their manuscript by explaining the methods more clearly. For example, it is unclear how the intensity graphs in Figure 1Q are obtained. The curves appear smoothed and therefore unlikely to be from individual samples, but this is not clearly explained. However, this quantification method is clearly not helpful, as it shows the overlap between somatic and germline markers, suggesting it cannot accurately distinguish between the two cell types. Additionally, using a nuclear marker (Tj) for the cyst cells and cytoplasmic marker (Vasa) for the germ cells risks being misleading, as one would not expect much overlap between cytoplasmic gstD1-GFP and nuclear Tj. Also related to the methods, it is unclear how Vasa+ cells at the hub were counted. The methods suggest this was from a single plane, but this runs the risk of being arbitrary since GSCs can be distributed around the hub in 3D. (As a note, the label on the graph "Vasa+ cells" is misleading, as there are many more cells that are Vasa-positive than the ones counted.)

We appreciate the reviewer’s careful evaluation of our manuscript and their insightful suggestions for improving the clarity of our methods. Below, we address each concern raised and describe the revisions made accordingly.

Clarification of Intensity Graphs in Figure 1Q

We have removed this graph, as we recognize that the markers previously used were not appropriate for distinguishing the different cell types. To address this concern, we have revised the text and now included a membrane marker discs-large (Dlg) in our revised Figure 1 and S1 to more clearly delineate cell boundaries. Due to technical difficulty associated with acquisition of images, we could not co-stain Vasa, Tj and Dlg together. Therefore, quantified the gstD-GFP intensity separately for GSCs and CySCs under similar acquisition conditions (Figure 1R).   

Counting of Vasa⁺ Cells at the Hub

We appreciate the reviewer’s concern regarding our method for counting Vasa+ cells. In our original analysis, we included GSCs as the Vasa-positive cells that were in direct contact with the hub. To account for the three-dimensional arrangement of GSCs, we used the Cell counter plugin of Fiji and performed counting across different focal planes to ensure all hub-associated cells were considered. For better clarity on cell distribution around the hub, we have presented a single focal place image sliced through mid of the hub zone. To enhance transparency, we have now provided a more detailed explanation of our counting approach in the Methods section (line no 400- 403).

We agree that the label "Vasa+ cells" may be misleading, as many cells express Vasa beyond the specific subset being counted. To address this, we have changed the label to " GSCs" to reflect the subset analyzed more accurately.

The crucial experiment for this manuscript is presented in Figures 1 G-S, arguing that Sod1 knockdown with Tj-Gal4 increases gstD1-GFP expression in germ cells. This needs strengthening as the current quantifications are not convincing and appear to show an overlap between Tj (a nuclear cyst cell marker) and Vasa (a cytoplasmic germ cell marker). Labeling cell outlines would help, or alternatively, labeling different cell types genetically can be used to determine whether the expression is increased specifically within that cell type. Similarly, the measurement of ROS shown in the supplemental data should be conducted in a cell-specific manner. To clearly make the case that Sod1 knockdown in cyst cells is impacting ROS in the germline, it would be important to manipulate germ cell ROS independently. Without this, it will be difficult to prove that any effects observed are a result of increased ROS in the germline rather than indirect effects on the germline of altered cyst cell behaviour. 

We appreciate the reviewer’s insightful feedback regarding the specificity of Sod1 knockdown effects in germ cells and the need for clearer quantification in Figures 1G–S. Below, we address each concern and outline the modifications made:

Clarification of Cell Type-Specific Expression:

We acknowledge the overlap observed between Tj (nuclear cyst cell marker) and Vasa (cytoplasmic germ cell marker) in the presented images. To strengthen our claim that gstD1GFP expression increases specifically in germ cells upon Sod1 knockdown, we have now labelled cell outlines using membrane marker discs-large (Dlg) to better distinguish cell boundaries, along with individual labelling of Vasa⁺ and Tj⁺ cells. Due to technical difficulty associated with acquisition of images, we could not co-stain Vasa, Tj and Dlg together. 

Cell-Specific Measurement of ROS:

We agree that a cell-type-specific ROS measurement is critical to establishing a direct effect on germ cells. To address this, we have now performed ROS measurements separately in germ cells and cyst cells under similar acquisition conditions. These data are now included in the revised (Figure 1R). Similarly, upon CySC-specific Sod1 depletion, we performed measurement of gstD1-GFP intensity which was found to be enhanced in GSCs, along with expected increase in CySCs (Fig 1S). We have independently manipulated ROS levels in GSCs (Nos Gal4> Sod1i) and observed that elevated ROS negatively impacts GSCs, leading to a reduction in their number, while having an insignificant effect on adjacent CySCs.(Fig S2 E, F).

Quantifications of mitochondrial localization in Figure 1 should include some adequate statistical method to evaluate whether the distribution is random or oriented towards the GSC/CySC interface. From the image provided (Figure 1B), it would appear that there are two clusters of mitochondria, on either side of a CySC nucleus, one cluster towards a GSC and one cluster away. Therefore evaluating bias would be important. Additional experiments will be necessary to support the statement that "Redox state of GSC is maintained by asymmetric distribution of CySC mitochondria". This would require manipulating mitochondrial distribution in CySCs.

We appreciate the reviewer’s suggestion regarding the quantification of mitochondrial localization. We agree that ing on mitochondrial distribution might be far-fetched. In revised manuscript, we have demarcated the cell boundary and limited our analysis to mitochondrial shape which was found to be different in GSC and CySC (Fig. 1, D, F, G and S1B). Mitochondrial shape was quantified based on the mitochondrial area and circularity (Figure 1F and G). To prevent any misinterpretation, we have removed the statement, "Redox state of GSC is maintained by asymmetric distribution of CySC mitochondria."

One point raised by the authors is that the increase of somatic cell numbers is driven by accelerated proliferation, based on an increased number of cells in various stages of the cell cycle as assessed by the FUCCI reporter. However, there are more somatic cells in this genetic background, so it could be argued that the observed increase in different phases of the cell cycle is due to an increased number of cells. In order to argue for an increased proliferation rate, the number of cells in each phase should be divided by the total number of cells, expecting to see an increase in S and G2/M phases along with a decrease in G1. Otherwise, the simplest explanation is a block or delay in differentiation, meaning that more cells remain in the cell cycle.

We appreciate the  regarding the interpretation of our FUCCI reporter data. We acknowledge that the observed increase in the number of cells in various phases of the cell cycle could be influenced by the overall higher number of somatic cells in this genetic background.

To address this concern, we have now re-analyzed our FUCCI data by normalizing the number of cells in each phase to the total number of cells and we did not observe a significant shift in the proportion of cells in S and G2/M phases relative to G1. This suggests presence of more proliferative cells, that is less cells in Go phase, rather than alterations in the timing of cell cycle progression stages. We are not sure about a block in differentiation because we see an enhanced accumulation of Eya+ cells near the niche. We have also supported our FUCCI data with pH3 staining where we have found more pH3+ spots under SOD1 depleted background. We have revised our manuscript accordingly (Figure 2I, K and S2U) to reflect this interpretation and appreciate the constructive feedback.

In Figure 3, the authors claim that knockdown of Sod1 in the soma decreases the attachment of GSCs to the hub-based on lower E-Cad levels compared to controls. Previous work has shown that in GSCs, E-Cad localizes to the Hub-GSC interface (PMID: 20622868). Therefore, the authors should quantify E-Cad staining at the interphase between the germ cells and the niche.

We appreciate the reviewer’s . As suggested, we have now quantified ECad staining specifically at the interface between the germ cells and the niche. Our analysis confirms that E-Cad levels are significantly reduced at this interphase upon Sod1 knockdown in the soma compared to controls, supporting our conclusion that Sod1 depletion affects GSC attachment to the hub as well as the whole niche. The revised Figure 3M now includes these quantifications, and we have updated the figure legend and results section accordingly.

The authors show decreased expression of the JAK/STAT targets socs36E and ptp61F, arguing that this could be a reason for decreased GSC adhesion to the hub. However, these data were obtained from whole testes and lacked spatial resolution, whereas a STAT92E staining in control and tj>Sod1 RNAi testes could easily prove this point. Indeed, previous work has shown that socs36E is expressed in the CySCs, not GSCs (PMID: 19797664), suggesting that any decrease in JAK/STAT may be autonomous to the CySCs.

We appreciate the reviewer’s observation regarding the spatial resolution of our JAK/STAT target expression analysis. To improve accuracy, we have attempted to collect only the tip of the testes while excluding the rest; however, we acknowledge that this approach may still obscure cell-specific changes. We had attempted to procure the STAT92E antibody but, despite multiple inquiries, we did not receive a positive response. While we agree that STAT92E staining would have strengthen our findings, we are currently unable to perform this experiment. Nevertheless, our observations align with prior work indicating that socs36E is predominantly expressed in CySCs (PMID: 19797664). We have revised the manuscript text accordingly to clarify this limitation.

Additional considerations should be taken regarding the rescue experiments where PI3KDN and Hh RNAi are expressed in a Tj>Sod1 RNAi background. To rule out that any rescue can be attributed to titration of the Gal4 protein when an additional UAS sequence is present, a titration control would be useful. These pathways are not described accurately since Insulin signaling is necessary for the differentiation of somatic cells (not maintenance as written in the text), and its inhibition has been shown to increase the number of undifferentiated somatic cells (PMID:27633989). As far as Hh is concerned, the expression of this molecule is restricted to the niche. It would be important to establish whether the expression is altered in this case, especially as the authors rescue the Sod1 knockdown by also knocking down Hh. One possibility that the authors need to rule out is that some of the effects they observe are due to the knockdown of Sod1 (and/or Hh) in the hub as Tj-Gal4 is expressed in the hub as well as the CySCs (PMID:27546574).

We appreciate the reviewer’s insightful s and suggestions. Below, we address each concern and describe the steps we have taken to incorporate the necessary modifications in our revised manuscript.

Titration Control for Rescue Experiments  

We acknowledge the reviewer’s concern regarding potential Gal4 titration effects when introducing additional UAS constructs. To address this, we conducted a control experiment quantifying SOD1 levels in control, Tj > Sod1 RNAi, and Tj > Sod1 RNAi, UAS hhRNAi backgrounds using real-time PCR (Figure S4 M). The Sod1 levels in single and double UAS copy conditions were comparable, indicating that Gal4 titration does not significantly affect the results.

Clarification of Insulin Signaling Role 

We appreciate the reviewer’s insight regarding the involvement of insulin signaling in this context. Initially, we included data on PI3K/TOR as we found it intriguing. However, as the data didn’t add much to the overall observations, we have removed them to ensure clarity and prevent any potential confusion.

Hh Expression and Niche Consideration 

We recognize the importance of evaluating whether Hedgehog (Hh) expression is altered in the Sod1 RNAi background. We have already quantified hh in qRT-PCR (Figure S4C). 

Potential Effects of Sod1 and Hh Knockdown in the Hub 

We acknowledge the concern that Tj-Gal4 is expressed in both the hub and CySCs, potentially affecting hub function upon Sod1 and Hh knockdown. To address this, we have included additional data using the CySC-specific driver C-587 Gal4 to distinguish CySC-intrinsic effects from potential hub contributions. Our results show that while the phenotypic changes are consistent across both drivers, the effects are significantly stronger with Tj-Gal4, suggesting a role of the hub in this process. These findings have been incorporated into the revised manuscript (Fig S1G-H, M-N).

In general, the GSCs (and other aspects) are difficult to see in the images; enlargements or higher-resolution images should be provided. Additionally, the manuscript contains several mistakes or inaccuracies (examples include referring to ROS having "evolved" in the abstract when it is cells that have evolved to use ROS, or the references to "cystic" cells when they are usually referred to as "cyst" cells, or that "CySCs also repress GSC differentiation by suppressing transcription of bag-of-marbles" when CySCs produce BMPs that lead to suppression of bam expression in the germline). These would need editing for both clarity and accuracy.

We appreciate the reviewer’s insightful feedback and have made the necessary revisions to address the concerns raised.

Image Clarity and Resolution: 

We have provided higher-resolution images in some of the revised images for better understanding. The revised figures now offer better clarity for key observations.

Clarification of Terminology and Accuracy:

The phrase regarding ROS in the abstract has been revised to reflect that cells have evolved to utilize ROS, rather than ROS itself evolving (line no. 27).

References to "cystic" cells have been corrected to "cyst" cells for consistency with standard terminology.

The statement about CySCs repressing GSC differentiation has been revised for accuracy, clarifying that CySCs produce BMPs, which lead to the suppression of bam expression in the germline (line no. 84).

We have carefully reviewed the manuscript for any additional inaccuracies or ambiguities to ensure clarity and precision. We appreciate the reviewer’s constructive s, which have helped improve the manuscript.

Reviewer #3 (Public review):

In response to Reviewer 3’s comments, we would like to highlight the point that in the present study we have focussed on the interplay between CySC and GSC and have accordingly conducted our experiments. We did observe some changes in the hub and do not rule out the effect of hub cells in exacerbating some of our phenotypes. We have included additional controls to highlight the effect of CySC ROS. These points have been appropriately discussed in the manuscript. Key revisions include:  

(1)  Data Clarity & Visualization: To improve mitochondrial lineage association, we incorporated a membrane marker (Dlg) in Figure 1, enhancing the distinction between CySCs and GSCs. Additionally, we refined gstD-GFP quantifications in individual cell types and provided high-resolution images.

(2) ROS Transfer & Measurement: We revised our discussion to acknowledge indirect ROS transfer mechanisms and added separate ROS quantifications in GSCs and CySCs, confirming higher ROS levels in CySCs (Figure 1R).

(3) Tj-Gal4 Specificity & Niche Characterization: Recognizing Tj-Gal4 expression in hub cells, we included C587-Gal4 as a CySC-specific driver, demonstrating that hub cells contribute partially to the phenotype (Figure S1G,H,M,N).

(4) Signaling Pathway Validation: We optimized dpERK staining, included controls (Tj>EGFRi), and clarified limitations regarding MAPK signaling. Due to lethality, we could not perform an EGFR gain-of-function rescue. We also validated increased Hh signaling via qPCR and a Tj>UAS Ci control (Figure S4).

(5) Conceptual & Terminological Refinements: We revised our discussion of BMP signaling, ROS gradients, and testis-specific terminology. All figures and labels now accurately represent GSC scoring (single Vasa⁺ cells in contact with the niche).

(6) Figure & Methods Improvements: We enhanced image resolution, provided grayscale versions where needed,and expanded Materials & Methods to clarify experimental conditions.

These revisions strengthen our conclusions and address the reviewer’s concerns, ensuring a more precise and transparent presentation of our findings. To align with the reviewer’s s we have changed the title of the manuscript to “Superoxide Dismutases maintain niche homeostasis in stem cell populations”.

Specific responses to the reviewer’s comments: 

(1) Data

a.  Problems proving which mitochondria are associated with which lineage.

We acknowledge the challenge of distinguishing CySCs from GSCs without additional cell surface markers. To enhance clarity, we have incorporated the membrane marker Discs-large (Dlg) in our revised Figure 1 to better delineate cell boundaries, providing a clearer depiction of mitochondrial distribution in GSCs and CySCs.

b.There is no evidence that ROS diffuses from CySCs into GSCs.

We acknowledge the reviewer’s concern. There are reports which talks about diffusion of ROS across cells on which we have included a few lines in the discussion (line no. 274-276). We do understand that our previous quantifications showed ROS diffusion from CySC to GSC rather indirectly. Therefore, in revised manuscript we have measured ROS separately in the two cell populations. We found that the CySCs show higher ROS profile than GSCs (Fig 1R).  

c.The changes in GST-GFP (redox readout) are possibly seen in differentiating germ cells (i.e., spermatogonia) but not in GSCs. This weakens their model that ROS in CySC is transferred to GSCs.

Thank you for your observation. We acknowledge that the changes in gstD-GFP (redox readout) are more prominent in differentiating germ cells. It is known that differentiating cells show higher ROS profile than the stem cells. Hence, expectedly the intensity of gstDGFP was lesser in stem cell zone compared to the differentiating zone. In our manuscript we are focussed on the redox state among stem cell populations. Therefore, we have included better quality images and measured the gstD1-GFP intensity individually in GSCs and CySCs (Figure 1R) by demarcating the cell boundaries (Figure 1M, S1C-D’’’). We found that CySCs show higher ROS profile than GSCs and enhancement of ROS in CySC by Sod1 depletion resulted in a consequent increase in ROS in GSCs. We believe this revision strengthens our model by addressing the potential discrepancy and providing a more comprehensive understanding of ROS dynamics within the GSC niche.

d.Most of the paper examines the effect of SOD depletion (which should increase ROS) on the CySC lineage and GSC lineage. One big caveat is that Tj-Gal4 is expressed in hub cells (Fairchild, 2016), so the loss of SOD from hub cells may also contribute to the phenotype. In fact, the niche in Figure 2D looks larger than the niche in the control in Figure 2C, arguing that the expression of Tj in niche cells may be contributing to the phenotype. The authors need to better characterize the niche in tj>SOD-RNAi testes.

We appreciate the reviewer’s insightful  regarding the potential contribution of hub cell to the observed phenotype. We acknowledge that Tj-Gal4 is expressed in hub cells and this could influence the niche size and overall phenotype.

To address this concern, we have included an additional control using C587-Gal4, a CySC specific driver, to distinguish CySC-specific effects from potential hub contributions. All the effects on cell number observed in Tj>Sod1i was replicated in C587>Sod1i testis, except that the observed phenotypes were comparatively weaker. These indicate partial contribution of hub cells to the observed phenotype, exacerbating its severity. However, the effect of Sod1 depletion in CySC on GSC lineages remains significant. These findings have been incorporated into Figure S1- G,H,M and N) and incorporated in the discussion (line no.308311). 

e. The Tj>SOD1-RNAi phenotype is an expansion of the Zfh1<sup+</sup> CySC pool, expansion of the Tj⁺ Zfh1- cyst cells (both due to increased somatic proliferation) and a non-autonomous disruption of the germline.

We appreciate the reviewer’s observation. Our data confirm that Tj>SOD-RNAi leads to an expansion of both Zfh1<sup+</sup> CySCs and Tj⁺ Zfh1- cyst cells, which we attribute to increased somatic proliferation. Additionally, we observe a non-autonomous disruption of the germline, likely due to dysregulated signaling from the altered somatic niche.

f. I am not convinced that MAPK signaling is decreased in tj>SOD-i testes. Not only is this antibody finicky, but the authors don't have any follow-up experiments to see if they can restore SOD-depleted CySCs by expressing an EGFR gain of function. Additionally, reduced EGFR activity causes fewer somatic cells (not more) (Amoyel, 2016) and also inhibits abscission between GSCs and gonial blasts (Lenhart 2015), which causes interconnected cysts of 8- to 16 germ cells with one GSC emanating from the hub.

We acknowledge that the dpERK antibody can be challenging. We took necessary precautions, including optimizing staining conditions and using positive control (Tj>EGFRi) (Figure: S4B). Our results consistently showed a decrease in dpERK levels in Tj>Sod1i testes, supporting our conclusion.

We agree that inclusion of an experiment using EGFR gain-of-function to rescue the effects of CySC-Sod1 depletion would have strengthened our findings. We had attempted this experiment; however, the progenies constitutively expressing EGFR under Sod1RNAi background were lethal, preventing us from completing the analysis.

We agree that our observations do not align with the reported effects of EGFR signaling on somatic cell numbers and abscission and we appreciate the references provided. Based on our observations, we feel that modulation of MAPK signaling in the niche probably, happens in a context-dependent manner. One possible explanation is that, the altered GSC -CySC balance and loss of contact in Tj>Sod1i testes, leads to insufficient ligand response, thereby failing to activate EGFR signaling. While it is well established that ROS can enhance EGFR signaling to promote cellular proliferation and early differentiation, our results indicate a more nuanced regulation in this context. However, further detailed analysis is required to completely understand the regulatory controls. We have clarified this point in the manuscript (line no.

313-320).

g. The increase in Hh signaling in SOD-depleted CySCs would increase their competitiveness against GSCs and GSCs would be lost (Amoyel 2014). The authors need to validate that Hh protein expression is indeed increased in SOD-depleted CySCs/cyst cells and which cells are producing this Hh. Normally, only hub cells produce Hh (Michel,2012; Amoyel 2013) to promote self-renewal in CySCs.

We appreciate the reviewer’s suggestion regarding the validation of Hh protein expression and its source. Since Tj-Gal4 is expressed in the hub, it is likely activating the Hh pathway and promoting CySC proliferation. Unfortunately, we could not procure Hh antibody to directly assess its protein levels. However, to address this, we performed real-time PCR from RNA derived from the tip region and found a significant increase in hh mRNA levels in SOD-depleted cyst cells. These findings support our hypothesis that elevated Hh signaling enhances CySC competitiveness, leading to GSC loss. To support this idea, we have included a Tj>Ci positive control which caused abnormal proliferation of Tj⁺ cells resulted in ablation of GSCs. We have incorporated these results in the revised manuscript (Results section, Figure S-4).

h.The increase in p4E-BP is an indication that Tor signaling is increased, but an increase in Tor in the CySC lineage does not significantly affect the number of CySCs or cyst cells (Chen, 2021). So again I am not sure how increased Tor factors into their phenotype.

We acknowledge the reviewer’s concern regarding the role of increased Tor signaling in our phenotype. The observed increase in Tor could indeed be a downstream effect of elevated ROS levels. However, establishing a direct causal relationship between Sod1 and Tor would require additional experiments, which we feel might be a good study in its own merit. To maintain clarity and focus in the revised manuscript, we have opted not to include this preliminary data at this stage.

I.The over-expression of SOD in CySCs part is incomplete. The authors would need to monitor ROS in these testes. They would also need to examine with tj>SOD affects the size of the hub.

We value the reviewer's . To address this, we have now monitored ROS levels in the testes upon SOD overexpression in CySCs using DHE (Figure S5 I). Our results indicate a significant reduction in ROS levels compared to controls. 

Additionally, we examined hub size upon Sod1 overexpression and observed a slight, but statistically insignificant, reduction. As our study primarily focuses on ROS-mediated GSCCySC interactions, we did not include a detailed investigation on hub size regulation.

(2) Concept

Why would it be important to have a redox gradient across adjacent cells? The authors mention that ROS can be passed between cells, but it would be helpful for them to provide more details about where this has been documented to occur and what biological functions ROS transfer regulates.

We thank the reviewer for this insightful . We acknowledge that the concept of a redox gradient was not adequately conveyed, as the cell boundary was not clearly defined. To address this, we have revised our interpretation to propose that high ROS levels in one cell may influence the ROS levels in an adjacent cell through either direct transfer or as a secondary effect of altered niche maintenance signaling, rather than through the establishment of a gradient.

Regarding ROS transfer between cells, it has been documented in several biological contexts. For instance, hydrogen peroxide (H₂O₂) can diffuse through aquaporins, influencing signaling pathways in neighbouring cells (PMID: 17105724). We have incorporated these details and relevant references into the revised manuscript to enhance the conceptual understanding of ROS transfer. 

(3) Issues with the scholarship of the testis

a. Line 82 - There is no mention of BMPs, which are the only GSC-self-renewal signal. Upd/Jak/STAT is required for the adhesion of GSCs to the niche but not self-renewal (Leatherman and Dinardo, 2008, 2010). The author should read a review about the testis. I suggest Greenspan et al 2015. The scholarship of the testis should be improved.

We appreciate the reviewer’s feedback regarding the role of BMPs in GSC selfrenewal, we have added this in the revised manuscript (line no. 83) We have now incorporated a discussion on BMP signaling as the primary self-renewal signal for GSCs, distinguishing it from the role of Upd/JAK/STAT in niche adhesion, as highlighted in Leatherman and Dinardo (2010). Additionally, we have cited and reviewed the work by Greenspan et al. (2015) and ensure a more comprehensive discussion of GSC regulation. These revisions can be found in the line no. 285-289 of the revised manuscript.

b. Line 82-84 - BMPs are produced by both hub cells and CySCs. BMP signaling in GSCs represses bam. So it is not technically correct to say the CySCs repress bam expression in GSCs.

We acknowledge the reviewer’s clarification regarding BMP signaling and its role in repressing bam expression in GSCs. We have revised the relevant section (line no.83-85). 

c.Throughout the figures the authors score Vasa⁺ cells for GSCs. This is technically not correct. What they are counting is single, Vasa⁺ cells in contact with the niche. All graphs should be updated with the label "GSCs" on the Y-axis.

We appreciate the reviewer’s careful assessment of our methodology. We acknowledge that scoring Vasa⁺ cells alone does not definitively identify GSCs. Our quantification specifically considers single Vasa^⁺ cells in direct contact with the niche. To ensure clarity and accuracy, we have updated all figure legends and Y-axis labels in the relevant graphs to explicitly state "GSCs" instead of "Vasa⁺ cells."

(4) Issues with the text

a. Line 1: multi-lineage is not correct. Multi-lineage refers to stem cells that produce multiple types of daughter cells. GSCs produce only one type of offspring and CySCs produce only one type of offspring. So both are uni-lineage. Please change accordingly.

We acknowledge the incorrect usage of "multi-lineage" and agree that both GSCs and CySCs are uni-lineage, as they each produce only one type of offspring. We have revised Line 1 accordingly and also updated the title. 

b. Lines 62-75 - Intestinal stem cells have constitutively high ROS (Jaspar lab paper), so low ROS in stem cell cells is not an absolute.

We appreciate the clarification. We have revised Lines 62–75 to acknowledge that low ROS is not universal in stem cells, citing the Jaspar lab study on intestinal stem cells (Line 70). Thank you for the valuable insight.

c.  Line 79: The term cystic is not used in the Drosophila testis. There are cyst stem cells (CySCs) that produce cyst cells. Please revise.

We have revised the text to replace "cystic" with the correct terminology, referring to cyst stem cells (CySCs) in the manuscript.

d. Line 90 - perfectly balanced is an overstatement and should be toned down.

Thank you for the suggestion. We have revised it to “balanced” instead of "perfectly balanced."  

e. Line 98 - division of labour is not supported by the data and should be rephrased.

Thank you for the feedback. We have rephrased it (line no. 98-101) to avoid the term "division of labor".

f. Line 200 - the authors provide no data on BMPs - the GSC self-renewal cue - so they should avoid discussing an absence of self-renewal cues.

We appreciate the reviewer’s point. We have revised it to avoid discussing the absence of self-renewal cues, given that we do not present data on BMP signaling. This ensures that our conclusions remain within the scope of the provided data.

(5) Issues with the figures

a The images are too small to appreciate the location of mitochondria in GSCs and CySCs.

b. Figure 1

c. cell membranes are not marked, reducing the precision of assigning mitochondria to GSC or CySCs. It would be very helpful if the authors depleted ATP5A from GSCs and showed that the puncta are reduced in these cells, and did a similar set of experiments for the Tj-Gal4 lineage. It would also be very helpful if the authors expressed membrane markers (like myrGFP) in the GSC and then in the CySC lineage and then stained with ATP5A. This would pinpoint in which cells ATP5A immunoreactivity is occurring.

d. The presumed changes in gst-GFP (redox readout) are possibly seen in differentiating germ cells (i.e.,spermatogonia) but not in GSC. iii. Panels F, Q, and S are not explained and currently are irrelevant.

e. Figure 3K - The evidence to support less Ecad in GSCs in tj>SOD-i testes is not compelling as the figure is too small and the insets show changes in Ecad in somatic cells, not GSC. d. Figure 4:

f. Panel A, B The apparent decline (not quantified) may not contribute to the phenotype.

ii.dpERK is a finicky antibody and the authors are showing a single example of each genotype. This is an important experiment because the authors are going to use it to conclude that MAPK is decreased in the tj>SOD-i samples. However, the authors don't have any positive (dominantactive EGFR) or negative (tj>mapk-i). As is standing, the data is not compelling. The graph in F does not convey any useful information.

g. Figure S1D - cannot discern green on black. It is critical for the authors to show monochromes (grayscale) for thereabouts that they want to emphasize. I cannot see the green on black in Figure S1D.

h. Figure S4 - there is no quantification of the number of Tj cells in K-N.

We appreciate your detailed feedback regarding the figures in our manuscript. Below, we address each concern and outline the revisions we have made.

(a) Image Size and Mitochondrial Localization in GSCs and CySCs 

We acknowledge the need for larger images to better visualize mitochondrial localization. We have now increased the resolution and size of the images in Figure 1. Additionally, we have included high-magnification insets to enhance clarity (Figure 1 B#)

(b) Figure 1 B,B#,C 

(i) We have now marked cell membranes using Dlg to improve the precision of mitochondrial assignment to GSCs and CySCs and then stained for ATP5A, which clearly demarcates ATP5A immunoreactivity in specific cell types.

(ii) We have revisited the gstD-GFP (redox readout) data and now provide revised images (Figure S1C-D’’’) and quantification (Figure 1 R,S) to better illustrate changes in the redox state. It is indeed intense in differentiating germ cells as expected but also present in the stem cell zone.

(iii) Panels F, Q, and S have now been removed in the revised figure legend. 

(C) Figure 3K: We have digitally magnified the figure size and improved contrast to better visualize E-cadherin levels. The insets have been revised to ensure they focus specifically on GSCs rather than somatic cells. Earlier, we quantified the E-cadherin intensity changes in the GSC-hub interface and provided statistical analysis to support our findings (Figure 3M).

(d) Figure 4: (i) Panels A and B have now been quantified, and we provide statistical comparisons to support our observations. (ii) We acknowledge the variability of dpERK staining. To strengthen our conclusions, we have provided negative (Tj>MAPK-i) controls (Figure S4 B). Additionally, we have removed panel F (MAPK area cover) to avoid confusion.

(e) We appreciate the suggestion regarding grayscale images and have provided the monochrome images for mitochondria and gstD-GFP image representation. We have now removed Figure S1D as it was no longer required.

(f) Figure S4: The quantification of the number of Tj-positive cells was actually included in the main figure along with statistical analysis.

(g) We sincerely appreciate the reviewer’s insightful s, which have significantly improved the quality and clarity of our manuscript. We hope that our revisions adequately address the concerns raised.

(6) Issues with Methods

a.  Materials and Methods are not described in sufficient depth - please revise.

b.  Note that Tj-Gal4 has real-time expression in hub cells and this is not considered by the authors. The ideal genotype for targeting CySCs is Tj-Gal4, Gal80TS, hh-Gal80. Additionally, the authors do not mention whether they are depleting throughout development into adulthood or only in adults. If the latter, then they must have used a temperature shift, growing the flies at 18C and then upshifting to 25C or 29C during adult stages.

c.  The authors need to show data points in all of the graphs. Some graphs do this but others do not.

d.  The authors state that all data points are from three biological replicates. This is not sufficient for GSC and CySC counts. Most labs count GSCs and CySCs from at least 10 testes of the correct genotype.

We appreciate the reviewer’s valuable feedback and have made the necessary revisions to improve the clarity and rigor of our study. Below, we address each concern in detail:

Materials and Methods

We have revised the Materials and Methods section to provide a more detailed description of the experimental procedures, including genotypes, sample preparation, and quantification methods.

Tj-Gal4 Expression and Experimental Design

We acknowledge the reviewer’s point regarding Tj-Gal4 expression in hub cells. While Tj-Gal4 is active in hub cells, our focus was on CySCs, and we have now included a discussion of this caveat in the revised manuscript (line no. 308-311)

Thank you for your suggestion on the ideal genotype for targeting CySCs. While we attempted to procure hh-Gal80, we couldn’t manage to get it, so we opted for another well-established Gal4 driver, C-587 Gal4, to target CySCs. Our results indicate that although the phenotypic changes are consistent across both drivers, the effects are significantly stronger with Tj-Gal4, highlighting the role of CySCs in this process with partial contributions from the hub. These findings have been incorporated into the revised manuscript (lines 309–311).

We now clarify whether gene depletion was conducted throughout development or restricted to adulthood. For adult-specific depletion using the UAS-Gal4 system, crosses were set up at 25°C, and after two days, progenies were shifted to 29°C and aged for 3–5 days at 29°C. This process is now explicitly detailed in the revised Methods section (line no. 345-348).

Data Presentation in Graphs

We have updated all graphs to ensure that individual data points are shown consistently across all figures.

Sample Size for GSC and CySC Counts

We acknowledge the reviewer’s concern regarding biological replicates. Our initial study was based on 10 biological replicates, each set consisting of at least 7-8 testes per genotype, in line with standard practice in the field. This change is reflected in the revised Results and Methods sections.

eLife Assessment

This study provides valuable insights into the influence of sex on bile acid metabolism and the risk of hepatocellular carcinoma (HCC). The data to support that there are inter-relationships between sex, bile acids, and HCC in mice are convincing, although this is a largely descriptive study. Future studies are needed to understand the interaction of sex hormones, bile acids, and chronic liver diseases and cancer at a mechanistic level. Also, there is not enough evidence to determine the clinical significance of the findings given the differences in bile acid composition between mice and men.

Reviewer #1 (Public review):

Liver cancer shows a high incidence in males than females with incompletely understood causes. This study utilized a mouse model that lacks the bile acid feedback mechanisms (FXR/SHP DKO mice) to study how dysregulation of bile acid homeostasis and a high circulating bile acid may underlie the gender-dependent prevalence and prognosis of HCC. By transcriptomics analysis comparing male and female mice, unique sets of gene signatures were identified and correlated with HCC outcomes in human patients. The study showed that ovariectomy procedure increased HCC incidence in female FXR/SHP DKO mice that were otherwise resistant to age-dependent HCC development, and that removing bile acids by blocking intestine bile acid absorption reduced HCC progression in FXR/SHP DKO mice. Based on these findings, the authors suggest that gender-dependent bile acid metabolism may play a role in the male-dominant HCC incidence, and that reducing bile acid level and signaling may be beneficial in HCC treatment. This study include many strengths: 1. Chronic liver diseases often proceed the development of liver and bile duct cancer. Advanced chronic liver diseases are often associated with dysregulation of bile acid homeostasis and cholestasis. This study takes advantage of a unique FXR/SHP DKO model that develop high organ bile acid exposure and spontaneous age-dependent HCC development in males but not females to identify unique HCC-associated gene signatures. The study showed that the unique gene signature in female DKO mice that had lower HCC incidence also correlated with lower grade HCC and better survival in human HCC patients. 2. The study also suggests that differentially regulated bile acid signaling or gender-dependent response to altered bile acids may contribute to gender-dependent susceptibility to HCC development and/or progression. 3. The sex-dependent differences in bile acid-mediated pathology clearly exist but are still not fully understood at the mechanistic level. Female mice have been shown to be more sensitive to bile acid toxicity in a few cholestasis models, while this study showed a male dominance of bile acid promotion of HCC. This study used ovariectomy to demonstrate that female hormones are possible underlying factors. Future studies are needed to understand the interaction of sex hormones, bile acids, and chronic liver diseases and cancer.

Author response:

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

Reviewer #1 (Public review):

Comments:

(1) HCC shows heterogeneity, and it is unclear what tissues (tumor or normal) were used from the DKO mice and human HCC gene expression dataset to obtain the gene signature, and how the authors reconcile these gene signatures with HCC prognosis.

Mice studies: Aged DKO mice develop aggressive tumors (major and minor nodules, See Figure 1), and the entire liver is burdened with multiple tumor nodules. It is technically challenging to demarcate the tumor boundaries as most of the surrounding tissues do not display normal tissue architecture. Therefore, livers from age- and sex-matched wild-type C57/BL6 mice were used as control tissue. All the mice were inbred in our facility. Spatial transcriptomics and longitudinal studies are ongoing to collect tumors at earlier time points wherein we can differentiate tumor and non-tumor tissue.

Human Studies: We mined five separate clinical data sets. The human HCC gene expression comprised of samples from the (i) National Cancer Institute (NCI) cohort (GEO accession numbers, GSE1898 and GSE4024) and (ii) Korea, (iii) Samsung, (iv) Modena, and (v) Fudan cohorts as previously described (GEO accession numbers, GSE14520, GSE16757, GSE43619, GSE36376, and GSE54236). We have added a new supplemental table 4, giving details of these datasets. Depending on the cohort, they are primarily HCC samples- surgical resections of HCC, control samples, with some tumors and paired non-tumor tissues.

(2) The authors identified a unique set of gene expression signatures that are linked to HCC patient outcomes, but analysis of these gene sets to understand the causes of cancer promotion is still lacking. The studies of urea cycle metabolism and estrogen signaling were preliminary and inconclusive. These mechanistic aspects may be followed up in revision or future studies.

We agree. Experiments to elicit HCC causality and promotion are complex, given the heterogeneous nature of liver cancer. Moreover, the length of time (12 months) needed to spontaneously develop cancer in this DKO mouse model makes it challenging. As mentioned by the reviewer, mechanistic studies are ongoing, and longitudinal time course experiments are actively being pursued to delineate causality. Having said that, we mined the TCGA LIHC (The Cancer Genome Atlas Liver Hepatocellular Carcinoma) database to examine the expression of the individual urea cycle genes and found them suppressed in liver tumorigenesis (new Supplementary Figure 4). We also evaluated if estrogen receptor a (Era) targets altered in DKO females (DKO_Estrogen) correlate with overall survival in HCC (new Supplementary Figure 6). We note that Era expression per se is reduced in males and females upon liver tumorigenesis. Also, DKO_Estrogen signature positively corroborated with better overall survival (new Supplementary Figure 6). These findings further bolster the relevance of urea cycle metabolism and estrogen signaling during HCC.

(3) While high levels of bile acids are convincingly shown to promote HCC progression, their role in HCC initiation is not established. The DKO model may be limited to conditions of extremely high levels of organ bile acid exposure. The DKO mice do not model the human population of HCC patients with various etiology and shared liver pathology (i.e. cirrhosis). Therefore, high circulating bile acids may not fully explain the male prevalence of HCC incidence.

We agree with this comment that our studies do not show bile acids can initiate HCC and may act as one of the many factors that contribute to the high male prevalence of HCC. This is exactly the reason why throughout the manuscript we do not write about HCC initiation. To clarify further, in the revised discussion of the manuscript, we have added a sentence to highlight this aspect, “while this study demonstrates bile acids promote HCC progression it does not investigate or provide evidence if excess bile acids are sufficient for HCC initiation.”

(4) The authors showed lower circulating bile acids and increased fecal bile acid excretion in female mice and hypothesized that this may be a mechanism underlying the lower bile acid exposure that contributed to lower HCC incidence in female DKO mice. Additional analysis of organ bile acids within the enterohepatic circulation may be performed because a more accurate interpretation of the circulating bile acids and fecal bile acids can be made in reference to organ bile acids and total bile acid pool changes in these mice.

As shown in this manuscript- we provide BA compositional analyses from the liver, serum, urine, and feces (Figures 5 and 6, new Supplementary Figure 8, Supplementary Tables 4 and 5). Unfortunately, we did not collect the intestinal tissue or gallbladders for BA analysis in this study. Separate cohorts of mice are being aged for future BA analyses from different organs within the enterohepatic loop. We thank you for this suggestion. Nevertheless, we have previously measured and reported BA values to be elevated in the intestines and the gall bladder of young DKO mice (PMC3007143).

Reviewer #2 (Public review)

Weaknesses:

(1) The translational value to human HCC is not so strong yet. Authors show that there is a correlation between the female-selective gene signature and low-grade tumors and better survival in HCC patients overall. However, these data do not show whether this signature is more highly correlated with female tumor burden and survival. In other words, whether the mechanisms of female protection may be similar between humans and mice. In that respect, it would also be good to elaborate on whether women have higher fecal BA excretion and lower serum BA concentration.

The reviewer poses an interesting question to test if the DKO female-specific signatures are altered differently in male vs. female HCC samples. As we found the urea cycle and estrogen signaling to be protective and enriched in our mouse model, we tested their expression pattern using the TCGA-LIHC RNA-seq data. We found urea cycle genes and Era transcripts broadly reduced in tumor samples irrespective of the sex (new Supplementary Figure 4 and Supplementary Figure 6), indicating that these pathways are compromised upon tumorigenesis even in the female livers.

While prior studies have shown (i) a smaller BA pool w synthesis in men than women (PMID: 22003820), we did not find a study that systematically investigated BA excretion between the sexes in HCC context. The reviewer is spot on in suggesting BA analysis from HCC and unaffected human fecal samples from both sexes. Designing and performing such studies in the future will provide concrete proof of whether BA excretion protects female livers from developing liver cancer. We thank you for these suggestions.

(2) The authors should perform a thorough spelling and grammar check.

We apologize for the typos, which have been fixed, and as suggested by the reviewer, we have performed a grammar check.

(3) There are quite some errors and inaccuracies in the result section, figures, and legends. The authors should correct this.

We apologize for the inadvertent errors in the manuscript, and we have clarified these inaccuracies in the revised version. Thank you.

eLife Assessment

This study presents data on sex differences in gene expression across organs of four mice taxa. The authors have generated a unique and convincing dataset that fills a gap left by previous studies. They claim that sex-biased expression in the soma can overlap between genetic males and females, and that the relevant patterns both turn over quickly over short evolutionary times and do so faster in somatic than gonadal tissues. These conclusions could largely have been predicted by extrapolating from previous findings in the field, but nevertheless demonstrating them directly is a fundamental advance.

[Editorial note: The work was originally assessed by colleagues who are active in the field of evolution of sex differences or in areas adjacent to this field (see initial assessment at https://doi.org/10.7554/eLife.99602.2). The appeals process involved consultation with experts working in other areas of evolutionary biology. The above assessment synthesises the opinions of both sets of reviewers.]

Reviewer #4 (Public review):

The paper by Xie et al. investigates the micro-evolutionary dynamics of sex-biased gene expression across somatic and gonadal tissues in four mouse taxa, with comparative analyses in humans. The study introduces a new metric, the Sex-Bias Index (SBI), to quantify individual-level variation in sex-biased gene expression, and explores the evolutionary turnover, variance, and adaptive evolution of these genes.

These strengths of the paper are not in dispute:

Novelty: The study is among the first to systematically analyze sex-biased gene expression at a micro-evolutionary scale in outbred animals, using closely related mouse taxa. This contrasts with most previous work, which focused on macro-evolutionary comparisons between distant species.

Controlled Sampling: The use of age-matched, outbred individuals raised under standardized conditions minimizes environmental confounders, allowing for robust within- and between-taxon comparisons.

Somatic vs. Gonadal Focus: Unlike many earlier studies that emphasized gonadal tissues, this work provides a detailed analysis of somatic organs, revealing rapid evolutionary turnover and mosaicism in sex-biased gene expression.

Sex-Bias Index (SBI): The SBI offers a cumulative, individual-level measure of sex-biased gene expression, facilitating visualization of variance and overlap between sexes within tissues. While one can argue about whether a new metric is necessary (as the authors argue), the combination of fold-change cutoffs, non-parametric Wilcoxon tests, and FDR correction reduces false positives, addressing concerns raised in the field about inflated detection of sex-biased genes.

Evolutionary implications: The study demonstrates that sex-biased gene expression in somatic tissues evolves more rapidly than in gonads, and that this turnover is often accompanied by signatures of adaptive protein evolution. The lack of correlation in SBI across tissues within individuals supports a mosaic model of sex-biased gene expression, challenging binary models of sexual differentiation.

The weaknesses are already listed by previous rounds of review but I will add one more: in an attempt to be comprehensive, the writing is quite dry and the main conclusions sort of get hidden within the less important observations.

Since the debate is mostly about what words to use to describe the importance and the strength of evidence, I thought it would be useful to directly compare this study to other studies that address the same topic:

Naqvi et al. Science 2019 (David Page lab): Conservation, acquisition, and functional impact of sex-biased gene expression in mammals

Oliva et al. Science 2020 (Stranger lab): The impact of sex on gene expression across human tissues

Rodríguez-Montes et al. Science 2023 (Kaessman, Cardoso-Moreira labs)

Let's start with the fact that all three peer studies have had a major impact. Second, although Naqvi et al. (2019) and Oliva et al. (2020) provided foundational cross-species and cross-tissue analyses of sex-biased gene expression, but did not address micro-evolutionary turnover or individual-level variance. Third, Rodríguez-Montes et al. (2023) focused on developmental and evolutionary patterns of sex-biased expression, but at a broader phylogenetic scale and without the individual-level or module-based analyses presented here. None of the peer studies addressed the possibility of mosaicism within individuals, none of them addressed the relations between expression bias and adaptive evolution. So the comparison is really a bit of an apples to oranges comparison: the peer studies are about patterns in deep phylogeny, whereas the present study is an amazing (to me) analysis of inter-individual mosaicism, which is at the heart of this kind of variation, which would totally be missed or worse misinterpreted in deep phylogenetic analyses. Having said that, in my subjective opinion, all three related papers are better written than the present one, but to me there is no question this belongs in the same pedestal as all of them.

Reviewer #5 (Public review):

Xie et al. present a data set of impressive size to study changes in sex-biased gene expression. A clear strength that sets the study apart from previous work is the use of age-matched outbred individuals raised in the same environment, which minimizes non-genetic variance, and the comparison of closely related taxa. Also in contrast to many previous studies, while gonads, which have often been the focus of sex-biased gene expression studies, are not ignored, multiple gonadal tissues are being compared to an array of somatic tissues. The study design therefore can offer a particularly rich and nuanced view of how sex differences change across tissues and over short evolutionary times.

I liked the idea of summarizing over the mean expression of gene sets, instead of just using numbers of DEGs for comparisons, even though the introduction of the term "Sex-Biased Index (SBI)" seems somewhat of an overkill. The summary analyses are definitely useful to visualize variability in sex-biased gene expression programs. The authors find that the expression patterns of sex-biased genes change faster than those of non-sex-biased genes - but only in somatic tissues. They also provide some evidence that this correlates with higher rates of potentially adaptive coding sequence changes in the taxa where expression is sex-biased, with the proviso that a stronger modeling framework would have made these inferences more robust.

I was most surprised by the finding that the fast change in expression patterns is linked to different gene expression modules becoming sex-biased in the different taxa studied. This is in my eyes a remarkable observation that could not have been predicted from previous knowledge.

The use of human GTEx and patient scRNA-seq data is a nice addition, although there are known confounding issues with these resources, given that these are not random samples and environmental conditions are uncontrolled. Nevertheless, as the human data echo the trends seen with the much more rigorous mouse data set, I do not have principal objections to this addition. Furthermore, the human data do allow the authors to conclude that only very few genes with sex-biased expression are shared in the soma of mice and humans.

In summary, I believe that this contribution has the potential to fundamentally change how we see sex-biased gene expression differences in vertebrates, given that the author's conclusions are grounded in a data set of compelling quality and size.

Author response:

The following is the authors’ response to the previous reviews

Reviewer #2 (Public review):

Summary:

The manuscript by Xie and colleagues presents transcriptomic experiments that measure gene expression in eight different tissues taken from adult female and male mice from four species. These data are used to make inferences regarding the evolution of sex-biased gene expression across these taxa.

Strengths:

The experimental methods and data analysis appear appropriate. The authors promote their study as unprecedented in its size and technical precision.

We do not understand the statement "the authors promote" as if there was a doubt about this. If there is a doubt, we welcome to see it specified.

Weaknesses:

The manuscript does not present a clear set of novel evolutionary conclusions. The major findings recapitulate many previous comparative transcriptomics studies - gene expression variation is prevalent between individuals, sexes, and species; and genes with sex-biased expression evolve more rapidly than genes with unbiased expression - but it is not clear how the study extends our understanding of gene expression or its evolution.

There have been no "previous comparative transcriptomics studies" at a micro- evolutionary scale in animals, hence, we do not "replicate" these. And our contrast between somatic and gonadal patterns reveals insights that have not been recognized before, namely that gonadal sex-specific expression turnover is actually not faster that the corresponding non-sex-specific truover. We have now further clarified this distinction throughout the text and have also adapted the title of the paper accordingly.

We agree with the overall statement that "gene expression variation is prevalent between individuals, sexes, and species" but the aspect of "sex-biased gene expression between individuals" has not been systematically analysed before in such a context.

Concerning the statement that "genes with sex-biased expression evolve more rapidly than genes with unbiased expression", we note that this is mostly derived from gonadal data and that there is no study that has quantified this so far at a population level and between subspecies in comparison to somatic data.

Our results show further that previous assumptions of a substantial set of genes with sex- biased expression conserved between mice and humans are due to underestimating the convergence issues when there is an extremly fast turnover of sex-biased gene expression. This has a major implication for using mice as a model for gender-speficic medicine questions in humans.

Many gene expression differences between individual animals are selectively neutral, because these differences in mRNA concentration are buffered at the level of translation, or differences in protein abundance have no effect on cellular or organismal function. The hypothesis that sex-biased genes are enriched for selectively neutral expression differences is supported by the excess of inter-individual expression variance and inter-specific expression differences in sex-biased genes.

This statement repeats a statement from the first round of reviews. We had added new data and extensive discussion on this topic. We do not understand why this has not been taken into account. In fact, a major strength of our paper is that it shows that most sex- biased gene expression differences are not neutral!

There are two major issues here: to identify sex-biased gene expression in the first place, we (and all other papers in the field) use the neutral model as null-hypothesis. Genes that are not compatible with this null-hypothesis are considered sex-biased. In contrast to most previous papers, we have the possibility to take into account the variances between individuals to add an additional significance test. Hence, we can apply a much more rigorous two-step process: first a ratio-cutoff plus a Wilcoxon rank sum test with correction for multiple testing to identify significant deviations from the null-hypothesis. We have added some additional statements in the Results and Discussion sections to emphasize this.Second, by focusing on the genes that are not following a neutral model, the variance and divergences data support the action of selection, rather than neutral drift.

A higher rate of adaptive coding evolution is inferred among sex-biased genes as a group, but it is not clear whether this signal is driven by many sex-biased genes experiencing a little positive selection, or a few sex-biased genes experiencing a lot of positive selection, so the relationship between expression and protein-coding evolution remains unclear.

Again, there are two major issues here. First, the distribution of alpha-values shown in Figure 3B are rather homogeneous, i.e. there is not support for a scenario that the average is driven by only a few genes.

Second, it seems that the referee wants to see an analysis where dn/ds ratios are broken down for every single gene. This has been done in previous papers, but it is now understood that this procedure is fraught with error because of the demographic contingencies inherent to natural populations that can yield wrong results for individual loci. We have added some statements to the text to clarify this further.

It is likely that only a subset of the gene expression differences detected here will have phenotypic effects relevant for fitness or medicine, but without some idea of how many or which genes comprise this subset, it is difficult to interpret the results in this context.

It is the basic underlying assumption for the whole research field that significantly sex- biased genes are phenotypically relevant for fitness, since they would otherwise not be sex- biased in the first place.

Throughout the paper the concepts of sexual selection and sexually antagonistic selection are conflated; while both modes of selection can drive the evolution of sexually dimorphic gene expression, the conditions promoting and consequence of both kinds of selection are different, and the manuscript is not clear about the significance of the results for either mode of selection.

We had explained in our previous response that our data collection was not designed to distinguish between these two processes. But given that the issue is being brought up again, we have now added some discussion on this issue.

The manuscript's conclusion that "most of the genetic underpinnings of sex-differences show no long-term evolutionary stability" is not supported by the data, which measured gene expression phenotypes but did not investigate the underlying genetic variation causing these differences between individuals, sexes, or species.

We agree that - under a strict definition - our use of the term "genetic underpinning" in this conclusion sentence can be criticized. The most correct term would be "transcriptional underpinnings", but of course, given that it is the current practice of the whole field to assume that "transcriptional" is part of the overall genetics, we do not consider our initial statement as incorrect. Still, we have changed the term accordingly.

Furthermore, most of the gene expression differences are observed between sex-specific organs such as testes and ovaries, which are downstream of the sex-determination pathway that is conserved in these four mouse species, so these conclusions are limited to gene expression phenotypes in somatic organs shared by the sexes.

Yes - correct. But the whole focus of the paper is on somatic expression, i.e. organs that share the same cell compositions. Of course, the comparison between gonadal organs is conflated by being composed of different cell types. We have extended the discussion of this point.

The differences between sex-biased expression in mice and humans are attributed to differences in the two species effective population sizes; but the human samples have significantly more environmental variation than the mouse samples taken from age-matched animals reared in controlled conditions, which could also explain the observed pattern.

These are indeed the two alternative explanations that we had discussed (last paragraph of the discussion section, now the penultimate paragraph).

The smoothed density plots in Figure 5 are confusing and misleading. Examining the individual SBI values in Table S9 reveals that all of the female and male SBI values for each species and organ are non-overlapping, with the exception of the heart in domesticus and mammary gland in musculus, where one male and one female individual fall within the range of the other sex. The smoothed plots therefore exaggerate the overlap between the sexes;

Smoothing across discrete values is an entirely standard procedure for continuous variables. It allows to visualize the inherent data trends that cannot easily be glanced from simple inspection of the actual values. This is a mathematical procedure, not an "exaggeration". We used the same smoothening procedure for all the comparisons, and it is clear that the distributions between females and males of the sex organs and a few somatic organs are well separated (non-overlapping), which serves as a control.

in particular, the extreme variation shown in the SBI in the mammary glands in spretus females and spicilegus males is hard to understand given the normalized values in Table S3. The R code used to generate the smoothed plots is not included in the Github repository, so it is not possible to independently recreate those plots from the underlying data.

We apologize that there was indeed an error in the Figure - the columns for SPR and SPI were accidentally interchanged. We have corrected this figure. Generally, the smoothened patterns we show are easily verified by looking up the respective primary values. We apologize that the code lines for the plots were accidentally omitted. We have used a standard function from ggplot2: geom_density, with "adjust=3, alpha=0.5" for all plots and included this description in the Methods. We have now added this to the R code in the GitHub repository.

The correlations provided in Table S9 are confusing - most of the reported correlations are 1.0, which are not recovered when using the SBI values in Table S9, and which does not support the manuscript's assertion that sex-biased gene expression can vary between organs within an individual. Indeed, using the SBI values in Table S9, many correlations across organs are negative, which is expected given the description of the result in the text.

There is a misunderstanding here. The tables do not report correlations, but only p-values for correlations, the raw ones and the ones after corrections for multiple testing. P = 1.0 means no significant correlation. We have adjusted the caption of this table to clarify this further.

Reviewer #3 (Public review):

This manuscript reports interesting data on sex differences in expression across several somatic and reproductive tissues among 4 mice species or subspecies. The focus is on sex- biased expression in the somatic tissues, where the authors report high rates of turnover such that the majority of sex-biased genes are only sex-biased in one or two taxa. The authors show sex-biased genes have higher expression variance than unbiased genes but also provide some evidence that sex-bias is likely to evolve from genes with higher expression variance. The authors find that sex-biased genes (both female- and male-biased) experience more adaptive evolution (i.e., higher alpha values) than unbiased genes. The authors develop a summary statistic (Sex-Bias Index, SBI) of each individual's degree of sex- bias for a given tissue. They show that the distribution of SBI values often overlap considerably for somatic (but not reproductive) tissues and that SBI values are not correlated across tissues, which they interpret as indicating an individual can be relatively "male-like" in one tissue and relatively "female-like" in another tissue.

This is a good summary of the data, but we are puzzled that it does not include the completely new module analysis and the finding of extremely fast evolution of sex-biased somatic gene expression compared to the gonadal one.

Though the data are interesting, there are some disappointing aspects to how the authors have chosen to present the work. For example, their criteria for sex-bias requires an expression ratio of one sex to the other of 1.25. A reasonably large fraction of the "sex- biased genes" have ratios just beyond this cut-off (Fig. S1). A gene which has a ratio of 1.27 in taxa 1 can be declared as "sex-biased" but which has a ratio of 1.23 in taxa 2 will not be declared as "sex-biased". It is impossible to know from how the data are presented in the main text the extent to which the supposed very high turnover represents substantial changes in dimorphic expression. A simple plot of the expression sex ratio of taxa 1 vs taxa 2 would be illuminating but the authors declined this suggestion.

Choosing a cutoff is the standard practice when dealing with continuously distributed data. As we have pointed out, we looked at various cutoff options and decided to use the present one, based on the observed data distributions. Note that some studies have used even lower ones (e.g. 1.1). To visualize the data distribution, we had provided the overall distribution of ratios, because one would have to look at many more plots otherwise. But we have now also added individual plots as Figure 1, Figure supplement 2, as requested. They confirm what is also evident from the overall plots, namely that most ratio changes are larger than the incremental values suggested by the reviewer. Note that the original data are of course also available for inspection.

I was particularly intrigued by the authors' inference of the proportion of adaptive substitutions ("alpha") in different gene sets. The show alpha is higher for sex-biased than unbiased genes and nicely shows that the genes that are unbiased in focal taxa but sex- biased in the sister taxa also have low alpha. It would be even stronger that sex-bias is associated with adaptive evolution to estimate alpha for only those genes that are sex- biased in the focal taxa but not in the sister taxa (the current version estimates alpha on all sex-biased genes within the focal taxa, both those that are sex-biased and those that are unbiased in the sister taxa).

We have added the respective values in the results section, but since fewer genes are involved, they are less comparable to the other sets of genes. Still, the tendencies remain.

The author's Sex Bias Index is measured in an individual sample as: SBI = median(TPM of female-biased genes) - median(TPM of male-biased genes). This index has some strange properties when one works through some toy examples (though any summary statistic will have limitations). The authors do little to jointly discuss the merits and limitations of this metric. It would have been interesting to examine their two key points (degree of overlapping distributions between sexes and correlation across tissues) using other individual measures of sex-bias.

We had responded to this comment before (including the explanation that it has no strange properties when one applies the normalization that is now implemented) and we have added a whole section devoted to the discussion of the merits of the SBI. We do not know which other "individual measures of sex-bias" this should be compared to. Still, we have now added a paragraph in the discussion about using PCA as an alternative to show that this would result in similar conclusions, but is technically less suitable for this purpose.

Figure 5 shows symmetric gaussian-looking distributions of SBI but it makes me wonder to what extent this is the magic of model fitting software as there are only 9 data points underlying each distribution. Whereas Figure 5 shows many broadly overlapping distributions for SBI, Figure 6 seems to suggest the sexes are quite well separated for SBI (e.g., brain in MUS, heart in DOM).

We use a standard fitting function in R (see above), which tries to fit a normalized distribution, but this function can also add an additional peak when the data are too heterogeneous (e.g. Mammary in Figure 7).

Fig. S1 should be shown as the log(F/M) ratio so it is easier to see the symmetry, or lack thereof, of female and male-biased genes.

The log will work differently for values <1, compared to values >1 when used in a single plot. We have now generated combined plots with symmetric values to allow a better comparability.

It is important to note that for the variance analysis that IQR/median was calculated for each gene within each sex for each tissue. This is a key piece of information that should be in the methods or legend of the main figure (not buried in Supplemental Table 17).

​We have now moved these descriptions into the Methods section.

eLife Assessment

This study investigated the role of insulin receptor (IR) and insulin-like growth factor 1 receptor (IGF1R) in the renal glomerular podocytes by characterizing the mice with dual deletion of both receptors in vivo as well as the cultured murine podocytes with induced deletion of both receptors in vitro. The solid data presented in this paper demonstrated the critical requirement of both IR and IGF1R signaling in normal podocyte physiology in mice, albeit a more detailed characterization of the mouse model is desired. Interestingly, long-range sequencing revealed significant retention of introns in mRNAs, due to an altered spliceosome level resulted from the loss of IR and IGF1 signaling in cultured podocytes. This new finding suggests an essential role of IR and IGF1R signaling in regulating RNA metabolism in podocyte, which provides useful information for the understanding of physiology and metabolism of podocytes. However, the underlying molecular mechanism for such a regulation is still unclear and awaits further studies.

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

Reviewer #1 (Public review):

Summary:

In this manuscript, the roles of the insulin receptor and the insulin growth factor receptor were investigated in podocytes. Mice in which both receptors were deleted developed glomerular dysfunction and developed proteinuria and glomerulrosclerosis over several months. Because of concerns about incomplete KO, the authors generated 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, the authors performed global proteomics and find that spliceosome proteins are down-regulated. They confirm this by using long-range sequencing. These results suggest a novel role for these pathways in podocytes.

This is primarily a descriptive study. The mechanism of how insulin and IGF1 signaling are linked to the spliceosome is not addressed and the phenotype of the mice is only superficially explored. 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. The mouse experiments would be improved if the serum creatinines were measured to provide some idea about the severity of the kidney injury. An attempt to rescue the phenotype by overexpression of SF3B4 would also be useful. If this didn't rescue the phenotype, an explanation in the text would suffice. As insulin and IGF are regulators of metabolism, some assessment of metabolic parameters would be an optional add-on. Lastly, in the cell line experiments, the authors should discuss the caveats associated with studying the 50% of the cells that survive vs the ones that died.

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, therefore, 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.

Comments on revision plan:

I agree with the suggested experiments especially, the experiments to examine whether insulin/IGF1 signaling have effects on splicing proteins. An alternative experiment would be to ask whether rescue of IR or IGF1R would ameliorate the splicing effects.

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, with bars/superimposed dot-plots.

Methods are generally well described. It would be helpful to say that tissue scoring was performed by an investigator masked to sample identity.

Specific comments:

(1) 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.

(2) 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 typical for this method; a reference could be helpful.

(3) Please explain "adjusted p value of 0.01." It is not clear how was it adjusted. The number of differentially-expressed proteins between the two cell types was 4842.

Comments on revision plan:

The authors suggest additional experiments that should address my concerns and probably the other reviewers' concerns.

I encourage the authors to proceed with their proposed experiments and revisions.

Reviewer #3 (Public review):

Summary:

These investigators have previously shown important roles for either insulin receptor (IR) or insulin-like growth factor receptor (IGF1R) in glomerular podocyte function. They now have studied mice with deletion of both receptors and find significant podocyte dysfunction. They then made a podocyte cell line with inducible deletion of both receptors and find abnormalities in transcriptional efficiency with decreased expression of spliceosome proteins and increased transcripts with impaired splicing or premature termination.

The studies appear to be performed well and the manuscript is clearly written.

There are a number of potential issues and questions with these studies.

(1) 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?

(2) 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.

(3) 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.

(4) There are no studies investigating signaling mechanisms mediating the spliceosome abnormalities.

Comments on revision plan:

I do not have any changes from my prior review. I applaud the authors for developing a plan to address the questions and concerns raised in my prior review.

Author response:

Evidence reducibility and clarity

Reviewer 1:

In this manuscript, the role of the insulin receptor and the insulin growth factor receptor was investigated in podocytes. Mice, were both receptors were deleted, developed glomerular dysfunction and developed proteinuria and glomerulosclerosis over several months. Because of concerns about incomplete KO, the authors generated 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, the authors performed global proteomics and find that spliceosome proteins are downregulated. They confirm this by using long-range sequencing. These results suggest a novel role for these pathways in podocytes.

Thank you

This is primarily a descriptive study and no technical concerns are raised. The mechanism of how insulin and IGF1 signaling are linked to the spiceosome is not addresed.

We do not think the paper is descriptive as we used non-biased phospho and total proteomics in the DKO cells to uncover the alterations in the spliceosome (that have not been previously described) that were detrimental. However, we are happy to look further into the underlying mechanism.

We would propose:

(1) Stimulating/inhibiting insulin/IGF signalling pathways in the Wild-type and DKO knockout cells and check expression levels and/or phosphorylation status of splice factors (including those in Figure 3E) and those revealed by phospho-proteomic data; a variety of inhibitors of insulin/IGF1 pathways could also be used along the pathways that are shown in Fig 2.

(2) Looking at the RNaseq data bioinformatically in more detail – the introns/exons that move up or down are targets of the splice factors involved; most splice factors binding sequences are known, so it should be possible to ask bioinformatically – from the sequences around the splice sites of the exons and introns that move in the DKO, which splice factors binding sites are seen most frequently? To uncover splice factors/RNA-binding proteins (RBPs) that are involved in the insulin signaling we will use a software named MATT which was specifically designed to look for RNA-binding motifs (PMID 30010778). In brief, using the long-sequencing data, we will test 250 nt sequences flanking the splice sites of all regulated splicing events (intronic and exonic) against all RNA- binding proteins in the CISBP-RNA database (PMID 23846655) using MATT. This will result in a list of RBPs potentially involved in the insulin signaling. We will validate these by activating insulin signaling (similar to Figures 2 B,C) and probe whether the RBPs are activated (e.g. phosphorylated or change in expression) or we will manipulate expression of the candidate RBPs and measure how they affect the insulin signaling.

(3) Examining the phospho and total proteomic data for IGF1R and Insulin receptor knockout alone podocytes (which we have already generated) and analysing these in more detail and include this data set to elucidate the relative importance of both receptors to spliceosome function.

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.

We apologise for not making clear but we did assess the level of receptor knockdown in 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 1B). This is why we made the in vitro  floxed podocyte cell lines in which we could robustly knockdown both the insulin receptor and IGF1 receptor (shown in Figure 2A)

The mouse experiments would be improved if the serum creatinines were measured to provide some idea how severe the kidney injury is.

We can address this:

We have further urinary Albumin:creatinine ratio (uACR) data at 12, 16 and 20 weeks. We also have more blood tests of renal function that can be added. There is variability in creatinine levels which is not uncommon in transgenic mouse models (probably partly due to variability in receptor knock down with cre-lox system). This is part of rationale of developing the robust double receptor knockout cell models where we knocked out both receptors by >80%.

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.

We would consider  over express SF3BF4 in the Wild type and DKO cells and assess the effects on spliceosome if deemed necessary.  However, we think it is unlikely to rescue the phenotype as so many other spliceosome components are downregulated in the DKO cells.

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

We have some detail on this and can add to the manuscript. However it is not extensive as not a major driver of this work.

Lastly, 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.

Thank you, we appreciate this and this was the rationale behind cells being studied after 2 days differentiation before significant cell loss in order to avoid the issue of studying the 50% of cells that survive.

Reviewer 2:

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.<br /> Specific comments.

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

Thank you

Evaluation.

Methods are generally well described. It would be helpful to say that tissue scoring was performed by an investigator masked to sample identity.

We did this and will add this information to the methods/figure legend.

Specific comments.

(1) 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.

Graphs can be changed to SD rather than SEM.

(2) 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 typical for this method; a reference could be helpful.

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)

(3) Please explain "adjusted p value of 0.01." It is not clear how was it adjusted. The number of differentially-expressed proteins between the two cell types was 4842.

We used the Benjamini-Hochberg method to adjust our data. We think the reviewer is referring to the transcriptomic data and not the proteomic data.

Minor comments

Page numbers in the text would help the reviewer communicate more effectively with the author.

We will do this

Reviewer 3:

These investigators have previously shown important roles for either insulin receptor (IR) or insulin-like growth factor receptor (IGF1R) in glomerular podocyte function. They now have studied mice with deletion of both receptors and find significant podocyte dysfunction. They then made a podocyte cell line with inducible deletion of both receptors and find abnormalities in transcriptional efficiency with decreased expression of spliceosome proteins and increased transcripts with impaired splicing or premature termination.

The studies appear to be performed well and the manuscript is clearly written.

Thank you

Referees cross-commenting

I am in agreement with Reviewer 1 that the studies are overly descriptive and do not provide sufficient mechanism and the lack of more investigation of the in vivo model is a significant weakness.

Please see our responses to reviewer 1 above.

Significance

Reviewer 1:

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.

Thank you. The receptor  KO in the mice is unlikely to be complete (Please see comments above and Supplementary Figure 1b). There are many examples of KO 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 is also terminally differentiated cells PMID:28595357 (barely 50% iof IGF1R knockdown was achieved in the target cells). 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 floxed gene (PMID: 38706850) hence we were not surprised that trying to excise two floxed genes (insulin receptor and IGF1 receptor) was challenging. This is the rationale for making the double receptor knockout cell lines to understand process / biology in more detail.

Reviewer 2:

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

Evaluation.

Methods are generally well described. It would be helpful to say that tissue scoring was performed by an investigator masked to sample identity.

Thank you we will do this.

Reviewer 3:

There are a number of potential issues and questions with these studies.

(1) 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?

Thank you we will add in further phenotyping data. We do not think there was a major developmental phenotype as  albuminuria did not become significantly different until several months of age. We could have used a doxycycline inducible model but we know the excision efficiency is much less than the podocin-cre driven model SUPP FIGURE 1. This would likely give a very mild (if any) phenotype and not reveal the biology adequately.

(2) 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.

Thank you for this we are happy to employ Immunohistochemistry (IHC) and immunofluorescence (IF) using spliceosome antibodies on tissue sections from DKO and control mice to examine spliceosome changes. However, as the DKO results in podocyte loss, there may not be that many DKO podocytes still present in the tissue sections. This will be taken into consideration.

(3) 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.

Thank you. We have full total and phospho-proteomic data sets from single insulin receptor and IGF1 receptor knockout cell lines that we will investigate for this point.

(4) There are not studies investigating signaling mechanisms mediating the spliceosome abnormalities.

Thank you as outlined as above to reviewer 1 point 1 we are very happy to investigate insulin / IGF signalling pathways in more detail.

eLife Assessment

In their important manuscript, Gangadharan, Kober and Rice focus on how Stu2/XMAP215-family microtubule polymerases use their TOG domains to catalytically promote microtubule growth, testing whether their mechanism follows an enzyme-like kinetic model similar to that of actin polymerases. The authors integrate measurements including microtubule polymerization rates and TOG-tubulin binding kinetics to convincingly show that Stu2 follows an enzyme-like model where tight tubulin binding enables efficient polymerization, revealing a shared mechanism with actin polymerases despite their evolutionary divergence. This work will be of general interest to the cell biology and biophysics communities.

Reviewer #1 (Public review):

This study by Gangadharan and colleagues provides significant progress towards a quantitative biochemical mechanism for Stu2 polymerase activity. A key conceptual advance is the novel application of an enzyme-like model, initially developed for the actin polymerase Ena/VASP, to Stu2.

New refined affinity measurements for a Stu2 TOG domain using Bio-layer interferometry show more than an order of magnitude higher affinity of TOG domains to tubulin compared to previously published reports.

The findings reinforce the "concentrating reactants" or, more specifically, for TOG-domain proteins, the "tubulin-shuttling antenna" model, compared to the "polarized unfurling" model, a more speculative structural hypothesis.

The manuscript builds upon a series of previous manuscripts that showcase the profound intellectual engagement with microtubule polymerization mechanisms by TOG-domain proteins from the Rice lab, a thought leader in microtubule polymerization for over a decade.

Minor remarks:

(1) A major new experimental finding of this paper is the affinity of TOG domains, which is more than an order of magnitude lower (10 nM) than previous measurements from the same lab (~200 nM). The authors attribute this change to ionic strength differences between buffer conditions, citing the lab's previous work (Ayaz et al., 2014). This argument left me contemplating what the buffer conditions are in both experiments, and I wonder if other readers would feel the same. After going down the rabbit hole, I believe the difference in ionic strength is ~2.3 fold, and at least on the back of my envelope, this works out beautifully with the measured differences in affinities. A short version of this argument may strengthen the manuscript.

(2) I am wondering if there may be an alternative explanation to tubulin binding by TOG being the kinetically rate-limiting step for polymerase function:

TOG + Tubulin ⇌ TOG:Tubulin (fast binding rate, high-affinity binding)<br /> TOG:Tubulin + MT_end → TOG:MT (tubulin is incorporated into MT, fast transfer rate)<br /> The binding rate is 3/s, and the transfer rate is 5/s.

I was wondering if the following step should be considered, which involves a conformational change of tubulin (e.g., straightening) TOG:MT → TOG + MT (rate-limiting straightening and unbinding of TOG from the lattice).

Presumably, the affinity of TOGs for straight tubulin is practically zero for the purpose of this discussion, as there is no lattice binding, which means unbinding is likely very rapid; however, straightening may be the rate-limiting factor here.

In theory, straightening should also be rapid; however, we lack measurements of how fast or slow this step occurs within the context of a TOG domain, which presumably skews the process towards curved tubulin.

A hypothetical Stu2, when bound to the microtubule end and with the TOG domain not disengaged from tubulin, would not permit the processivity of that molecule or the binding of a new molecule.<br /> To emphasize the importance of unbinding, when it is not efficient, as reported for the T238 mutant that results in Stu2 lattice binding (Geyer et al., 2018), the polymerase becomes inefficient.

Reviewer #2 (Public review):

Summary:

The manuscript from the Rice lab by Gangadharan et al. investigates the polymerization mechanism of the yeast microtubule polymerase Stu2. The lab has published a number of articles demonstrating the structural basis by which the two TOG domains of Stu2 each bind free tubulin heterodimers, and has developed a tethered polymerization model by which the TOG domains drive polymerization by shuttling those tubulin subunits onto the microtubule plus end. A second model was proposed by Nithianantham et al. (eLife, 2018) based on a closed-to-open transitional state in which Stu2 unfurls and loads two longitudinally associated tubulin heterodimers onto the microtubule plus end. While the second model is not directly tested, the current work aims to further characterize/model the tethered polymerization model using a kinetic framework developed by Breitsprecher et al. for Ena/VASP actin polymerization activity, using a model that is enzymatic (EMBO J., 2011). The general architecture and function of Ena/VASP on actin polymerization versus Stu2 on microtubule polymerization is a reasonable relation and hits upon, as the authors note, potential convergent mechanistic evolution across distinct cytoskeletal networks. The model effectively treats tubulin as the substrate, and the polymerized microtubule plus end as the product. If Stu2 is "enzymatic" in this framework, the model predicts it would behave with Michaelis-Menten kinetics, that there would a Vmax, and polymerase activity would either be "affinity limited" by TOG:tubulin affinity (KD) and/or "kinetically limited" by TOG:tubulin association (Kon) and transfer of tubulin to the microtubule plus end (Kt). The authors find that the Brietsprecher model works well for Stu2 activity, and that Stu2 best aligns with a "kinetically limited" model. The work is interesting and adds to the growing elucidation of the Stu2 microtubule polymerase model. While yeast microtubule polymerases are somewhat distinct in their architecture, there is significant overlap that findings from the manuscript can be utilized to inform the mechanisms of larger, more complex microtubule polymerases such as human ch-TOG.

Strengths:

The manuscript invokes the enzymatic model of Breitsprecher et al. used for Ena/VASP and conducts an elegant series of (mostly established) experiments to determine whether Stu2 microtubule polymerase activity aligns with the model, which they conclude does align, supported by the data/results obtained.

Weaknesses:

The authors used biolayer interferometry to measure TOG:tubulin affinity. The affinities obtained were significantly higher than the lab obtained in an earlier publication using analytical ultracentrifugation. While differences in buffer and salt conditions may underlie these differences, additional runs using comparable buffer systems, or the use of a third independent assay to measure affinities, would have added rigor.

The discussion could be expanded to better compare and contrast the results with both existing polymerase models introduced in the introduction, as well as expanded to look at reversible enzymatic activity (microtubule depolymerization at low to zero tubulin concentrations) and microtubule plus versus minus end activity.

Reviewer #3 (Public review):

Summary:

This study by Gangadharan and colleagues seeks to establish a quantitative biochemical model for the microtubule polymerase activity of Stu2. Stu2 is the budding yeast member of the XMAP215 protein family, which is broadly conserved across eukaryotes. XMAP215 proteins play a wide variety of important roles in cells, and these are attributed to effects on microtubule dynamics. Many studies over the last ~20 years have shown that XMA215 proteins selectively associate with microtubule ends, where they increase rates of microtubule assembly and disassembly. More recently, structural biology and biochemical studies by the authors and other groups have shown that the multiple TOG domains on XMAP215 proteins are tubulin-binding domains that selectively bind to curved tubulin, which is present in solution and at microtubule ends, but not to straight tubulin which is present in the walls of the microtubule lattice. This has led to the general model that XMAP215 proteins promote polymerization by delivering soluble tubulin to the growing plus end, and two distinct models have been proposed to explain the mechanism. The 'concentrating reactants' model proposed previously by the authors suggests that TOG domains grab hold of tubulin in solution and concentrate at the microtubule end. The 'polarized unfurling' model proposed by the Al Bassam lab suggests that XMAP215 delivers multiple tubulins to the end, using a step-wise mechanism involving different roles for each TOG domain. The current study seeks to improve our understanding of the mechanism by developing a quantitative model to explain the binding and release of tubulins, the number of Stu2 molecules at the end, and the overall rate of tubulin addition. The authors accomplish this goal using new experimental data. The final model fills in new details of the mechanism. The authors draw a comparison between Stu2 and the actin polymerase, which bears similarity to Ena/VASP, and suggest a convergent strategy for cytoskeletal polymerases.

Strengths:

This is a focused and clearly written study that incorporates prior knowledge of XMAP215 and draws inspiration from the actin field. The data are clear and convincing, and the study accomplishes its goal of generating a new, quantitative model for Stu2. The model will be important for microtubule researchers to predict and test key points for altering XMAP215 activity across different organisms and potentially for different tubulin substrates. The comparison to Ena/VASP may also inspire similar comparisons across other microtubule and actin regulators, which could lead to new insights across the cytoskeletal fields.

Weaknesses:

The study is without major weaknesses, but there are several minor weaknesses worth noting. One is that the final model provides new details regarding the Stu2 mechanism, but does not provide a major new advance in our understanding of how the polymerase works. For example, the discussion does not clearly argue for whether the new results and model rule out either of the prior models. This appears consistent with the 'concentrating reactants' model, but does it clearly rule out the 'polarized unfurling' model? A second minor weakness is that the comparison to Ena/VASP is not developed at a deep level based on the final model. I found these ideas exciting and want more critical consideration here, but perhaps it is better suited for a commentary piece to follow.

eLife Assessment

This valuable study provides new insights into the movement of ions through the bacterial pump KdpFABC, which regulates intracellular potassium concentration, by solving a 2.1 Å cryo-EM structure of the nanodisc-embedded active wild-type protein, and carrying out mutagenesis and activity assays. Although the structural data and analysis are solid, additional information about other structural classes identified in the EM data, as well as a discussion of relevant work done by others, would further strengthen these findings. The description of the activity assays is currently incomplete because more information is required to rigorously assess these experiments. This work will be of interest to the membrane transporter and channel communities and to microbiologists interested in osmoregulation and potassium homeostasis.

Reviewer #1 (Public review):

Summary:

This study on potassium ion transport by the protein complex KdpFABC from E. coli reveals a 2.1 Å cryo-EM structure of the nanodisc-embedded transporter under turnover conditions. The results confirm that K+ ions pass through a previously identified tunnel that connects the channel-like subunit with the P-type ATPase-type subunit.

Strengths:

The excellent resolution of the structure and the thorough analysis of mutants using ATPase and ion transport measurements help to strengthen new and previous interpretations. The evidence supporting the conclusions is solid, including biochemical assays and analysis of mutants. The work will be of interest to the membrane transporter and channel communities and to microbiologists interested in osmoregulation and potassium homeostasis.

Weaknesses:

There is insufficient credit and citation of previous work.

Reviewer #2 (Public review):

Summary:

The paper describes the high-resolution structure of KdpFABC, a bacterial pump regulating intracellular potassium concentrations. The pump consists of a subunit with an overall structure similar to that of a canonical potassium channel and a subunit with a structure similar to a canonical ATP-driven ion pump. The ions enter through the channel subunit and then traverse the subunit interface via a long channel that lies parallel to the membrane to enter the pump, followed by their release into the cytoplasm.

Strengths:

The work builds on the previous structural and mechanistic studies from the authors' and other labs. While the overall architecture and mechanism have already been established, a detailed understanding was lacking. The study provides a 2.1 Å resolution structure of the E1-P state of the transport cycle, which precedes the transition to the E2 state, assumed to be the rate-limiting step. It clearly shows a single K+ ion in the selectivity filter of the channel and in the canonical ion binding site in the pump, resolving how ions bind to these key regions of the transporter. It also resolves the details of water molecules filling the tunnel that connects the subunits, suggesting that K+ ions move through the tunnel transiently without occupying well-defined binding sites. The authors further propose how the ions are released into the cytoplasm in the E2 state. The authors support the structural findings through mutagenesis and measurements of ATPase activity and ion transport by surface-supported membrane (SSM) electrophysiology.

Weaknesses:

While the results are overall compelling, several aspects of the work raised questions. First, the authors determined the structure of the pump in nanodiscs under turnover conditions and observed several structural classes, including E1-P, which is detailed in the paper. Two other structural classes were identified, including one corresponding to E2. It is unclear why they are not described in the paper. Notably, the paper considers in some detail what might occur during the E1-P to E2 state transition, but does not describe the 3.1 Å resolution map for the E2 state that has already been obtained. Does the map support the proposed structural changes?

The paper relies on the quantitative activity comparisons between mutants measured using SSM electrophysiology. Such comparisons are notoriously tricky due to variability between SSM chips and reconstitution efficiencies. The authors should include raw traces for all experiments in the supplementary materials, explain how the replicates were performed, and describe the reproducibility of the results. Related to this point above, size exclusion chromatography profiles and reconstitution efficiencies for mutants should be shown to facilitate comparison between measured activities. For example, could it be that the inactive V496R mutant is misfolded and unstable?

Similarly, are the reduced activities of V496W and V496H (and many other mutants) due to changes in the tunnel or poor biochemical properties of these variants? Without these data, the validity of the ion transport measurements is difficult to assess.

The authors propose that the tunnel connecting the subunits is filled with water and lacks potassium ions. This is an important mechanistic point that has been debated in the field. It would be interesting to calculate the volume of the tunnel and estimate the number of ions that might be expected in it, given their concentration in bulk. It may also be helpful to provide additional discussion on whether some of the observed densities correspond to bound ions with low occupancy.

Reviewer #3 (Public review):

Summary:

By expressing protein in a strain that is unable to phosphorylate KdpFABC, the authors achieve structures of the active wild-type protein, capturing a new intermediate state, in which the terminal phosphoryl group of ATP has been transferred to a nearby Asp, and ADP remains covalently bound. The manuscript examines the coupling of potassium transport and ATP hydrolysis by a comprehensive set of mutants. The most interesting proposal revolves around the proposed binding site for K+ as it exits the channel near T75. Nearby mutations to charged residues cause interesting phenotypes, such as constitutive uncoupled ATPase activity, leading to a model in which lysine residues can occupy/compete with K+ for binding sites along the transport pathway.

Strengths:

Although this structure is not so different from previous structures, its high resolution (2.1 Å) is impressive and allows the resolution of many new densities in the potassium transport pathway. The authors are judicious about assigning these as potassium ions or water molecules, and explain their structural interpretations clearly. In addition to the nice structural work, the mechanistic work is thorough. A series of thoughtful experiments involving ATP hydrolysis/transport coupling under various pH and potassium concentrations bolsters the structural interpretations and lends convincing support to the mechanistic proposal.

Weaknesses:

The structures are supported by solid membrane electrophysiology. These data exhibit some weaknesses, including a lack of information to assess the rigor and reproducibility (i.e., the number of replicates, the number of sensors used, controls to assess proteoliposome reconstitution efficiency, and the stability of proteoliposome absorption to the sensor).

eLife Assessment

This study presents an important computational framework, FLiSimBA (Fluorescence Lifetime Simulation for Biological Applications), for modeling experimental limitations in Fluorescence Lifetime Imaging Microscopy (FLIM). FLiSimBA is readily available in MATLAB and Python, enables users to simulate effects of noise and varying sensor expression levels, and provides practical guidance for both lifetime imaging experiments and biosensor development. The analyses are robust, and the evidence supporting the tool's utility in distinguishing between multiple lifetime signals is compelling, indicating strong potential for multiplexed dynamic imaging. However, users should also consider that the tool's effectiveness depends on the suitability of a two-component discrete exponential model.

Reviewer #1 (Public review):

In this study, Ma et al. aimed to determine previously uncharacterized contributions of tissue autofluorescence, detector afterpulse, and background noise on fluorescence lifetime measurement interpretations. They introduce a computational framework they named "Fluorescence Lifetime Simulation for Biological Applications (FLiSimBA)" to model experimental limitations in Fluorescence Lifetime Imaging Microscopy (FLIM) and determine parameters for achieving multiplexed imaging of dynamic biosensors using lifetime and intensity. By quantitatively defining sensor photon effects on signal to noise in either fitting or averaging methods of determining lifetime, the authors contradict any claims of FLIM sensor expression insensitivity to fluorescence lifetime and highlight how these artifacts occur differently depending on analysis method. Finally, the authors quantify how statistically meaningful experiments using multiplexed imaging could be achieved.

A major strength of the study is the effort to present results in a clear and understandable way given that most researcher do not think about these factors on a day-to-day basis. Additionally, the model code is readily available in Matlab and Python, which should allow for open access to a larger community.

Overall, the authors' achieved their aims of demonstrating how common factors (autofluorescence, background, and sensor expression) will affect lifetime measurements and they present a clear strategy for understanding how sensor expression may confound results if not properly considered. This work should bring to awareness an issue that new users of lifetime biosensors may not be aware of and that experts, while aware, have not quantitatively determine the conditions where these issues arise. This work will also point to future directions for improving experiments using fluorescence lifetime biosensors and the development of new sensors with more favorable properties.

Reviewer #3 (Public review):

Summary:

This study presents a useful computational tool, termed FLiSimBA. The MATLAB-based FLiSimBA simulations allow users to examine the effects of various noise factors (such as autofluorescence, afterpulse of the photomultiplier tube detector, and other background signals) and varying sensor expression levels. Under the conditions explored, the simulations unveiled how these factors affect the observed lifetime measurements, thereby providing useful guidelines for experimental designs. Further simulations with two distinct fluorophores uncovered conditions in which two different lifetime signals could be distinguished, indicating multiplexed dynamic imaging may be possible.

Strengths:

The simulations and their analyses were done systematically and rigorously. FliSimba can be useful for guiding and validating fluorescence lifetime imaging studies. The simulations could define useful parameters such as the minimum number of photons required to detect a specific lifetime, how sensor protein expression level may affect the lifetime data, the conditions under which the lifetime would be insensitive to the sensor expression levels, and whether certain multiplexing could be feasible.

Weaknesses:

The analyses have relied on a key premise that the fluorescence lifetime in the system can be described as a two-component discrete exponential decay. This means that the experimenter should ensure that this is the right model for their fluorophores a priori.

Author response:

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

Reviewer #1 (Public review): 

In this study, Ma et al. aimed to determine previously uncharacterized contributions of tissue autofluorescence, detector afterpulse, and background noise on fluorescence lifetime measurement interpretations. They introduce a computational framework they named "Fluorescence Lifetime Simulation for Biological Applications (FLiSimBA)" to model experimental limitations in Fluorescence Lifetime Imaging Microscopy (FLIM) and determine parameters for achieving multiplexed imaging of dynamic biosensors using lifetime and intensity. By quantitatively defining sensor photon effects on signal-to-noise in either fitting or averaging methods of determining lifetime, the authors contradict any claims of FLIM sensor expression insensitivity to fluorescence lifetime and highlight how these artifacts occur differently depending on the analysis method. Finally, the authors quantify how statistically meaningful experiments using multiplexed imaging could be achieved. 

A major strength of the study is the effort to present results in a clear and understandable way given that most researchers do not think about these factors on a day-to-day basis. The model code is available and written in Matlab, which should make it readily accessible, although a version in other common languages such as Python might help with dissemination in the community. One potential weakness is that the model uses parameters that are determined in a

specific way by the authors, and it is not clear how vastly other biological tissue and microscope setups may differ from the values used by the authors. 

Overall, the authors achieved their aims of demonstrating how common factors

(autofluorescence, background, and sensor expression) will affect lifetime measurements and they present a clear strategy for understanding how sensor expression may confound results if not properly considered. This work should bring to awareness an issue that new users of lifetime biosensors may not be aware of and that experts, while aware, have not quantitatively determined the conditions where these issues arise. This work will also point to future directions for improving experiments using fluorescence lifetime biosensors and the development of new sensors with more favorable properties. 

We appreciate the comments and helpful suggestions. We now also include FLiSimBA simulation code in Python in addition to Matlab to make it more accessible to the community.

One advantage of FLiSimBA is that the simulation package is flexible and adaptable, allowing users to input parameters based on the specific sensors, hardware, and autofluorescence measurements for their biological and optical systems. We used parameters based on a FRETbased sensor, measured autofluorescence from mouse tissue, and measured dark count/after pulse of our specific GaAsP PMT in this manuscript as examples. In Discussion and Materials and methods, we now emphasize this advantage and further clarify how these parameters can be adapted to diverse tissues, imaging systems, and sensors based on individual experiments. We further explain that these input parameters will not affect the conclusions of our study, but the specific input parameters would alter the quantitative thresholds.

Reviewer #2 (Public review): 

Summary: 

By using simulations of common signal artefacts introduced by acquisition hardware and the sample itself, the authors are able to demonstrate methods to estimate their influence on the estimated lifetime, and lifetime proportions, when using signal fitting for fluorescence lifetime imaging. 

Strengths: 

They consider a range of effects such as after-pulsing and background signal, and present a range of situations that are relevant to many experimental situations. 

Weaknesses: 

A weakness is that they do not present enough detail on the fitting method that they used to estimate lifetimes and proportions. The method used will influence the results significantly. They seem to only use the "empirical lifetime" which is not a state of the art algorithm. The method used to deconvolve two multiplexed exponential signals is not given. 

We appreciate the comments and constructive feedback. Our revision based on the reviewer’s suggestions has made our manuscript clearer and more user friendly. We originally described the detail of the fitting methods in Materials and methods. Given the importance of these methodological details for evaluating the conclusions of this study, we have moved the description of the fitting method from Materials and methods to Results. In addition, we provide further clarification and more details of the rationale of using these different methods of lifetime estimates in Discussion to aid users in choosing the best metric for evaluating fluorescence lifetime data.

More specifically, we modified our writing to highlight the following.

(1) In Results, we describe that lifetime histograms were fitted to Equation 3 with the GaussNewton nonlinear least-square fitting algorithm and the fitted P<sub1</sub> was used as lifetime estimation.

(2) In Results, we clarify that our simulation of multiplexed imaging was modeled with two sensors, each displaying a single exponential decay, but the two sensors have different decay constants. We also describe that Equation 3 with the Gauss-Newton nonlinear least-square fitting algorithm was used to deconvolve the two multiplexed exponential signals (Fig. 8)

Reviewer #3 (Public review): 

Summary: 

This study presents a useful computational tool, termed FLiSimBA. The MATLAB-based FLiSimBA simulations allow users to examine the effects of various noise factors (such as autofluorescence, afterpulse of the photomultiplier tube detector, and other background signals) and varying sensor expression levels. Under the conditions explored, the simulations unveiled how these factors affect the observed lifetime measurements, thereby providing useful guidelines for experimental designs. Further simulations with two distinct fluorophores uncovered conditions in which two different lifetime signals could be distinguished, indicating multiplexed dynamic imaging may be possible. 

Strengths: 

The simulations and their analyses were done systematically and rigorously. FliSimba can be useful for guiding and validating fluorescence lifetime imaging studies. The simulations could define useful parameters such as the minimum number of photons required to detect a specific lifetime, how sensor protein expression level may affect the lifetime data, the conditions under which the lifetime would be insensitive to the sensor expression levels, and whether certain multiplexing could be feasible. 

Weaknesses: 

The analyses have relied on a key premise that the fluorescence lifetime in the system can be described as two-component discrete exponential decay. This means that the experimenter should ensure that this is the right model for their fluorophores a priori and should keep in mind that the fluorescence lifetime of the fluorophores may not be perfectly described by a twocomponent discrete exponential (for which alternative algorithms have been implemented: e.g., Steinbach, P. J. Anal. Biochem. 427, 102-105, (2012)). In this regard, I also couldn't find how good the fits were for each simulation and experimental data to the given fitting equation (Equation 2, for example, for Figure 2C data). 

We thank the reviewer for the constructive feedback. We agree that the FLiSimBA users should ensure that the right decay equations are used to describe the fluorescent sensors. In this study, we used a FRET-based PKA sensor FLIM-AKAR to provide proof-of-principle demonstration of the capability of FLiSimBA. The donor fluorophore of FLIM-AKAR, truncated monomeric enhanced GFP, displays a single exponential decay. FLIM-AKAR, a FRET-based sensor, displays a double exponential decay. The time constants of the two exponential components were determined and reported previously (Chen, et al, Neuron (2017)).  Thus, a double exponential decay equation with known τ₁ and τ₂ was used for both simulation and fitting. The goodness of fit is now provided in Supplementary Fig. 1 for both simulated and experimental data. In addition to referencing our prior study characterizing the double exponential decay model of FLIM-AKAR in Materials and methods, we have emphasized in Discussion the versality of FLiSimBA to adapt to different sensors, tissues, and analysis methods, and the importance of using the right mathematical models to describe the fluorescence decay of specific sensors. 

Also, in Figure 2C, the 'sensor only' simulation without accounting for autofluorescence (as seen in Sensor + autoF) or afterpulse and background fluorescence (as seen in Final simulated data) seems to recapitulate the experimental data reasonably well. So, at least in this particular case where experimental data is limited by its broad spread with limited data points, being able to incorporate the additional noise factors into the simulation tool didn't seem to matter too much.  

In the original Fig 2C, the sensor fluorescence was much higher than the contributions from autofluorescence, afterpulse, and background signals, resulting in minimal effects of these other factors, as the reviewer noted. This original figure was based on photon counts from single neurons expressing FLIM-AKAR. For the rest of the manuscript, photon counts were based on whole fields of view (FOV). Since the FOV includes cells that do not express fluorescent sensors, the influence of autofluorescence, dark currents, and background is much more pronounced, as shown in Fig. 2B. 

Both approaches – using photon counts from the whole FOV or from individual neurons – have their justifications. Photon counts from the whole FOV simulate data from fluorescence lifetime photometry (FLiP), whereas photon counts from individual neurons simulate data from fluorescence lifetime imaging microscopy (FLIM). However, the choice of approach does not affect the conclusions of the manuscript, as a range of photon count values are simulated. To maintain consistency throughout the manuscript, we have revised the photon counts in this figure (now Supplementary Fig. 1C) to match those from the whole FOV.

Additionally, we have made some modifications in our analyses of Supplementary Fig. 1C and Fig. 2B, detailed in the “FLIM analysis” section of Materials and methods. For instance, to minimize system artifact interference at the histogram edges, we now use a narrower time range (1.8 to 11.5 ns) for fitting and empirical lifetime calculation.

Reviewer #1 (Recommendations for the authors): 

(1) The authors report how autofluorescence was measured from "imaged brain slices from mice at postnatal 15 to 19 days of age without sensor expression." However, it remains unclear how many acute slices and animals were used (for example, were all 15um x 15um FOV from a single slice) and if mouse age affects autofluorescence quantification. Furthermore, would in vivo measurements have different autofluorescence conditions given that blood flow would be active? It would help if the authors more clearly explained how reliable their autofluorescence measurement is by clarifying how they obtained it, whether this would vary across brain areas, and whether in vitro vs in vivo conditions would affect autofluorescence. 

We have added description in Materials and methods that for autofluorescence ‘Fluorescence decay histograms from 19 images of two brain slices from a single mouse were averaged.’ We have added in Discussion that users should carefully ‘measure autofluorescence that matches the age, brain region, and data collection conditions (e.g., ex vivo or in vivo) of their tissue…’, and emphasize that FLiSimBA offers customization of inputs, and it is important for users to adapt the inputs such as autofluorescence to their experimental conditions. We also clarify in Discussion that the change of input parameters such as autofluorescence across age and brain region would not affect the general insights from this study, but will affect quantitative values.

(2) Does sensor expression level issues arise more with in-utero electroporation compared to AAV-based delivery of biosensors? A brief comment on this in the discussion may help as most users in the field today may be using AAV strategies to deliver biosensors.

In our experience, in-utero electroporation results in higher sensor expression than AAV-based delivery, and so pose less concern for expression-level dependence. However, both delivery methods can result in expression level dependence, especially with a sensor that is not bright. We have added in Discussion ‘For a sensor with medium brightness delivered via in utero electroporation, adeno-associated virus, or as a knock-in gene, the brightness may not always fall within the expression level-independent regime.’

(3) Figure 1. Should the x-axis on the top figures be "Time (ns)" instead of "Lifetime (ns)"?

Similarly in Figure 8A&B, wouldn't it make more sense to have the x-axis be Time not Lifetime?

The x-axis labels in Fig. 1 and Fig. 8A-8B have been changed to ‘Time (ns)’.   

(4) Figure 2b: why is the empirical lifetime close to 3.5ns? Shouldn't it be somewhere between

2.14 and 0.69? 

In our empirical lifetime calculation, we did not set the peak channel to have a time of 0.0488 ns (i.e. the laser cycle 12.5 ns divided by 256 time channels). Rather, we set the first time channel within a defined calculation range (i.e. 1.8 ns in Supplementary Fig. 1B) to have a time of 0.0488 ns (i.e.). Thus, the empirical lifetime exceeds 2.14 ns and depends on the time range of the histogram used for calculation. 

For Fig. 2B and Supplementary Fig. 1C, we have now adjusted the range to 1.8-11.5 ns to eliminate FLIM artifacts at the histogram edges in our experimental data, resulting in an empirical lifetime around 2.255 ns. In contrast, the range for calculating the empirical lifetime of simulated data in the rest of the study (e.g. Fig. 4D) is 0.489-11.5 ns, yielding a larger lifetime of ~3.35 ns. 

We have clarified these details and our rationale in Materials and methods.

(5) Figure 2b: how come the afterpulse+background contributes more to the empirical lifetime than the autofluorescence (shorter lifetime). This was unclear in the results text why autofluorescence photons did not alter empirical lifetime as much as did the afterpulse/background.

With a histogram range from 1.8 ns to 11.5 ns used in Fig. 2B, the empirical lifetime for FLIM-AKAR sensor fluorescence, autofluorescence, and background/afterpulse are: 2-2.3 ns, around 1.69 ns, and around 4.90 ns. The larger difference of background/afterpulse from FLIM-AKAR sensor fluorescence leads to larger influence of afterpulse+background than autofluorescence. We have added an explanation of this in Results.

(6) One overall suggestion for an improvement that could help active users of lifetime biosensors understand the consequences would be to show either a real or simulated example of a "typical experiment" conducted using FLIM-AKAR and how an incorrect interpretation could be drawn as a consequence of these artifacts. For example, do these confounds affect experiments involving comparisons across animals more than within-subject experiments such as washing a drug onto the brain slice, and the baseline period is used to normalize the change in signal? I think this type of direct discussion will help biosensor users more deeply grasp how these factors play out in common experiments being conducted.

We have added the following in Discussion, ‘…While this issue is less problematic when the same sample is compared over short periods (e.g. minutes), It can lead to misinterpretation when fluorescence lifetime is compared across prolonged periods or between samples when comparison is made across chronic time periods or between samples with different sensor expression levels. For example, apparent changes in fluorescence lifetime observed over days, across cell types, or subcellular compartments may actually reflect variations in sensor expression levels rather than true differences in biological signals (Fig. 6), Therefore, considering biologically realistic factors in FLiSimBA is essential, as it qualitatively impacts the conclusions.’

Reviewer #2 (Recommendations for the authors): 

The paper would be improved with more detail on the fitting methods, and the use of state-of-theart methods. Consult for example the introduction of this paper where many methods are listed: https://www.mdpi.com/1424-8220/22/19/7293

We have moved the description of the Gauss-Newton nonlinear least-square fitting algorithm from Materials and methods to Results to enhance clarity. We appreciate the reviewer’s suggestion to combine FLiSimBA with various analysis methods. However, the primary focus of our manuscript is to call for attention of how specific contributing factors in biological experiments influence FLIM data, and to provide a tool that rigorously considers these factors to simulate FLIM data, which can then be used for fitting. Therefore, we did not expand the scope of our manuscript. Instead, we have added in the Discussion that ‘‘FLiSimBA can be used to test multiple fitting methods and lifetime metrics as an exciting future direction for identifying the best analysis method for specific experimental conditions’, citing relevant references.

I would also improve the content of the GitHub repository as it is very hard to identify to source code used for simulation and fitting. 

We have reorganized and relabeled our GitHub repository and now have three folders labeled as ‘Simulation_inMatlab’, ‘DataAnalysis_inMatlab’, and ‘SimulationAnalysis_inPython’. We also updated the clarification of the contents of each folder in the README file.

Reviewer #3 (Recommendations for the authors): 

(1) P. 10 "For example, to detect a P1 change of 0.006 or a lifetime change of 5 ps with one sample measurement in each comparison group, approximately 300,000 photons are needed." If I am reading the graphs in Figures 3B and C, this sentence is talking about the red line. However, the intersection of 0.006 in the MDD of P1 in 3B and red is not 3E5 photons. And the intersection of 0.005 ns and red in 3C is not 3E5 photons either. Are you sure you are talking about n=1? Maybe the values are correct for the blue curve with n=5.

Thank you for catching our error. We have corrected the text to ‘with five sample measurements’.

(2) Figure 2 (B) legend: It would be helpful to specify what is being compared in the legend. For example, consider revising "* p < 0.05 vs sensor only; n.s. not significant vs sensor + autoF; # p < 0.05 vs sensor + autoF. Two-way ANOVA with Šídák's multiple comparisons test" to "* p <0.05 for sensor + auto F (cyan) vs sensor only; n.s. not significant for final simulated data (purple) vs sensor + autoF; # p < 0.05 for final simulated data (purple) vs sensor + autoF. Twoway ANOVA with Šídák's multiple comparisons test".

We’ve made the change and thanks for the suggestion to make it clearer.

(3) Figure 2 (c) Can you please show the same Two-way ANOVA test values for Experimental vs. Sensor only and for Experimental vs. Sensor + autoF? Currently, the value (n.s.) is marked only for Experimental vs. Final simulation. Given that the experimental data are sparse (compared to the simulations), it seems likely that there may be no significant difference among the 3 different simulations regarding how well they match the experimental data. Also, can you specify the P1 and P2 of the experimental data  used to generate the simulated data on this panel? Also, what is the reason why P1=0.5 was used for panels A and B, instead of the value matching the experimental value?

As the reviewer suggested, we have included statistical tests in the figure (now Supplementary Fig. 1C). Please see our response to the Public Review of Reviewer 3’s comments as well as our changes in Materials and Methods on other changes and their rationale for this figure. We have now specified the P₁ value of the experimental data used to generate the simulated data on this panel both in Figure Legends and Materials and Methods. Based on the suggestion, we have now used the same P₁ value in Fig. 2B.

eLife Assessment

This study presents important findings on increased ground beetle diversity in strip cropping compared with crop monocultures. Solid methods are used to analyze data from multiple sites with heterogeneous systems of mixed crops, allowing broad conclusions, albeit at the expense of lacking taxonomic specificity. The work will be of interest to all those applying plant diversity treatments to improve the diversity of associated animals in agricultural fields.

Joint Public Review:

Summary:

In this paper the authors examined the effects of strip cropping, a relatively new agricultural technique of alternating crops in small strips of several meters wide, on ground beetle diversity. The results show an increase in species diversity (i.e. abundance and species richness) of the ground beetle communities compared to monocultures.

Strengths:

The article is well written; it has an easily readable tone of voice without too much jargon or overly complicated sentence structure. Moreover, as far as reviewing the models in depth without raw data and R scripts allows, the statistical work done by the authors looks good. They have well thought out how to handle heterogenous, unbalanced and taxonomically unspecific yet spatially and temporarily correlated field data. The models applied and the model checks performed are appropriate for the data at hand. Combining RDA and PCA axes together is a nice touch. Moreover, after the first round of reviews, the authors have done a great job at rewriting the paper to make it less overstated, more relevant to the data at hand and more solid in the findings. Many of the weaknesses noted in the first review have been dealt with. The overall structure of the paper is good, with a clear introduction, hypotheses, results section and discussion.

Author response:

The following is the authors’ response to the previous reviews

Reviewer #3 (Public Review)

Summary:

In this paper the authors examined the effects of strip cropping, a relatively new agricultural technique of alternating crops in small strips of several meters wide, on ground beetle diversity. The results show an increase in species diversity (i.e. abundance and species richness) of the ground beetle communities compared to monocultures.

Strengths:

The article is well written; it has an easily readable tone of voice without too much jargon or overly complicated sentence structure. Moreover, as far as reviewing the models in depth without raw data and R scripts allows, the statistical work done by the authors looks good. They have well thought out how to handle heterogenous, unbalanced and taxonomically unspecific yet spatially and temporarily correlated field data. The models applied and the model checks performed are appropriate for the data at hand. Combining RDA and PCA axes together is a nice touch. Moreover, after the first round of reviews, the authors have done a great job at rewriting the paper to make it less overstated, more relevant to the data at hand and more solid in the findings. Many of the weaknesses noted in the first review have been dealt with. The overall structure of the paper is good, with a clear introduction, hypotheses, results section and discussion.

We are grateful for this positive feedback. We are glad that our extensive revision after extensive review from three reviewers has paid off in addressing earlier weakness of our manuscript.

Weaknesses:

The weaknesses that remain are mainly due to a difficult dataset and choices that could have stressed certain aspects more, like the relationship between strip cropping and intercropping. The mechanistic understanding of strip cropping is what is at stake here. Does strip cropping behave similar to intercropping, a technique which has been proven to be beneficial to biodiversity because of added effects due to increased resource efficiency and greater plant species richness.

Unfortunately, the authors do not go into this in the introduction or otherwise and simply state that they consider strip cropping a form of intercropping.

We agree with the reviewer that a mechanistic understanding on how intercropping and strip cropping differ would be very interesting. However, we also feel that this topic is somewhat beyond the scope of the current manuscript. We are already planning work to elucidate mechanisms that may explain the pest and suppressive effects of strip cropping.

I also do not like the exclusive focus on percentages, as these are dimensionless. I think more could have been done to show underlying structure in the data, even after rarefaction.

While we generally agree with this point raised by the reviewer, for our heterogeneous dataset it was difficult to come up with meaningful units with dimensions. Therefore, we believe that percentages are the most suitable approach to present readers a fair comparison of the treatments.

A further weakness is a limited embedding into the larger scientific discourses other than providing references. But this may be a matter of style and/or taste

We believe our manuscript to be well-embedded within the relevant scientific discourse, but as indicated by reviewer 3 this might indeed be a matter of style/taste. Without exact examples it is difficult for us to judge this point.

Reviewer #3 (Recommendations for the authors): 

Suggestion for title: "Strip cropping shows promising preliminary increases in ground beetle community diversity compared to monocultures"

We agree that the title could indeed be nuanced. We incorporated the suggested title, except for the word “preliminary”, as we felt that this is slightly misplaced for a 4-year study conducted at 4 locations.

line 26: the word previous may be confusing to readers, as it suggests previous research on beetles or insects. I think it would be better to use for instance "related" or "productivity focused research"

We agree that this wording might be confusing, and changed it to “other studies showed”.

Line 84-85: this is vague. can you make explicit what you are trying to answer here?

We made “biodiversity metric changes” more explicit, and changed the sentence accordingly.

Line 88-89: I think this would fit better with the first question in line 83-84, so I suggest placing it upwards. Also, I think you mean abundant instead of common. Common suggests commonness in the entire population. Abundant suggests found often in this study. While these definitions may very much overlap, they are distinctly different.

We have moved this sentence up and changed “common” to “abundant”. To make the result section more in line with this section, we also moved the section on the relationship between crop configuration and abundant genera up.  

Line 146: defining rareness of species should be in the methods section. Also "following" would be better than "according"

We now added a sentence on how we examine habitat preferences and rarity in the methods section (line 316-317). We also changed “according to” to “following”.

Line 291: it is called being "flush" with the soil surface. This expression is not much used by non-native speakers, but is regularly encountered in studies on pitfalls, so the authors could decide to change the sentence using the proper English vernacular.

Suggestion incorporated.

Line 322-327, this method could do with a reference

This method is a relatively standard calculation to calculate relative changes and to center variation around zero. Nevertheless, we added a reference to a paper that used the same method.

Line: 333-335. I would still like to see a reference for this method.

This methodology has not been described in literature to the best of our knowledge. As we compared two crops within strip cropping with their respective monoculture references, we compare one strip cropping field with two monocultural fields. Here we took a conservative approach by comparing the strip crop field with the monoculture with the highest richness and activity density, to see if strip cropped fields outperformed monocultures with diverse ground beetle communities.

Line 364-366. references?

We have added references for these R packages.

eLife Assessment

This study shows, for the first time, the structure and snapshots of the dynamics of the full-length soluble Angiotensin-I converting enzyme dimer. The combination of structural and computational analyses provides compelling evidence that reveals the conformational dynamics of the complex and key regions mediating the conformational change. This fundamental work illustrates how conformational heterogeneity can be used to gain insights into protein function.

Reviewer #1 (Public review):

Summary:

The authors report four cryoEM structures (2.99 to 3.65 Å resolution) of the 180 kDa, full-length, glycosylated, soluble Angiotensin-I converting enzyme (sACE) dimer, with two homologous catalytic domains at the N- and C-terminal ends (ACE-N and ACE-C). ACE is a protease capable of effectively degrading Aβ. The four structures are C2 pseudo-symmetric homodimers and provide insight into sACE dimerization. These structures were obtained using discrete classification in cryoSPARC and show different combinations of open, intermediate, and closed states of the catalytic domains, resulting in varying degrees of solvent accessibility to the active sites.

To deepen the understanding of the gradient of heterogeneity (from closed to open states) observed with discrete classification, the authors performed all-atom MD simulations and continuous conformational analysis of cryo-EM data using cryoSPARC 3DVA, cryoDRGN, and RECOVAR. cryoDRGN and cryoSPARC 3DVA revealed coordinated open-closed transitions across four catalytic domains, whereas RECOVAR revealed independent motion of two ACE-N domains, also observed with cryoSPARC focused classification. The authors suggest that the discrepancy in the results of the different methods for continuous conformational analysis in cryo-EM could results from different approaches used for dimensionality reduction and trajectory generation in these methods.

Strengths:

This is an important study that shows, for the first time, the structure and the snapshots of the dynamics of the full-length sACE dimer. Moreover, the study highlights the importance of combining insights from different cryo-EM methods that address questions difficult or impossible to tackle experimentally, while lacking ground truth for validation.

Weaknesses (from the last round of review):

The open, closed, and intermediate states of ACE-N and ACE-C in the four cryo-EM structures from discrete classification were designated quantitatively (based on measured atomic distances on the models fitted into cryo-EM maps). Unfortunately, atomic models were not fitted into cryo-EM maps obtained with cryoSPARC 3DVA, cryoDRGN, and RECOVAR, and the open/closed states in these cases were designated based on a qualitative analysis.

Reviewer #2 (Public review):

The manuscript presents a valuable contribution to the field of ACE structural biology and dynamics by providing the first complete full-length dimeric ACE structure in four distinct states. The study integrates cryo-EM and molecular dynamics simulations to offer important insights into ACE dynamics. The depth of analysis is commendable, and the combination of structural and computational approaches enhances our understanding of the protein's conformational landscape.

Reviewer #3 (Public review):

Summary:

Mancl et al. report four Cryo-EM structures of glycosylated and soluble Angiotensin-I converting enzyme (sACE) dimer. This moves forward the structural understanding of ACE, as previous analysis yielded partially denatured or individual ACE domains. By performing a heterogeneity analysis, the authors identify three structural conformations (open, intermediate open, and closed) that define the openness of the catalytic chamber and structural features governing the dimerization interface. They show that the dimer interface of soluble ACE consists of an N-terminal glycan and protein-protein interaction regions, as well as C-terminal protein-protein interactions. Further heterogeneity mining and all-atom molecular dynamic simulations show structural rearrangements that lead to the opening and closing of the catalytic pocket, which could explain how ACE binds its substrate. These studies could contribute to future drug design targeting the active site or dimerization interface of ACE.

Strengths:

The authors make significant efforts to address ACE denaturation on cryo-EM grids, testing various buffers and grid preparation techniques. These strategies successfully reduce denaturation and greatly enhance the quality of the structural analysis. The integration of cryoDRGN, 3DVA, RECOVAR, and all-atom simulations for heterogeneity analysis proves to be a powerful approach, further strengthening the overall experimental methodology.

Weaknesses:

No weaknesses noted.

Author response:

The following is the authors’ response to the previous reviews

We would like to thank you and your chosen reviewers for the diligent work and insightful comments. Following the latest round of feedback, we have made the following changes to the manuscript:

(1) We have added details regarding the specific versions of Cryosparc and cryoDRGN used in our analysis.

(2) We have addressed Reviewer 2’s comment concerning the negative RMSF values in Figure S12. The negative values occur because this display shows the difference in RMSF values from the MD simulations of glycosylated versus non-glycosylated ACE. To avoid similar confusion, we have split Figure S12 into three panels. Panels A and B show the RMSF values for each residue in the glycosylated and non-glycosylated sACE MD simulations, respectively, and all values here are positive. Panel C (the original Figure S12) now includes expanded labeling to clarify that it depicts the difference in RMSF values between the presence and absence of glycans. In this panel, a negative value indicates that the residues exhibit higher RMSF in simulations where glycans are present. The figure legend has been revised to accurately describe the updated figure.

eLife Assessment

This important study provides a potential framework for understanding the regulatory mechanisms of DON toxin biosynthesis in F. graminearum and identifies potential molecular targets for Fusarium head blight control. While FgDML1 remains under-explored with an unclear role in the biology of filamentous fungi, the supporting evidence in this study is incomplete. Providing details on methods and adding controls will strengthen the work.

Reviewer #1 (Public review):

Summary:

In their study, the authors investigated the F. graminearum homologue of the Drosophila Misato-Like Protein DML1 for a function in secondary metabolism and sensitivity to fungicides.

Strengths:

Generally, the topic of the study is interesting and timely, and the manuscript is well written, albeit in some cases, details on methods or controls are missing.

Weaknesses:

However, a major problem I see is with the core result of the study, the decrease in the DON content associated with the deletion of FgDML1. Although some growth data are shown in Figure 6, indicating a severe growth defect, the DON production presented in Figure 3 is not related to biomass. Also, the method and conditions for measuring DON are not described. Consequently, it could well be concluded that the decreased amount of DON detected is simply due to decreased growth, and the specific DON production of the mutant remains more or less the same.

To alleviate this concern, it is crucial to show the details on the DON measurement and growth conditions and to relate the biomass formation under the same conditions to the DON amount detected. Only then can a conclusion as to an altered production in the mutant strains be drawn.

Reviewer #2 (Public review):

Summary:

The manuscript entitled "Mitochondrial Protein FgDML1 Regulates DON Toxin Biosynthesis and Cyazofamid Sensitivity in Fusarium graminearum by affecting mitochondrial homeostasis" identified the regulatory effect of FgDML1 in DON toxin biosynthesis and sensitivity of Fusarium graminearum to cyazofamid. The manuscript provides a theoretical framework for understanding the regulatory mechanisms of DON toxin biosynthesis in F. graminearum and identifies potential molecular targets for Fusarium head blight control. The paper is innovative, but there are issues in the writing that need to be addressed and corrected.

Weaknesses:

(1) The authors speculate that cyazofamid treatment caused upregulation of the assembly factors, leading to a change in the conformation of the Qi protein, thus restoring the enzyme activity of complex III. But no speculation was given in the discussion as to why this would lead to the upregulation of assembly factors, and how the upregulation of assembly factors would change the protein conformation, and is there any literature reporting a similar phenomenon? I would suggest adding this to the discussion.

(2) Would increased sensitivity of the mutant to cell wall stress be responsible for the excessive curvature of the mycelium?

(3) The vertical coordinates of Figure 7B need to be modified with positive inhibition rates for the mutants.

Reviewer #3 (Public review):

Summary:

The manuscript "Mitochondrial 1 protein FgDML1 regulates DON toxin biosynthesis and cyazofamid sensitivity in Fusarium graminearum by affecting mitochondrial homeostasis" describes the construction of a null mutant for the FgDML1 gene in F. graminearum and assays characterising the effects of this mutation on the pathogen's infection process and lifecycle. While FgDML1 remains underexplored with an unclear role in the biology of filamentous fungi, and although the authors performed several experiments, there are fundamental issues with the experimental design and execution, and interpretation of the results.

Strengths:

FgDML1 is an interesting target, and there are novel aspects in this manuscript. Studies in other organisms have shown that this protein plays important roles in mitochondrial DNA (mtDNA) inheritance, mitochondrial compartmentalisation, chromosome segregation, mitochondrial distribution, mitochondrial fusion, and overall mitochondrial dynamics. Indeed, in Saccharomyces cerevisiae, the mutation is lethal. The authors have carried out multi-faceted experiments to characterise the mutants.

Weaknesses:

However, I have concerns about how the study was conceived. Given the fundamental importance of mitochondrial function in eukaryotic cells and how the absence of this protein impacts these processes, it is unsurprising that deletion of this gene in F. graminearum profoundly affects fungal biology. Therefore, it is misleading to claim a direct link between FgDML1 and DON toxin biosynthesis (and virulence), as the observed effects are likely indirect consequences of compromised mitochondrial function. In fact, it is reasonable to assume that the production of all secondary metabolites is affected to some extent in the mutant strains and that such a strain would not be competitive at all under non-laboratory conditions. The order in which the authors present the results can be misleading, too. The results on vegetative growth rate appeared much later in the manuscript, which should have come first, as the FgDML1 mutant exhibited significant growth defects, and subsequent results should be discussed in that context. Moreover, the methodologies are not described properly, making the manuscript hard to follow and difficult to replicate.

eLife Assessment

This work presents potentially important findings suggesting that a combination of transcranial stimulation approaches applied for a short period could improve memory performance. However, the evidence supporting the conclusions is currently incomplete. In particular, the claims relating to the specific neural mechanisms and anatomical sites of action underlying effects were viewed as overstated in the current version. The results potentially have implications for non-invasive enhancement of cognitive functions.

Reviewer #1 (Public review):

Summary:

The authors make a bold claim that a combination of repetitive transcranial magnetic stimulation (intermittent theta burst-iTBS) and transcranial alternating current stimulation (gamma tACS) causes slight improvements in memory in a face/name/profession task.

Strengths:

The idea of stimulating the human brain non-invasively is very attractive because, if it worked, it could lead to a host of interesting applications. The current study aims to evaluate one such exciting application.

Weaknesses:

(1) The title refers to the "precuneus-hippocampus" network. A clear definition of what is meant by this terminology is lacking. More importantly, mechanistic evidence that the precuneus and the hippocampus are involved in the potential effects of stimulation remains unconvincing.

(2) The question of the extent to which the stimulation approach and the stimulation parameters used in these experiments causes specific and functionally relevant neural effects remains open. Invasive recordings that could address this question remain out of the scope of this non-invasive study. The authors conducted scalp EEG experiments in an attempt to address this question using non-invasive methods. However, the results shown in Fig. 3 are unclear. The results are inconsistently reported in units of microvolts squared in some panels (3A, 3B) and in units of microvolts in other panels (3C). Also, there is insufficient consideration of potential contamination by signal components reflecting eye movements, other muscle artifacts, or another volume-conducted signal reflecting aggregate activity inside the brain.

(3) Figure 3 indicates "Precuneus oscillatory activity ...", but evidence that the activity presented reflects precuneus activity is lacking. The maps shown at the bottom of Figure 3C suggest that the EEG signals recorded with scalp EEG reflect activity generated across a wide spatial range, with a peak encompassing at least tens of centimeters. Thus, evidence that effects specifically reflect precuneus activity, as the paper's title and text throughout the manuscript suggest, is lacking.

(4) The paper as currently presented (e.g., Figure 3) also lacks rigorous evidence of relevant oscillatory activity. Prior to filtering EEG signals in a particular frequency band, clear evidence of oscillations in the frequency band of interest should be shown (e.g., demonstration of a clear peak that emerges naturally in the frequency range of interest when spectral analysis is applied to "raw" signals). The authors claim that gamma oscillations change because of the stimulation, but a clear peak in the gamma range prior to stimulation is not apparent in the data as currently presented. Thus, the extent to which spectral measurements during stimulation reflect physiological gamma oscillations remains unclear.

(5) Concerns remain regarding the rigor of statistical analyses in the revised manuscript (see also point 8 below). Figure 3B shows an undefined statistical test with p<0.05. The statistical test that was used is not explained. Also, a description of how corrections for multiple comparisons were made is missing. Figures 3A and 3C are not accompanied by statistics, making the results difficult to interpret. For Figure 4C, a claim was made based on a significant p-value for one statistical test and a non-significant p-value in another test. This is a common statistical mistake (see Figure 1 and accompanying discussion in Makin and Orban de Xivry (2019) Science Forum: Ten common statistical mistakes to watch out for when writing or reviewing a manuscript. eLife 8:e48175).

(6) In the second question posed in the original review, I highlighted that it was unclear how such stimulation would produce memory enhancement. The authors replied that, in the absence of mechanisms, there are many other studies that suffer from the same problem. This raises the question of placebo effects. The paper does not sufficiently address or discuss the possibility that any potential stimulation effects may reflect placebo effects.

(7) The third major concern in the original review was the lack of evidence for a mechanism that is specific to the precuneus. Evidence for specific involvement of the precuneus remains lacking in the revised manuscript. The authors state: "the non-invasive stimulation protocol was applied to an individually identified precuneus for each participant". However, the meaning of this statement is unclear. Specifically, it is unclear how the authors know that they are specifically targeting the precuneus. Without directly recording from the precuneus and directly demonstrating effects, which is outside of the scope of the study, specific involvement of the precuneus seems speculative. Also, it does not seem as though a figure was included in the paper to show how the stimulation protocol specifically targets the precuneus. In their response to the original reviews, the authors state that posterior medial parietal areas are the only regions that show significant differences following the stimulation, but they did not cite a specific figure, or statistics reported in the text, that show this. In any event, posterior medial parietal areas encompass a wide area of the brain, so this would still not provide evidence for an effect specifically involving the precuneus.

(8) Regarding chance levels, it is unfortunate that the authors cannot quantify what chance levels are in the immediate and delayed recall conditions. This makes interpretation of the results challenging. In the immediate and delayed conditions, the authors state that the chance level is 33%. It would be useful to mark this in the figures. If I understand correctly, chance is 33% in Fig. 2A. If this is the case and if I am interpreting the figure correctly:<br /> Gray bars for the sham condition appear to be below chance (~20-25%). Why is this condition associated with an accuracy level that is lower than chance?<br /> Cyan bars and red bars do not appear to be significantly different from chance (i.e., 33%), with red slightly higher than cyan. What statistic was performed to obtain the level of significance indicated in the figure? The highest average value for the red condition appears to be around 35%. More details are needed to fully explain this figure and to support the claims associated with this figure.

(9) In the revised version of the paper, the authors did not address concerns associated with the block design (please see question 4d in the original review).

In sum, this study presents an admirable aspirational goal, the notion that a non-invasive stimulation protocol could modulate activity in specific brain regions to enhance memory. However, the evidence presented at the behavioral level and at the mechanistic level (e.g. the putative involvement of specific brain regions) remains unconvincing.

Reviewer #2 (Public review):

Summary:

The manuscript by Borghi and colleagues provides evidence that the combination of intermittent theta burst TMS stimulation and gamma transcranial alternating current stimulation (γtACS) targeting the precuneus increases long-term associative memory in healthy subjects compared to iTBS alone and sham conditions. Using a rich dataset of TMS-EEG and resting-state functional connectivity (rs-FC) maps and structural MRI data, the authors also provide evidence that dual stimulation increased gamma oscillations and functional connectivity between the precuneus and hippocampus. Enhanced memory performance was linked to increased gamma oscillatory activity and connectivity through white matter tracts.

Strengths:

The combination of personalized repetitive TMS (iTBS) and gamma tACS is a novel approach to targeting the precuneus, and thereby, connected memory-related regions to enhance long-term associative memory. The authors leverage an existing neural mechanism engaged in memory binding, theta-gamma coupling, by applying TMS at theta burst patterns and tACS at gamma frequencies to enhance gamma oscillations. The authors conducted a thorough study that suggests that simultaneous iTBS and gamma tACS could be a powerful approach for enhancing long-term associative memory. The paper was well-written, clear, and concise.

Comments on Revision:

I thank the authors for their thoughtful responses to my first review and their inclusion of more detailed methodological discussion of their rationale for the stimulation protocol conditions and timing. Regarding the apparent difference in connectivity at baseline between conditions, the explanation that this is due to intrinsic dynamics, state, or noise implies the baseline is reflecting transient changes in dynamics rather than a true or stable baseline. Based on this, it looks like iTBS solely is significantly greater than the baseline before the iTBS and _γtACS condition but maybe not that much lower than post-stimulation period for iTBS and _γtACS. A longer baseline period should be used to ensure transient states are not driving baseline levels such that these endogenous fluctuations would average out. This also raises questions about whether the effect of iTBS and _γtACS or iTBS alone are dependent on the intrinsic state at the time when stimulation begins. Their additional clarification of memory scoring is helpful but also reveals that the effect of dual iTBS+_γtACS specifically on the association between faces and names is just significant. This modest increase in associative memory should be taken into consideration when interpreting these findings.

Reviewer #3 (Public review):

Summary:

Borghi and colleagues present results from 4 experiments aimed at investigating the effects of dual _γtACS and iTBS stimulation of the precuneus on behavioral and neural markers of memory formation. In their first experiment (n = 20), they find that a 3-minute offline (i.e., prior to task completion) stimulation that combines both techniques leads to superior memory recall performance in an associative memory task immediately after learning associations between pictures of faces, names, and occupation, as well as after a 15-minute delay, compared to iTBS alone (+ tACS sham) or no stimulation (sham for both iTBS and tACS). Performance in a second task probing short-term memory was unaffected by the stimulation condition. In a second experiment (n = 10), they show that these effects persist over 24 hours and up to a full week after initial stimulation. A third (n = 14) and fourth (n = 16) experiment were conducted to investigate neural effects of the stimulation protocol. The authors report that, once again, only combined iTBS and _γtACS increases gamma oscillatory activity and neural excitability (as measured by concurrent TMS-EEG) specific to the stimulated area at the precuneus compared to a control region, as well as precuneus-hippocampus functional connectivity (measured by resting state MRI), which seemed to be associated with structural white matter integrity of the bilateral middle longitudinal fasciculus (measured by DTI).

Strengths:

Combining non-invasive brain stimulation techniques is a novel, potentially very powerful method to maximize the effects of these kinds of interventions that are usually well-tolerated and thus accepted by patients and healthy participants. It is also very impressive that the stimulation-induced improvements in memory performance resulted from a short (3 min) intervention protocol. If the effects reported here turn out to be as clinically meaningful and generalizable across populations as implied, this approach could represent a promising avenue for treatment of impaired memory functions in many conditions.

Methodologically, this study is expertly done! I don't see any serious issues with the technical setup in any of the experiments. It is also very commendable that the authors conceptually replicated the behavioral effects of experiment 1 in experiment 2 and then conducted two additional experiments to probe the neural mechanisms associated with these effects. This certainly increases the value of the study and the confidence in the results considerably.

The authors used a within-subject approach in their experiments, which increases statistical power and allows for stronger inferences about the tested effects. They also used to individualize stimulation locations and intensities, which should further optimize the signal-to-noise ratio.

Weaknesses:

I think one of the major weaknesses of this study is the overall low sample size in all of the experiments (between n = 10 and n = 20). This is, as I mentioned when discussing the strengths of the study, partly mitigated by the within-subject design and individualized stimulation parameters. The authors mention that they performed a power analysis but this analysis seemed to be based on electrophysiological readouts similar to those obtained in experiment 3. It is thus unclear whether the other experiments were sufficiently powered to reliably detect the behavioral effects of interest. In the revised manuscript, the authors provide post-hoc sensitivity analyses that help contextualize the strength of the findings.

While the authors went to great lengths trying to probe the neural changes likely associated with the memory improvement after stimulation, it is impossible from their data to causally relate the findings from experiments 3 and 4 to the behavioral effects in experiments 1 and 2. This is acknowledged by the authors and there are good methodological reasons for why TMS-EEG and fMRI had to be collected in separate experiments, but readers should keep in mind that this limits inferences about how exactly dual iTBS and _γtACS of the precuneus modulate learning and memory.

Author response:

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

Reviewer #1 (Public review):

Summary:

The authors claim that they can use a combination of repetitive transcranial magnetic stimulation (intermittent theta burst-iTBS) and transcranial alternating current stimulation (gamma tACS) to cause slight improvements in memory in a face/name/profession task.

Strengths:

The idea of stimulating the human brain non-invasively is very attractive because, if it worked, it could lead to a host of interesting applications. The current study aims to evaluate one such exciting application.

Weaknesses:

(1) It is highly unclear what, if anything, transpires in the brain with non-invasive stimulation. To cite one example of many, a rigorous study in rats and human cadavers, compellingly showed that traditional parameters of transcranial electrical stimulation lead to no change in brain activity due to the attenuation by the soft tissue and skull (Mihály Vöröslakos et al Nature Communications 2018): https://www.nature.com/articles/s41467-018-02928-3. It would be very useful to demonstrate via invasive neurophysiological recordings that the parameters used in the current study do indeed lead to any kind of change in brain activity. Of course, this particular study uses a different non-invasive stimulation protocol.

Thank you for raising the important issue regarding the actual neurophysiological effects of non-invasive brain stimulation. Unfortunately, invasive neurophysiological recordings in humans for this type of study are not feasible due to ethical constraints, while studies on cadavers or rodents would not fully resolve our question. Indeed, the authors of the cited study (Mihály Vöröslakos et al., Nature Communications, 2018) highlight the impossibility of drawing definitive conclusions about the exact voltage required in the in-vivo human brain due to significant differences between rats and humans, as well as the in-vivo human brain and cadavers due to alterations in electrical conductivity that occur in postmortem tissue. Huang and colleagues addressed the difficulties in reaching direct evidence of non-invasive brain stimulation (NIBS) effects in a review published in Clinical Neurophysiology in 2017. They conclude that the use of EEG to assess brain response to TMS has great potential for a less indirect demonstration of plasticity mechanisms induced by NIBS in humans.

To address this challenge, we conducted Experiments 3 and 4, which respectively examined the neurophysiological and connectivity changes induced by the stimulation in a non-invasive manner using TMS-EEG and fMRI. The observed changes in brain oscillatory activity (increased gamma oscillatory activity), cortical excitability (enhanced posteromedial parietal cortex reactivity), and brain connectivity (strengthened connections between the precuneus and hippocampi) provided evidence of the effects of our non-invasive brain stimulation protocol, further supporting the behavioral data.

Additionally, we carefully considered the issue of stimulation distribution and, in response, performed a biophysical modeling analysis and E-field calculation using the parameters employed in our study (see Supplementary Materials).

We acknowledge that further exploration of this aspect would be highly valuable, and we agree that it is worth discussing both as a technical limitation and as a potential direction for future research. We therefore, modify the discussion accordingly (main text, lines 280-289).

“Although we studied TMS and tACS propagation through the E-field modeling and observed an increase in the precuneus gamma oscillatory activity, excitability and connectivity with the hippocampi, we cannot exclude that our results might reflect the consequences of stimulating more superficial parietal regions other than the precuneus nor report direct evidence of microscopic changes in the brain after the stimulation. Invasive neurophysiological recordings in humans for this type of study are not feasible due to ethical constraints. Studies on cadavers or rodents would not fully resolve our question due to significant differences between them (i.e. rodents do not have an anatomical correspondence while cadavers have an alterations in electrical conductivity occurring in postmortem tissue). However, further exploration of this aspect in future studies would help in the understanding of γtACS+iTBS effects.”

(2) If there is any brain activity triggered by the current stimulation parameters, then it is extremely difficult to understand how this activity can lead to enhancing memory. The brain is complex. There are hundreds of neuronal types. Each neuron receives precise input from about 10,000 other neurons with highly tuned synaptic strengths. Let us assume that the current protocol does lead to enhancing (or inhibiting) simultaneously the activity of millions of neurons. It is unclear whether there is any activity at all in the brain triggered by this protocol, it is also unclear whether such activity would be excitatory, or inhibitory. It is also unclear how many neurons, let alone what types of neurons would change their activity. How is it possible that this can lead to memory enhancement? This seems like using a hammer to knock on my laptop and hope that the laptop will output a new Mozart-like sonata.

Thank you for your comment. As you correctly point out, we still do not have precise knowledge of which neurons—and to what extent—are activated during non-invasive brain stimulation in humans. However, this challenge is not limited to brain stimulation but applies to many other therapeutic interventions, including psychiatric medications, without limiting their use.

Nevertheless, a substantial body of research has investigated the mechanisms underlying the efficacy of TMS and tACS in producing behavioral after-effects, primarily through its ability to induce long-term potentiation (Bliss & Collingridge, The Journal of Physiology, 1993a; Ridding & Rothwell, Nature Reviews Neuroscience, 2007; Huang et al., Clinical Neurophysiology, 2017; Koch et al., Neuroimage 2018; Koch et al., Brain 2022; Jannati et al., Neuropsychopharmacology, 2023; Wischnewski et al., Trends in Cognitive Science, 2023; Griffiths et al., Trends in Neuroscience, 2023).

We acknowledge that we took this important aspect for granted. We consequently expanded the introduction accordingly (main text, lines 48-60).

“Repetitive transcranial magnetic stimulation (rTMS) and transcranial alternating current stimulation (tACS) are two forms of NIBS widely used to enhance memory performances (Grover et al., 2022; Koch et al., 2018; Wang et al., 2014). rTMS, based on the principle of Faraday, induces depolarization of cortical neuronal assemblies and leads to after-effects that have been linked to changes in synaptic plasticity involving mechanisms of long-term potentiation (LTP) (Huang et al., 2017; Jannati et al., 2023). On the other hand, tACS causes rhythmic fluctuations in neuronal membrane potentials, which can bias spike timing, leading to an entrainment of the neural activity (Wischnewski et al., 2023). In particular, the induction of gamma oscillatory a has been proposed to play an important role in a type of LTP known as spike timing-dependent plasticity, which depends on a precise temporal delay between the firing of a presynaptic and a postsynaptic neuron (Griffiths and Jensen, 2023). Both LTP and gamma oscillations have a strong link with memory processes such as encoding (Bliss and Collingridge, 1993; Griffiths and Jensen, 2023; Rossi et al., 2001), pointing to rTMS and tACS as good candidates for memory enhancement.”

(3) Even if there is any kind of brain activation, it is unclear why the authors seem to be so sure that the precuneus is responsible. Are there neurophysiological data demonstrating that the current protocol only activates neurons in the precuneus? Of note, the non-invasive measurements shown in Figure 3 are very weak (Figure 3A top and bottom look very similar, and Figure 3C left and right look almost identical). Even if one were to accept the weak alleged differences in Figure 3, there is no indication in this figure that there is anything specific to the precuneus, rather a whole brain pattern. This would be the kind of minimally rigorous type of evidence required to make such claims. In a less convincing fashion, one could look at different positions of the stimulation apparatus. This would not be particularly compelling in terms of making a statement about the precuneus. But at least it would show that the position does matter, and over what range of distances it matters, if it matters.

Thank you for your feedback. Our assumption that the precuneus plays a key role in the observed effects is based on several factors:

(1) The non-invasive stimulation protocol was applied to an individually identified precuneus for each participant. Given existing evidence on TMS propagation, we can reasonably assume that the precuneus was at least a mediator of the observed effects (Ridding & Rothwell, Nature Reviews Neuroscience 2007). For further details about target identification and TMS and tACS propagation, please refer to the MRI data acquisition section in the main text and Biophysical modeling and E-field calculation section in the supplementary materials.

(2) To investigate the effects of the neuromodulation protocol on cortical responses, we conducted a whole-brain analysis using multiple paired t-tests comparing each data point between different experimental conditions. To minimize the type I error rate, data were permuted with the Monte Carlo approach and significant p-values were corrected with the false discovery rate method (see the Methods section for details). The results identified the posterior-medial parietal areas as the only regions showing significant differences across conditions.

(3) To control for potential generalized effects, we included a control condition in which TMS-EEG recordings were performed over the left parietal cortex (adjacent to the precuneus). This condition did not yield any significant results, reinforcing the cortical specificity of the observed effects.

However, as stated in the Discussion, we do not claim that precuneus activity alone accounts for the observed effects. As shown in Experiment 4, stimulation led to connectivity changes between the precuneus and hippocampus, a network widely recognized as a key contributor to long-term memory formation (Bliss & Collingridge, Nature 1993). These connectivity changes suggest that precuneus stimulation triggered a ripple effect extending beyond the stimulation site, engaging the broader precuneus-hippocampus network.

Regarding Figure 3A, it represents the overall expression of oscillatory activity detected by TMS-EEG. Since each frequency band has a different optimal scaling, the figure reflects a graphical compromise. A more detailed representation of the significant results is provided in Figure 3B. The effect sizes for gamma oscillatory activity in the delta T1 and T2 conditions were 0.52 and 0.50, respectively, which correspond to a medium effect based on Cohen’s d interpretation.

We add a paragraph in the discussion to improve the clarity of the manuscript regarding this important aspect (lines 193-198).

“Given the existing evidence on TMS propagation and the computation of the Biophysical model with the Efield, we can reasonably assume that the individually identified PC was a mediator of the observed effects (Ridding and Rothwell, 2007). Moreover, we observed specific cortical changes in the posteromedial parietal areas, as evidenced by the whole-brain analysis conducted on TMS-EEG data and the absence of effect on the lateral posterior parietal cortex used as a control condition.”

(4) In the absence of any neurophysiological documentation of a direct impact on the brain, an argument in this type of study is that the behavioral results show that there must be some kind of effect. I agree with this argument. This is also the argument for placebo effects, which can be extremely powerful and useful even if the mechanism is unrelated to what is studied. Then let us dig into the behavioral results.

Hoping to have already addressed your concern regarding the neurophysiological impact of the stimulation on the brain, we would like to emphasize that the behavioral results were obtained controlling for placebo effects. This was achieved by having participants perform the task under different stimulation conditions, including a sham condition.

4a. There does not seem to be any effect on the STMB task, therefore we can ignore this.

4b. The FNAT task is minimally described in the supplementary material. There are no experimental details to understand what was done. What was the size of the images? How long were the images presented for? Were there any repetitions of the images? For how long did the participants study the images? Presumably, all the names and occupations are different? What were the genders of the faces? What is chance level performance? Presumably, the same participant saw different faces across the different stimulation conditions. If not, then there can be memory effects across different conditions that are even more complex to study. If yes, then it would be useful to show that the difficulty is the same across the different stimuli.

We thank you for signaling the lack in the description of FNAT task. We added the information required in the supplementary information (lines 93-101).

“Each picture's face size was 19x15cm. In the learning phase, faces were shown along with names and occupations for 8 seconds each (totaling approximately 2 minutes). During immediate recall, the faces were displayed alone for 8 seconds. In the delayed recall and recognition phase, pictures were presented until the subject provided answers. We used a different set of stimuli for each stimulation condition, resulting in a total of 3 parallel task forms balanced across conditions and session order. All parallel forms comprised 6 male and 6 female faces; for each sex, there were 2 young adults (around 30 years old), 2 middle-aged adults (around 50 years old), and 2 elderly adults (around 70 years old). Before the experiments, we conducted a pilot study to ensure no differences existed between the parallel forms of the task.”

The chance level in the immediate and delayed recall is not quantifiable since the participants had to freely recall the name and the occupation without a multiple choice. In the recognition, the chance level was around 33% (since the possible answers were 3).

4c. Although not stated clearly, if I understand FNAT correctly, the task is based on just 12 presentations. Each point in Figure 2A represents a different participant. Unfortunately, there is no way of linking the performance of individual participants across the conditions with the information provided. Lines joining performance for each participant would be useful in this regard. Because there are only 12 faces, the results are quantized in multiples of 100/12 % in Figure 3A. While I do not doubt that the authors did their homework in terms of the statistical analyses, it is difficult to get too excited about these 12 measurements. For example, take Figure 3A immediate condition TOTAL, arguably the largest effect in the whole paper. It seems that on average, the participants may remember one more face/name/occupation.

Thank you for the suggestion. We added graphs showing lines linking the performance of individual participants across conditions to improve clarity, please see Fig.2 revised. We apologize for the lack of clarity in the description of the FNAT. As you correctly pointed out, we used the percentage based on the single association between face, name and occupation (12 in total). However, each association consisted of three items, resulting in a total of 36 items to learn and associate – we added a paragraph to make it more explicit in the manuscript (lines 425-430).

“We considered a correct association when a subject was able to recall all the information for each item (i.e. face, name and occupation), resulting in a total of 36 items to learn and associate. To further investigate the effect on FNAT we also computed a partial recall score accounting for those items where subjects correctly matched only names with faces (FNAT NAME) and only occupations with faces (FNAT OCCUPATION). See supplementary information for score details.”

In the example you mentioned, participants were, on average, able to correctly recall and associate three more items compared to the other conditions. While this difference may not seem striking at first glance, it is important to consider that we assessed memory performance after a single, three-minute stimulation session. Similar effects are typically observed only after multiple stimulation sessions (Koch et al., NeuroImage, 2018; Grover et al., Nature Neuroscience, 2022). Moreover, memory performance changes are often measured by a limited set of stimuli due to methodological constraints related to memory capacity. For example, Rey Auditory Verbal learning task, requiring to learn and recall 15 words, is a typical test used to detect memory changes (Koch et al., Neuroimage, 2018; Benussi et al., Brain stimulation 2021; Benussi et al., Annals of Neurology, 2022). 

4d. Block effects. If I understand correctly, the experiments were conducted in blocks. This is always problematic. Here is one example study that articulated the big problems in block designs (Li et al TPAMI 2021):https://ieeexplore.ieee.org/document/9264220

Thank you for the interesting reference. According to this paper, in a block design, EEG or fMRI recordings are performed in response to different stimuli of a given class presented in succession. If this is the case, it does not correspond to our experimental design where both TMS-EEG and fMRI were conducted in resting state on different days according to the different stimulation conditions.

4e. Even if we ignore the lack of experimental descriptions, problems with lack of evidence of brain activity, the minimalistic study of 12 faces, problems with the block design, etc. at the end of the day, the results are extremely weak. In FNAT, some results are statistically significant, some are not. The interpretation of all of this is extremely complex. Continuing with Figure 3A, it seems that the author claims that iTBS+gtACS > iTBS+sham-tACS, but iTBS+gtACS ~ sham+sham. I am struggling to interpret such a result. When separating results by name and occupation, the results are even more perplexing. There is only one condition that is statistically significant in Figure 3A NAME and none in the occupation condition.

Thank you again for your feedback. Hoping to have thoroughly addressed your initial concerns in our previous responses, we now move on to your observations regarding the behavioral results, assuming you were referring to Figure 2A. The main finding of this study is the improvement in long-term memory performance, specifically the ability to correctly recall the association between face, name, and occupation (total FNAT), which was significantly enhanced in both Experiments 1 and 2. However, we also aimed to explore the individual contributions of name and occupation separately to gain a deeper understanding of the results. Our analysis revealed that the improvement in total FNAT was primarily driven by an increase in name recall rather than occupation recall. We understand that this may have caused some confusion. We consequently modified the manuscript in the (lines 97-99; 107-111; 425-430) to make it clearer and moved the graph relative to FNAT NAME and OCCUPATION from fig.2 in the main text to fig. S4 in supplementary information.

“Dual iTBS+γtACS increased the performances in recalling the association between face, name and occupation (FNAT accuracy) both for the immediate (F_2,38=7.18; p =0.002; η²_p=0.274) and the delayed (F_2,38=5.86; p =0.006; η²_p=0.236) recall performances (Fig. 2, panel A).”

“The in-depth analysis of the FNAT accuracy investigating the specific contribution of face-name and face-occupation recall reveald that dual iTBS+γtACS increased the performances in the association between face and name (FNAT NAME) delayed recall (F_2,38 =3.46; p =0.042; η²p =0.154; iTBS+γtACS vs. sham-iTBS+sham-tACS: 42.9±21.5 % vs. 33.8±19 %; p=0.048 Bonferroni corrected) (Fig. S4, supplementary information).”

“We considered a correct association when a subject was able to recall all the information for each item (i.e. face, name and occupation), resulting in a total of 36 items to learn and associate. To further investigate the effect on FNAT we also computed a partial recall score accounting for those items where subjects correctly matched only names with faces (FNAT NAME) and only occupations with faces (FNAT OCCUPATION). See supplementary information for score details.”

Regarding the stimulation conditions, your concerns about the performance pattern (iTBS+gtACS > iTBS+sham-tACS, but iTBS+gtACS ~ sham+sham) are understandable. However, this new protocol was developed precisely in response to the variability observed in behavioral outcomes following non-invasive brain stimulation, particularly when used to modulate memory functions (Corp et al., 2020; Pabst et al., 2022). As discussed in the manuscript, it is intended as a boost to conventional non-invasive brain stimulation protocols, leveraging the mechanisms outlined in the Discussion section.

(5) In sum, it would be amazing to be able to use non-invasive stimulation for any kind of therapeutic purpose as the authors imagine. More work needs to be done to convince ourselves that this kind of approach is viable. The evidence provided in this study is weak.

We hope our response will be carefully considered, fostering a constructive exchange and leading to a reassessment of your evaluation.

Reviewer #2 (Public review):

Summary:

The manuscript "Dual transcranial electromagnetic stimulation of the precuneus-hippocampus network boosts human long-term memory" by Borghi and colleagues provides evidence that the combination of intermittent theta burst TMS stimulation and gamma transcranial alternating current stimulation (γtACS) targeting the precuneus increases long-term associative memory in healthy subjects compared to iTBS alone and sham conditions. Using a rich dataset of TMS-EEG and resting-state functional connectivity (rs-FC) maps and structural MRI data, the authors also provide evidence that dual stimulation increased gamma oscillations and functional connectivity between the precuneus and hippocampus. Enhanced memory performance was linked to increased gamma oscillatory activity and connectivity through white matter tracts.

Strengths:

The combination of personalized repetitive TMS (iTBS) and gamma tACS is a novel approach to targeting the precuneus, and thereby, connected memory-related regions to enhance long-term associative memory. The authors leverage an existing neural mechanism engaged in memory binding, theta-gamma coupling, by applying TMS at theta burst patterns and tACS at gamma frequencies to enhance gamma oscillations. The authors conducted a thorough study that suggests that simultaneous iTBS and gamma tACS could be a powerful approach for enhancing long-term associative memory. The paper was well-written, clear, and concise.

Weaknesses:

(1) The study did not include a condition where γtACS was applied alone. This was likely because a previous work indicated that a single 3-minute γtACS did not produce significant effects, but this limits the ability to isolate the specific contribution of γtACS in the context of this target and memory function

Thank you for your comments. As you pointed out, we did not include a condition where γtACS was applied alone. This decision was based on the findings of Guerra et al. (Brain Stimulation 2018), who investigated the same protocol and reported no aftereffects. Given the substantial burden of the experimental design on patients and our primary goal of demonstrating an enhancement of effects compared to the standalone iTBS protocol, we decided to leave out this condition. However, you raise an important aspect that should be further discussed, we modified the limitation section accordingly (lines 290-297).

“We did not assess the effects of γtACS alone. This decision was based on the findings of Guerra et al. (Guerra et al., 2018), who investigated the same protocol and reported no aftereffects. Given the substantial burden of the experimental design on patients and our primary goal of demonstrating an enhancement of effects compared to the standalone iTBS protocol, we decided to leave out this condition. While examining the effects of γtACS alone could help isolate its specific contribution to this target and memory function, extensive research has shown that achieving a cognitive enhancement aftereffect with tACS alone typically requires around 20–25 minutes of stimulation (Grover et al., 2023).”

(2) The authors applied stimulation for 3 minutes, which seems to be based on prior tACS protocols. It would be helpful to present some rationale for both the duration and timing relative to the learning phase of the memory task. Would you expect additional stimulation prior to recall to benefit long-term associative memory?

Thank you for your comment and for raising this interesting point. As you correctly noted, the protocol we used has a duration of three minutes, a choice based on previous studies demonstrating its greater efficacy with respect to single stimulation from a neurophysiological point of view. Specifically, these studies have shown that the combined stimulation enhanced gamma-band oscillations and increased cortical plasticity (Guerra et al., Brain Stimulation 2018; Maiella et al., Scientific Reports 2022). Given that the precuneus (Brodt et al., Science 2018; Schott et al., Human Brain Mapping 2018), gamma oscillations (Osipova et al., Journal of Neuroscience 2006; Deprés et al., Neurobiology of Aging 2017; Griffiths et al., Trends in Neurosciences 2023), and cortical plasticity (Brodt et al., Science 2018) are all associated with memory formation and encoding processes, we decided to apply the co-stimulation immediately before it to enhance the efficacy. We added this paragraph to the manuscript rationale (lines 48-60).

“Repetitive transcranial magnetic stimulation (rTMS) and transcranial alternating current stimulation (tACS) are two forms of NIBS widely used to enhance memory performances (Grover et al., 2022; Koch et al., 2018; Wang et al., 2014). rTMS, based on the principle of Faraday, induces depolarization of cortical neuronal assemblies and leads to after-effects that have been linked to changes in synaptic plasticity involving mechanisms of long-term potentiation (LTP) (Huang et al., 2017; Jannati et al., 2023). On the other hand, tACS causes rhythmic fluctuations in neuronal membrane potentials, which can bias spike timing, leading to an entrainment of the neural activity (Wischnewski et al., 2023). In particular, the induction of gamma oscillatory a has been proposed to play an important role in a type of LTP known as spike timing-dependent plasticity, which depends on a precise temporal delay between the firing of a presynaptic and a postsynaptic neuron (Griffiths and Jensen, 2023). Both LTP and gamma oscillations have a strong link with memory processes such as encoding (Bliss and Collingridge, 1993; Griffiths and Jensen, 2023; Rossi et al., 2001), pointing to rTMS and tACS as good candidates for memory enhancement.”

Regarding the question of whether stimulation could also benefit recall, the answer is yes. We can speculate that repeating the stimulation before recall might provide an additional boost. This is supported by evidence showing that both the precuneus and gamma oscillations are involved in recall processes (Flanagin et al., Cerebral Cortex 2023; Griffiths et al., Trends in Neurosciences 2023). Furthermore, previous research suggests that reinstating the same brain state as during encoding can enhance recall performance (Javadi et al., The Journal of Neuroscience 2017). We added this consideration to the discussion (lines 305-311).

“Future studies should further investigate the effects of stimulation on distinct memory processes. In particular, stimulation could be applied before retrieval (Rossi et al., 2001), to better elucidate its specific contribution to the observed enhancements in memory performance. Additionally, it would be worth examining whether repeated stimulation - administered both before encoding and before retrieval - could produce a boosting effect. This is especially relevant in light of findings showing that matching the brain state between retrieval and encoding can significantly enhance memory performance (Javadi et al., 2017).”

(3) How was the burst frequency of theta iTBS and gamma frequency of tACS chosen? Were these also personalized to subjects' endogenous theta and gamma oscillations? If not, were increases in gamma oscillations specific to patients' endogenous gamma oscillation frequencies or the tACS frequency?

The stimulation protocol was chosen based on previous studies (Guerra et al., Brain Stimulation 2018; Maiella et al., Scientific Reports 2022).  Gamma tACS sinusoid frequency wave was set at 70 Hz while iTBS consisted of ten bursts of three pulses at 50 Hz lasting 2 s, repeated every 10 s with an 8 s pause between consecutive trains, for a total of 600 pulses total lasting 190 s (see iTBS+γtACS neuromodulation protocol section). In particular, the theta iTBS has been inspired by protocols used in animal models to elicit LTP in the hippocampus (Huang et al., Neuron 2005). Consequently, neither Theta iTBS nor the gamma frequency of tACS were personalized. The increase in gamma oscillations was referred to the patient’s baseline and did not correspond to the administrated tACS frequency.

(4) The authors do a thorough job of analyzing the increase in gamma oscillations in the precuneus through TMS-EEG; however, the authors may also analyze whether theta oscillations were also enhanced through this protocol due to the iTBS potentially targeting theta oscillations. This may also be more robust than gamma oscillations increases since gamma oscillations detected on the scalp are very low amplitude and susceptible to noise and may reflect activity from multiple overlapping sources, making precise localization difficult without advanced techniques.

Thank you for the suggestion. We analyzed theta oscillations, finding no changes.

(5) Figure 4: Why are connectivity values pre-stimulation for the iTBS and sham tACS stimulation condition so much higher than the dual stimulation? We would expect baseline values to be more similar.

We acknowledge that the pre-stimulation connectivity values for the iTBS and sham tACS conditions appear higher than those for the dual stimulation condition. However, as noted in our statistical analyses, there were no significant differences at baseline between conditions (p-FDR= 0.3514), suggesting that any apparent discrepancy is due to natural variability rather than systematic bias. One potential explanation for these differences is individual variability in baseline connectivity measures, which can fluctuate due to factors such as intrinsic neural dynamics, participant state, or measurement noise. Despite these variations, our statistical approach ensures that any observed post-stimulation effects are not confounded by pre-existing differences.

(6) Figure 2: How are total association scores significantly different between stimulation conditions, but individual name and occupation associations are not? Further clarification of how the total FNAT score is calculated would be helpful.

We apologize for any lack of clarity. The total FNAT score reflects the ability to correctly recall all the information associated with a person—specifically, the correct pairing of the face, name, and occupation. Participants received one point for each triplet they accurately recalled. The scores were then converted into percentages, as detailed in the Face-Name Associative Task Construction and Scoring section in the supplementary materials.

Total FNAT was the primary outcome measure. However, we also analyzed name and occupation recall separately to better understand their partial contributions. Our analysis revealed that the improvement in total FNAT was primarily driven by an increase in name recall rather than occupation recall.

We acknowledge that this distinction may have caused some confusion. To improve clarity, we revised the manuscript accordingly (lines 97-98; 107-111; 425-430).

“Dual iTBS+γtACS increased the performances in recalling the association between face, name and occupation (FNAT accuracy) both for the immediate (F_2,38=7.18 ;p=0.002; η²_p=0.274) and the delayed (F_2,38=5.86;p=0.006; η²_p=0.236) recall performances (Fig. 2, panel A).”

“The in-depth analysis of the FNAT accuracy investigating the specific contribution of face-name and face-occupation recall revealed that dual iTBS+γtACS increased the performances in the association between face and name (FNAT NAME) delayed recall (F_2,38 =3.46; p =0.042; η²p =0.154; iTBS+γtACS vs. sham-iTBS+sham-tACS: 42.9±21.5 % vs. 33.8±19 %; p=0.048 Bonferroni corrected) (Fig. S4, supplementary information).”

“We considered a correct association when a subject was able to recall all the information for each item (i.e. face, name and occupation), resulting in a total of 36 items to learn and associate. To further investigate the effect on FNAT we also computed a partial recall score accounting for those items where subjects correctly matched only names with faces (FNAT NAME) and only occupations with faces (FNAT OCCUPATION). See supplementary information for score details.”

We also moved the data regarding the specific contribution of name and occupation recall in the supplementary information (fig.S4) and further specified how we computed the score in the score (lines 102-104).

“The score was computed by deriving an accuracy percentage index dividing by 12 and multiplying by 100 the correct association sum. The partial recall scores were computed in the same way only considering the sum of face-name (NAME) and face-occupation (OCCUPATION) correctly recollected.”

Reviewer #3 (Public review):

Summary:

Borghi and colleagues present results from 4 experiments aimed at investigating the effects of dual γtACS and iTBS stimulation of the precuneus on behavioral and neural markers of memory formation. In their first experiment (n = 20), they found that a 3-minute offline (i.e., prior to task completion) stimulation that combines both techniques leads to superior memory recall performance in an associative memory task immediately after learning associations between pictures of faces, names, and occupation, as well as after a 15-minute delay, compared to iTBS alone (+ tACS sham) or no stimulation (sham for both iTBS and tACS). Performance in a second task probing short-term memory was unaffected by the stimulation condition. In a second experiment (n = 10), they show that these effects persist over 24 hours and up to a full week after initial stimulation. A third (n = 14) and fourth (n = 16) experiment were conducted to investigate the neural effects of the stimulation protocol. The authors report that, once again, only combined iTBS and γtACS increase gamma oscillatory activity and neural excitability (as measured by concurrent TMS-EEG) specific to the stimulated area at the precuneus compared to a control region, as well as precuneus-hippocampus functional connectivity (measured by resting-state MRI), which seemed to be associated with structural white matter integrity of the bilateral middle longitudinal fasciculus (measured by DTI).

Strengths:

Combining non-invasive brain stimulation techniques is a novel, potentially very powerful method to maximize the effects of these kinds of interventions that are usually well-tolerated and thus accepted by patients and healthy participants. It is also very impressive that the stimulation-induced improvements in memory performance resulted from a short (3 min) intervention protocol. If the effects reported here turn out to be as clinically meaningful and generalizable across populations as implied, this approach could represent a promising avenue for the treatment of impaired memory functions in many conditions.

Methodologically, this study is expertly done! I don't see any serious issues with the technical setup in any of the experiments (with the only caveat that I am not an expert in fMRI functional connectivity measures and DTI). It is also very commendable that the authors conceptually replicated the behavioral effects of experiment 1 in experiment 2 and then conducted two additional experiments to probe the neural mechanisms associated with these effects. This certainly increases the value of the study and the confidence in the results considerably.

The authors used a within-subject approach in their experiments, which increases statistical power and allows for stronger inferences about the tested effects. They are also used to individualize stimulation locations and intensities, which should further optimize the signal-to-noise ratio.

Weaknesses:

I want to state clearly that I think the strengths of this study far outweigh the concerns I have. I still list some points that I think should be clarified by the authors or taken into account by readers when interpreting the presented findings.

I think one of the major weaknesses of this study is the overall low sample size in all of the experiments (between n = 10 and n = 20). This is, as I mentioned when discussing the strengths of the study, partly mitigated by the within-subject design and individualized stimulation parameters. The authors mention that they performed a power analysis but this analysis seemed to be based on electrophysiological readouts similar to those obtained in experiment 3. It is thus unclear whether the other experiments were sufficiently powered to reliably detect the behavioral effects of interest. That being said, the authors do report significant effects, so they were per definition powered to find those. However, the effect sizes reported for their main findings are all relatively large and it is known that significant findings from small samples may represent inflated effect sizes, which may hamper the generalizability of the current results. Ideally, the authors would replicate their main findings in a larger sample. Alternatively, I think running a sensitivity analysis to estimate the smallest effect the authors could have detected with a power of 80% could be very informative for readers to contextualize the findings. At the very least, however, I think it would be necessary to address this point as a potential limitation in the discussion of the paper.

Thank you for the observation. As you mentioned, our power analysis was based on our previous study investigating the same neuromodulation protocol with a corresponding experimental design. The relatively small sample could be considered a possible limitation of the study which we will add to the discussion. A fundamental future step will be to replay these results on a larger population, however, to strengthen our results we performed the sensitivity analysis you suggested.

In detail, we performed a sensitivity analysis for repeated-measures ANOVA with α=0.05 and power(1-β)=0.80 with no sphericity correction. For experiment 1, a sensitivity analysis with 1 group and 3 measurements showed a minimal detectable effect size of f=0.524 with 20 participants. In our paper, the ANOVA on total FNAT immediate performance revealed an effect size of η²=0.274 corresponding to f=0.614; the ANOVA on FNAT delayed performance revealed an effect size of η²=0.236 corresponding to f=0.556. For experiment 2, a sensitivity analysis for total FNAT immediate performance (1 group and 3 measurements) showed a minimal detectable effect size of f=0.797 with 10 participants. In our paper, the ANOVA on total FNAT immediate performance revealed an effect size of η²=0.448 corresponding to f=0.901. The sensitivity analysis for total FNAT delayed performance (1 group and 6 measurements) showed a minimal detectable effect size of f=0.378 with 10 participants. In our paper, the ANOVA on total FNAT delayed performance revealed an effect size of η²=0.484 corresponding to f=0.968. Thus, the sensitivity analysis showed that both experiments were powered enough to detect the minimum effect size computed in the power analysis. We have now added this information to the manuscript and we thank the reviewer for her/his suggestion in the statistical analysis and results section (lines 99-100; 127-128; 130-131; 543-545).

“The sensitivity analysis showed a minimal detectable effect size of  η²=0.215 with 20 participants.”

“The sensitivity analysis showed a minimal detectable effect size of  η²=0.388 with 10 participants.”

“The sensitivity analysis showed a minimal detectable effect size of η²=0.125 with 10 participants.”

“Since we do not have an a priori effect size for experiment 1 and 2, we performed a sensitivity power analysis to ensure that these experiments were able to detect the minimum effect size with 80% power and alpha level of 0.05.”

It seems that the statistical analysis approach differed slightly between studies. In experiment 1, the authors followed up significant effects of their ANOVAs by Bonferroni-adjusted post-hoc tests whereas it seems that in experiment 2, those post-hoc tests where "exploratory", which may suggest those were uncorrected. In experiment 3, the authors use one-tailed t-tests to follow up their ANOVAs. Given some of the reported p-values, these choices suggest that some of the comparisons might have failed to reach significance if properly corrected. This is not a critical issue per se, as the important test in all these cases is the initial ANOVA but non-significant (corrected) post-hoc tests might be another indicator of an underpowered experiment. My assumptions here might be wrong, but even then, I would ask the authors to be more transparent about the reasons for their choices or provide additional justification. Finally, the authors sometimes report exact p-values whereas other times they simply say p < .05. I would ask them to be consistent and recommend using exact p-values for every result where p >= .001.

Thank you again for the suggestions. Your observations are correct, we used a slightly different statistical depending on our hypothesis. Here are the details:

In experiment 1, we used a repeated-measure ANOVA with one factor “stimulation condition” (iTBS+γtACS; iTBS+sham-tACS; sham-iTBS+sham-tACS). Following the significant effect of this factor we performed post-hoc analysis with Bonferroni correction.

In experiment 2, we used a repeated-measures with two factors “stimulation condition” and “time”. As expected, we observed a significant effect of condition, confirming the result of experiment 1, but not of time. Thus, this means that the neuromodulatory effect was present regardless of the time point. However, to explore whether the effects of stimulation condition were present in each time point we performed some explorative t-tests with no correction for multiple comparisons since this was just an explorative analysis.

In experiment 3, we used the same approach as experiment 1. However, since we had a specific hypothesis on the direction of the effect already observed in our previous study, i.e. increase in spectral power (Maiella et al., Scientific Report 2022), our tests were 1-tailed.

For the p-values, we corrected the manuscript reporting the exact values for every result.

While the authors went to great lengths trying to probe the neural changes likely associated with the memory improvement after stimulation, it is impossible from their data to causally relate the findings from experiments 3 and 4 to the behavioral effects in experiments 1 and 2. This is acknowledged by the authors and there are good methodological reasons for why TMS-EEG and fMRI had to be collected in sperate experiments, but it is still worth pointing out to readers that this limits inferences about how exactly dual iTBS and γtACS of the precuneus modulate learning and memory.

Thank you for your comment. We fully agree with your observation, which is why this aspect has been considered in the study's limitations. To address your concern, we add this sentence to the limitation discussion (lines 299-301).

“Consequently, these findings do not allow precise inferences regarding the specific mechanisms by which dual iTBS and γtACS of the precuneus modulate learning and memory.”

There were no stimulation-related performance differences in the short-term memory task used in experiments 1 and 2. The authors argue that this demonstrates that the intervention specifically targeted long-term associative memory formation. While this is certainly possible, the STM task was a spatial memory task, whereas the LTM task relied (primarily) on verbal material. It is thus also possible that the stimulation effects were specific to a stimulus domain instead of memory type. In other words, could it be possible that the stimulation might have affected STM performance if the task taxed verbal STM instead? This is of course impossible to know without an additional experiment, but the authors could mention this possibility when discussing their findings regarding the lack of change in the STM task.

Thank you for your interesting observation. We argue that the intervention primarily targeted long-term associative memory formation, as our findings demonstrated effects only on FNAT. However, as you correctly pointed out, we cannot exclude the possibility that the stimulation may also influence short-term verbal associative memory. We add this aspect when discussing the absence of significant findings in the STM task (lines 205-210).

“Visual short-term associative memory, measured by STBM performance, was not modulated by any experimental condition. Even if we cannot exclude the possibility that the stimulation could have influenced short-term verbal associative memory, we expected this result since short-term associative memory is known to rely on a distinct frontoparietal network while FNAT, used to investigate long-term associative memory, has already been associated with the neural activity of the PC and the hippocampus (Parra et al., 2014; Rentz et al., 2011).”

While the authors discuss the potential neural mechanisms by which the combined stimulation conditions might have helped memory formation, the psychological processes are somewhat neglected. For example, do the authors think the stimulation primarily improves the encoding of new information or does it also improve consolidation processes? Interestingly, the beneficial effect of dual iTBS and γtACS on recall performance was very stable across all time points tested in experiments 1 and 2, as was the performance in the other conditions. Do the authors have any explanation as to why there seems to be no further forgetting of information over time in either condition when even at immediate recall, accuracy is below 50%? Further, participants started learning the associations of the FNAT immediately after the stimulation protocol was administered. What would happen if learning started with a delay? In other words, do the authors think there is an ideal time window post-stimulation in which memory formation is enhanced? If so, this might limit the usability of this procedure in real-life applications.

Thank you for your comment and for raising these important points.

We hypothesized that co-stimulation would enhance encoding processes. Previous studies have shown that co-stimulation can enhance gamma-band oscillations and increase cortical plasticity (Guerra et al., Brain Stimulation 2018; Maiella et al., Scientific Reports 2022). Given that the precuneus (Brodt et al., Science 2018; Schott et al., Human Brain Mapping 2018), gamma oscillations (Osipova et al., Journal of Neuroscience 2006; Deprés et al., Neurobiology of Aging 2017; Griffiths et al., Trends in Neurosciences 2023), and cortical plasticity (Brodt et al., Science 2018) have all been associated with encoding processes, we decided to apply co-stimulation before the encoding phase, to boost it. We enlarged the introduction to specify the link between neural mechanisms and the psychological process of the encoding (lines 55-60).

“In particular, the induction of gamma oscillatory activity has been proposed to play an important role in a type of LTP known as spike timing-dependent plasticity, which depends on a precise temporal delay between the firing of a presynaptic and a postsynaptic neuron (Griffiths and Jensen, 2023). Both LTP and gamma oscillations have a strong link with memory processes such as encoding (Bliss and Collingridge, 1993; Griffiths and Jensen, 2023; Rossi et al., 2001), pointing to rTMS and tACS as good candidates for memory enhancement.”

We applied the co-stimulation immediately before the learning phase to maximize its potential effects. While we observed a significant increase in gamma oscillatory activity lasting up to 20 minutes, we cannot determine whether the behavioral effects we observed would have been the same with a co-stimulation applied 20 minutes before learning. Based on existing literature, a reduction in the efficacy of co-stimulation over time could be expected (Huang et al., Neuron 2005; Thut et al., Brain Topography 2009). However, we hypothesize that multiple stimulation sessions might provide an additional boost, helping to sustain the effects over time (Thut et al., Brain Topography 2009; Koch et al., Neuroimage 2018; Koch et al., Brain 2022).

Regarding the absence of further forgetting in both stimulation conditions, we think that the clinical and demographical characteristics of the sample (i.e. young and healthy subjects) explain the almost absence of forgetting after one week.

Reviewer #1 (Recommendations for the authors):

To address the concerns, the authors should:

(1) Include invasive neuronal recordings (e.g., in rats or monkeys if not possible in humans) demonstrating that the current stimulation protocol leads to direct changes in brain activity.

We understand the interest of the first reviewer in the understanding of neurophysiological correlates of the stimulation protocol, however, we are skeptical about this request as we think it goes beyond the aims of the study. As already mentioned in the response to the reviewer, invasive neurophysiological recordings in humans for this type of study are not feasible due to ethical constraints. At the same time, studies on cadavers or rodents would not fully resolve the question. Indeed, the authors of the study cited by the reviewer (Mihály Vöröslakos et al., Nature Communications, 2018) highlight the impossibility of drawing definitive conclusions about the exact voltage required in the in-vivo human brain due to significant differences between rats and humans, as well as the in-vivo human cadavers due to alterations in electrical conductivity that occur in postmortem tissue. Huang and colleagues addressed the difficulties in reaching direct evidence of non-invasive brain stimulation (NIBS) effects in a review published in Clinical Neurophysiology in 2017. They conclude that the use of EEG to assess brain response to TMS has a great potential for a less indirect demonstration of plasticity mechanisms induced by NIBS in humans.

It is exactly to meet the need to investigate the changes in brain activity after the stimulation protocol that we conducted Experiments 3 and 4. These experiments respectively examined the neurophysiological and connectivity changes induced by the stimulation in a non-invasive manner using TMS-EEG and fMRI. The observed changes in brain oscillatory activity (increased gamma oscillatory activity), cortical excitability (enhanced posteromedial parietal cortex reactivity), and brain connectivity (strengthened connections between the precuneus and hippocampi) provided evidence of the effects of our non-invasive brain stimulation protocol, further supporting the behavioral data.

Additionally, we carefully considered the issue of stimulation distribution and, in response, performed a biophysical modeling analysis and E-field calculation using the parameters employed in our study (see Supplementary Materials).

Acknowledging the reviewer's point of view, we modified the manuscript accordingly, discussing this aspect both as a technical limitation and as a potential direction for future research (main text, lines 280-289).

“Although we studied TMS and tACS propagation through the E-field modeling and observed an increase in the precuneus gamma oscillatory activity, excitability and connectivity with the hippocampi, we cannot exclude that our results might reflect the consequences of stimulating more superficial parietal regions other than the precuneus nor report direct evidence of microscopic changes in the brain after the stimulation. Invasive neurophysiological recordings in humans for this type of study are not feasible due to ethical constraints. Studies on cadavers or rodents would not fully resolve our question due to significant differences between them (i.e. rodents do not have an anatomical correspondence while cadavers have an alterations in electrical conductivity occurring in postmortem tissue). However, further exploration of this aspect in future studies would help in the understanding of γtACS+iTBS effects.”

(2) Address all the technical questions about the experimental design.

We addressed all the technical questions about the experimental design.

(3) Repeat the experiments with randomized trial order and without a block design.

The experiments were conducted with randomized trial order and we did not use a block design.

(4) Add many more faces to the study. It is extremely difficult to draw any conclusion from merely 12 faces. Ideally, there would be lots of other relevant memory experiments where the authors show compelling positive results.

We understand your perplexity about drawing conclusions from 12 faces, however, this is not the case. As we explained in the response reviewer, the task we implemented did not rely on the recall of merely 12 faces. Instead, participants had to correctly learn, associate and recall 12 faces, 12 names and 12 occupations for a total of 36 items. To improve the clarity of the manuscript, we added a paragraph to make this aspect more explicit (lines 425-430).

“We considered a correct association when a subject was able to recall all the information for each item (i.e. face, name and occupation), resulting in a total of 36 items to learn and associate. To further investigate the effect on FNAT we also computed a partial recall score accounting for those items where subjects correctly matched only names with faces (FNAT NAME) and only occupations with faces (FNAT OCCUPATION). See supplementary information for score details.”

The behavioral changes we observed are similar to those who are typically observed after multiple stimulation sessions (Koch et al., NeuroImage, 2018; Grover et al., Nature Neuroscience, 2022, Benussi et al., Annals of Neurology, 2022). Moreover, memory performance changes are often measured by a limited set of stimuli due to methodological constraints related to memory capacity. For example, Rey Auditory Verbal learning task, requiring to learn and recall 15 words, is a typical test used to detect memory changes (Koch et al., Neuroimage, 2018; Benussi et al., Brain stimulation 2021; Benussi et al., Annals of Neurology, 2022). 

(5) Provide a clear explanation of the apparent randomness of which results are statistically significant or not in Figure 3. But perhaps with many more experiments, a lot more memory evaluations, many more stimuli, and addressing all the other technical concerns, either the results will disappear or there will be a more interpretable pattern of results.

We provided explanations for all the concerns shown by the reviewer.

Reviewer #2 (Recommendations for the authors):

Minor comments:

(1) Figure 4: Why are connectivity values pre-stimulation for the iTBS and sham tACS stimulation condition so much higher than the dual stimulation? We would expect baseline values to be more similar.

We acknowledge that the pre-stimulation connectivity values for the iTBS and sham tACS conditions appear higher than those for the dual stimulation condition. However, as noted in our statistical analyses, there were no significant differences at baseline between conditions (p-FDR= 0.3514), suggesting that any apparent discrepancy is due to natural variability rather than systematic bias. One potential explanation for these differences is individual variability in baseline connectivity measures, which can fluctuate due to factors such as intrinsic neural dynamics, participant state, or measurement noise. Despite these variations, our statistical approach ensures that any observed post-stimulation effects are not confounded by pre-existing differences.

(2) Figure 2: How are total association scores significantly different between stimulation conditions, but individual name and occupation associations are not? Further clarification of how the total FNAT score is calculated would be helpful.

We apologize for any lack of clarity. The total FNAT score reflects the ability to correctly recall all the information associated with a person—specifically, the correct pairing of the face, name, and occupation. Participants received one point for each triplet they accurately recalled. The scores were then converted into percentages, as detailed in the Face-Name Associative Task Construction and Scoring section in the supplementary materials.

Total FNAT was the primary outcome measure. However, we also analyzed name and occupation recall separately to better understand their partial contributions. Our analysis revealed that the improvement in total FNAT was primarily driven by an increase in name recall rather than occupation recall.

We acknowledge that this distinction may have caused some confusion. To improve clarity, we revised the manuscript accordingly (lines 97-98; 107-111; 425-430).

“Dual iTBS+γtACS increased the performances in recalling the association between face, name and occupation (FNAT accuracy) both for the immediate (F_2,38=7.18; p=0.002; η²_p=0.274) and the delayed (F_2,38=5.86; p =0.006; η²_p=0.236) recall performances (Fig. 2, panel A).”

“The in-depth analysis of the FNAT accuracy investigating the specific contribution of face-name and face-occupation recall revealed that dual iTBS+γtACS increased the performances in the association between face and name (FNAT NAME) delayed recall (F_2,38 =3.46; p =0.042; η²p =0.154; iTBS+γtACS vs. sham-iTBS+sham-tACS: 42.9±21.5 % vs. 33.8±19 %; p=0.048 Bonferroni corrected) (Fig. S4, supplementary information).”

“We considered a correct association when a subject was able to recall all the information for each item (i.e. face, name and occupation), resulting in a total of 36 items to learn and associate. To further investigate the effect on FNAT we also computed a partial recall score accounting for those items where subjects correctly matched only names with faces (FNAT NAME) and only occupations with faces (FNAT OCCUPATION). See supplementary information for score details.”

We also moved the data regarding the specific contribution of name and occupation recall in the supplementary information (fig.S4) and further specified how we computed the score in the score (lines 102-104).

“The score was computed by deriving an accuracy percentage index dividing by 12 and multiplying by 100 the correct association sum. The partial recall scores were computed in the same way only considering the sum of face-name (NAME) and face-occupation (OCCUPATION) correctly recollected.”

Reviewer #3 (Recommendations for the authors):

A very small detail, in the caption for Figure 2A, OCCUPATION is described as being shown on the 'left' but it should be 'right'.

We corrected this error.

Author response:

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

Reviewer #1 (Public Review):

(1) Figure 1: It might be simpler to streamline  acronyms for different test cases, e.g,  E01contra, E01 ipsi (rather than EO1IPS), E02, and control. Thus, it would be possible to label  each of the three schematic panels as E01, E02, control.

Please describe what the dots in the brain mean and move the V1 label so it does not occlude  dots.

Please make clear that the "track reconstructions" are the bright spheres in the micrographs (there are track-like elements in some micrographs which may be tears or?)

Thank you. We relabeled the groups as control, EO1contra, EO1ipsi, and EO2. These were  changed in all figures and in the document at several places.

We indicated in the new caption that “Dots schematize ocular dominance columns”.

We indicated that electrode track penetrations were the “(bright spots at right/posterior)”.

(2) Figure 2: Should "horizontal" be vertical (line  556) of the caption? When describing the  scale bar for firing rate, please explain the meaning of italicized vs regular font.

Please make the purple lines in Figures I and J easier to see (invisible in my PDF).

Not quite clear what is significantly different from what when viewing the figure at a glance.  Would it be possible to clarify using standard methods?

Yes, it should say vertical, thank you. We explained the italics (they denote the standard scale  bar size if no number is provided.)

We changed the purple lines to yellow in all figures.

We added comparison bars that help indicate significance.

(3) Figures 3-5. Please make corrections like those  noted above.

Yes, we applied the previous changes to Figures 3 - 5.

(4) Minor. Sometimes the authors spell out temporal  frequency and sometimes abbreviate it.  Perhaps adopt a consistent style.

Fixed, thanks.

Reviewer #2 (Public Review):

(1) The assessment of the tuning properties is  based on fits to the data. Presumably,  neurons for which the fits were poor were excluded? It would be useful to know what the criteria  were, how many neurons were excluded, and whether there was a significant difference  between the groups in the numbers of neurons excluded (which could further point to  differences between the groups).

Yes, this is an important omission, thank you for catching it. We now write in methods (line 213):  “ Inclusion/exclusion: For each stimulus type, we examined  the set of all responses to visual  stimuli and blanks with an ANOVA test to evaluate the null hypothesis that the mean response  to all of these stimuli were the same; cells with a p<0.05 to this visual responsiveness test were  included in fits and analyses, and cells with p>0.05 were excluded. ”

(2) For the temporal frequency data, low- and high-frequency  cut-offs are defined, but then  only used for the computation of the bandwidth. Given that the responses to low temporal  frequencies change profoundly with premature eye opening, it would be useful to directly  compare the low- and high-frequency cut-offs between groups, in addition to the index that is  currently used.

We now provide this data in Figure 3 - figure supplement  1 .

(3) In addition to the tuning functions and firing  rates that have been analyzed so far, are  there any differences in the temporal profiles of neural responses between the groups  (sustained versus transient responses, rates of adaptation, latency)? If the temporal dynamics  of the responses are altered significantly, that could be part of an explanation for the altered  temporal tuning.

This is a great topic for future studies. Unfortunately, with drifting gratings, it is difficult to  establish these properties, which could be better assessed with standing or  square-wave-modulated gratings or other stimuli. We did not run standing gratings in our battery  of stimuli for this initial study.

(4) It would be beneficial for the general interpretation  of the results to extend the discussion. First, it would be useful to provide a more detailed discussion of what type of visual information might make it through the closed eyelids (the natural state), in contrast to the structured  information available through open eyes. Second, it would be useful to highlight more clearly  that these data were collected in peripheral V1 by discussing what might be expected in  binocular, more central V1 regions. Third, it would be interesting to discuss the observed  changes in firing rates in the context of the development of inhibitory neurons in V1 (which still  undergo significant changes through the time period of premature visual experience chosen  here).

Thank you, good ideas. Let’s take these three suggestions in turn.

First, in the discussion, we added a subsection “ Biology  of early development in mustelids ” that  focuses on the developmental conditions of wild and laboratory animals:

In the wild, mustelids raise their young in nests in the ground, in cavities such as holes in trees  or caves, or in areas of dense vegetation (Ruggiero et al. 1994). They may move the young  from one nest to another as they grow, but otherwise the young are primarily in the relatively  dark nest. It is highly likely that some light penetrates and that information about the 24-hour  cycle is available, but the light is likely to be dim and unlikely to provide a basis for high  luminance, high contrast stimulation through the closed lids. The animals begin to spend  substantial time outside the nest after eye opening.

The ferret is a domesticated strain of the European polecat. In laboratory settings, ferret  jills give birth and keep their kits in a nest box. A laboratory typically maintains a 24-hour cycle  with 12 or 14 hours of light, and the light reaching the closed lids must first pass through the  cage, the nest box, and the nesting material. Therefore, developing ferrets have an obvious  circadian light signal but the light available for image formation is likely dim and of low contrast.

Although the light that reaches the close lids in developing ferrets is likely to be relatively  dim, and any image-forming signal passing through the closed lids would be highly filtered in  luminance, spatial frequency, and contrast, it is important to remember that visual input before  natural eye opening (through the closed lids) can drive activity in retina, LGN, and cortex  (Huttenlocher 1967, Chapman and Stryker 1993, Krug et al., 2001, Akerman et al., 2002,Akerman et al., 2004). Further, orientation selectivity can be observed through the closed lids  (Krug et al., 2001), indicating that some coarse image-forming information does make it through  the closed lids.

Second, we added text speculating about binocular cortex (lines 492 - 500): … our recordings  were performed in monocular cortex so that we could be sure of the developmental condition of  the eye that drove the classic responses. It is interesting to speculate about what might occur  more centrally in binocular visual cortex. Ocular dominance shifts are not induced when one eye  is opened prematurely (Issa et al 1999), indicating that ocular dominance plasticity is not  engaged at this early stage, but one might imagine that the impacts on temporal frequency and  spontaneous firing rates would still be present.

Third, on inhibition, we added a paragraph (lines 502 - 509):

We introduced premature patterned vision at a time when cortical inhibition is undergoing  substantial changes. GABAergic signaling has already undergone its switch (Ben-Ari, 2002)  from providing primarily depolarizing input to hyperpolarizing input by P21-23 (Mulholland et al.,  2021). In the days prior to eye opening, inhibitory cells exhibit activity that is closely associated  with the emerging functional modules that will reflect orientation columns (Mulholland et al.,  2021), but do not yet exhibit selectivity to orientation, in contrast to excitatory neurons, which do  exhibit selectivity to orientation at that time (Chang and Fitzpatrick, 2022).

(5) In the methods section, the statement 'actively  kept in nesting box' is unclear. Presumably  this means that the jill prevents the kits from leaving the nesting box? It also would be worth at  least mentioning in this context that there obviously are still visual events in the nesting box too.

Thanks. We improved this description (lines 118 - 121):  Ferret kits in laboratory housing receive  limited visual stimulation through their closed lids, as the mother actively keeps the kits in their  relatively dark nest . In order to ensure that animals  with early-opened eyes actually had  patterned visual experience  (and animals with closed  lids had the same stimulation filtered  through the lids) , animals were brought to the lab  for 2 hours a day for 4 consecutive days  beginning at P25.

(6) The stimulus presentation could be more clearly  described. Is every stimulus presented in  an individual trial (surrounded by periods with a blank screen), or are all stimuli shown as a  continuous sequence? The description of the parameter screening is also potentially confusing  ('orientation was co-varied with stimuli consisting of drifting gratings at different spatial  frequencies' sounds as if there are separate stimuli for orientation; might be better to say  something like 'in the first set, orientation, spatial frequency, ... were covaried...')

Yes, thank you, we fixed this (lines 184 - 201). We deleted the text indicated and added a  sentence “Each individual grating stimulus was full screen and had a single set of parameters  (direction, spatial frequency, temporal frequency), and was separated from the other stimuli by a  gray screen interstimulus interval.”. We also deleted a repetition of 100% contrast in the  description of the second set.

(7) Description of low-pass index is unclear. What  is the 'largest temporal frequency response  observed'? The maximum response or the response to the largest temporal frequency tested?

Thanks. We added a paragraph at line 236:

We defined a low pass index as the response to the lowest temporal frequency tested (in this case 0.5 Hz) to the maximum response obtained to the set of temporal frequencies shown. LPI =  R(TF=0.5 Hz)/max(R(TF=0.5Hz), R(TF=1Hz), … R(TF=32Hz)).  If a cell exhibited the highest  firing for a temporal frequency of 0.5 Hz, then it would have an low pass index of 1. If it  exhibited a similar firing rate in response to a temporal frequency of 0.5 Hz even if the preferred  temporal frequency were higher, then the low pass index would still be near 1. If the cell  responded poorly at a temporal frequency of 0.5 Hz, then it would have a low pass index near 0.

(8) The discussion should also cite the results  of strobe-reared cats by Pasternak et al (1981  and 1985).

Thank you for pointing out the omission. We now write (lines 430-435):  Cats raised in a  strobe-light environment (mostly after eye opening) exhibited strong changes in subsequent  direction selectivity (Kennedy and Orban 1983; Humphrey and Saul 1998)  and behavioral  sensitivity to motion (Pasternak et al., 1981; Pasternak et al., 1985) that partially recovers with  motion detection training . However, temporal frequency  tuning of these animals has not been  reported in detail.  Pasternak et al (1981) reported  that strobe-reared ferrets exhibited greater  difficulty in distinguishing slow moving stimuli from static stimuli compared to controls, an  ability that slightly improved with practice, suggesting possible temporal frequency deficits.

(9) Finally, it would be useful to include a mention  of the early development of MT in  marmosets in the discussion of impacts of prematurity on motion vision (Bourne & Rosa 2006).

Yes, thank you. We cited Bourne & Rosa and also Lempel and Nielsen (for ferret PSS). (Lines  492-501):

Several other basic mechanistic questions remain unanswered. It is unclear where in the visual  circuit cascade these deficits first arise. Does the lateral geniculate nucleus or retina exhibit  altered temporal frequency tuning? Is the influence of the patterned visual stimulation  instructive, so that if one provided premature stimulation with only certain temporal frequencies,  one would see selectivity for those temporal frequencies, or would tuning always be broad?  Other questions remain concerning the top-down influence on V1 from “higher” motion areas  such as MT (monkeys) or PSS (ferret); MT exhibits mature neural markers earlier than V1  (Bourne and Rosa, 2006), and suppression of PSS impacts motion selectivity in V1 (Lempel and  Nielsen, 2021).  Future studies will be needed to  address these questions.

eLife Assessment

This carefully conducted study aims to understand how the early visual experience of premature infants induces lasting deficits, including compromised motion processing. The authors address this important question in a ferret animal model, exposing the developing visual system prematurely to patterned visual input by opening one or both eyes at a time when both retinal waves and light traveling through closed lids can drive sensory responses. Convincing evidence is presented, suggesting that eye opening at this time impacts temporal frequency tuning and elevates spontaneous firing rates. These findings will have great relevance for neuroscientists studying visual system development, particularly in the context of premature birth.

Reviewer #1 (Public review):

The authors note that very premature infants experience the visual world early and, as a consequence, sustain lasting deficits including compromised motion processing. Here they investigate the effects of early eye opening in ferret, choosing a time point after birth when both retinal waves and light traveling through closed lids drive sensory responses. The laboratory has long experience in quantitative studies of visual response properties across development and this study reflects their expertise.

The investigators find little or no difference in mean orientation and direction selectivity, or in spatial frequency tuning, as a result of early eye opening but marked differences in temporal frequency tuning. These changes are especially interesting as they relate to deficits seen in prematurely delivered children. Temporal frequency bandwidth for responses evoked from early-opened contralateral eyes were broader than for controls; this is the case for animals in which either one or both eyes were opened prematurely. Further, when only one eye was opened early, responses to low temporal frequencies were relatively stronger.

The investigators also found changes in firing rate and sign of response to visual stimuli. Premature eye-opening increased spontaneous rates in all test configurations. When only one eye was opened early, firing rates recorded from the ipsilateral cortex were strongly suppressed, with more modest effects in other test cases.

As the authors' discussion notes, these observations are just a starting point for studies underlying mechanism. The experiments are so difficult to perform and so carefully described that the results will be foundational for future studies of how premature birth influences cortical development.

Reviewer #2 (Public review):

In this paper, Griswold and Van Hooser investigate what happens if animals are exposed to patterned visual experience too early, before its natural onset. To this end, they make use of the benefits of the ferret as a well-established animal model for visual development. Ferrets naturally open their eyes around postnatal day 30; here, Griswold and Van Hooser opened either one or both eyes prematurely. Subsequent recordings in the mature primary visual cortex show that while some tuning properties like orientation and direction selectivity developed normally, the premature visual exposure triggered changes in temporal frequency tuning and overall firing rates. These changes were widespread, in that they occurred even for neurons responding to the eye that was not opened prematurely. These results demonstrate that the nature of the visual input well before eye opening can have profound consequences on the developing visual system.

The conclusions of this paper are well supported by the data, but in the initially submitted version of the paper, there were a few questions regarding the data processing and suggestions for the discussion:

(1) The assessment of the tuning properties is based on fits to the data. Presumably, neurons for which the fits were poor were excluded? It would be useful to know what the criteria were, how many neurons were excluded, and whether there was a significant difference between the groups in the numbers of neurons excluded (which could further point to differences between the groups).

(2) For the temporal frequency data, low- and high-frequency cut-offs are defined, but then only used for the computation of the bandwidth. Given that the responses to low temporal frequencies change profoundly with premature eye opening, it would be useful to directly compare the low- and high-frequency cut-offs between groups, in addition to the index that is currently used.

(3) In addition to the tuning functions and firing rates that have been analyzed so far, are there any differences in the temporal profiles of neural responses between the groups (sustained versus transient responses, rates of adaptation, latency)? If the temporal dynamics of the responses are altered significantly, that could be part of an explanation for the altered temporal tuning.

(4) It would be beneficial for the general interpretation of the results to extend the discussion. First, it would be useful to provide a more detailed discussion of what type of visual information might make it through the closed eyelids (the natural state), in contrast to the structured information available through open eyes. Second, it would be useful to highlight more clearly that these data were collected in peripheral V1 by discussing what might be expected in binocular, more central V1 regions. Third, it would be interesting to discuss the observed changes in firing rates in the context of the development of inhibitory neurons in V1 (which still undergo significant changes through the time period of premature visual experience chosen here).

eLife Assessment

In this valuable study, the authors show the physiological response and molecular pathway mediating the effect of quinofumelin, a developed fungicide with an unknown mechanism. The authors present convincing data suggesting the involvement of the uridine/uracil biosynthesis pathway, by combining in vivo microbiology characterization as well as in vitro biochemical binding results.

Reviewer #2 (Public review):

Summary:

In the current study, the authors aim to identify the mode of action/molecular mechanism of characterized a fungicide, quinofumelin, and its biological impact on transcriptomics and metabolomics in Fusarium graminearum and other Fusarium species. Two sets of data were generated between quinofumelin and no treatment group, and differentially abundant transcripts and metabolites were identified, suggesting a potential role of pyrimidine biosynthesis. Upon studying the genetic mutants of the uridine/uracil biosynthesis pathway with quinofumelin treatment and metabolite supplementation, combining in vitro biochemical assay of quinofumelin and F.graminearum dihydroorotate dehydrogenase protein, the authors identified that quinofumelin inhibits the dihydroorotate dehydrogenase and blocks downstream metabolite biosynthesis, limiting fungal metabolism and growth.

Strengths:

Omics datasets were leveraged to understand the physiological impact of quinofumelin, showing the intracellular impact of the fungicide. The characterization of FgDHODHII deletion strains with supplemented metabolites clearly showed the impact of the enzyme on fungal growth. Corroborating in vitro and in vivo data revealed the direct interaction of quinofumelin with Fusarium protein target.

Potential Impact:

Understanding this new mechanism could facilitate rational design or screen for molecules targeting the same pathway, or improve binding affinity and inhibitor potency. Confirming the target of quinofumelin may also help understand its resistance mechanism, and further development of other inhibitory molecules against the target.

Reviewer #3 (Public review):

Summary:

The manuscript shows the mechanism of action of quinofumelin, a novel fungicide, against the fungus Fusarium graminearum. Through omics analysis, phenotypic analysis and in silico approaches, the role of quinofumelin in targeting DHODH is uncovered.

Strengths:

The phenotypic analysis and mutant generation are nice data and add to the role of metabolites in bypassing pyrimidine biosynthesis.

Weaknesses:

The role of DHODH in this class of fungicides has been known and this data does not add any further significance to the field.

Author response:

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

Reviewer #1 (Public review):

Summary:

Phytophathogens including fungal pathogens such as F. graminearum remain a major threat to agriculture and food security. Several agriculturally relevant fungicides including the potent Quinofumelin have been discovered to date, yet the mechanisms of their action and specific targets within the cell remain unclear. This paper sets out to contribute to addressing these outstanding questions.

We appreciate the reviewer's accurate summary of our manuscript.

Strengths:

The paper is generally well-written and provides convincing data to support their claims for the impact of Quinofumelin on fungal growth, the target of the drug, and the potential mechanism. Critically the authors identify an important pyrimidine pathway dihydroorotate dehydrogenase (DHODH) gene FgDHODHII in the pathway or mechanism of the drug from the prominent plant pathogen F. graminearum, confirming it as the target for Quinofumelin. The evidence is supported by transcriptomic, metabolomic as well as MST, SPR, molecular docking/structural biology analyses.

We appreciate the reviewer's recognition of the strengths of our manuscript.

Weaknesses:

Whilst the study adds to our knowledge about this drug, it is, however, worth stating that previous reports (although in different organisms) by Higashimura et al., 2022 https://pmc.ncbi.nlm.nih.gov/articles/PMC9716045/ had already identified DHODH as the target for Quinofumelin and hence this knowledge is not new and hence the authors may want to tone down the claim that they discovered this mechanism and also give sufficient credit to the previous authors work at the start of the write-up in the introduction section rather than in passing as they did with reference 25? other specific recommendations to improve the text are provided in the recommendations for authors section below.

We appreciate the reviewer's suggestion. In the revised manuscript, we have incorporated the reference in the introduction section and expanded the discussion of previous work on quinofumelin by Higashimura et al., 2022 in the discussion section to more effectively contextualize their contributions. Moreover, we have made revisions and provided responses in accordance with the recommendations.

Reviewer #2 (Public review):

Summary:

In the current study, the authors aim to identify the mode of action/molecular mechanism of characterized a fungicide, quinofumelin, and its biological impact on transcriptomics and metabolomics in Fusarium graminearum and other Fusarium species. Two sets of data were generated between quinofumelin and no treatment group, and differentially abundant transcripts and metabolites were identified. The authors further focused on uridine/uracil biosynthesis pathway, considering the significant up- and down-regulation observed in final metabolites and some of the genes in the pathways. Using a deletion mutant of one of the genes and in vitro biochemical assays, the authors concluded that quinofumelin binds to the dihydroorotate dehydrogenase.

We appreciate the reviewer's accurate summary of our manuscript.

Strengths:

Omics datasets were leveraged to understand the physiological impact of quinofumelin, showing the intracellular impact of the fungicide. The characterization of FgDHODHII deletion strains with supplemented metabolites clearly showed the impact of the enzyme on fungal growth.

We appreciate the reviewer's recognition of the strengths of our manuscript.

Weaknesses:

Some interpretation of results is not accurate and some experiments lack controls. The comparison between quinofumelin-treated deletion strains, in the presence of different metabolites didn't suggest the fungicide is FgDHODHII specific. A wild type is required in this experiment.

Potential Impact: Confirming the target of quinofumelin may help understand its resistance mehchanism, and further development of other inhibitory molecules against the target.

The manuscript would benefit more in explaining the study rationale if more background on previous characterization of this fungicide on Fusarium is given.

We appreciate the reviewer's suggestion. Under no treatment with quinofumelin, mycelial growth remains normal and does not require restoration. In the presence of quinofumelin treatment, the supplementation of downstream metabolites in the de novo pyrimidine biosynthesis pathway can restore mycelial growth that is inhibited by quinofumelin. The wild-type control group is illustrated in Figure 4. Figure 5b depicts the phenotypes of the deletion mutants. With respect to the relationship among quinofumelin, FgDHODHII, and other metabolites, quinofumelin specifically targets the key enzyme FgDHODHII in the de novo pyrimidine biosynthesis pathway, disrupting the conversion of dihydroorotate to orotate, which consequently inhibits the synthesis downstream metabolites including uracil. In our previous study, quinofumelin not only exhibited excellent antifungal activity against the mycelial growth and spore germination of F. graminearum, but also inhibited the biosynthesis of deoxynivalenol (DON). We have added this part to the introduction section.

Reviewer #3 (Public review):

Summary:

The manuscript shows the mechanism of action of quinofumelin, a novel fungicide, against the fungus Fusarium graminearum. Through omics analysis, phenotypic analysis, and in silico approaches, the role of quinofumelin in targeting DHODH is uncovered.

We appreciate the reviewer's accurate summary of our manuscript.

Strengths:

The phenotypic analysis and mutant generation are nice data and add to the role of metabolites in bypassing pyrimidine biosynthesis.

We appreciate the reviewer's recognition of the strengths of our manuscript.

Weaknesses:

The role of DHODH in this class of fungicides has been known and this data does not add any further significance to the field. The work of Higashimura et al is not appreciated well enough as they already showed the role of quinofumelin upon DHODH II.

There is no mention of the other fungicide within this class ipflufenoquin, as there is ample data on this molecule.

We appreciate the reviewer's suggestion. We sincerely appreciate the reviewer's insightful comment regarding the work of Higashimura et al. We agree that their investigation into the role of quinofumelin in DHODH II inhibition provides critical foundational insights for this field. In the revised manuscript, we have incorporated the reference in the introduction section and expanded the discussion of their work in the discussion section to more effectively contextualize their contributions. The information regarding action mechanism of ipflufenoquin against filamentous fungi was added in discussion section.

Reviewer #1 (Recommendations for the authors):

(1) Given that the DHODH gene had been identified as a target earlier, could the authors perform blast experiments with this gene instead and let us know the percentage similarity between the FgDHODHII gene and the Pyricularia oryzae class II DHODH gene in the report by Higashimura et al., 2022.

BLAST experiment revealed that the percentage similarity between the FgDHODHII gene and the class II DHODH gene of P. oryzae was 55.41%. We have added the description ‘Additionally, the amino acid sequence of the FgDHODHII exhibits 55.41% similarity to that of DHODHII from Pyricularia oryzae, as previously reported (Higashimura et al., 2022)’ in section Results.

(2) Abstract:

The authors started abbreviating new terms e.g. DEG, DMP, etc but then all of a sudden stopped and introduced UMP with no full meaning of the abbreviation. Please give the full meaning of all abbreviations in the text, UMP, STC, RM, etc.

We have provided the full meaning for all abbreviations as requested.

(3) Introduction section:

The introduction talks very little about the work of other groups on quinofumelin. Perhaps add this information in and reference them including the work of Higashimura et al., 2022 which has done quite significant work on this topic but is not even mentioned in the background

We have added the work of other groups on quinofumelin in section introduction.

(4) General statements:

Please show a model of the pyrimidine pathway that quinofumelin attacks to make it easier for the reader to understand the context. They could just copy this from KEGG

We have added the model (Fig. 7).

(5) Line 186:

The authors did a great job of demonstrating interactions with the Quinofumelin and went to lengths to perform MST, SPR, molecular docking, and structural biology analyses yet in the end provide no details about the specific amino acid residues involved in the interaction. I would suggest that site-directed mutagenesis studies be performed on FgDHODHII to identify specific amino acid residues that interact with Quinofumelin and show that their disruption weakens Quinofumelin interaction with FgDHODHII.

Thank you for this insightful suggestion. We fully agree with the importance of elucidating the interaction mechanism. At present, we are conducting site-directed mutagenesis studies based on interaction sites from docking results and the mutation sites of FgDHODHII from the resistant mutants; however, due to the limitations in the accuracy of existing predictive models, this work remains ongoing. Additionally, we are undertaking co-crystallization experiments of FgDHODHII with quinofumelin to directly and precisely reveal their interaction pattern

(6) Line 76:

What is the reference or evidence for the statement 'In addition, quinofumelin exhibits no cross-resistance to currently extensively used fungicides, indicating its unique action target against phytopathogenic fungi.

If two fungicides share the same mechanism of action, they will exhibit cross resistance. Previous studies have demonstrated that quinofumelin retains effective antifungal activity against fungal strains resistant to commercial fungicides, indicating that quinofumelin does not exhibit cross-resistance with other commercially available fungicides and possesses a novel mechanism of action. Additionally, we have added the relevant inference.

(7) Line 80-82:

Again, considering the work of previous authors, this target is not newly discovered. Please consider toning down this statement 'This newly discovered selective target for antimicrobial agents provides a valuable resource for the design and development of targeted pesticides.'

We have rewritten the description of this sentence.

(8) Line 138: If the authors have identified DHODH in experimental groups (I assume in F. graminearum), what was the exact locus tag or gene name in F. graminearum, and why not just continue with this gene you identified or what is the point of doing a blast again to find the gene if the DHODH gene if it already came up in your transcriptomic or metabolic studies? This unfortunately doesn't make sense but could be explained better.

The information of FgDHODHII (gene ID: FGSG_09678) has been added. We have revised this part.

Reviewer #2 (Recommendations for the authors):

(1) Line 40:

Please add a reference.

We have added the reference

(2) Line 47:

Please add a reference.

We have added the reference.

(3) Line 50:

The lack of target diversity in existing fungicides doesn't necessarily serve as a reason for discovering new targets being more challenging than identifying new fungicides within existing categories, please consider adjusting the argument here. Instead, the authors can consider reasons for the lack of new targets in the field.

We have revised the description.

(4) Line 63:

Please cite your source with the new technology.

We have added the reference.

(5) Line 68:

What are you referring to for "targeted medicine", do you have a reference?

We have revised the description and the reference.

(6) Line 74:

One of the papers referred to "quinoxyfen", what are the similarities and differences between the two? Please elaborate for the readership.

Quinoxyfen, similar to quinofumelin, contains a quinoline ring structure. It inhibits mycelial growth by disrupting the MAP kinase signaling pathway in fungi (https://www.frac.info). In addition, quinoxyfen still exhibits excellent antifungal activity against the quinofumelin-resistant mutants (the findings from our group), indicating that action mechanism for quinofumelin and quinoxyfen differ.

(7) Line 84:

Please introduce why RNA-Seq was designed in the study first. What were the groups compared? How was the experiment set up? Without this background, it is hard to know why and how you did the experiment.

According to your suggestions, we have added the description in Section Results. In addition, the experimental process was described in Section Materials and methods as follows: A total of 20 mL of YEPD medium containing 1 mL of conidia suspension (1×105 conidia/mL) was incubated with shaking (175 rpm/min) at 25°C. After 24 h, the medium was added with quinofumelin at a concentration of 1 μg/mL, while an equal amount of dimethyl sulfoxide was added as the control (CK). The incubation continued for another 48 h, followed by filtration and collection of hyphae. Carry out quantitative expression of genes, and then analyze the differences between groups based on the results of DESeq2 for quantitative expression.

(8) Figures:

The figure labeling is missing (Figures 1,2,3 etc). Please re-order your figure to match the text

The figures have been inserted.

(9) Line. 97:

"Volcano plot" is a common plot to visualize DEGs, you can directly refer to the name.

We have revised the description.

(10) Figure 1d, 1e:

Can you separate down- and up-regulated genes here? Does the count refer to gene number?

The expression information for down- and up-regulated genes is presented in Figure 1a and 1b. However, these bubble plots do not distinguish down- and up-regulated genes. Instead, they only display the significant enrichment of differentially expressed genes in specific metabolic pathways. To more clearly represent the data, we have added the detailed counts of down- and up-regulated genes for each metabolic pathway in Supplementary Table S1 and S2. Here, the term "count" refers to differentially expressed genes that fall within a certain pathway.

(11) Line 111:

Again, no reasoning or description of why and how the experiment was done here.

Based on the results of KEGG enrichment analysis, DEMs are associated with pathways such as thiamine metabolism, tryptophan metabolism, nitrogen metabolism, amino acid sugar and nucleotide sugar metabolism, pantothenic acid and CoA biosynthesis, and nucleotide sugar production compounds synthesis. To specifically investigate the metabolic pathways involved action mechanism of quinofumelin, we performed further metabolomic experiments. Therefore, we have added this description according the reviewer’s suggestions.

(12) Figure 2a:

It seems many more metabolites were reduced than increased. Is this expected? Due to the antifungal activity of this compound, how sick is the fungus upon treatment? A physiological study on F. graminearum (in a dose-dependent manner) should be done prior to the omics study. Why do you think there's a stark difference between positive and negative modes in terms of number of metabolites down- and up-regulated?

Quinofumelin demonstrates exceptional antifungal activity against Fusarium graminearum. The results indicate that the number of reduced metabolites significantly exceeds the number of increased metabolites upon quinofumelin treatment. Mycelial growth is markedly inhibited under quinofumelin exposure. Prior to conducting omics studies, we performed a series of physiological and biochemical experiments (refer to Qian Xiu's dissertation https://paper.njau.edu.cn/openfile?dbid=72&objid=50_49_57_56_49_49&flag=free). Upon quinofumelin treatment, the number of down-regulated metabolites notably surpasses that of up-regulated metabolites compared to the control group. Based on the findings from the down-regulated metabolites, we conducted experiments by exogenously supplementing these metabolites under quinofumelin treatment to investigate whether mycelial growth could be restored. The results revealed that only the exogenous addition of uracil can restore mycelial growth impaired by quinofumelin.

Quinofumelin exhibits an excellent antifungal activity against F. graminearum. At a concentration of 1 μg/mL, quinofumelin inhibits mycelial growth by up to 90%. This inhibitory effect indicates that life activities of F. graminearum are significantly disrupted by quinofumelin. Consequently, there is a marked difference in down- and up-regulated metabolites between quinofumelin-treated group and untreated control group. The detailed results were presented in Figures 1 and 2.

(13) Figure 2e:

This is a good analysis. To help represent the data more clearly, the authors can consider representing the expression using fold change with a p-value for each gene.

To more clearly represent the data, we have incorporated the information on significant differences in metabolites in the de novo pyrimidine biosynthesis pathway, as affected by quinofumelin, in accordance with the reviewer’s suggestions.

(14) Line 142:

Please indicate fold change and p-value for statistical significance. Did you validate this by RT-qPCR?

We validated the expression level of the DHODH gene under quinofumelin treatment using RT-qPCR. The results indicated that, upon treatment with the EC50 and EC90 concentrations of quinofumelin, the expression of the DHODH gene was significantly reduced by 11.91% and 33.77%, respectively (P<0.05). The corresponding results have been shown in Figure S4.

(15) Line 145:

It looks like uracil is the only metabolite differentially abundant in the samples - how did you conclude this whole pathway was impacted by the treatment?

The experiments involving the exogenous supplementation of uracil revealed that the addition of uracil could restore mycelial growth inhibited by quinofumelin. Consequently, we infer that quinofumelin disrupts the de novo pyrimidine biosynthesis pathway. In addition, as uracil is the end product of the de novo pyrimidine biosynthesis pathway, the disruption of this pathway results in a reduction in uracil levels.

(16) Figure 3:

What sequence was used as the root of the tree? Why were the species chosen? Since the BLAST query was Homo sapiens sequence, would it be good to use that as the root?

FgDHODHII sequence was used as the root of the tree. These selected fungal species represent significant plant-pathogenic fungi in agriculture production. According to your suggestion, we have removed the BLAST query of Homo sapiens in Figure 3.

(17) Figure 4:

How were the concentrations used to test chosen?

Prior to this experiment, we carried out concentration-dependent exogenous supplementation experiments. The results indicated that 50 μg/mL of uracil can fully restore mycelial growth inhibited by quinofumelin. Consequently, we chose 50 μg/mL as the testing concentration.

(18) Line 164:

Why do you hypothesize supplementing dihydroorotate would restore resistance? The metabolite seemed accumulated in the treatment condition, whereas downstream metabolites were comparable or even depleted. The DHODH gene expression was suppressed. Would accumulation of dihydroorotate be associated with growth inhibition by quinofumelin? Please include the hypothesis and rationale for the experimental setup.

DHODH regulates the conversion of dihydroorotate to orotate in the de novo pyrimidine biosynthesis pathway. The inhibition of DHODH by quinofumelin results in the accumulation of dihydroorotate and the depletion of the downstream metabolites, including UMP, uridine and uracil. Consequently, downstream metabolites were considered as positive controls, while upstream metabolite dihydroorotate served as a negative control. This design further demonstrates DHODH as action target of quinofumelin against F. graminearum. In addition, the accumulation of dihydroorotate is not associated with growth inhibition by quinofumelin; however, but the depletion of downstream metabolites in the de novo pyrimidine biosynthesis pathway is closely associated with growth inhibition by quinofumelin.

(19) Line 168:

I'm not sure if this conclusion is valid from your results in Figure 4 showing which metabolites restore growth.

o minimize the potential influence of strain-specific effects, five strains were tested in the experiments shown in Figure 4. For each strain, the first row (first column) corresponds to control condition, while second row (first column) represents treatment with 1 μg/mL of quinofumelin, which completely inhibits mycelial growth. The second row (second column) for each strain represents the supplementation with 50 μg/mL of dihydroorotate fails to restore mycelial growth inhibited by quinofumelin. In contrast, the second row (third column, fourth column, fifth colomns) for each strain demonstrated that the supplementation of 50 μg/mL of UMP, uridine and uracil, respectively, can effectively restore mycelial growth inhibited by quinofumelin.

(20) Figure 5a:

The fact you saw growth of the deletion mutant means it's not lethal. However, the growth was severely inhibited.

Our experimental results indicate that the growth of the deletion mutant is lethal. The mycelial growth observed originates from mycelial plugs that were not exposed to quinofumelin, rather than from the plates amended with quinofumelin.

(21) Figure 5b:

Would you expect different restoration of growth in the presence of quinofumelin vs. no treatment? The wild type control is missing here. Any conclusions about the relationship between quinofumelin, FgDHODHII, and other metabolites in the pathway?

Under no treatment with quinofumelin, mycelial growth remains normal and does not require restoration. In the presence of quinofumelin treatment, the supplementation of downstream metabolites in the de novo pyrimidine biosynthesis pathway can restore mycelial growth that is inhibited by quinofumelin. The wild-type control group is illustrated in Figure 4. Figure 5b depicts the phenotypes of the deletion mutants. With respect to the relationship among quinofumelin, FgDHODHII, and other metabolites, quinofumelin specifically targets the key enzyme FgDHODHII in the de novo pyrimidine biosynthesis pathway, disrupting the conversion of dihydroorotate to orotate, which consequently inhibits the synthesis downstream metabolites including uracil.

(22) Figure 6b:

Lacking positive and negative controls (known binder and non-binder). What does the Kd (in comparison to other interactions) indicate in terms of binding strength?

We tested the antifungal activities of publicly reported DHODH inhibitors (such as leflunomide and teriflunomide) against F. graminearum. The results showed that these inhibitors exhibited no significant inhibitory effects against the strain PH-1. Therefore, we lacked an effective chemical for use as a positive control in subsequent experiments. Biacore experiments offers detailed insights into molecular interactions between quinofumelin and DHODHII. As shown in Figure 6b, the left panel illustrates the time-dependent kinetic curve of quinofumelin binding to DHODHII. Within the first 60 s after quinofumelin was introduced onto the DHODHII surface, it bound to the immobilized DHODHII on the chip surface, with the response value increasing proportionally to the quinofumelin concentration. Following cessation of the injection at 60 s, quinofumelin spontaneously dissociated from the DHODHII surface, leading to a corresponding decrease in the response value. The data fitting curve presented on the right panel indicates that the affinity constant KD of quinofumelin for DHODHII is 6.606×10-6 M, which falls within the typical range of KD values (10-3 ~ 10-6 M) for protein-small molecule interaction patterns. A lower KD value indicates a stronger affinity; thus, quinofumelin exhibits strong binding affinity towards DHODHII.

Reviewer #3 (Recommendations for the authors):

The authors should add information about the other molecule within this class, ipflufenoquin, and what is known about it. There are already published data on its mode of action on DHODH and the role of pyrimidine biosynthesis.

We have added the information regarding action mechanism of ipflufenoquin against filamentous fungi in discussion section.

The work of Higashimura et al is not appreciated well enough as they already showed the role of quinofumelin upon DHODH II.

We sincerely appreciate the reviewer's insightful comment regarding the work of Higashimura et al. We agree that their investigation into the role of quinofumelin in DHODH II inhibition provides critical foundational insights for this field. In the revised manuscript, we have incorporated the reference in the introduction section and expanded the discussion of their work in the discussion section to more effectively contextualize their contributions.

It is unclear how the protein model was established and this should be included. What species is the molecule from and how was it obtained? How are they different from Fusarium?

The three-dimensional structural model of F. graminearum DHODHII protein, as predicted by AlphaFold, was obtained from the UniProt database. Additionally, a detailed description along with appropriate citations has been incorporated in the ‘Manuscript’ file.

Author response:

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

Reviewer #1 (Public Review):

We thank the reviewer for the positive feedback on the work. The reviewer has raised two weaknesses and in the following we discuss how those can be addressed.  

Weaknesses:

The impact of the article is limited by using a network with discrete time- steps, and only a small number of time steps from stimulus to reward. They assume that each time step is on the order of hundreds of ms. They justify this by pointing to some slow intrinsic mechanisms, but they do not implement these slow mechanisms is a network with short time steps, instead they assume without demonstration that these could work as suggested. This is a reasonable first approximation, but its validity should be explicitly tested.

Our goal here was to give a proof of concept that online random feedback is sufficient to train an RNN to estimate value. Indeed, it is important to show that the idea works in a model where the slow mechanisms are explicitly implemented. However, this is a non-trivial task and desired to be addressed in future works.  

As the delay between cue and reward increases the performance decreases. This is not surprising given the proposed mechanism, but is still a limitation, especially given that we do not really know what a is the reasonable value of a single time step.

In reply to this comment and the other reviewer's related comment, we have conducted two sets of additional simulations, one for examining incorporation of eligibility traces, and the other for considering (though not mechanistically implementing) behavioral time-scale synaptic plasticity (BTSP). We have added their results to the revised manuscript as Appendix. We think that the results addressed this point to some extent while how longer cue-reward delay can be learnt by elaboration of the model remains as a future issue.

Reviewer #2 (Public Review):

We thank the reviewer for the positive feedback on the work. The reviewer gave comments on our revisions, and here we discuss how those can be addressed.

Comments on revisions: I would still want to see how well the network learns tasks with longer time delays (on the order of 100 or even 1000 timesteps). Previous work has shown that random feedback struggles to encode longer timescales (see Murray 2019, Figure 2), so I would be interested to see how that translates to the RL context in your model.

We would like to note that in Murray et al 2019 the random feedback per se appeared not to be primarily responsible for the difficulty in encoding longer timesclaes. In the Figure 2d (Murray 2019), the author compared his RFLO (random feedback local online) and BPTT with two intermediate algorithms, which incorporated either one of the two approximations made in RFLO: i) random feedback instead of symmetric feedback, and ii) omittance of non-local effect (i.e., dependence of the derivative of the loss with respect to a given weight on the other weights). The performance difference between RFLO and BPTT was actually mostly explained by ii), as the author mentioned "The results show that the local approximation is essentially fully responsible for the performance difference between RFLO and BPTT, while there is no significant loss in performance due to the random feedback alone. (Line 6-8, page 7 of Murray, 2019, eLife)".

Meanwhile, regarding the difference in the performance of the model with random feedback vs the model with symmetric feedback in our settings, actually it appeared (already) in the case with 6 time-steps or less (the biologically constrained model with random feedback performed worse: Fig. 6J, left).

In practice, our model, either with random or symmetric feedback, would not be able to learn the cases with very long delays. This is indeed a limitation of our model. However, our model is critically different from the model of Murray 2019 in that we use RL rather than supervised learning and we use a scalar bootstrapped (TD) reward-prediction-error rather than the true output error. We would think that these differences may be major reasons for the limited learning ability of our model.

Regarding the feasibility of the model when tasks involve longer time delays: Indeed this is a problem and the other reviewers have also raised the same point. Our model can be extended by incorporating either a kind of eligibility trace (similar one to those contained in RFLO and e-prop) or behavioral time-scale synaptic plasticity (BTSP), and we have added the results of simulations incorporating each to the revised manuscript as Appendix. But how longer cue-reward delay can be learnt by elaboration of the model remains as a future issue.

Reviewer #3 (Public Review):

Comments on revisions: Thank you for addressing all my comments in your reply.

We are happy to learn that all concerns raised by the reviewer in the previous round were addressed adequately. We agree with the reviewer that there are several ways the work can be improved.

The various points raised by the reviewers at weaknesses are desired to be taken up in future works.

eLife Assessment

In this important study, the authors model reinforcement-learning experiments using a recurrent neural network. The work examines if the detailed credit assignment necessary for back-propagation through time can be replaced with random feedback. The authors provide solid evidence that the solution is adequate within relatively simple tasks.

Reviewer #1 (Public review):

Summary:

Can a plastic RNN serve as a basis function for learning to estimate value. In previous work this was shown to be the case, with a similar architecture to that proposed here. The learning rule in previous work was back-prop with an objective function that was the TD error function (delta) squared. Such a learning rule is non-local as the changes in weights within the RNN, and from inputs to the RNN depends on the weights from the RNN to the output, which estimates value. This is non-local, and in addition, these weights themselves change over learning. The main idea in this paper is to examine if replacing the values of these non-local changing weights, used for credit assignment, with random fixed weights can still produce similar results to those obtained with complete bp. This random feedback approach is motivated by a similar approach used for deep feed-forward neural networks.

This work shows that this random feedback in credit assignment performs well but is not as well as the precise gradient-based approach. When more constraints due to biological plausibility are imposed performance degrades. These results are consistent with previous results on random feedback.

Strengths:

The authors show that random feedback can approximate well a model trained with detailed credit assignment.

The authors simulate several experiments including some with probabilistic reward schedules and show results similar to those obtained with detailed credit assignments as well as in experiments.

The paper examines the impact of more biologically realistic learning rules and the results are still quite similar to the detailed back-prop model.

Reviewer #2 (Public review):

Summary:

Tsurumi et al. show that recurrent neural networks can learn state and value representations in simple reinforcement learning tasks when trained with random feedback weights. The traditional method of learning for recurrent network in such tasks (backpropogation through time) requires feedback weights which are a transposed copy of the feed-forward weights, a biologically implausible assumption. This manuscript builds on previous work regarding "random feedback alignment" and "value-RNNs", and extends them to a reinforcement learning context. The authors also demonstrate that certain non-negative constraints can enforce a "loose alignment" of feedback weights. The author's results suggest that random feedback may be a powerful tool of learning in biological networks, even in reinforcement learning tasks.

Strengths:

The authors describe well the issues regarding biologically plausible learning in recurrent networks and in reinforcement learning tasks. They take care to propose networks which might be implemented in biological systems and compare their proposed learning rules to those already existing in literature. Further, they use small networks on relatively simple tasks, which allows for easier intuition into the learning dynamics.

Weaknesses:

The principles discovered by the authors in these smaller networks are not applied to larger networks or more complicated tasks with long temporal delays (>100 timesteps), so it remains unclear to what degree these methods can scale or can be used more generally.

Reviewer #3 (Public review):

Summary:

The paper studies learning rules in a simple sigmoidal recurrent neural network setting. The recurrent network has a single layer of 10 to 40 units. It is first confirmed that feedback alignment (FA) can learn a value function in this setting. Then so-called bio-plausible constraints are added: (1) when value weights (readout) is non-negative, (2) when the activity is non-negative (normal sigmoid rather than downscaled between -0.5 and 0.5), (3) when the feedback weights are non-negative, (4) when the learning rule is revised to be monotic: the weights are not downregulated. In the simple task considered all four biological features do not appear to impair totally the learning.

Strengths:

(1) The learning rules are implemented in a low-level fashion of the form: (pre-synaptic-activity) x (post-synaptic-activity) x feedback x RPE. Which is therefore interpretable in terms of measurable quantities in the wet-lab.

(2) I find that non-negative FA (FA with non negative c and w) is the most valuable theoretical insight of this paper: I understand why the alignment between w and c is automatically better at initialization.

(3) The task choice is relevant, since it connects with experimental settings of reward conditioning with possible plasticity measurements.

eLife Assessment

This important study reveals how Drosophila may be used to investigate the role of missense variants in the PLCG1 phospholipase gene in human diseases. The experimental evidence is compelling and brings together rigorous analysis of clinical and model organism phenotypes with a structural analysis of the PLCG1 protein.

Reviewer #2 (Public review):

The manuscript by Ma et al. reports the identification of three unrelated people who are heterozygous for de novo missense variants in PLCG1, which encodes phospholipase C-gamma 1, a key signaling protein. These individuals present with partially overlapping phenotypes, including hearing loss, ocular pathology, cardiac defects, abnormal brain imaging results, and immune defects. None of the patients present with all of the above phenotypes. PLCG1 has also been implicated as a possible driver for cell proliferation in cancer.

The three missense variants found in the patients result in the following amino acid substitutions: His380Arg, Asp1019Gly, and Asp1165Gly. PLCG1 (and the closely related PLCG2) have a single Drosophila ortholog called small wing (sl). sl-null flies are viable but have small wings with ectopic wing veins and supernumerary photoreceptors in the eye. As all three amino acids affected in the patients are conserved in the fly protein, in this work Ma et al. tested whether they are pathogenic by expressing either reference or patient variant fly or human genes in Drosophila and determining the phenotypes produced by doing so.

Expression in Drosophila of the variant forms of PLCG1 found in these three patients is toxic; highly so for Asp1019Gly and Asp1165Gly, much more modestly for His380Arg. Another variant, Asp1165His which was identified in lymphoma samples and shown by others to be hyperactive, was also found to be toxic in the Drosophila assays. However, a final variant, Ser1021Phe, identified by others in an individual with severe immune dysregulation, produced no phenotype upon expression in flies.

Based on these results, the authors conclude that the PLCG1 variants found in patients are pathogenic, producing gain-of-function phenotypes through hyperactivity. In my view, the data supporting this conclusion are robust, despite the lack of a detectable phenotype with Ser1021Phe, and I have no concerns about the core experiments that comprise the paper.

Fig. 6, the last in the paper, provides information about PLCG1 structure and how the different variants would affect it. It shows that His380, Asp1019 and Asp1165 all lie within catalytic domains or intramolecular interfaces, and that variants in the latter two affect residues essential for autoinhibition. It also shows that Ser1021 falls outside the key interface occupied by Asp1019, but more could have been said about the potential effects of Ser1021Phe.

Overall, I believe the authors fully achieved the aims of their study. The work will have a substantial impact because it reports the identification of novel disease-linked genes, and because it further demonstrates the high value of the Drosophila model for finding and understanding gene-disease linkages.

Comments on revisions:

The single recommendation I made on the original version, which was to further examine H380 mutants, has been satisfactorily addressed in the revised version.

Author response:

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

Reviewer #1 (Public Review):

Summary:

This manuscript provides an initial characterization of three new missense variants of the PLCG1 gene associated with diverse disease phenotypes, utilizing a Drosophila model to investigate their molecular effects in vivo. Through the meticulous creation of genetic tools, the study assesses the small wing (sl) phenotype - the fly's ortholog of PLCG1 - across an array of phenotypes from longevity to behavior in both sl null mutants and variants. The findings indicate that the Drosophila PLCG1 ortholog displays aberrant functions. Notably, it is demonstrated that overexpression of both human and Drosophila PLCG1 variants in fly tissue leads to toxicity, underscoring their pathogenic potential in vivo.

Strengths:

The research effectively highlights the physiological significance of sl in Drosophila. In addition, the study establishes the in vivo toxicity of disease-associated variants of both human PLCG1 and Drosophila sl.

Weaknesses:

The study's limitations include the human PLCG1 transgene's inability to compensate for the Drosophila sl null mutant phenotype, suggesting potential functional divergence between the species. This discrepancy signals the need for additional exploration into the mechanistic nuances of PLCG1 variant pathogenesis, especially regarding their gain-of-function effects in vivo.

Overall:

The study offers compelling evidence for the pathogenicity of newly discovered disease-related PLCG1 variants, manifesting as toxicity in a Drosophila in vivo model, which substantiates the main claim by the authors. Nevertheless, a deeper inquiry into the specific in vivo mechanisms driving the toxicity caused by these variants in Drosophila could significantly enhance the study's impact.

Reviewer #2 (Public Review):

The manuscript by Ma et al. reports the identification of three unrelated people who are heterozygous for de novo missense variants in PLCG1, which encodes phospholipase C-gamma 1, a key signaling protein. These individuals present with partially overlapping phenotypes including hearing loss, ocular pathology, cardiac defects, abnormal brain imaging results, and immune defects. None of the patients present with all of the above phenotypes. PLCG1 has also been implicated as a possible driver for cell proliferation in cancer.

The three missense variants found in the patients result in the following amino acid substitutions: His380Arg, Asp1019Gly, and Asp1165Gly. PLCG1 (and the closely related PLCG2) have a single Drosophila ortholog called small wing (sl). sl-null flies are viable but have small wings with ectopic wing veins and supernumerary photoreceptors in the eye. As all three amino acids affected in the patients are conserved in the fly protein, in this work Ma et al. tested whether they are pathogenic by expressing either reference or patient variant fly or human genes in Drosophila and determining the phenotypes produced by doing so.

Expression in Drosophila of the variant forms of PLCG1 found in these three patients is toxic; highly so for Asp1019Gly and Asp1165Gly, much more modestly for His380Arg. Another variant, Asp1165His which was identified in lymphoma samples and shown by others to be hyperactive, was also found to be toxic in the Drosophila assays. However, a final variant, Ser1021Phe, identified by others in an individual with severe immune dysregulation, produced no phenotype upon expression in flies.

Based on these results, the authors conclude that the PLCG1 variants found in patients are pathogenic, producing gain-of-function phenotypes through hyperactivity. In my view, the data supporting this conclusion are robust, despite the lack of a detectable phenotype with Ser1021Phe, and I have no concerns about the core experiments that comprise the paper.

Figure 6, the last in the paper, provides information about PLCG1 structure and how the different variants would affect it. It shows that the His380, Asp1019, and Asp1165 all lie within catalytic domains or intramolecular interfaces and that variants in the latter two affect residues essential for autoinhibition. It also shows that Ser1021 falls outside the key interface occupied by Asp1019, but more could have been said about the potential effects of Ser1021Phe.

Overall, I believe the authors fully achieved the aims of their study. The work will have a substantial impact because it reports the identification of novel disease-linked genes, and because it further demonstrates the high value of the Drosophila model for finding and understanding gene-disease linkages.

Reviewer #3 (Public Review):

Summary:

The paper attempts to model the functional significance of variants of PLCG2 in a set of patients with variable clinical manifestations.

Strengths:

A study attempting to use the Drosophila system to test the function of variants reported from human patients.

Weaknesses:

Additional experiments are needed to shore up the claims in the paper. These are listed below.

Major Comments:

(1) Does the pLI/ missense constraint Z score prediction algorithm take into consideration whether the gene exhibits monoallelic or biallelic expression?

To our knowledge, pLI and missense Z don't consider monoallelic or biallelic expression. Instead, they reflect sequence constraint and are calculated based on the observed versus expected variant frequencies in population databases.

(2) Figure 1B: Include human PLCG2 in the alignment that displays the species-wide conserved variant residues.

We have updated Figure 1B and incorporated the alignment of PLCG2.

(3) Figure 4A:

Given that

(i) sl is predicted to be the fly ortholog for both mammalian PLCγ isozymes: PLCG1 and PLCG2 [Line 62]

(ii) they are shown to have non-redundant roles in mammals [Line 71]

(iii) reconstituting PLCG1 is highly toxic in flies, leading to increased lethality.

This raises questions about whether sl mutant phenotypes are specifically caused by the absence of PLCG1 or PLCG2 functions in flies. Can hPLCG2 reconstitution in sl mutants be used as a negative control to rule out the possibility of the same?

The studies about the non-redundant roles of PLCG1 and PLCG2 mainly concern the immune system.

We have assessed the phenotypes in the sl^T2A/Y; UAS-hPLCG2 flies. Expression of human PLCG2 in flies is also toxic and leads to severely reduced eclosion rate.

We have updated the manuscript with these results, and included the eclosion rate of sl^T2A/Y; UAS-hPLCG2 flies in the new Figure 4B.

(4) Do slT2A/Y; UAS-PLCG1Reference flies survive when grown at 22{degree sign}C? Since transgenic fly expressing PLCG1 cDNA when driven under ubiquitous gal4s, Tubulin and Da, can result in viable progeny at 22{degree sign}C, the survival of slT2A/Y; UAS-PLCG1Reference should be possible.

The eclosion rate of sl^T2A/Y >PLCG1^Reference flies at 22°C is slightly higher than at 25°C, but remains severely reduced compared to the UAS-Empty control. We have presented these results in the updated Figure S3.

and similarly

Does slT2A flies exhibit the phenotypes of (i) reduced eclosion rate (ii) reduced wing size and ectopic wing veins and (iii) extra R7 photoreceptor in the fly eye at 22{degree sign}C?

The mutant phenotypes are still observed at 22 °C.

If so, will it be possible to get a complete rescue of the slT2A mutant phenotypes with the hPLCG1 cDNA at 22{degree sign}C? This dataset is essential to establish Drosophila as an ideal model to study the PLCG1 de novo variants.

Thank you for the suggestion. It is difficult to directly assess the rescue ability of the PLCG1 cDNAs due to the toxicity. However, our ectopic expression assays show that the variants are more toxic than the reference with variable severities, suggesting that the variants are deleterious.

The ectopic expression strategy has been used to evaluate the consequence of genetic variants and has significantly contributed to the interpretation of their pathogenicity in many cases (reviewed in Her et al., Genome, 2024, PMID: 38412472).

(5) Localisation and western blot assays to check if the introduction of the de novo mutations can have an impact on the sub-cellular targeting of the protein or protein stability respectively.

Thank you for the suggestion.

We expressed PLCG1 cDNAs in the larval salivary glands and performed antibody staining (rabbit anti-Human PLCG1; 1:100, Cell Signaling Technology, #5690). The larval salivary gland are composed of large columnar epithelia cells that are ideal for analyzing subcellular localization of proteins. The PLCG1 proteins are cytoplasmic and localize near the cell surface, with some enrichment in the plasma membrane region. The variant proteins are detected, and did not show significant difference in expression level or subcellular distribution compared to the reference. We did not include this data.

(6) Analysing the nature of the reported gain of function (experimental proof for the same is missing in the manuscript) variants:

Instead of directly showing the effect of introducing the de novo variant transgenes in the Drosophila model especially when the full-length PLCG1 is not able to completely rescue the slT2A phenotype;

(i) Show that the gain-of-function variants can have an impact on the protein function or signalling via one of the three signalling outputs in the mammalian cell culture system: (i) inositol-1,4,5-trisphosphate production, (ii) intracellular Ca2+ release or (iii) increased phosphorylation of extracellular signal-related kinase, p65, and p38.

We appreciate the reviewer’s suggestion. We utilized the CaLexA (calcium-dependent nuclear import of LexA) system (Masuyama et al., J Neurogenet, 2012, PMID: 22236090) to assess the intracellular Ca²⁺ change associated with the expression of PLCG1 cDNAs in fly wing discs. The results show that, compared to the reference, expression of the D1019G or D1165G variants leads to elevated intracellular Ca²⁺ levels, similar to the hyperactive S1021F and D1165H variants. However, the H380R or L597F variants did not show a detectable phenotype in this assay. These results suggest that D1019G and D1165G are hyperactive variants, whereas H380R and L597F variant are not, or their effect is too mild to be detected in this assay. We have updated the related sections in the manuscript and Figures 5A and S5.

OR

(ii) Run a molecular simulation to demonstrate how the protein's auto-inhibited state can be disrupted and basal lipase activity increased by introducing D1019G and D1165G, which destabilise the association between the C2 and cSH2 domains. The H380R variant may also exhibit characteristics similar to the previously documented H335A mutation which leaves the protein catalytically inactive as the residue is important to coordinate the incoming water molecule required for PIP2 hydrolysis.

We utilized the DDMut platform, which predicts changes in the Gibbs Free Energy (ΔΔG) upon single and multiple point mutations (Zhou et al., Nucleic Acid Res, 2023, PMID: 37283042), to gain insight into the molecular dynamics changes of variants. The results are now presented in Figure S7.

Additionally, we performed Molecular dynamics (MD) simulations. The results show that, similar to the hyperactive D1165H variant, the D1019G and D11656G variants exhibit increased disorganization, with a higher root mean square deviations (RMSD) compared to the reference PLCG1.The data are also presented in the updated Figure S7.

(7) Clarify the reason for carrying out the wing-specific and eye-specific experiments using nub-gal4 and eyless-gal4 at 29˚C despite the high gal4 toxicity at this temperature.

We used high temperature and high expression level to see if the mild H380R and L597F variants could show phenotypes in this condition.

The toxicity of the two strong variants (D1019G and D1165G) has been consistently confirmed in multiple assays at different temperatures.

(8) For the sake of completeness the authors should also report other variants identified in the genomes of these patients that could also contribute to the clinical features.

Thank you!

The additional variants and their potential contributions to the clinical features are listed and discussed in Table 1 and its legend.

Reviewer #1 (Recommendations For The Authors):

The manuscript's significant contribution is tempered by a lack of comprehensive analysis using the generated genetic reagents in Drosophila. To enhance our understanding of the PLCG1 orthologs, I suggest the following:

(1) A more detailed molecular analysis to distinguish the actions of sl variants from the wild-type could be very informative. For example, utilizing the HA-epitope tag within the current UAS-transgenes could reveal more about the cellular dynamics and abundance of these variants, potentially elucidating mechanisms beyond gain-of-function.

We appreciate the reviewer’s suggestion. The UAS-sl cDNA constructs contain stop codon and do not express an HA-epitope tag. Alternatively, we utilized commercially available antibodies against human PLCG1 antibodies to assess the subcellular localization and protein stability by expressing the reference and variant PLCG1 cDNAs in Drosophila larval salivary glands. The reference proteins are cytoplasmic with some enrichment along the plasma membrane. However, we did not observe significant differences between the reference and variant proteins in this assay. We did not include this data.

(2) I suggest further investigating the relative contributions of developmental processes and acute (Adult) effects on the sl-variant phenotypes observed. For example, employing systems that allow for precise temporal control of gene expression, such as the temperature-sensitive Gal80, could differentiate between these effects, shedding light on the mechanisms that affect longevity and locomotion. This knowledge would be vital for a deeper understanding of the corresponding human disorders and for developing therapeutic interventions.

We appreciate the reviewer’s suggestion. We utilized Tub-GAL4, Tub-GAL80^ts to drive the expression of sl wild-type or variant cDNAs, and performed temperature shifts after eclosion to induce expression of the cDNAs only in adult flies. The sl^D1184G variant (corresponding to PLCG1^D1165G) caused severely reduced lifespan and the flies mostly die within 10 days. The sl^D1041G variant (corresponding to PLCG1^D1019G) led to reduced longevity and locomotion. The sl^H384R variant (corresponding to PLCG1^H380R) showed only a mild effect on longevity and no significant effect on climbing ability. These results suggest that the two strong variants (sl<sup>D1041G<sup> and sl^D1184G) contribute to both developmental and acute effects while the H384R variant mainly contributes to developmental stages.

I also suggest a more refined analysis of overexpression toxicity. Rather than solely focusing on ubiquitous transgene expression, overexpressing transgene in endogenous pattern using sl-t2a-Gal4 may yield a more nuanced understanding of the pathogenic mechanisms of gain-of-function mutations, particularly in the pathogenesis associated with these variants exclusively located in the coding regions.

We appreciate the reviewer’s suggestion. We therefore performed the experiments using sl^T2A to drive overexpression ofPLCG1cDNAs in heterozygous female progeny with one copy of wild-type sl+ (sl^T2A/ yw > UAS-cDNAs). In this context, expression of PLCG1<sup>Reference<sup>, PLCG1^H380RorPLCG1^L597F is viable whereas expression of PLCG1^D1019G or PLCG1^D1165G is lethal, suggesting that the PLCG1^D1019G and PLCG1^D1165G variants exert a strong dominant toxic effect while the PLCG1^H380Rand PLCG1<sup>L597F<sup> are comparatively milder. Similar patterns have been consistently observed in other ectopic expression assays with varying degrees of severity. These results are updated in the manuscript and figures.

Reviewer #2 (Recommendations For The Authors):

The work in the paper could be usefully extended by determining the effects of expressing His380Phe and His380Ala in flies. These variants suppress PLCG1 activity, so their phenotype, if any, would be predicted not to be the same as His380Arg. Determining this would add further strength to the conclusions of the paper.

We thank the reviewer for the constructive suggestions! We have tested the enzymatic-dead H380A variant, which still exhibits toxicity when expressed in sl^T2A/Y hemizygous flies, but it is not toxic in heterozygous females suggesting that the reduced eclosion rate is likely not directly associated with enzymatic activity. We have updated the manuscript and figures accordingly.

eLife Assessment

This useful study characterizes the evolution of medial prefrontal cortex activity during the learning of an odor-based choice task. While the evidence for an increase in task-informative cells with learning, the emergence of population sequences, and the presence of replay events is intriguing, it remains incomplete; notably, the study does not adequately consider the extensive literature on the role of olfactory and hippocampal networks in similar odor-guided tasks. Furthermore, the experimental design appears insufficient to support strong conclusions regarding pre-existing representations or the functional relevance of neural sequences. The study will be of interest to neuroscientists investigating learning and decision-making processes.

Reviewer #1 (Public review):

Summary:

The authors use longitudinal in vivo 1-photon calcium recordings in mouse prefrontal cortex throughout the learning of an odor-guided spatial memory task, with the goal of examining the development of task-related prefrontal representations over the course of learning in different task stages and during sleep sessions. They report replication of their previous results, Muysers et al. 2025, that task and representations in prefrontal cortex arise de novo after learning, comprising of goal selective cells that fire selectively for left or right goals during the spatial working memory component of the task, and generalized task phase selective cells that fire equivalently in the same place irrespective of goal, together comprising task-informative cells. The number of task-informative cells increases over learning, and covariance structure changes resulting in increased sequential activation in the learned condition, but with limited functional relevance to task representation. Finally, the authors report that similar to hippocampal trajectory replay, prefrontal sequences are replayed at reward locations.

Strengths:

The major strength of the study is the use of longitudinal recordings, allowing identification of task-related activity in the prefrontal cortex that emerges de novo after learning, and identification of sub-second sequences at reward wells.

Weaknesses:

(1) The study mainly replicates the authors' previously reported results about generalized and trajectory-specific coding of task structure by prefrontal neurons, and stable and changing representations over learning (Muysers et al., 2024, PMID: 38459033; Muysers et al., 2025, PMID: 40057953), although there are useful results about changes in goal-selective and task-phase selective cells over learning. There are basic shortcomings in the scientific premise of two new points in this manuscript, that of the contribution of pre-existing spatial representations, and the role of replay sequences in the prefrontal cortex, both of which cannot be adequately tested in this experimental design.

(2) The study denotes neurons that show precise spatial firing equivalently irrespective of goal, as generalized task representations, and uses this as a means to testing whether pre-existing spatial representations can contribute to task coding and learning. A previous study using this data has already shown that these neurons preferentially emerge during task learning (Muysers et al., 2025, PMID: 40057953). Furthermore, in order to establish generalization for abstract task rules or cognitively flexibility, as motivated in the manuscript, there is a need to show that these neurons "generalize" not just to firing in the same position during learning of a given task, but that they can generalize across similar tasks, e.g., different mazes with similar rules, different rules with similar mazes, new odor-space associations, etc. For an adequate test of pre-existing spatial structure, either a comparison task, as in the examples above, is needed, or at least a control task in which animals can run similar trajectories without the task contingencies. An unambiguous conclusion about pre-existing spatial structure is not possible without these controls.

(3) The scientific premise for the test of replay sequences is motivated using hippocampal activity in internally guided spatial working memory rule tasks (Fernandez-Ruiz et al., 2019, PMID: 31197012; Kay et al., PMID: 32004462; Tang et al., 2021, PMID: 33683201), and applied here to prefrontal activity in a sensory-cue guided spatial memory task (Muysers et al., 2024, PMID: 38459033; Symanski et al., PMID: 36480255; Taxidis et al, 2020, PMID: 32949502). There are several issues with the conclusion in the manuscript that prefrontal replay sequences are involved in evaluating behavioral outcomes rather than planning future outcomes.

(4) First, odor sampling in odor-guided memory tasks is an active sensory processing state that leads to beta and other oscillations in olfactory regions, hippocampus, prefrontal cortex, and many other downstream networks, as documented in a vast literature of studies (Martin et al., 2007, PMID: 17699692; Kay, 2014, PMID: 24767485; Martin et al., 2014; Ramirez-Gordillo, 2022, PMID: 36127136; Symanski et al., 2022, PMID: 36480255). This is an active sensory state, not conducive to internal replay sequences, unlike references used in this manuscript to motivate this analysis, which are hippocampal spatial memory studies with internally guided rather than sensory-cue guided decisions, where internal replay is seen during immobility at reward wells. These two states cannot be compared with the expectation of finding similar replay sequences, so it is trivially expected that internal replay sequences will not be seen during odor sampling.

(5) Second, sequence replay is not the only signature of reactivation. Many studies have quantified prefrontal replay using template matching and reactivation strength metrics that do not involve sequences (Peyrache et al., 2009, PMID: 19483687; Sun et al., 2024, PMID: 38872470). Third, previous studies have explicitly shown that prefrontal activity can be decoded during odor sampling to predict future spatial choices - this uses sensory-driven ensemble activity in prefrontal cortex and not replay, as odor sampling leads to sensory driven processing and recall rather than a reactivation state (Symanski et al., 2022, PMID: 36480255). It is possible that 1-photon recordings do not have the temporal resolution and information about oscillatory activity to enable these kinds of analyses. Therefore, an unambiguous conclusion about the existence and role of prefrontal reactivation is not possible in this experimental and analytical design.

Reviewer #2 (Public review):

Summary:

The first part of the manuscript quantifies the proportion of goal-arm specific and task-phase specific cells during the learning and learned conditions, and similar to their previously published Muysers et al. (2025) paper, find that the task-phase coding cells (Muysers et al. call them path equivalent cells) increase in the learned condition. However, compared to the Muysers et al. 2025 paper, this work quantifies the proportion of cells that change coding type across learning and learned conditions. The second part of the paper reports firing sequences using a sequence similarity clustering-based method that the group developed previously and applied to hippocampal data in the past.

Strengths:

Identifying sequences by a clustering method in which sequence patterns of individual events are compared is an interesting idea.

Weaknesses:

Further controls are needed to validate the results.

Reviewer #3 (Public review):

In the study, the authors performed longitudinal 1P calcium imaging of mouse mPFC across 8 weeks during learning of an olfactory-guided task, including habituation, training, and sleep periods. The task had 3 arms. Odor was sampled at the end of the middle arm (named the "Sample" period). The animal then needed to run to one of the two other arms (R or L) based on the odor. The whole period until they reached the end of one of the choice arms was the "Outward" period. The time at the reward end was the "Reward" period. They noted several changes from the learning condition to the learned condition (there are some questions for the authors interspersed):

(1) They classified cells in a few ways. First, each cell was classified as SI (spatially informative) if it had significantly more spatial information than shuffled activity, and ~50% of cells ended up being SI cells. Then, among the SI cells, they classified a cell as a TC (task cell) if it had statistically similar activity maps for R versus L arms, and a GC (goal arm cell) otherwise. Note that there are 4 kinds of these cells: outer arm TCs and GCs, and middle arm TCs and GCs (with middle arm GCs essentially being like "splitter cells" since they are not similarly active in the middle arm for R versus L trials). There was an increase in TCs from the learning to the learned condition sessions.

(2) They analyze activity sequences across cells. They extracted 500 ms duration bursts (defined as periods of activity > 0.5 standard deviations over what I assume is the mean - if so, the authors can add "over the mean" to the burst definition in the methods). They first noted that the resulting "Burst rates were significantly larger during behavioral epochs than during sleep and during periods of habituation to the arena", and "Moreover, burst rates during correct trials were significantly lower than during error trials". For the sequence analysis, they only considered bursts consisting of at least 5 active cells. A cell's activity within the burst was set to the center of mass of calcium activity. Then they took all the sequences from all learned and learning sessions together and hierarchically clustered them based on Spearman's rank correlation between the order of activity in each pair of sequences (among the cells active in both). The iterative hierarchical clustering process produces groups (clusters) of sequences such that there are multiple repeats of sequences within a cluster. Different sequences are expressed across all the longitudinally recorded sessions. They noted "large differences of sequence activation between learning and learned condition, both in the spatial patterns (example animal in Figure 3D) and the distribution of the sequences (Figures 3D, E). Rastermap plots (Figure 3D) also reveal little similarity of sequence expression between task and habituation or sleep condition." They also note that the difference in the sequences between learning and learned conditions was larger than the difference between correct and error trials within each condition. They conclude that during task learning, new representations are established, as measured by the burst sequence content. They do additional analyses of the sequence clusters by assessing the spatial informativeness (SI) of each sequence cluster. Over learning, they find an increase in clusters that are spatially informative (clusters that tend to occur in specific locations). Finally, they analyzed the SI clusters in a similar manner to SI cells and classified them as task phase selective sequences (TSs) and goal arm selective sequences (GSs), and did some further analysis. However, they themselves conclude that the frequency of TSs and GSs is limited (I believe because most sequence clusters were non-SI - the authors can verify this and write it in the text?). In the discussion, they say, "In addition to GSs and TSs, we found that most of the recurring sequences are not related to behavior".

(3) As an alternative to analyzing individual cells and sequences of individual cells, they then look for trajectory replay using Bayesian population decoding of location during bursts. They analyze TS bursts, GS bursts, and non-SI bursts. They say "we found correlations of decoded position with time bin (within a 500 ms burst) strongly exceeding chance level only during outward and reward phase, for both GSs and TSs (Fig 4H)." Figure 4H shows distributions indicating statistically significant bias in the forward direction (using correlations of decoded location versus time bin across 10 bins of 50 ms each within each 500-ms burst). They find that the Outward trajectories appear to reflect the actual trajectory during running itself, so they are likely not replay. But the sequences at the Reward are replay as they do not reflect the current location. Furthermore, replay at the Reward is in the forward direction (unlike the reverse replay at Reward seen in the hippocampus), and this replay is only seen in the learned and not the learning condition. At the same time, they find that replay is not seen during odor Sampling, from which they conclude there is no evidence of replay used for planning. Instead, they say the replay at the Reward could possibly be for evaluation during the Reward phase, though this would only be for the learned condition. They conclude "Together with our finding of strong changes in sequence expression after learning (Figure 3E) these findings suggest that a representation of task develops during learning, however, it does not reflect previous network structure." I am not sure what is meant here by the second part of this sentence (after "however ..."). Is it the idea that the replay represents network structure, and the lack of Reward replay in the learning condition means that the network structure must have been changed to get to the learned condition? Please clarify.

This study provides valuable new information about the evolution of mPFC activity during the learning of an odor-based 2AFC T-maze-like task. They show convincing evidence of changes in single-cell tuning, population sequences, and replay events. They also find novel forward replay at the Reward, and find that this is present only after the animal has learned the task. In the discussion, the authors note "To our knowledge, this study identified for the first time fast recurring neural sequence activity from 1-p calcium data, based on correlation analysis."

(1) There are some statements that are not clear, such as at the end of the introduction, where the authors write, "Both findings suggest that the mPFC task code is locally established during learning." What is the reasoning behind the "locally established" statement? Couldn't the learning be happening in other areas and be inherited by the mPFC? Or are the authors assuming that newly appearing sequences within a 500-ms burst period must be due to local plasticity? I have also pointed out a question about the statement "however, it does not reflect previous network structure" in (3) above.

(2) The threshold for extracting burst events (0.5 standard deviations, presumably above the mean, but the authors should verify this) seems lower than what one usually sees as a threshold for population burst detection. What fraction of all data is covered by 500 ms periods around each such burst? However, it is potentially a strength of this work that their results are found by using this more permissive threshold.

eLife Assessment

This important study presents JABS, an open-source platform that integrates hardware and user-friendly software for standardized mouse behavioral phenotyping. The work has practical implications for improving reproducibility and accessibility in behavioral neuroscience, especially for linking behavior to genetics across diverse mouse strains. The strength of evidence is convincing, with validation of key platform components, although incomplete methodological details and limited documentation, particularly around pose estimation and classifier generalizability, currently limit its interpretability and broader adoption.

Reviewer #1 (Public review):

Summary:

This manuscript provides an open-source tool including hardware and software, and a dataset to facilitate and standardize behavioral classification in laboratory mice. The hardware for behavioral phenotyping was extensively tested for safety. The software is GUI-based, facilitating the usage of this tool across the community of investigators who do not have a programming background. The behavioral classification tool is highly accurate, and the authors deposited a large dataset of annotations and pose tracking for many strains of mice. This tool has great potential for behavioral scientists who use mice across many fields; however, there are many missing details that currently limit the impact of this tool and publication.

Strengths:

(1) There is software-hardware integration for facilitating cross-lab adaptation of the tool and minimizing the need to annotate new data for behavioral classification.

(2) Data from many strains of mice were included in the classification and genetic analyses in this manuscript.

(3) A large dataset was annotated and deposited for the use of the community.

(4) The GUI-based software tool decreases barriers to usage across users with limited coding experience.

Weaknesses:

(1) The authors only report the quality of the classification considering the number of videos used for training, but not considering the number of mice represented or the mouse strain. Therefore, it is unclear if the classification model works equally well in data from all the mouse strains tested, and how many mice are represented in the classifier dataset and validation.

(2) The GUI requires pose tracking for classification, but the software provided in JABS does not do pose tracking, so users must do pose tracking using a separate tool. Currently, there is no guidance on the pose tracking recommendations and requirements for usage in JABS. The pose tracking quality directly impacts the classification quality, given that it is used for the feature calculation; therefore, this aspect of the data processing should be more carefully considered and described.

(3) Many statistical and methodological details are not described in the manuscript, limiting the interpretability of the data presented in Figures 4,7-8. There is no clear methods section describing many of the methods used and equations for the metrics used. As an example, there are no details of the CNN used to benchmark the JABS classifier in Figure 4, and no details of the methods used for the metrics reported in Figure 8.

Reviewer #2 (Public review):

Summary:

This manuscript presents the JAX Animal Behavior System (JABS), an integrated mouse phenotyping platform that includes modules for data acquisition, behavior annotation, and behavior classifier training and sharing. The manuscript provides details and validation for each module, demonstrating JABS as a useful open-source behavior analysis tool that removes barriers to adopting these analysis techniques by the community. In particular, with the JABS-AI module, users can download and deploy previously trained classifiers on their own data, or annotate their own data and train their own classifiers. The JABS-AI module also allows users to deploy their classifiers on the JAX strain survey dataset and receive an automated behavior and genetic report.

Strengths:

(1) The JABS platform addresses the critical issue of reproducibility in mouse behavior studies by providing an end-to-end system from rig setup to downstream behavioral and genetic analyses. Each step has clear guidelines, and the GUIs are an excellent way to encourage best practices for data storage, annotation, and model training. Such a platform is especially helpful for labs without prior experience in this type of analysis.

(2) A notable strength of the JABS platform is its reuse of large amounts of previously collected data at JAX Labs, condensing this into pretrained pose estimation models and behavioral classifiers. JABS-AI also provides access to the strain survey dataset through automated classifier analyses, allowing large-scale genetic screening based on simple behavioral classifiers. This has the potential to accelerate research for many labs by identifying particular strains of interest.

(3) The ethograph analysis will be a useful way to compare annotators/classifiers beyond the JABS platform.

Weaknesses:

(1) The manuscript as written lacks much-needed context in multiple areas: what are the commercially available solutions, and how do they compare to JABS (at least in terms of features offered, not necessarily performance)? What are other open-source options? How does the supervised behavioral classification approach relate to the burgeoning field of unsupervised behavioral clustering (e.g., Keypoint-MoSeq, VAME, B-SOiD)? What kind of studies will this combination of open field + pose estimation + supervised classifier be suitable for? What kind of studies is it unsuited for? These are all relevant questions that potential users of this platform will be interested in.

(2) Throughout the manuscript, I often find it unclear what is supported by the software/GUI and what is not. For example, does the GUI support uploading videos and running pose estimation, or does this need to be done separately? How many of the analyses in Figures 4-6 are accessible within the GUI?

(3) While the manuscript does a good job of laying out best practices, there is an opportunity to further improve reproducibility for users of the platform. The software seems likely to perform well with perfect setups that adhere to the JABS criteria, but it is very likely that there will be users with suboptimal setups - poorly constructed rigs, insufficient camera quality, etc. It is important, in these cases, to give users feedback at each stage of the pipeline so they can understand if they have succeeded or not. Quality control (QC) metrics should be computed for raw video data (is the video too dark/bright? are there the expected number of frames? etc.), pose estimation outputs (do the tracked points maintain a reasonable skeleton structure; do they actually move around the arena?), and classifier outputs (what is the incidence rate of 1-3 frame behaviors? a high value could indicate issues). In cases where QC metrics are difficult to define (they are basically always difficult to define), diagnostic figures showing snippets of raw data or simple summary statistics (heatmaps of mouse location in the open field) could be utilized to allow users to catch glaring errors before proceeding to the next stage of the pipeline, or to remove data from their analyses if they observe critical issues.

eLife Assessment

This important study uses long-term behavioural observations to understand the factors that influence female-on-female aggression in gorilla social groups. The evidence supporting the claims is convincing, as it includes novel methods of assessing aggression and considers other potential factors. The work will be of interest to broad biologists working on the social interactions of animals.

Joint Public Review:

Summary:

This work aims to improve our understanding of the factors that influence female-on-female aggressive interactions in gorilla social hierarchies, using 25 years of behavioural data from five wild groups of two gorilla species. Researchers analysed aggressive interactions between 31 adult females, using behavioural observations and dominance hierarchies inferred through Elo-rating methods. Aggression intensity (mild, moderate, severe) and direction (measured as the rank difference between aggressor and recipient) were used as key variables. A linear mixed-effects model was applied to evaluate how aggression direction varied with reproductive state (cycling, trimester-specific pregnancy, or lactation) and sex composition of the group. This study highlights the direction of aggressive interactions between females, with most interactions being directed from higher- to lower-ranking adult females close in social rank. However, the results show that 42% of these interactions are directed from lower- to higher-ranking females. Particularly, lactating and pregnant females targeted higher-ranking individuals, which the authors suggest might be due to higher energetic needs, which increase risk-taking in lactating and pregnant females. Sex composition within the group also influenced which individuals were targeted. The authors suggest that male presence buffers female-on-female aggression, allowing females to target higher-ranking females than themselves. In contrast, females targeted lower-ranking females than themselves in groups with a larger ratio of females, which supposes a lower risk for the females since the pool of competitors is larger. The findings provide an important insight into aggression heuristics in primate social systems and the social and individual factors that influence these interactions, providing a deeper understanding of the evolutionary pressures that shape risk-taking, dominance maintenance, and the flexibility of social strategies in group-living species.

The authors achieved their aim by demonstrating that aggression direction in female gorillas is influenced by factors such as reproductive condition and social context, and their results support the broader claim that aggression heuristics are flexible. However, some specific interpretations require further support. Despite this, the study makes a valuable contribution to the field of behavioural ecology by reframing how we think about intra-sexual competition and social rank maintenance in primates.

Strengths:

One of the study's major strengths is the use of an extensive dataset that compiles 25 years of behavioural data and 6871 aggressive interactions between 31 adult females in five social groups, which allows for a robust statistical analysis. This study uses a novel approach to the study of aggression in social groups by including factors such as the direction and intensity of aggressive interactions, which offers a comprehensive understanding of these complex social dynamics. In addition, this study incorporates ecological and physiological factors such as the reproductive state of the females and the sex composition of the group, which allows an integrative perspective on aggression within the broader context of body condition and social environment. The authors successfully integrate their results into broader evolutionary and ecological frameworks, enriching discussions around social hierarchies and risk sensitivity in primates and other animals.

Author response:

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

Reviewer #1 (Recommendations for the authors):

Suggestions:

Although this study has an impressive dataset, I felt that some parts of the discussion would benefit from further explanation, specifically when discussing the differences in female aggression direction between groups with different sex compositions. In the discussion is suggested that males buffer female-on-female aggression and that they 'support' lower-ranking females (see line 212), however, the study only tested the sex composition of the group and does not provide any evidence of this buffering. Thus, I would suggest adding more information on how this buffering or protection from males might manifest (for example, listing male behaviours that might showcase this protection) or referencing other studies that support this claim. Another example of this can be found in lines 223-224, which suggests that females choose lower-ranking individuals when they are presented with a larger pool of competitors; however, in lines 227-228, it's stated that this result contradicts previous work in baboons, which makes the previous claim seem unjustified. I recommend adding other examples from studies that support the results of this paper and adding a line that addresses reasons why these differences between gorillas and baboons might be caused (for example, different social dynamics or ecological constraints). In addition, I suggest the inclusion of physiological data such as direct measures of energy expenditure, caloric intake, or hormone levels, as it would strengthen the claims made in the second paragraph of the discussion. However, I understand this might not be possible due to data or time constraints, so I suggest adding more robust justification on why lactation and pregnancy were used as a proxy for energetic need. In the methods (lines 127-128), it is unclear which phase of the pregnancy or lactation is more energetically demanding. I would also suggest adding a comment on the limitations of using reproductive state to infer energetic need. Lastly, if the data is available, I believe it would be interesting to add body size and age of the females or the size difference between aggressor and target as explanatory variables in the models to test if physiological characteristics influence female-on-female aggression.

Male support:

We have now added more references (Watts 1994, 1997) and enriched our arguments regarding male presence buffering aggression. Previous research suggests that male gorillas may support lower-ranking females and they may intervene in female-female conflicts (Sicotte 2002). Unfortunately, our dataset did not allow us to test for male protection. We conduct proximity scans every 10 minutes and these scans are not associated to each interaction, meaning that we cannot reliably test if proximity to a male influences the likelyhood to receive aggression.

Number of competitors and choice of weaker competitors:

We added a very relevant reference in humans, showing that people choose weaker competitors when they have they can choose. We removed the example to baboons because it used sex ratio and the relevance to our study was not that straightforward.

Reproductive state as a proxy for energetic needs:

We now mention clearly that reproductive state is an indirect measure of energetic needs.

We rephrased our methods to: “Lactation is often considered more energetically demanding than pregnancy as a whole but the latest stages of pregnancy are highly energetically demanding, potentially even more than lactation”

Unfortunately, we do not have access to physiological and body size data. Regarding female age, for many females, ages are estimates with errors up to a decade, and thus, we choose not to use them as a reliable predictor. Having accurate values for all these variables, would indeed be very valuable and improve the predicting power of our study.

Recommendations for writing and presentation:

Overall, the manuscript is well-organised and well-written, but there are certain areas that could improve in clarity. In the introduction, I believe that the term 'aggression heuristic' should be introduced earlier and properly defined in order to accommodate a broader audience. The main question and aims of the study are not stated clearly in the last paragraph of the introduction. In the methods, I think it would improve the clarity to add a table for the classification of each type of agonistic interactions instead of naming them in the text. For example, a table that showcase the three intensity categories (severe, mild and moderate), than then dives into each behaviour (e.g. hit, bite, attack, etc.) and a short description of these behaviours, I think this would be helpful since some of the behaviours mentioned can be confusing (what's the difference between attack, hit and fight?). In addition, in line 104, it states that all interactions were assigned equal intensity, which needs to be explained.

We now define aggression heuristics in both the abstract and the first paragraph of the introduction. We have also explained aggressive interactions that their nature was not obvious from their names. Hopefully, these explanations make clear the differences among the recorded behaviours.

We have now specified that the “equal intensity” refers to avoidances and displacements used to infer power relationships: “We assigned to all avoidance/displacement interactions equal intensity, that is, equal influence to the power relationship of the interacting individuals”

Minor corrections:

(1) In line 41, there is a 1 after 'similar'. I am unsure if it's a mistake or a reference.

We corrected the typo.

(2) In lines 68-69, there is mention of other studies, but no references are provided.

We added citations as suggested.

(3) Remove the reference to Figure 1 (line 82) from the introduction; the figure should be referenced in the text just before the image, however, your figure is in a different section.

We removed the reference as suggested.

(4) Line 98 and 136, it's written 'ad libtum' but the correct spelling is 'ad libitum'.

We corrected the typo.

(5) Figure 3, remove the underscores between the words in the axis titles.

We removed the underscores.

Reviewer #2 (Recommendations for the authors):

Here, I have outlined some specific suggestions that require attention. Addressing these comments will enhance the readability and enhance the quality of the manuscript.

(1) L69. Add citation here, indicating the studies focusing on aggression rates.

We added citations as suggested.

(2) L88. The study periods used in this study and the authors' previous study (Reference 11) are different. So please add one table as Table 1 showing the details info on the sampling efforts and data included in their analysis of this study. For example, the study period, the numbers of females and males, sampling hours, the number of avoidance/displacement behaviors used to calculate individual Elo-ratings, and the number of mild/moderate/severe aggressive interactions, etc.

We have now added another table, as suggested (new Table 1) and we have also made clear that we used the hierarchies presented in detail in (Smit & Robbins 2025).

(3) L103. If readers do not look over Reference 25 on purpose, they do not know what the authors want to talk about and why they mention the optimized Elo-rating method. Clarify this statement and add more content explaining the differences between the two methods, or just remove it.

We rephrased the text and in response to the previous comment, we clearly state that there are more details about our approach in Smit & Robbins 2025. At the end of the relevant sentence, we added the following parenthesis “(see “traditional Elo rating method”; we do not use the “optimized Elorating method” as it yields similar results and it is not widely used)” and we removed the sentence referring to the optimized Elo-rating method.

(4) L110. Here, the authors stated that the individual with the standardized Elo-score 1 was the highest-ranking. L117, the "aggression direction" score of each aggressive interaction was the standardized Elo-score of the aggressor, subtracting that of the recipient. So, when the "aggression direction" score was 1, it should mean that the aggressor was the highest-ranking and the recipient was the lowest-ranking female. This is not as the authors stated in L117-120 (where the description was incorrectly reversed). Please clarify.

The highest ranking individual has indeed Elo_score equal to 1 and we calculated the interaction score (or "aggression direction score") of each aggressive interaction by subtracting the standardized Elo-score of the aggressor from that of the recipient (Elo_recepient – Elo_aggressor). So, when the aggressor is the lowest-ranking female (Elo_score=0) and the recipient the highestranking female one (Elo_score=1), the "aggression direction score" is 1-0 = 1.

(5) Regarding point 3 of the Public Review, please also revise/expand the paragraph L193-208 in the Discussion section accordingly.

Please see our response to the public review. We have enriched the results section, added pairwise comparisons in a new table (Table 2) and modified the discussion accordingly.

(6) Table 1. It's not clear why authors added the column 'Aggression Rate' but did not provide any explanation in the Methods/Results section. How did they calculate the correlation between each tested variable and the "overall adult female aggression rates"? Correlating the number of females in the first trimester of female pregnancy with the female aggression rates in each study group? What did the correlation coefficients mean? L202-204 may provide some hints as to why the authors introduced the Aggression Rate. But it should be made clear in the previous text.

We now added more details in the legend of the table to make our point clear: “To highlight that aggression rates can increase due to increase in interactions of different score, we also include the effect of some of the tested variables on overall adult female aggression rates, based on results of linear mixed effects models from (Smit & Robbins 2024).”  We did not include detailed methods to calculate those results because they are detailed in (Smit & Robbins 2024). We find it valuable to show the results of both aggression rates and aggression directionality according to the same predictor variables as a means to clarify that aggression rates and aggression directionality are not always coordinated to one another (they do not always change in a consistent manner relative to one another).

(7) L166.This is not rigorous. Please rephrase. There is only one western gorilla group containing only one resident male included in the analysis.

We have toned down our text: “Our results did not show any significant difference between femalefemale aggression patterns within the one western and four mountain gorillas groups”

(8) L167. I don't think the interaction scores in the third trimester of female pregnancy were significantly higher than those in the first trimester. The same concern applies in L194-195.

We have now added a new table with post hoc pairwise comparisons among the different reproductive states that clarifies that.

(9) L202. There is no column 'Aggression rates' in Table 1 of Reference 11.

We have rephrased to make clear that we refer to Table 1 of the present study.

(10) L204-205. Reference 49. Maybe not a proper citation here. This claim requires stronger evidence or further justification. Additionally, please rephrase and clarify the arguments in L204208 for better readability and precision.

We have added three more references and rephrased to clarify our argument.

Reviewer #3 (Recommendations for the authors):

(1) Line 41: The word "similar" is misspelled.

We corrected the typo.

eLife Assessment

This work investigates ZC3H11A as a cause of high myopia through the analysis of human data and experiments with genetic knockout of Zc3h11a in mouse, providing a useful model of myopia. The evidence supporting the conclusion is still incomplete in the revised manuscript as the concerns raised in the previous review were not fully addressed. The article would benefit from a more robust genetic analysis and comprehensive presentation of human phenotypic data to clarify the modes of inheritance in the families, currently limited by loss of patient follow-up and addressing whether there is a reduction in bipolar cell number or decreased marker protein expression through cell counts or quantifiable, less saturated Western blots. The work will be of interest to ophthalmologists and researchers working on myopia

Reviewer #1 (Public Review):

The authors reported that mutations were identified in the ZC3H11A gene in four adolescents from 1015 high myopia subjects in their myopia cohort. They further generated Zc3h11a knockout mice utilizing the CRISPR/Cas9 technology.

The main claims are only partially supported. The reviewers still have the concerns of 1) the modes of inheritance for the families need to be shown; 2) the phenotype of heterozygous mutant mice is too weak; 3) the authors still have not addressed the biological question of whether there are fewer bipolar cells or decreased expression of the marker protein. This would involve counting cells, which they have not done. The blots they show do not appear to support their quantifications. Considering the sensitivity of quantifying nearly saturated blots, the authors should show blots that are not exposed to that level of saturation.

eLife Assessment

This important study provides convincing evidence that the Kinesin protein family member KIF7 regulates the development of the cerebral cortex and its connectivity and the specificity of Sonic Hedgehog signaling by controlling the details of Gli repressor vs activator functions. This study provides new insights into general aspects of cortical development.

Reviewer #1 (Public review):

Summary:

This is an interesting follow-up to a paper published in Human Molecular Genetics reporting novel roles in corticogenesis of the Kif7 motor protein that can regulate the activator as well as the repressor functions of the Gli transcription factors in Shh signalling. This new work investigates how a null mutation in the Kif7 gene affects the formation of corticofugal and thalamocortical axon tracts and the migration of cortical interneurons. It demonstrates that Kif7 null mutant embryos present with ventriculomegaly and heterotopias as observed in patients carrying KIF7 mutations. The Kif7 mutation also disrupts the connectivity between cortex and thalamus and leads to an abnormal projection of thalamocortical axons. Moreover, cortical interneurons show migratory defects that are mirrored in cortical slices treated with the Shh inhibitor cyclopamine suggesting that the Kif7 mutation results in a down-regulation of Shh signalling. Interestingly, these defects are much less severe at later stages of corticogenesis.

Strengths/weaknesses:

The findings of this manuscript are clearly presented and are based on detailed analyses. Using a compelling set of experiments, especially the live imaging to monitor interneuron migration, the authors convincingly investigate Kif7's roles and their results support their major claims. The migratory defects in interneurons and the potential role of Shh signalling present novel findings and provide some mechanistic insights but rescue experiments would further support Kif7's role in interneuron migration. Similarly, the mechanism underlying the misprojection which has previously been reported in other cilia mutants remains unexplored. Taken together, this manuscript makes novel contributions to our understanding of the role of primary cilia in forebrain development and to the aetiology of the neural symptons in ciliopathy patients.

Comments on revisions:

The authors addressed most of the points I raised in my original review.

Reviewer #2 (Public review):

Summary:

This study investigates the role of KIF7, a ciliary kinesin involved in the Sonic Hedgehog (SHH) signaling pathway, in cortical development using Kif7 knockout mice. The researchers examined embryonic cortex development (mainly at E14.5), focusing on structural changes and neuronal migration abnormalities.

Strengths:

(1) The phenotype observed is interesting, and the findings provide neurodevelopmental insight into some of the symptoms and malformations seen in patients with KIF7 mutations.

(2) The authors assess several features of cortical development, including structural changes in layers of the developing cortex, connectivity of the cortex with thalamus, as well as migration of cINs from CGE and MGE to cortex.

Comments on revisions:

The authors have made significant and thoughtful responses as well as experimental additions to the authors comments. Their efforts are appreciated and the manuscript is much improved.

Author response:

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

Reviewer #1 (Recommendations for the authors):

(1) I am not convinced by the figures the authors present on Shh protein expression. The "bright tiny dots" of Shh protein in the cortex are not visible on the images in Figure 7. I wonder whether the authors could present higher magnification and/or black and white images with increased contrast.

We have modified Figure 7: we now present a higher magnification and a black and white image with increased contrast to better visualize SHH (+) bright tiny dots in the lateral cortex.

(2)The manuscript also contains several typos.

We apologize for these mistakes which have all been corrected.

eLife Assessment

This study presents useful findings on the application of HPV cfDNA as a marker for monitoring treatment response and prognosis in patients with recurrent or metastatic cervical cancer. The evidence supporting the claims of the authors is solid, although inclusion of a larger number of patient samples would have strengthened the study. The work will be of interest to medics and biologists working on cervical cancer.

Reviewer #1 (Public review):

Summary:

The study by Zhuomin Yin and colleagues focuses on the relationship between cell-free HPV (cfHPV) DNA and metastatic or recurrent cervical cancer patients. It expands the application of cfHPV DNA in tracking disease progression and evaluating treatment response in cervical cancer patients. The study is overall well-designed, including appropriate analyses.

Strengths:

The findings provide valuable reference points for monitoring drug efficacy and guiding treatment strategies in patients with recurrent and metastatic cervical cancer. The concordance between HPV cfDNA fluctuations and changes in disease status suggests that cfDNA could play a crucial role in precision oncology, allowing for more timely interventions. As with similar studies, the authors used Droplet Digital PCR to measure cfDNA copy numbers, a technique that offers ultrasensitive nucleic acid detection and absolute quantification, lending credibility to the conclusions.

Weaknesses:

Despite including 28 clinical cases, only 7 involved recurrent cervical cancer, which may not be sufficient to support some of the authors' conclusions fully. Future studies on larger cohorts could solidify HPV cfDNA's role as a standard in the personalized treatment of recurrent cervical cancer patients.

Comments on revisions:

Thanks for your additional efforts and for addressing my concerns.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public review):

Summary:

The study "Monitoring of Cell-free Human Papillomavirus DNA in Metastatic or Recurrent Cervical Cancer: Clinical Significance and Treatment Implications" by Zhuomin Yin and colleagues focuses on the relationship between cell-free HPV (cfHPV) DNA and metastatic or recurrent cervical cancer patients. It expands the application of cfHPV DNA in tracking disease progression and evaluating treatment response in cervical cancer patients. The study is overall well-designed, including appropriate analyses.

Strengths:

The findings provide valuable reference points for monitoring drug efficacy and guiding treatment strategies in patients with recurrent and metastatic cervical cancer. The concordance between HPV cfDNA fluctuations and changes in disease status suggests that cfDNA could play a crucial role in precision oncology, allowing for more timely interventions. As with similar studies, the authors used Droplet Digital PCR to measure cfDNA copy numbers, a technique that offers ultrasensitive nucleic acid detection and absolute quantification, lending credibility to the conclusions.

Weaknesses:

Despite including 28 clinical cases, only 7 involved recurrent cervical cancer, which may not be sufficient to support some of the authors' conclusions fully. Future studies on larger cohorts could solidify HPV cfDNA's role as a standard in the personalized treatment of recurrent cervical cancer patients.

(1) The authors should provide source data for Figures 2, 3, and 4 as supplementary material.

We greatly appreciate your evaluation of our study and fully agree with the limitations you have pointed out. We appreciate your constructive feedback. Based on your suggestions, we have made the following additions to the article. We have realized that the information provided in Figures 2, 3, and 4 is limited. Therefore, we have presented the original data from Figures 2, 3, and 4 in tabular form in Supplementary Table 2.

(2) Description of results in Figure 2: Figure 2 would benefit from clearer annotations regarding HPV virus subtypes. For example, does the color-coding in Figure 2B imply that all samples in the LR subgroup are of type HPV16? If that is the case, is it possible that detection variations are due to differences in subtype detection efficiency rather than cfDNA levels? The authors should clarify these aspects. Annotation of Figure 2B suggests that the p-value comes from comparing the LR and LN + H + DSM groups. This should be clarified in the legend. If this p-value comes from comparing HPV cfDNA copies for the (LR, LNM, HM) and (LN + HM, LN + HM + DSM) groups, did the authors carry out post-hoc pairwise comparisons? It would be helpful to include acronyms for these groups in the legend also.

We fully agree with your point regarding the need for clearer labeling of HPV genotypes in Figures 2B and 2C. If each data point could be color-coded to represent the HPV genotype, Figures 2B and 2C would be clearer and provide more information. However, we must acknowledge that due to the limitations of our current graphing software and our graphical expertise, we were unable to fully represent each HPV genotype in the figures. To address this, we have presented the data in Supplementary Table 2. This table shows the HPV genotype for each patient, the corresponding metastasis patterns, and the baseline HPV copy numbers. We hope this will address the limitation of insufficient information in Figure 2.

The point you raised regarding whether the differences in detection results might stem from variations in subtype detection efficiency rather than cfDNA levels is a valid limitation of this study. Due to the limited sample size, we did not perform subgroup analyses based on different HPV genotypes, which may have introduced bias in the results presented in Figures 2B and 2C. In response, we have added the following clarification in the discussion section (lines 416-422) and addressed this limitation in the limitations section (lines 499-502). Based on your suggestion, we believe that it is essential to expand the sample size and perform subgroup analysis of the baseline copy numbers for each HPV genotype before treatment. We hope to achieve this goal in future studies.

Thank you for your thoughtful comments regarding the statistical analyses in the study. The p-value in Figure 2B comes from the comparison among five groups, using a two-sided Kruskal-Wallis test. Your suggestion to perform post-hoc pairwise comparisons is excellent and has made the data presentation in the article more rigorous. Following your advice, we conducted pairwise comparisons between the groups. We used the Mann-Whitney U test to compare HPV cfDNA copy numbers between two groups. Since the LR group only had one value, it could not be included in the pairwise comparisons. Significant differences were observed in two comparisons: LNM vs. LN + H + DSM (P = 0.006) and HM vs. LN + H + DSM (P = 0.036). No significant differences were found between the other groups: LNM vs. HM (P = 0.768), LNM vs. LN + HM (P = 0.079), HM vs. LN + HM (P = 0.112), and LN + HM vs. LN + H + DSM (P = 0.145), as determined by the Mann-Whitney U test  (Figure 2B). (Lines 258-263).

Thank you for your thoughtful suggestion regarding the inclusion of group acronyms in the legends of Figures 2B and 2C. Including the full names corresponding to the abbreviations would indeed enhance clarity. While we attempted to add both acronyms and full names to the figure legend, the full names were too lengthy and impacted the figure's presentation. Therefore, we have provided the full names corresponding to the abbreviations in the figure caption below, to help readers easily understand the abbreviations used in the figure.

(3) Interpretation of results in Figure 2 and elsewhere: Significant differences detected in Figure 2B could imply potential associations between HPV cfDNA levels (or subtypes) and recurrence/metastasis patterns. Figure 2C shows that there is a difference in cfDNA levels between the groups compared, suggesting an association but this would not necessarily be a direct "correlation". Overall, interpretation of statistical findings would benefit from more precise language throughout the text and overstatement should be avoided.

Thank you for your insightful comments regarding the interpretation of results in Figure 2 and elsewhere. We acknowledge that there are several limitations in this study, and the interpretation of the results should be more careful and cautious. Indeed, in the results section, there were issues with inaccurate wording and exaggeration. We have made revisions in the discussion section, which are presented as follows: Preliminary results indicate that baseline HPV cfDNA levels may be linked to recurrence/metastasis patterns, potentially reflecting tumor burden and spread (Lines 411-413). Additionally, we have also made changes in the conclusion section, which are presented as follows: The baseline copy number of HPV cfDNA may be associated with metastatic patterns, thereby reflecting tumor burden and the extent of spread to some extent (Lines 511-513).

(4) The authors state that six patients showed cfDNA elevation with clinically progressive disease, yet only three are represented in Figure 3B1 under "Patients whose disease progressed during treatment." What is the expected baseline variability in cfDNA for patients? If we look at data from patients with early-stage cancer would we see similar fluctuations? And does the degree of variability vary for different HPV subtypes? Without understanding the normal fluctuations in cfDNA levels, interpreting these changes as progression indicators may be premature.

Thank you for your feedback. We appreciate your thorough review and attention to detail. Six cervical squamous cell carcinoma (SCC) patients exhibited elevated HPV cfDNA levels as their clinical condition progressed. In the previous Figures 3A1 and 3A2, we only presented data from three patients, as we initially believed that displaying the cfDNA curves from three patients would offer a clearer view, while including six patients might lead to overlap and reduce clarity. However, this may have caused confusion for readers. Based on your suggestion, we have revised Figure 3A1 to include the cfDNA curves for all six patients who with squamous cell carcinoma who experienced clinical disease progression during treatment (Figure 3A1), along with the corresponding SCC-Ag curves (Figure 3A2).

Thank you for highlighting the issue of baseline variability in HPV cfDNA. This is indeed a limitation of our study, which did not address this aspect. If baseline variability is defined as changes in HPV cfDNA levels measured at different time points before treatment in the same patient, fluctuations at different time points are inevitable and objective. Following your suggestion, we have added a discussion on baseline variability in the limitations section of the manuscript to provide readers with a more objective understanding of our study's findings (Lines 501-502).In future studies, we will incorporate baseline variability into the research design to better understand pre-treatment HPV cfDNA fluctuations and provide support for clinical decision-making.

(5) It would be helpful if where p-values are given, the test used to derive these values was also stated within parentheses e.g. (P < 0.05, permutation test with Benjamini-Hochberg procedure).

Thank you for your valuable suggestions and examples. Following your advice, we have included the statistical test methods used to obtain the p-values in parentheses wherever they appear in the results section. Additionally, we have specified the statistical test methods for the p-values below the figures in the results section.

Reviewer #2 (Public review):

Summary:

The authors conducted a study to evaluate the potential of circulating HPV cell-free DNA (cfDNA) as a biomarker for monitoring recurrent or metastatic HPV+ cervical cancer. They analyzed serum samples from 28 patients, measuring HPV cfDNA levels via digital droplet PCR and comparing these to squamous cell carcinoma antigen (SCC-Ag) levels in 26 SCC patients, while also testing the association between HPV cfDNA levels and clinical outcomes. The main hypothesis that the authors set out to test was whether circulating HPV cfDNA levels correlated with metastatic patterns and/or treatment response in HPV+ CC.

The main claims put forward by the paper are that:

(1) HPV cfDNA was detected in all 28 CC patients enrolled in the study and levels of HPV cfDNA varied over a median 2-month monitoring period.

(2) 'Median baseline' HPV cfDNA varied according to 'metastatic pattern' in individual patients.

(3) Positivity rate for HPV cfDNA was more consistent than SCC-Ag.

(4) In 20 SCC patients monitored longitudinally, concordance with changes in disease status was 90% for HPV cfDNA.

This study highlights HPV cfDNA as a promising biomarker with advantages over SCC-Ag, underscoring its potential for real-time disease surveillance and individualized treatment guidance in HPV-associated cervical cancer.

Strengths:

This study presents valuable insights into HPV+ cervical cancer with potential translational significance for management and guiding therapeutic strategies. The focus on a non-invasive approach is particularly relevant for women's cancers, and the study exemplifies the promising role of HPV cfDNA as a biomarker that could aid personalized treatment strategies.

Weaknesses:

While the authors acknowledge the study's small cohort and variability in sequential sampling protocols as a limitation, several revisions should be made to ensure that (1) the findings are presented in a way that aligns more closely with the data without overstatement and (2) that the statistical support for these findings is made more clear. Specific suggestions are outlined below.

(1) Line 54 in the abstract refers to 'combined multiple-metastasis pattern' but it is not clear what this refers to at this point in the text.

Thank you for your detailed feedback. You are correct that the "combined multi-metastatic pattern" was not adequately explained in the abstract, which may have caused confusion. To address this, we have clarified the definitions of the combined multi-metastatic pattern and single-metastatic pattern in lines 53-55 of the manuscript. Patients with a combined multi-metastatic pattern (lymph node + hematogenous ± diffuse serosal metastasis)  exhibited a higher median baseline HPV cfDNA level compared to those with a single-metastasis pattern (local recurrence, lymph node metastasis, or hematogenous metastasis) (P = 0.003).

(2) Line 90 The reference to 'prospective clinical study (NCT03175848) in primary stage IVB CC to investigate the role of radiotherapy (RT) in combination therapy' seems not to be at all relevant at this point in the text. I would limit the description of this study to the methods.

Thank you for your thoughtful and thorough review. Your suggestions are highly relevant. Upon further reflection, we recognized that this sentence was redundant in its original placement. Following your recommendation, we have removed it from this section and moved it to the methods section (Lines 109-111). The revised statement is as follows: "Notably, 19 cases from the primary CC group participated in our prospective clinical study (NCT03175848), focused on stage IVB cervical cancer."

(3) Line 56 refers to HPV cfDNA levels (range 0.3-16.9) but what units?

Thank you for your feedback regarding the manuscript format. While you highlighted this specific issue, we have since identified several other instances of omitted units in parentheses throughout the manuscript. We acknowledge that such formatting oversights can create ambiguity for readers. Following your suggestions, we have corrected all such issues in the manuscript. We greatly appreciate your careful and thorough review.

(4) Lines 247-248 claim that higher baseline HPV cfDNA levels correlated with a more substantial post-chemotherapy decrease. This correlation should be statistically validated, and the p-value should be included.

Thank you for your insightful comments, which highlighted an issue with this sentence. Upon review, I have made the necessary revisions. Since no statistical analysis was conducted and the P-value was not provided, the original sentence was imprecise. Given the small sample size, statistical analysis is not feasible. I have revised the sentence as follows: “For patients in whom systemic cytotoxic chemotherapy was effective, a significant decrease in HPV cfDNA levels could be detected after chemotherapy” (Lines 297-298).

(5) The authors mention that baseline samples were collected "between Day -14 and Day +30 preceding initial treatment." If Day -14 indicates two weeks before treatment, then this would imply some samples were taken up to 30 days post-treatment. This notation should be clarified. To what extent might outliers or more extreme values in Figure 2 driven by variability in how baseline sampling was carried out?

Thank you for your insightful comments. Undoubtedly, this is indeed a major limitation of our study. These factors could lead to a certain degree of bias in the detection data. The primary reason is that the study was conducted during the COVID-19 pandemic, making it sometimes difficult to conduct sampling regularly. In accordance with your suggestion, I have already added this part of the content to the results section of the article (Lines 266-275). We have also included the variation in baseline sampling as a limitation in the discussion section (Lines 497-499). In future studies, we will strive to improve the study design by ensuring baseline samples are collected prior to treatment, thereby enhancing the reliability of statistical and analytical results.

(6) Would be useful to amend Figure 1 to show a subset of patients with SCC and a subset of patients who underwent longitudinal monitoring.

Thank you for your detailed suggestion. Including a subset of pathological types could indeed add more information to Figure 1. However, regarding the pathological types of the patients in this group, we have listed them in Table 1 and Supplementary Table 2. Among the 28 patients, 26 are diagnosed with squamous cell carcinoma, so 92.9% of the patients in this study have squamous cell carcinoma. To avoid making Figure 1 too complex, we decided not to include the pathological type in the figure.

(7) Line 120 "a time point matching or closely following HPV cfDNA sampling" - what is the time range for 'closely following' here? A couple of hours or days after sampling?

Thank you for your detailed feedback. Based on your suggestion, we have revised the sentence as follows:

"For patients with squamous cell CC in the sequential sampling group, concurrent SCC-Ag testing was performed at a time point that matched, or was within 7 days before or after, the HPV cfDNA sampling." (Line 123-125)

(8) Lines 178-190 and lines 179-180 seem to make exactly the same point.

Thank you very much for your careful review. Indeed, these two sentences were repetitive and conveyed the same point. I have removed the previous sentence here (lines 206-207).

(9) In Figure 4, please indicate the number of patients in each group in the legend e.g. HPV16+ (n=x number of patients).

Thank you for your feedback on the details of Figure 4 and the examples provided. We have updated Figure 4 according to your suggestions and included the number of patients in each group in the figure legend.

(10) Lines 322-3 'HPV cfDNA predicted treatment response or disease progression at an earlier time point than imaging assessments' - based on the data available and the numbers of patients, I would argue that this is too bold a claim.

Thank you very much for pointing out this issue. We fully agree with your view. We have modified this sentence as follows: "Secondly, dynamically monitored HPV cfDNA levels appeared to predict treatment response and disease progression. " (Lines 391-392).

eLife Assessment

This valuable study introduces a modern and accessible PyTorch reimplementation of the widely used SpliceAI model for splice site prediction. The authors provide solid evidence that their OpenSpliceAI implementation matches the performance of the original while improving usability and enabling flexible retraining across species. These advances are likely to be of broad interest to the computational genomics community.

Reviewer #1 (Public review):

Summary:

Chao et al. produced an updated version of the SpliceAI package using modern deep learning frameworks. This includes data preprocessing, model training, direct prediction, and variant effect prediction scripts. They also added functionality for model fine-tuning and model calibration. They convincingly evaluate their newly trained models against those from the original SpliceAI package and investigate how to extend SpliceAI to make predictions in new species. While their comparisons to the original SpliceAI models are convincing on the grounds of model performance, their evaluation of how well the new models match the original's understanding of non-local mutation effects is incomplete. Further, their evaluation of the new calibration functionality would benefit from a more nuanced discussion of what set of splice sites their calibration is expected to hold for, and tests in a context for which calibration is needed.

Strengths:

(1) They provide convincing evidence that their new implementation of SpliceAI matches the performance of the original model on a similar dataset while benefiting from improved computational efficiencies. This will enable faster prediction and retraining of splicing models for new species as well as easier integration with other modern deep learning tools.

(2) They produce models with strong performance on non-human model species and a simple, well-documented pipeline for producing models tuned for any species of interest. This will be a boon for researchers working on splicing in these species and make it easy for researchers working on new species to generate their own models.

(3) Their documentation is clear and abundant. This will greatly aid the ability of others to work with their code base.

Weaknesses:

(1) The authors' assessment of how much their model retains SpliceAI's understanding of "non-local effects of genomic mutations on splice site location and strength" (Figure 6) is not sufficiently supported. Demonstrating this would require showing that for a large number of (non-local) mutations, their model shows the same change in predictions as SpliceAI or that attribution maps for their model and SpliceAI are concordant even at distances from the splice site. Figure 6A comes close to demonstrating this, but only provides anecdotal evidence as it is limited to 2 loci. This could be overcome by summarizing the concordance between ISM maps for the two models and then comparing across many loci. Figure 6B also comes close, but falls short because instead of comparing splicing prediction differences between the models as a function of variants, it compares the average prediction difference as a function of the distance from the splice site. This limits it to only detecting differences in the model's understanding of the local splice site motif sequences. This could be overcome by looking at comparisons between differences in predictions with mutants directly and considering non-local mutants that cause differences in splicing predictions.

(2) The utility of the calibration method described is unclear. When thinking about a calibrated model for splicing, the expectation would be that the models' predicted splicing probabilities would match the true probabilities that positions with that level of prediction confidence are splice sites. However, the actual calibration that they perform only considers positions as splice sites if they are splice sites in the longest isoform of the gene included in the MANE annotation. In other words, they calibrate the model such that the model's predicted splicing probabilities match the probability that a position with that level of confidence is a splice site in one particular isoform for each gene, not the probability that it is a splice site more broadly. Their level of calibration on this set of splice sites may very well not hold to broader sets of splice sites, such as sites from all annotated isoforms, sites that are commonly used in cryptic splicing, or poised sites that can be activated by a variant. This is a particularly important point as much of the utility of SpliceAI comes from its ability to issue variant effect predictions, and they have not demonstrated that this calibration holds in the context of variants. This section could be improved by expanding and clarifying the discussion of what set of splice sites they have demonstrated calibration on, what it means to calibrate against this set of splice sites, and how this calibration is expected to hold or not for other interesting sets of splice sites. Alternatively, or in addition, they could demonstrate how well their calibration holds on different sets of splice sites or show the effect of calibrating their models against different potentially interesting sets of splice sites and discuss how the results do or do not differ.

(3) It is difficult to assess how well their calibration method works in general because their original models are already well calibrated, so their calibration method finds temperatures very close to 1 and only produces very small and hard to assess changes in calibration metrics. This makes it very hard to distinguish if the calibration method works, as it doesn't really produce any changes. It would be helpful to demonstrate the calibration method on a model that requires calibration or on a dataset for which the current model is not well calibrated, so that the impact of the calibration method could be observed.

Reviewer #2 (Public review):

Summary:

The paper by Chao et al offers a reimplementation of the SpliceAI algorithm in PyTorch so that the model can more easily/efficiently be retrained. They apply their new implementation of the SpliceAI algorithm, which they call OpenSpliceAI, to several species and compare it against the original model, showing that the results are very similar and that in some small species, pre-training on other species helps improve performance.

Strengths:

On the upside, the code runs fine, and it is well documented.

Weaknesses:

The paper itself does not offer much beyond reimplementing SpliceAI. There is no new algorithm, new analysis, new data, or new insights into RNA splicing. There is no comparison to many of the alternative methods that have since been published to surpass SpliceAI. Given that some of the authors are well-known with a long history of important contributions, our expectations were admittedly different. Still, we hope some readers will find the new implementation useful.

Reviewer #3 (Public review):

Summary:

The authors present OpenSpliceAI, a PyTorch-based reimplementation of the well-known SpliceAI deep learning model for splicing prediction. The core architecture remains unchanged, but the reimplementation demonstrates convincing improvements in usability, runtime performance, and potential for cross-species application.

Strengths:

The improvements are well-supported by comparative benchmarks, and the work is valuable given its strong potential to broaden the adoption of splicing prediction tools across computational and experimental biology communities.

Major comments:

Can fine-tuning also be used to improve prediction for human splicing? Specifically, are models trained on other species and then fine-tuned with human data able to perform better on human splicing prediction? This would enhance the model's utility for more users, and ideally, such fine-tuned models should be made available.

Author response:

Reviewer #1 (Public review):

Summary:

Chao et al. produced an updated version of the SpliceAI package using modern deep learning frameworks. This includes data preprocessing, model training, direct prediction, and variant effect prediction scripts. They also added functionality for model fine-tuning and model calibration. They convincingly evaluate their newly trained models against those from the original SpliceAI package and investigate how to extend SpliceAI to make predictions in new species. While their comparisons to the original SpliceAI models are convincing on the grounds of model performance, their evaluation of how well the new models match the original's understanding of non-local mutation effects is incomplete. Further, their evaluation of the new calibration functionality would benefit from a more nuanced discussion of what set of splice sites their calibration is expected to hold for, and tests in a context for which calibration is needed.

Strengths:

(1) They provide convincing evidence that their new implementation of SpliceAI matches the performance of the original model on a similar dataset while benefiting from improved computational efficiencies. This will enable faster prediction and retraining of splicing models for new species as well as easier integration with other modern deep learning tools.

(2) They produce models with strong performance on non-human model species and a simple, well-documented pipeline for producing models tuned for any species of interest. This will be a boon for researchers working on splicing in these species and make it easy for researchers working on new species to generate their own models.

(3) Their documentation is clear and abundant. This will greatly aid the ability of others to work with their code base.

We thank the reviewer for these positive comments.  

Weaknesses:

(1) The authors' assessment of how much their model retains SpliceAI's understanding of "nonlocal effects of genomic mutations on splice site location and strength" (Figure 6) is not sufficiently supported. Demonstrating this would require showing that for a large number of (non-local) mutations, their model shows the same change in predictions as SpliceAI or that attribution maps for their model and SpliceAI are concordant even at distances from the splice site. Figure 6A comes close to demonstrating this, but only provides anecdotal evidence as it is limited to 2 loci. This could be overcome by summarizing the concordance between ISM maps for the two models and then comparing across many loci. Figure 6B also comes close, but falls short because instead of comparing splicing prediction differences between the models as a function of variants, it compares the average prediction difference as a function of the distance from the splice site. This limits it to only detecting differences in the model's understanding of the local splice site motif sequences. This could be overcome by looking at comparisons between differences in predictions with mutants directly and considering non-local mutants that cause differences in splicing predictions.

We agree that two loci are insufficient to demonstrate preservation of non-local effects. To address this, we have extended our analysis to a larger set of sites: we randomly sampled 100 donor and 100 acceptor sites, applied our ISM procedure over a 5,001 nt window centered at each site for both models, and computed the ISM map as before. We then calculated the Pearson correlation between the collection of OSAI_MANE and SpliceAI ISM importance scores. We also created 10 additional ISM maps similar to those in Figure 6A, which are now provided in Figure S23.

Follow is the revised paragraph in the manuscript’s Results section:

First, we recreated the experiment from Jaganathan et al. in which they mutated every base in a window around exon 9 of the U2SURP gene and calculated its impact on the predicted probability of the acceptor site. We repeated this experiment on exon 2 of the DST gene, again using both SpliceAI and OSAI_MANE . In both cases, we found a strong similarity between the resultant patterns between SpliceAI and OSAI_MANE , as shown in Figure 6A. To evaluate concordance more broadly, we randomly selected 100 donor and 100 acceptor sites and performed the same ISM experiment on each site. The Pearson correlation between SpliceAI and OSAI_MANE yielded an overall median correlation of 0.857 (see Methods; additional DNA logos in Figure S23). 

To characterize the local sequence features that both models focus on, we computed the average decrease in predicted splice-site probability resulting from each of the three possible singlenucleotide substitutions at every position within 80bp for 100 donor and 100 acceptor sites randomly sampled from the test set (Chromosomes 1, 3, 5, 7, and 9). Figure 6B shows the average decrease in splice site strength for each mutation in the format of a DNA logo, for both tools.

We added the following text to the Methods section:

Concordance evaluation of ISM importance scores between OSAI_MANE and SpliceAI

To assess agreement between OSAI_MANE and SpliceAI across a broad set of splice sites, we applied our ISM procedure to 100 randomly chosen donor sites and 100 randomly chosen acceptor sites. For each site, we extracted a 5,001 nt window centered on the annotated splice junction and, at every coordinate within that window, substituted the reference base with each of the three alternative nucleotides. We recorded the change in predicted splice-site probability for each mutation and then averaged these Δ-scores at each position to produce a 5,001-score ISM importance profile per site.

Next, for each splice site we computed the Pearson correlation coefficient between the paired importance profiles from ensembled OSAI_MANE and ensembled SpliceAI. The median correlation was 0.857 for all splice sites. Ten additional zoom-in representative splice site DNA logo comparisons are provided in Supplementary Figure S23.

(2) The utility of the calibration method described is unclear. When thinking about a calibrated model for splicing, the expectation would be that the models' predicted splicing probabilities would match the true probabilities that positions with that level of prediction confidence are splice sites. However, the actual calibration that they perform only considers positions as splice sites if they are splice sites in the longest isoform of the gene included in the MANE annotation. In other words, they calibrate the model such that the model's predicted splicing probabilities match the probability that a position with that level of confidence is a splice site in one particular isoform for each gene, not the probability that it is a splice site more broadly. Their level of calibration on this set of splice sites may very well not hold to broader sets of splice sites, such as sites from all annotated isoforms, sites that are commonly used in cryptic splicing, or poised sites that can be activated by a variant. This is a particularly important point as much of the utility of SpliceAI comes from its ability to issue variant effect predictions, and they have not demonstrated that this calibration holds in the context of variants. This section could be improved by expanding and clarifying the discussion of what set of splice sites they have demonstrated calibration on, what it means to calibrate against this set of splice sites, and how this calibration is expected to hold or not for other interesting sets of splice sites. Alternatively, or in addition, they could demonstrate how well their calibration holds on different sets of splice sites or show the effect of calibrating their models against different potentially interesting sets of splice sites and discuss how the results do or do not differ.

We thank the reviewer for highlighting the need to clarify our calibration procedure. Both SpliceAI and OpenSpliceAI are trained on a single “canonical” transcript per gene: SpliceAI on the hg 19 Ensembl/Gencode canonical set and OpenSpliceAI on the MANE transcript set. To calibrate each model, we applied post-hoc temperature scaling, i.e. a single learnable parameter that rescales the logits before the softmax. This adjustment does not alter the model’s ranking or discrimination (AUC/precision–recall) but simply aligns the predicted probabilities for donor, acceptor, and non-splice classes with their observed frequencies. As shown in our reliability diagrams (Fig. S16-S22), temperature scaling yields negligible changes in performance, confirming that both SpliceAI and OpenSpliceAI were already well-calibrated. However, we acknowledge that we didn’t measure how calibration might affect predictions on non-canonical splice sites or on cryptic splicing. It is possible that calibration might have a detrimental effect on those, but because this is not a key claim of our paper, we decided not to do further experiments. We have updated the manuscript to acknowledge this potential shortcoming; please see the revised paragraph in our next response.

(3) It is difficult to assess how well their calibration method works in general because their original models are already well calibrated, so their calibration method finds temperatures very close to 1 and only produces very small and hard to assess changes in calibration metrics. This makes it very hard to distinguish if the calibration method works, as it doesn't really produce any changes. It would be helpful to demonstrate the calibration method on a model that requires calibration or on a dataset for which the current model is not well calibrated, so that the impact of the calibration method could be observed.

It’s true that the models we calibrated didn’t need many changes. It is possible that the calibration methods we used (which were not ours, but which were described in earlier publications) can’t improve the models much. We toned down our comments about this procedure, as follows.

Original:

“Collectively, these results demonstrate that OSAIs were already well-calibrated, and this consistency across species underscores the robustness of OpenSpliceAI’s training approach in diverse genomic contexts.” Revised:

“We observed very small changes after calibration across phylogenetically diverse species, suggesting that OpenSpliceAI’s training regimen yielded well‐calibrated models, although it is possible that a different calibration algorithm might produce further improvements in performance.”

Reviewer #2 (Public review):

Summary:

The paper by Chao et al offers a reimplementation of the SpliceAI algorithm in PyTorch so that the model can more easily/efficiently be retrained. They apply their new implementation of the SpliceAI algorithm, which they call OpenSpliceAI, to several species and compare it against the original model, showing that the results are very similar and that in some small species, pretraining on other species helps improve performance.

Strengths:

On the upside, the code runs fine, and it is well documented.

Weaknesses:

The paper itself does not offer much beyond reimplementing SpliceAI. There is no new algorithm, new analysis, new data, or new insights into RNA splicing. There is no comparison to many of the alternative methods that have since been published to surpass SpliceAI. Given that some of the authors are well-known with a long history of important contributions, our expectations were admittedly different. Still, we hope some readers will find the new implementation useful.

We thank the reviewer for the feedback. We have clarified that OpenSpliceAI is an open-source PyTorch reimplementation optimized for efficient retraining and transfer learning, designed to analyze cross-species performance gains, and supported by a thorough benchmark and the release of several pretrained models to clearly position our contribution.

Reviewer #3 (Public review):

Summary:

The authors present OpenSpliceAI, a PyTorch-based reimplementation of the well-known SpliceAI deep learning model for splicing prediction. The core architecture remains unchanged, but the reimplementation demonstrates convincing improvements in usability, runtime performance, and potential for cross-species application.

Strengths:

The improvements are well-supported by comparative benchmarks, and the work is valuable given its strong potential to broaden the adoption of splicing prediction tools across computational and experimental biology communities.

Major comments:

Can fine-tuning also be used to improve prediction for human splicing? Specifically, are models trained on other species and then fine-tuned with human data able to perform better on human splicing prediction? This would enhance the model's utility for more users, and ideally, such fine-tuned models should be made available.

We evaluated transfer learning by fine-tuning models pretrained on mouse (OSAI_Mouse), honeybee (OSAI_Honeybee), Arabidopsis (OSAI_Arabidopsis), and zebrafish (OSAI_Zebrafish) on human data. While transfer learning accelerated convergence compared to training from scratch, the final human splicing prediction accuracy was comparable between fine-tuned and scratch-trained models, suggesting that performance on our current human dataset is nearing saturation under this architecture.

We added the following paragraph to the Discussion section:

We also evaluated pretraining on mouse (OSAI_Mouse), honeybee (OSAI_Honeybee), zebrafish (OSAI_Zebrafish), and Arabidopsis (OSAI_Arabidopsis) followed by fine-tuning on the human MANE dataset. While cross-species pretraining substantially accelerated convergence during fine-tuning, the final human splicing-prediction accuracy was comparable to that of a model trained from scratch on human data. This result indicates that our architecture seems to capture all relevant splicing features from human training data alone, and thus gains little or no benefit from crossspecies transfer learning in this context (see Figure S24).

Reviewer #1 (Recommendations for the authors):

We thank the editor for summarizing the points raised by each reviewer. Below is our point-bypoint response to each comment:

(1) In Figure 3 (and generally in the other figures) OpenSpliceAI should be replaced with OSAI_{Training dataset} because otherwise it is hard to tell which precise model is being compared. And in Figure 3 it is especially important to emphasize that you are comparing a SpliceAI model trained on Human data to an OSAI model trained and evaluated on a different species.

We have updated the labels in Figures 3, replacing “OpenSpliceAI” with “OSAI_{training dataset}” to more clearly specify which model is being compared.

(2) Are genes paralogous to training set genes removed from the validation set as well as the test set? If you are worried about data leakage in the test set, it makes sense to also consider validation set leakage.

Thank you for this helpful suggestion. We fully agree, and to avoid any data leakage we implemented the identical filtering pipeline for both validation and test sets: we excluded all sequences paralogous or homologous to sequences in the training set, and further removed any sequence sharing > 80 % length overlap and > 80 % sequence identity with training sequences. The effect of this filtering on the validation set is summarized in Supplementary Figure S7C.

Figure S7. (C) Scatter plots of DNA sequence alignments between validation and training sets for Human-MANE, mouse, honeybee, zebrafish, and Arabidopsis. Each dot represents an alignment, with the x-axis showing alignment identity and the y-axis showing alignment coverage. Alignments exceeding 80% for both identity and coverage are highlighted in the redshaded region and were excluded from the test sets.

Reviewer #3 (Recommendations for the authors):

(1) The legend in Figure 3 is somewhat confusing. The labels like "SpliceAI-Keras (species name)" may imply that the model was retrained using data from that species, but that's not the case, correct?

Yes, “SpliceAI-Keras (species name)” was not retrained; it refers to the released SpliceAI model evaluated on the specified species dataset. We have revised the Figure 3 legends, changing “SpliceAI-Keras (species name)” to “SpliceAI-Keras” to clarify this.

(2) Please address the minor issues with the code, including ensuring the conda install works across various systems.

We have addressed the issues you mentioned. OpenSpliceAI is now available on Conda and can be installed with:  conda install openspliceai. 

The conda package homepage is at: https://anaconda.org/khchao/openspliceai We’ve also corrected all broken links in the documentation.

(3) Utility:

I followed all the steps in the Quick Start Guide, and aside from the issues mentioned below, everything worked as expected.

I attempted installation using conda as described in the instructions, but it was unsuccessful. I assume this method is not yet supported.

In Quick Start Guide: predict, the link labeled "GitHub (models/spliceai-mane/10000nt/)" appears to be incorrect. The correct path is likely "GitHub (models/openspliceaimane/10000nt/)".

In Quick Start Guide: variant (https://ccb.jhu.edu/openspliceai/content/quick_start_guide/quickstart_variant.html#quick-startvariant), some of the download links for input files were broken. While I was able to find some files in the GitHub repository, I think the -A option should point to data/grch37.txt, not examples/data/input.vcf, and the -I option should be examples/data/input.vcf, not data/vcf/input.vcf.

Thank you for catching these issues. We’ve now addressed all issues concerning Conda installation and file links. We thank the editor for thoroughly testing our code and reviewing the documentation.

eLife Assessment

The manuscript by Hawes et al. provides important findings on how striatal projection neurons regulate spontaneous locomotion speed in the context of implicit motivation and distinct contextual valence. The supporting evidence for the findings is convincing. This work will be of broad interest to neuroscientists in the fields of basal ganglia, movement control, and cognition.

Reviewer #1 (Public review):

Summary:

This fundamental work employed multidisciplinary approaches and conducted rigorous experiments to study how a specific subset of neurons in the dorsal striatum (i.e., "patchy" striatal neurons) modulates locomotion speed depending on the valence of naturalistic contexts.

Strengths:

The scientific findings are novel and original and significantly advance our understanding of how the striatal circuit regulates spontaneous movement in various contexts.

Weaknesses:

This is extensive research involving various circuit manipulation approaches. Some of these circuit manipulations are not physiological. A balanced discussion of the technical strengths and limitations of the present work would be helpful and beneficial to the field.

Reviewer #2 (Public review):

Hawes et al. investigated the role of striatal neurons in the patch compartment of the dorsal striatum. Using Sepw1-Cre line, the authors combined a modified version of the light/dark transition box test that allows them to examine locomotor activity in different environmental valence with a variety of approaches, including cell-type-specific ablation, miniscope calcium imaging, fiber photometry, and opto-/chemogenetics. First, they found ablation of patchy striatal neurons resulted in an increase in movement vigor when mice stayed in a safe area or when they moved back from more anxiogenic to safe environments. The following miniscope imaging experiment revealed that a larger fraction of striatal patchy neurons was negatively correlated with movement speed, particularly in an anxiogenic area. Next, the authors investigated differential activity patterns of patchy neurons' axon terminals, focusing on those in GPe, GPi, and SNr, showing that the patchy axons in SNr reflect movement speed/vigor. Chemogenetic and optogenetic activation of these patchy striatal neurons suppressed the locomotor vigor, thus demonstrating their causal role in the modulation of locomotor vigor when exposed to valence differentials. Unlike the activation of striatal patches, such a suppressive effect on locomotion was absent when optogenetically activating matrix neurons by using the Calb1-Cre line, indicating distinctive roles in the control of locomotor vigor by striatal patch and matrix neurons. Together, they have concluded that nigrostriatal neurons within striatal patches negatively regulate movement vigor, dependent on behavioral contexts where motivational valence differs.

The strengths of this work include the use of multiple experimental approaches, including genetic/viral ablation of patch neurons, miniscope single-cell imaging, as well as projection-specific recording of axonal activity by fiber photometry, and causal manipulation of the neurons by chemogenetic and optogenetics. Although similar findings were reported previously, the authors' results will be of value owing to multiple levels of investigation. In my view, this study will add to the important literature by demonstrating how patch (striosomal) neurons in the striatum controls movement vigor.

Reviewer #3 (Public review):

Hawes et al. combined behavioral, optical imaging, and activity manipulation techniques to investigate the role of striatal patch SPNs in locomotion regulation. Using Sepw1-Cre transgenic mice, they found that patch SPNs encode locomotion deceleration in a light-dark box procedure through optical imaging techniques. Moreover, genetic ablation of patch SPNs increased locomotion speed, while chemogenetic activation of these neurons decreased it. The authors concluded that a subtype of patch striatonigral neurons modulates locomotion speed based on external environmental cues.

In the revision, the authors have largely addressed my concerns with additional explanation and discussion, although some of the key experiments to strengthen the authors' claim by identifying the function of specific cell populations remain to be conducted due to technical challenges. Nevertheless, the current results remain valuable and interesting to a wide audience in the field.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

This fundamental work employed multidisciplinary approaches and conducted rigorous experiments to study how a specific subset of neurons in the dorsal striatum (i.e., "patchy" striatal neurons) modulates locomotion speed depending on the valence of the naturalistic context.

Strengths:

The scientific findings are novel and original and significantly advance our understanding of how the striatal circuit regulates spontaneous movement in various contexts.

We appreciate the reviewer’s positive evaluation.

Weaknesses:

This is extensive research involving various circuit manipulation approaches. Some of these circuit manipulations are not physiological. A balanced discussion of the technical strengths and limitations of the present work would be helpful and beneficial to the field. Minor issues in data presentation were also noted.

We have incorporated the recommended discussion of technical limitations and addressed the physiological plausibility of our manipulations on Page 33 of the revised Discussion section. Specifically, we wrote:

“Judicious interpretation of the present data must consider the technical limitations of the various methods and circuit-level manipulations applied. Patchy neurons are distributed unevenly across the extensive structure of the striatum, and their targeted manipulation is constrained by viral spread in the dorsal striatum. Somatic calcium imaging using single-photon microscopy captures activity from only a subset of patchy neurons within a narrow focal plane beneath each implanted GRIN lens. Similarly, limitations in light diffusion from optical fibers may reduce the effective population of targeted fibers in both photometry and optogenetic experiments. For example, the more modest locomotor slowing observed with optogenetic activation of striatonigral fibers in the SNr compared to the stronger effects seen with Gq-DREADD activation across the dorsal striatum could reflect limited fiber optic coverage in the SNr. Alternatively, it may suggest that non-striatonigral mechanisms also contribute to generalized slowing. Our photometry data does not support a role for striatopallidal projections from patchy neurons in movement suppression. The potential contribution of intrastriatal mechanisms, discussed earlier, remains to be empirically tested. Although the behavioral assays used were naturalistic, many of the circuit-level interventions were not. Broad ablation or widespread activation of patchy neurons and their efferent projections represent non-physiological manipulations. Nonetheless, these perturbation results are interpreted alongside more naturalistic observations, such as in vivo imaging of patchy neuron somata and axon terminals, to form a coherent understanding of their functional role”.

Reviewer #2 (Public review):

Hawes et al. investigated the role of striatal neurons in the patch compartment of the dorsal striatum. Using Sepw1-Cre line, the authors combined a modified version of the light/dark transition box test that allows them to examine locomotor activity in different environmental valence with a variety of approaches, including cell-type-specific ablation, miniscope calcium imaging, fiber photometry, and opto-/chemogenetics. First, they found ablation of patchy striatal neurons resulted in an increase in movement vigor when mice stayed in a safe area or when they moved back from more anxiogenic to safe environments. The following miniscope imaging experiment revealed that a larger fraction of striatal patchy neurons was negatively correlated with movement speed, particularly in an anxiogenic area. Next, the authors investigated differential activity patterns of patchy neurons' axon terminals, focusing on those in GPe, GPi, and SNr, showing that the patchy axons in SNr reflect movement speed/vigor. Chemogenetic and optogenetic activation of these patchy striatal neurons suppressed the locomotor vigor, thus demonstrating their causal role in the modulation of locomotor vigor when exposed to valence differentials. Unlike the activation of striatal patches, such a suppressive effect on locomotion was absent when optogenetically activating matrix neurons by using the Calb1-Cre line, indicating distinctive roles in the control of locomotor vigor by striatal patch and matrix neurons. Together, they have concluded that nigrostriatal neurons within striatal patches negatively regulate movement vigor, dependent on behavioral contexts where motivational valence differs.

We are grateful for the reviewer’s thorough summary of our main findings.

In my view, this study will add to the important literature by demonstrating how patch (striosomal) neurons in the striatum control movement vigor. This study has applied multiple approaches to investigate their functionality in locomotor behavior, and the obtained data largely support their conclusions. Nevertheless, I have some suggestions for improvements in the manuscript and figures regarding their data interpretation, accuracy, and efficacy of data presentation.

We appreciate the reviewer’s overall positive assessment and have made substantial improvements to the revised manuscript in response to reviewers’ constructive suggestions. 

(1) The authors found that the activation of the striatonigral pathway in the patch compartment suppresses locomotor speed, which contradicts with canonical roles of the direct pathway. It would be great if the authors could provide mechanistic explanations in the Discussion section. One possibility is that striatal D1R patch neurons directly inhibit dopaminergic cells that regulate movement vigor (Nadal et al., Sci. Rep., 2021; Okunomiya et al., J Neurosci., 2025). Providing plausible explanations will help readers infer possible physiological processes and give them ideas for future follow-up studies.

We have added the recommended data interpretation and future perspectives on Page 30 of the revised Discussion section. Specifically, we wrote:

“Potential mechanisms by which striatal patchy neurons reduce locomotion involve the suppression of dopamine availability within the striatum. Dopamine, primarily supplied by neurons in the SNc and VTA, broadly facilitates locomotion (Gerfen and Surmeier 2011, Dudman and Krakauer 2016). Recent studies have shown that direct activation of patchy neurons leads to a reduction in striatal dopamine levels, accompanied by decreased walking speed (Nadel, Pawelko et al. 2021, Dong, Wang et al. 2025, Okunomiya, Watanabe et al. 2025). Patchy neuron projections terminate in structures known as “dendron bouquets”, which enwrap SNc dendrites within the SNr and can pause tonic dopamine neuron firing (Crittenden, Tillberg et al. 2016, Evans, Twedell et al. 2020). The present work highlights a role for patchy striatonigral inputs within the SN in decelerating movement, potentially through GABAergic dendron bouquets that limit dopamine release back to the striatum (Dong, Wang et al. 2025). Additionally, intrastriatal collaterals of patch spiny projection neurons (SPNs) have been shown to suppress dopamine release and associated synaptic plasticity via dynorphin-mediated activation of kappa opioid receptors on dopamine terminals (Hawes, Salinas et al. 2017). This intrastriatal mechanism may further contribute to the reduction in striatal dopamine levels and the observed decrease in locomotor speed, representing a compelling avenue for future investigation.”

(2) On page 14, Line 301, the authors stated that "Cre-dependent mCheery signals were colocalized with the patch marker (MOR1) in the dorsal striatum (Fig. 1B)". But I could not find any mCherry on that panel, so please modify it.

We have included representative images of mCherry and MOR1 staining in Supplementary Fig. S1 of the revised manuscript.

(3) From data shown in Figure 1, I've got the impression that mice ablated with striatal patch neurons were generally hyperactive, but this is probably not the case, as two separate experiments using LLbox and DDbox showed no difference in locomotor vigor between control and ablated mice. For the sake of better interpretation, it may be good to add a statement in Lines 365-366 that these experiments suggest the absence of hyperactive locomotion in general by ablating these specific neurons.

As suggested by the reviewer, we have added the following statement on Page 17 of the revised manuscript: “These data also indicate that PA elevates valence-specific speed without inducing general hyperactivity”.

(4) In Line 536, where Figure 5A was cited, the author mentioned that they used inhibitory DREADDs (AAV-DIO-hM4Di-mCherrry), but I could not find associated data on Figure 5. Please cite Figure S3, accordingly.

We have added the citation for the now Fig. S4 on Page 25 of the revised manuscript.

(5) Personally, the Figure panel labels of "Hi" and "ii" were confusing at first glance. It would be better to have alternatives.

As suggested by the reviewer, we have now labeled each figure panel with a distinct single alphabetical letter.

(6) There is a typo on Figure 4A: tdTomata → tdTomato

We have made the correction on the figure.

Reviewer #3 (Public review):

Hawes et al. combined behavioral, optical imaging, and activity manipulation techniques to investigate the role of striatal patch SPNs in locomotion regulation. Using Sepw1-Cre transgenic mice, they found that patch SPNs encode locomotion deceleration in a light-dark box procedure through optical imaging techniques. Moreover, genetic ablation of patch SPNs increased locomotion speed, while chemogenetic activation of these neurons decreased it. The authors concluded that a subtype of patch striatonigral neurons modulates locomotion speed based on external environmental cues. Below are some major concerns:

The study concludes that patch striatonigral neurons regulate locomotion speed. However, unless I missed something, very little evidence is presented to support the idea that it is specifically striatonigral neurons, rather than striatopallidal neurons, that mediate these effects. In fact, the optogenetic experiments shown in Fig. 6 suggest otherwise. What about the behavioral effects of optogenetic stimulation of striatonigral versus striatopallidal neuron somas in Sepw1-Cre mice?

Our photometry data implicate striatonigral neurons in locomotor slowing, as evidenced by a negative cross-correlation with acceleration and a negative lag, indicating that their activity reliably precedes—and may therefore contribute to—deceleration. In contrast, photometry results from striatopallidal neurons showed no clear correlation with speed or acceleration.

Figure 6 demonstrates that optogenetic manipulation within the SNr of Sepw1-Cre⁺ striatonigral axons recapitulated context-dependent locomotor changes seen with Gq-DREADD activation of both striatonigral and striatopallidal Sepw1-Cre⁺ cells in the dorsal striatum but failed to produce the broader locomotor speed change observed when targeting all Sepw1-Cre⁺ cells in the dorsal striatum using either ablation or Gq-DREADD activation. The more subtle speed-restrictive phenotype resulting from ChR activation in the SNr could, as the reviewer suggests, implicate striatopallidal neurons in broad locomotor speed regulation. However, our photometry data indicate that this scenario is unlikely, as activity of striatopallidal Sepw1-Cre⁺ fibers is not correlated with locomotor speed. Another plausible explanation is that the optogenetic approach may have affected fewer striatonigral fibers, potentially due to the limited spatial spread of light from the optical fiber within the SNr. Broad locomotor speed change in LDbox might require the recruitment of a larger number of striatonigral fibers than we were able to manipulate with optogenetics. We have added discussion of these technical limitations to the revised manuscript. Additionally, we now discuss the possibility that intrastriatal collaterals may contribute to reduced local dopamine levels by releasing dynorphin, which acts on kappa opioid receptors located on dopamine fibers (Hawes, Salinas et al. 2017), thereby suppressing dopamine release.

The reviewer also suggests an interesting experiment involving optogenetic stimulation of striatonigral versus striatopallidal somata in Sepw1-Cre mice. While we agree that this approach would yield valuable insights, we have thus far been unable to achieve reliable results using retroviral vectors. Moreover, selectively targeting striatopallidal terminals optogenetically remains technically challenging, as striatonigral fibers also traverse the pallidum, and the broad anatomical distribution of the pallidum complicates precise targeting. This proposed work will need to be pursued in a future study, either with improved retrograde viral tools or the development of additional mouse lines that offer more selective access to these neuronal populations as we documented recently (Dong, Wang et al. 2025).

In the abstract, the authors state that patch SPNs control speed without affecting valence. This claim seems to lack sufficient data to support it. Additionally, speed, velocity, and acceleration are very distinct qualities. It is necessary to clarify precisely what patch neurons encode and control in the current study.

We believe the reviewer’s interpretation pertains to a statement in the Introduction rather than the Abstract: “Our findings reveal that patchy SPNs control the speed at which mice navigate the valence differential between high- and low-anxiety zones, without affecting valence perception itself.” Throughout our study, mice consistently preferred the dark zone in the Light/Dark box, indicating intact perception of the valence differential between illuminated areas. While our manipulations altered locomotor speed, they did not affect time spent in the dark zone, supporting the conclusion that valence perception remained unaltered. We appreciate the reviewer’s insight and agree it is an intriguing possibility that locomotor responses could, over time, influence internal states such as anxiety. We addressed this in the Discussion, noting that while dark preference was robust to our manipulations, future studies are warranted to explore the relationship between anxious locomotor vigor and anxiety itself.

We report changes in scalar measures of animal speed across Light/Dark box conditions and under various experimental manipulations. Separately, we show that activity in both patchy neuron somata and striatonigral fibers is negatively correlated with acceleration—indicating a positive correlation with deceleration. Notably, the direction of the cross-correlational lag between striatonigral fiber activity and acceleration suggests that this activity precedes and may causally contribute to mouse deceleration, thereby influencing reductions in speed. To clarify this, we revised a sentence in the Results section: “Moreover, patchy neuron efferent activity at the SNr may causally contribute to deceleration, as indicated by the negative cross-correlational lag, thereby reducing animal speed.”. We also updated the Discussion to read: “Together, these data specifically implicate patchy striatonigral neurons in slowing locomotion by acting within the SNr to drive deceleration.”

One of the major results relies on chemogenetic manipulation (Figure 5). It would be helpful to demonstrate through slice electrophysiology that hM3Dq and hM4Di indeed cause changes in the activity of dorsal striatal SPNs, as intended by the DREADD system. This would support both the positive (Gq) and negative (Gi) findings, where no effects on behavior were observed.

We were unable to perform this experiment; however, hM3Dq has previously been shown to be effective in striatal neurons (Alcacer, Andreoli et al. 2017). The lack of effect observed in Gi-DREADD mice serves as an unintended but valuable control, helping to rule out off-target effects of the DREADD agonist JHU37160 and thereby reinforcing the specificity of hM3Dq-mediated activation in our study. We have now included an important caveat regarding the Gi-DREADD results, acknowledging the possibility that they may not have worked effectively in our target cells: “Potential explanations for the negative results in Gi-DREADD mice include inherently low basal activity among patchy neurons or insufficient expression of GIRK channels in striatal neurons, which may limit the effectiveness of Gi-coupling in suppressing neuronal activity (Shan, Fang et al. 2022).

Finally, could the behavioral effects observed in the current study, resulting from various manipulations of patch SPNs, be due to alterations in nigrostriatal dopamine release within the dorsal striatum?

We agree that this is an important potential implication of our work, especially given that we and others have shown that patchy striatonigral neurons provide strong inhibitory input to dopaminergic neurons involved in locomotor control (Nadel, Pawelko et al. 2021, Lazaridis, Crittenden et al. 2024, Dong, Wang et al. 2025, Okunomiya, Watanabe et al. 2025). Accordingly, we have expanded the discussion section to include potential mechanistic explanations that support and contextualize our main findings.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Here are some minor issues for the authors' reference:

(1) This work supports the motor-suppressing effect of patchy SPNs, and >80% of them are direct pathway SPNs. This conclusion is not expected from the traditional basal ganglia direct/indirect pathway model. Most experiments were performed using nonphysiological approaches to suppress (i.e., ablation) or activate (i.e., continuous chemo-optogenetic stimulation). It remains uncertain if the reported observations are relevant to the normal biological function of patchy SPNs under physiological conditions. Particularly, under what circumstances an imbalanced patch/matrix activity may be induced, as proposed in the sections related to the data presented in Figure 6. A thorough discussion and clarification remain needed. Or it should be discussed as a limitation of the present work.

We have added discussion and clarification of physiological limitations in response to reviewer feedback. Additionally, we revised the opening sentence of an original paragraph in the discussion section to emphasize that it interprets our findings in the context of more physiological studies reporting natural shifts in patchy SPN activity due to cognitive conflict, stress, or training. The revised opening sentence now reads: “Together with previous studies of naturally occurring shifts in patchy neuron activation, these data illustrate ethologically relevant roles for a subgroup of genetically defined patchy neurons in behavior.”

(2) Lines 499-500: How striato-nigral cells encode speed and deceleration deserves a thorough discussion and clarification. These striatonigral cells can target both SNr GABAergic neurons and dendrites of the dopaminergic neurons. A discussion of microcircuits formed by the patchy SPNs axons in the SNr GABAergic and SNC DAergic neurons should be presented.

We have added this point at lines 499–500, including a reference to a relevant review of microcircuitry. Additionally, we expanded the discussion section to address microcircuit mechanisms that may underlie our main findings.

(3) Line 70: "BNST" should be spelled out at the first time it is mentioned.

This has been done.

(4) Line 133: only GCaMP6 was listed in the method, but GCaMP8 was also used (Figure 4). Clarification or details are needed.

Thank you for your careful attention to detail. We have corrected the typographical errors in the Methods section. Specifically, in the Stereotaxic Injections section, we corrected “GCaMP83” to “GCaMP8s.” In the Fiber Implant section, we removed the incorrect reference to “GCaMP6s” and clarified that GCaMP8s was used for photometry, and hChR2 was used for optogenetics.

(5) Line 183: Can the authors describe more precisely what "a moment" means in terms of seconds or minutes?

This has been done.

(6) Line 288: typo: missing / in ΔF.

Thank you this has been fixed.

(7) Line 301-302: the statement of "mCherry and MOR1 colocalization" does not match the images in Figure 1B.

This has been corrected by proving a new Supplementary Figure S1.

(8) Related to the statement between Lines 303-304: Figure 1c data may reflect changes in MOR1 protein or cell loss. Quantification of NeuN+ neurons within the MOR1 area would strengthen the conclusion of 60% of patchy cell loss in Figure 1C.

Since the efficacy of AAV-FLEX-taCasp3 in cell ablation has been well established in our previous publications and those of others (Yang, Chiang et al. 2013, Wu, Kung et al. 2019), we do not believe the observed loss of MOR1 staining in Fig. 1C merely reflects reduced MOR1 expression. Moreover, a general neuronal marker such as NeuN may not reliably detect the specific loss of patchy neurons in our ablation model, given the technical limitations of conventional cell-counting methods like MBF’s StereoInvestigator, which typically exhibit a variability margin of 15–20%.

(9) Lines 313-314: "Similarly, PA mice demonstrated greater stay-time in the dark zone (Figure 1E)." Revision is needed to better reflect what is shown in Figure 1E and avoid misunderstandings.

Thank you this has been addressed.

(10) The color code in Figure 2Gi seems inconsistent with the others? Clarifications are needed.

Color coding in Figure 2Gi differs from that in 2Eii out of necessity. For example, the "Light" cells depicted in light blue in 2Eii are represented by both light gray and light red dots in 2Gi. Importantly, Figure 2G does not encode specific speed relationships; instead, any association with speed is indicated by a red hue.

(11) Lines 538-539: the statement of "Over half of the patch was covered" was not supported by Figure 5C. Clarification is needed.

Thank you. For clarity, we updated the x-axis labels in Figures 1C and 5C from “% area covered” to “% DS area covered,” and defined “DS” as “dorsal striatal” in the corresponding figure legends. Additionally, we revised the sentence in question to read: “As with ablation, histological examination indicated that a substantial fraction of dorsal patch territories, identified through MOR1 staining, were impacted (Fig. 5C).”

(12) Figure 3: statistical significance in Figure 3 should be labeled in various panels.

We believe the reviewer's concern pertains to the scatter plot in panel F—specifically, whether the data points are significantly different from zero. In panel 3F, the 95% confidence interval clearly overlaps with zero, indicating that the results are not statistically significant.

(13) Figures 6D-E: no difference in the speed of control mice and ChR2 mice under continuous optical stimulation was not expected. It was different from Gq-DRADDS study in Figure 5E-F. Clarifications are needed.

For mice undergoing constant ChR2 activation of Sepw1-Cre⁺ SNr efferents, overall locomotor speed does not differ from controls. However, the BIL (bright-to-illuminated) effect on zone transitions is disrupted: activating Sepw1-Cre⁺ fibers in the SNr blunts the typical increase in speed observed when mice flee from the light zone toward the dark zone. This impaired BIL-related speed increase upon exiting the light was similarly observed in the Gq-DREADD cohort. The reviewer is correct that this optogenetic manipulation within the SNr did not produce the more generalized speed reductions seen with broader Gq-DREADD activation of all Sepw1-Cre⁺ cells in the dorsal striatum. A likely explanation is the difference in targeting—ChR2 specifically activates SNr-bound terminals, whereas Gq-DREADD broadly activates entire Sepw1-Cre⁺ cells. Notably, many of the generalized speed profile changes observed with chemogenetic activation are opposite to those resulting from broad ablation of Sepw1-Cre⁺ cells.

The more subtle speed-restrictive phenotype observed with ChR2 activation targeted to the SNr may suggest that fewer striatonigral fibers were affected by this technique, possibly due to the limited spread of light from the fiber optic. Broad locomotor speed change in LDbox might require the recruitment of a larger number of striatonigral fibers than we were able to manipulate with an optogenetic approach. Alternatively, it could indicate that non-striatonigral Sepw1-Cre+ projections—such as striatopallidal or intrastriatal pathways—play a role in more generalized slowing. If striatopallidal fibers contributed to locomotor slowing, we would expect to see non-zero cross-correlations between neural activity and speed or acceleration, along with negative lag indicating that neural activity precedes the behavioral change. However, our fiber photometry data do not support such a role for Sepw1-Cre+ striatopallidal fibers.

We have also referenced the possibility that intrastriatal collaterals could suppress striatal dopamine levels, potentially explaining the stronger slowing phenotype observed when the entire striatal population is affected, as opposed to selectively targeting striatonigral terminals.

These technical considerations and interpretive nuances have been incorporated and clarified in the revised discussion section.

(14) Lines 632: "compliment": a typo?

Yes, it should be “complement”.

(15) Figure 4 legend: descriptions of panels A and B were swapped.

Thank you. This has been corrected.

6) Friedman (2020) was listed twice in the bibliography (Lines 920-929).

Thank you. This has been corrected.

Reviewer #3 (Recommendations for the authors):

It will be helpful to label and add figure legends below each figure.

Thank you for the suggestion.

Editor's note:

Should you choose to revise your manuscript, if you have not already done so, please include full statistical reporting including exact p-values wherever possible alongside the summary statistics (test statistic and df) and, where appropriate, 95% confidence intervals. These should be reported for all key questions and not only when the p-value is less than 0.05 in the main manuscript. We noted some instances where only p values are reported.

Readers would also benefit from coding individual data points by sex and noting N/sex.

We have included detailed statistical information in the revised manuscript. Both male and female mice were used in all experiments in approximately equal numbers. Since no sex-related differences were observed, we did not report the number of animals by sex.

References

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Crittenden, J. R., P. W. Tillberg, M. H. Riad, Y. Shima, C. R. Gerfen, J. Curry, D. E. Housman, S. B. Nelson, E. S. Boyden and A. M. Graybiel (2016). "Striosome-dendron bouquets highlight a unique striatonigral circuit targeting dopamine-containing neurons." Proc Natl Acad Sci U S A 113(40): 11318-11323.

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eLife Assessment

This important study is the first characterization of the phenotype caused by a lack of Eml3 expression in mice. Mutant animals present a disrupted pial basement membrane, leading to focal extrusions from the cerebral cortex, called ectopias. The methodology is convincing and the conclusions are solid, although further investigations on the mechanisms and inclusion of the experiments performed, but not presented, will improve the manuscript. This work would be of interest to neural development biologists and human geneticists working on brain disorders.

Reviewer #1 (Public review):

Summary:

The paper describes the initial characterization of Eml3 knockout mice. Eml3 global inactivation leads to delayed embryonic development, perinatal lethality apparently due to failure to inflate lungs, and a cobblestone brain-like phenotype represented by focal neuronal ectopias in the marginal zone or subarachnoid space of dorsal telencephalon. The neural ectopias are associated with interruptions in the pial basal membrane (PBM), which appear around E11.5. The authors also confirmed previously described protein interactions, using coIP-MS experiments of placenta and embryonic tissues (TUBB3, several 14-3-3 proteins, and DYNLL). The authors generated mice carrying a TQT86AAA homozygous mutation in EML3 (a motif required for EML3-DYNLL interactions) that were normal and showed no focal neuronal ectopias, indicating that this particular protein interaction is dispensable. The authors propose Eml3 knockout mice as a model of cobblestone brain malformation.

Strengths:

The brain phenotype described in this work is relevant for the neural development field and with potential clinical relevance. The initial phenotyping is appropriate but will require additional experiments to establish the cause of the failure to inflate the lungs. The study shows convincing data regarding the main characteristics of the brain phenotype and data supporting the timing when these abnormalities arise during development.

Weaknesses:

The study would benefit from clearer evidence and additional experiments that would help to establish the molecular and cellular mechanisms underlying the brain phenotype, the central topic of the work.

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors investigate the role of the microtubule-binding protein EML3 during cortical development through the generation and characterization of an Eml3 mouse mutant. The authors focus mainly on the effects of EML3 loss on brain development, although Eml3 mouse mutants also present with developmental delay and growth restriction, and die perinatally due to respiratory distress caused by delayed maturation of the lungs. The main finding in the developing cortex is the presence of focal neuronal ectopias, which contain neurons from all cortical layers, as revealed by immunostaining. The authors use electron microscopy to show that ectopias seem to be caused by disruption to the pial basement membrane at early stages of development, which allows neurons to breach through it. To find a functional link between EML3 and the observed phenotype, studies are conducted that demonstrate expression of EML3 in radial glia cells and mesenchymal cells, both cell types involved in the formation and maintenance of the pial basement membrane. Furthermore, interaction partners for EML3 are identified through coIP-MS analysis, including tubulin beta-3, 14-3-3 proteins, and cytoplasmic dynein light chain. However, mice carrying a mutant EML3 allele engineered to abolish the interaction between EML3 and cytoplasmic dynein light chain do not recapitulate any of the symptoms of complete EML3 loss.

Strengths:

The manuscript offers several important strengths that contribute significantly to the field. This study presents the first characterization of Eml3 knockout animals, providing novel insights into the role of Eml3 in vivo. Information on Eml3 function so far was restricted to cell culture data, so the results in this manuscript start to fill an important gap in our knowledge about this microtubule-binding protein. The experimental approach is carefully designed, with appropriate controls that ensure the reliability of the data. Moreover, the authors have addressed a key challenge in the analysis, namely the developmental delay of the knockout animals. By implementing a strategy to match developmental stages between wild-type and knockout groups, they allow for meaningful and valid comparisons between the two genotypes. Importantly, the authors have successfully generated three different Eml3 mutant mouse lines (knockout, floxed, and with disrupted binding to cytoplasmic dynein light chain), which are very valuable tools for the broader scientific community to further study the roles of this gene in development and disease in the future.

Weaknesses:

While the manuscript presents valuable data, there are also several weaknesses that limit the overall impact of the study. Most notably, there is no clear mechanistic link established between the loss of Eml3 function and the observed phenotype, leaving the biological significance of the findings somewhat speculative, as it is not straightforward how a microtubule-associated protein can have an impact on the stability of the pial basement membrane. In this respect, but also in general for the whole manuscript, there seems to be a considerable amount of experimental work that has been conducted but is not presented, possibly due to the negative nature of the results. At least some of those results could be shown, particularly (but not only) the stainings for the composition of the ECM components. Additionally, the phenotype reported appears to be dependent on the genetic background, as it is absent in the CD1 strain. This observation raises concerns as to how robust the results are and how much they can be generalized to other mouse strains, but, more importantly, to humans. There is no data included in the manuscript about the generation and analysis of the Eml3AAA/AAA mouse line. This is an important omission, especially as no details on the validation or phenotypic characterization of this additional mouse line are provided. Including these elements would greatly strengthen the rigor and interpretability of the work, especially if that mouse line is to be shared with the scientific community.

Reviewer #3 (Public review):

Summary:

This work aims to understand the role of Echinoderm Microtubule-associated Protein-like 3 (EML3) in embryogenesis and neocortical development. Importantly, this work shows that depletion of EML3 causes focal neuronal ectopias by disrupting the structural integrity of the pial basement membrane, describing a new model of cobblestone brain malformation. Another member of the EML family, EML1, has already been shown to trigger neuronal migration disorders, particularly subcortical band heterotopia, by affecting cell polarity. The results presented here point to a different mechanism of action. The authors show that EML3 is expressed in radial glia cells and mesenchymal cells in the pial region, and upon EML3 depletion (i.e., Eml3 mutant mice), the pial basement membrane is structurally damaged, allowing migrating neuroblasts to ectopically migrate through. Answering, in this case, that the weakening of the pial basement membrane is a prerequisite for focal neuronal ectopias. The authors provide a meticulous characterization of the Eml3 mutant mice, strengthening the conclusions of the results.

Strengths:

The authors provide a very detailed analysis of the defects observed in Eml3 mutant mice, by providing not only results by inferred day of conception but also by classifying embryos by their number of somite pairs.

Weaknesses:

(1) Besides the data provided in the figures, the authors report a significant amount of experiments/results as "Data not shown". Negative data is still important data to report, and the authors may want to choose some crucial "not shown data" to report in the manuscript.

(2) Results in Figure 3A apparently contradict results in 3B. A better explanation of the results should improve understanding of the data. Even though the conclusion that the "onset and progression of neurogenesis is normal in Eml3 null mice" seems logical based on the data, the final numbers are not (Figure 3A) and this should be acknowledged, as well.

(3) The authors should define which cell types are identified by SOX1 and PAX6.

Author response:

Reviewer #1 (Public Review):

The study would benefit from clearer evidence and additional experiments that would help to establish the molecular and cellular mechanisms underlying the brain phenotype, the central topic of the work.

We agree that additional experiments are necessary to elucidate the mechanism(s) by which EML3 deficiency causes the observed developmental phenotypes. However, as no further experimentation is possible due to the closure of our laboratory, we are committed to sharing available materials—including custom antibodies and cryopreserved sperm from our mouse lines. We will include previously generated experimental data not presented in the original submission. While these additional data do not reveal the mechanisms, we believe that sharing hypotheses that were experimentally ruled out will benefit the scientific community.

Reviewer #2 (Public Review):

While the manuscript presents valuable data, there are also several weaknesses that limit the overall impact of the study. Most notably, there is no clear mechanistic link established between the loss of Eml3 function and the observed phenotype, leaving the biological significance of the findings somewhat speculative, as it is not straightforward how a microtubule-associated protein can have an impact on the stability of the pial basement membrane. In this respect, but also in general for the whole manuscript, there seems to be a considerable amount of experimental work that has been conducted but is not presented, possibly due to the negative nature of the results. At least some of those results could be shown, particularly (but not only) the stainings for the composition of the ECM components.

We agree that additional experiments are necessary to elucidate the mechanisms at play. While we cannot conduct further experiments, we will include additional existing data, including supplemental ECM component staining, in a new figure or panel. As this reviewer rightly anticipated, these results might not clarify the mechanism but sharing the hypotheses that were already experimentally tested will be helpful.

Additionally, the phenotype reported appears to be dependent on the genetic background, as it is absent in the CD1 strain. This observation raises concerns as to how robust the results are and how much they can be generalized to other mouse strains, but, more importantly, to humans.

Indeed, we have determined that genetic background greatly influences the manifestation of developmental defects caused by absence or mutation of the EML3 protein in mice. Modifier genes appear to play a significant role in phenotypic expression. In humans, the presence or absence of such modifiers may result in a broad spectrum of outcomes—from no clinical relevance, as seen in CD1 mice, to potential intrauterine mortality. We agree that this underscores the challenge of translating mouse model findings to human implications. Future studies could include a search for EML3 non-coding regulatory mutations and expanded analysis of neuronal development defects, such as COB, as well as cases of intrauterine growth restriction (IUGR).

There is no data included in the manuscript about the generation and analysis of the Eml3AAA/AAA mouse line. This is an important omission, especially as no details on the validation or phenotypic characterization of this additional mouse line are provided. Including these elements would greatly strengthen the rigor and interpretability of the work, especially if that mouse line is to be shared with the scientific community.

We acknowledge this oversight and will add a Materials and Methods section describing the generation of Eml3 TQT86AAA mice as well as validation and phenotypic characterizations that were done for that mouse line.

Reviewer #3 (Public Review):

Besides the data provided in the figures, the authors report a significant amount of experiments/results as "Data not shown". Negative data is still important data to report, and the authors may want to choose some crucial "not shown data" to report in the manuscript.

We will incorporate key datasets previously omitted, with priority given to those requested by Reviewer #2.

Results in Figure 3A apparently contradict results in 3B. A better explanation of the results should improve understanding of the data. Even though the conclusion that the "onset and progression of neurogenesis is normal in Eml3 null mice" seems logical based on the data, the final numbers are not (Figure 3A) and this should be acknowledged, as well.

We will provide further explanations for the data presented in figures 3A and 3B to better convey the fact that the two datasets are not contradicting. In essence, since Eml3 null mice are developmentally delayed (as determined by the number of somites at a specific age, Fig. 1C), the milestones in neurogenesis are reached at a later age in Eml3 null mice (Fig. 3A). However, Eml3 null mice have reached the same neurogenesis milestones as their WT counterparts when they have the same number of somites (Fig. 3B).

The authors should define which cell types are identified by SOX1 and PAX6.

We will expand our manuscript to define the expression timing and cell identity marked by SOX1 and PAX6 in neural progenitors during cortical development.

eLife Assessment

This paper presents the important finding that BNIP3/NIX, a mitophagy receptor, and its binding to ATG18 are required for mitophagy during muscle cell reorganization in Drosophila. Although the involvement of the BNIP3-ATG18/WIPI axis in mitophagy induction has been reported in mammalian cell culture systems, this study provides the first compelling evidence for this pathway in vivo in animals. The physiological significance of this BNIP3-dependent mitophagy will require further investigation.

Reviewer #1 (Public review):

During early Drosophila pupal development, a subset of larval abdominal muscles (DIOMs) is remodelled using an autophagy dependent mechanism.

To better understand this not very well studied process, the authors have generated a systematic transcriptomics time course using dissected larval abdominal muscles of various stages from wild type and autophagy deficient mutants. The authors have further identified a function for BNIP3 for executing mitophagy during DIOM remodelling.

Strengths:

The paper does provide a detailed mRNA time course resource for the DIOM remodelling.

The paper does find an interesting BNIP3 loss of function phenotype, a block of mitophagy during muscle remodelling and hence identifies a specific linker between mitochondria and the core autophagy

machinery. This adds to the mechanism how mitochondria are degraded.

Sophisticated fly genetics demonstrates that the larval muscle mitochondria are, to a large extend, degraded by autophagy during DIOM remodelling.

Quantitative electron microscopy data show that BNIP3 is required for initiating mito-phagosomes. It needs either its LIR and MER domain for function.

Weakness:

Mitophagy during DIOM remodelling is not novel (earlier papers from Fujita et al.).

Other weaknesses have been eliminated during the revision.

Reviewer #2 (Public review):

Summary:

Autophagy (macroautophagy) is known to be essential for muscle function in flies and mammals. To date, many mitophagy (selective mitochondrial autophagy) receptors have been identified in mammals and other species. While loss of mitophagy receptors has been shown to impair mitochondrial degradation (e.g., OPTN and NDP52 in Parkin-mediated mitophagy and NIX and BNIP3 in hypoxia-induced mitophagy) at the level of cultured cells, it remains unclear, especially under physiological conditions in vivo. In this study, the authors revealed that one of the receptors BNIP3 plays a critical role in mitochondrial degradation during muscle remodeling in vivo.

Overall, the manuscript provides solid evidence that BNIP3 is involved in mitophagy during muscle remodeling with in vivo analyses performed. In particular, all experiments in this study are well designed. The text is well written and the figures are very clear.

Strengths:

(1) In each experiment, appropriate positive and negative controls are used to indicate what is responsible for the phenomenon observed by the authors: e.g. FIP200, Atg18, Stx17 siRNAs during DIOM remodeling in Fig2 and Full, del-LIR, del-MER in Fig5.

(2) Although the transcriptional dynamics of DIOM remodeling during metamorphosis is autophagy-independent, the transcriptome data obtained by the authors would be valuable for future studies.

(3) In addition to the simple observation that loss of BNIP3 causes mitochondrial accumulation, the authors further observed that, by combining siRNA against STX17, which is required for fusion of autophagosomes with lysosomes, BNIP3 KO abolishes mitophagosome formation, which will provide solid evidence for BNIP3-mediated mitophagy. Furthermore, using a Gal80 temperature-sensitive approach, the authors showed that mitochondria derived from larval muscle, but not those synthesized during hypertrophy, remain in BNIP3 KO fly muscles.

Weaknesses:

(1) Because BNIP3 KO causes mitochondrial accumulation, it is expected that adult flies will have some physiological defects, but this has not been fully analyzed or sufficiently mentioned in the manuscript.

(2) In Fig 5, the authors showed that BNIP3 binds to Atg18a by co-IP, but no data are provided on whether MER-mut or del-MER attenuates the affinity for Atg18a.

Comments on revisions: The authors answered all the reviewer's concerns.

Reviewer #3 (Public review):

Summary:

Fujita et al build on their earlier, 2017 eLife paper that showed the role of autophagy in the developmental remodeling of a group of muscles (DIOM) in the abdomen of Drosophila. Most larval muscles undergo histolysis during metamorphosis, while DIOMs are programmed to regrow after initial atrophy to give rise to temporary adult muscles, which survive for only 1 day after eclosion of the adult flies (J Neurosci. 1990;10:403-1. and BMC Dev Biol 16, 12, 2016). The authors carry out transcriptomics profiling of these muscles during metamorphosis, which are in agreement with the atrophy and regrowth phases of these muscles. Expression of the known mitophagy receptor BNIP3/NIX is high during atrophy, so the authors start to delve more into the role of this protein/mitophagy in their model. BNIP3 KO indeed impairs mitophagy and muscle atrophy, which they convincingly demonstrate via nice microscopy images. They also show that the already known Atg8a-binding LIR and Atg18a-binding MER motifs of human NIX are conserved in the Drosophila protein, although the LIR turned out to be less critical for in vivo protein function than the MER motif.

Strengths:

Established methodology, convincing data, in vivo model

Weaknesses:

Significance for Drosophila physiology and for human muscles remains to be established

Author Response:

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

Reviewer #1 (Public review):

Summary: 

During early Drosophila pupal development, a subset of larval abdominal muscles (DIOMs) is remodelled using an autophagy-dependent mechanism. 

To better understand this not very well studied process, the authors have generated a transcriptomics time course using dissected abdominal muscles of various stages from wild-type and autophagy-deficient mutants. The authors have further identified a function for BNIP3 in muscle mitophagy using this system. 

Strengths: 

(1) The paper does provide a detailed mRNA time course resource for DIOM remodeling. 

(2) The paper does find an interesting BNIP3 loss of function phenotype, a block of mitophagy during muscle remodeling, and hence identifies a specific linker between mitochondria and the core autophagy machinery. This adds to the mechanism of how mitochondria are degraded. 

(3) Sophisticated fly genetics demonstrates that the larval muscle mitochondria are, to a large extent, degraded by autophagy during DIOM remodeling. 

Weaknesses: 

(1) Mitophagy during DIOM remodeling is not novel (earlier papers from Fujita et al.). 

(2) The transcriptomics time course data are not well connected to the autophagy part. Both could be separated into 2 independent manuscripts. 

(3) The muscle phenotypes need better quantifications, both for the EM and light microscopy data in various figures. 

(4) The transcriptomics data are hard to browse in the provided PDF format. 

Thank you for reviewing our manuscript and for your feedback. While we understand and appreciate the suggestion to divide the manuscript into two separate studies, we believe that presenting the work as a single manuscript is more appropriate. This is because the time-course RNA-seq of DIOMs provides critical insight into BNIP3-mediated mitophagy during DIOM remodeling, which ties together the two components of our study. In response to Reviewer #1’s recommendations, we have quantified data from both EM and confocal images, and we have revised the RNA counts table in Supplementary File 1 accordingly. Please see our detailed responses and revisions on the following pages.

Reviewer #2 (Public review): 

Summary: 

Autophagy (macroautophagy) is known to be essential for muscle function in flies and mammals. To date, many mitophagy (selective mitochondrial autophagy) receptors have been identified in mammals and other species. While the loss of mitophagy receptors has been shown to impair mitochondrial degradation (e.g., OPTN and NDP52 in Parkin-mediated mitophagy and NIX and BNIP3 in hypoxia-induced mitophagy) at the level of cultured cells, it remains unclear, especially under physiological conditions in vivo. In this study, the authors revealed that one of the receptors BNIP3 plays a critical role in mitochondrial degradation during muscle remodeling in vivo. 

Overall, the manuscript provides solid evidence that BNIP3 is involved in mitophagy during muscle remodeling with in vivo analyses performed. In particular, all experiments in this study are well-designed. The text is well written and the figures are very clear. 

Strengths: 

(1) In each experiment, appropriate positive and negative controls are used to indicate what is responsible for the phenomenon observed by the authors: e.g. FIP200, Atg18, Stx17 siRNAs during DIOM remodeling in Figure 2 and Full, del-LIR, del-MER in Figure 5. 

(2) Although the transcriptional dynamics of DIOM remodeling during metamorphosis is autophagy-independent, the transcriptome data obtained by the authors would be valuable for future studies. 

(3) In addition to the simple observation that loss of BNIP3 causes mitochondrial accumulation, the authors further observed that, by combining siRNA against STX17, which is required for fusion of autophagosomes with lysosomes, BNIP3 KO abolishes mitophagosome formation, which will provide solid evidence for BNIP3-mediated mitophagy. Furthermore, using a Gal80 temperature-sensitive approach, the authors showed that mitochondria derived from larval muscle, but not those synthesized during hypertrophy, remain in BNIP3 KO fly muscles. 

Weaknesses: 

(1) Because BNIP3 KO causes mitochondrial accumulation, it is expected that adult flies will have some physiological defects, but this has not been fully analyzed or sufficiently mentioned in the manuscript. 

(2) In Figure 5, the authors showed that BNIP3 binds to Atg18a by co-IP, but no data are provided on whether MER-mut or del-MER attenuates the affinity for Atg18a. 

Thank you for pointing out the critical issues in the previous version of our manuscript. In this revision, we have conducted several physiological assays using BNIP3 KO flies, as well as co-IP experiments to confirm that the DMER weakens the interaction with Atg18a. We have also addressed all the recommendations provided. Please see our detailed point-by-point responses below.

Reviewer #3 (Public review): 

Summary: 

Fujita et al build on their earlier, 2017 eLife paper that showed the role of autophagy in the developmental remodeling of a group of muscles (DIOM) in the abdomen of Drosophila. Most larval muscles undergo histolysis during metamorphosis, while DIOMs are programmed to regrow after initial atrophy to give rise to temporary adult muscles, which survive for only 1 day after eclosion of the adult flies (J Neurosci. 1990;10:403-1. and BMC Dev Biol 16, 12, 2016). The authors carry out transcriptomics profiling of these muscles during metamorphosis, which is in agreement with the atrophy and regrowth phases of these muscles. Expression of the known mitophagy receptor BNIP3/NIX is high during atrophy, so the authors have started to delve more into the role of this protein/mitophagy in their model. BNIP3 KO indeed impairs mitophagy and muscle atrophy, which they convincingly demonstrate via nice microscopy images. They also show that the already known Atg8a-binding LIR and Atg18a-binding MER motifs of human NIX are conserved in the Drosophila protein, although the LIR turned out to be less critical for in vivo protein function than the MER motif. 

Strengths: 

Established methodology, convincing data, in vivo model. 

Weaknesses: 

The significance for Drosophila physiology and for human muscles remains to be established. 

Thank you for reviewing our manuscript. In response to the comment, we have performed lifespan, adult locomotion, and eclosion assays in BNIP3 KO flies. Although we observed substantial mitochondrial accumulation in the DIOMs of BNIP3 KO flies, no significant differences were detected in these physiological assays under our experimental conditions. We plan to further investigate the physiological role of BNIP3 in flies and extend our studies to human muscle in future work. Please see our detailed responses below.

Reviewer #1 (Recommendations for the authors): 

Major points: 

(1) Unfortunately, the RNA counts file table in Supplementary file 1 is a PDF and not an Excel sheet. The labelling makes it unclear from which time points and genotype the listed values on the 650-page files are. 

We have now corrected the labelling of time points and genotypes in Supplementary File 1 to improve clarity and have provided the updated Excel file.

Looking at these counts it seems that sarcomere genes (Mhc, bt, sls, wupA, TpnC ) are 10x to 100x lower in sample "ctrl_1" compared to the three other control samples. Which time point is that? It is essential to have access to the full dataset, wild type and autophagy-deficient, to be able to assess the quality of the RNA SEQ data. These need to be deposited in a public database or to be provided in a useful format. 

Thank you for pointing that out. In the previous version, “Ctrl_1” referred to the Control sample at 1 day APF, when atrophy occurs. We have corrected the labeling in Supplementary File 1 accordingly and have deposited the RNA-seq data to GEO, where it is now publicly available (GSE293359).

(2) Which statistical test was used to assess the differences in muscle volumes in Figure 2E? I was not able to find a table with the measured data.

In Figure 2E, we used the Mann-Whitney test for statistical analysis. The raw data used for quantification have also been provided (Supplementary File 2).

The shown volumes do not correlate with the scheme shown in Figure 2A, in particular at the larval stage the muscle seems much larger.

We have revised the schematic models of muscle cells in Figures 1C and 2A in accordance with the reviewer’s suggestion.

(3) It is important to remember that adult Drosophila muscles are not homogenous, at least not the adult leg and abdominal muscles, as they are organised as tubes with myofibrils closer to the surface, and nuclei as well as mitochondria largely in the centre (see PMID 33828099). Hence, only showing a single plane in the muscle images can be very misleading. The authors should at least provide virtual XZ-cross section views in Figure 3G to ensure that similar muscle planes are compared. This applies to the interpretation of both, the mitochondria and the myofibril phenotypes in wildtype vs BNIP3-KO. 

Thank you for your comment. As suggested, we have added XZ-cross-sectional views in Figure 3G. The XY plane corresponds to a central section of the Z-stack, as indicated in the figure.

(4) The EM images are nice, however only 2 of the 4 conditions shown were quantified. As the section plane can be misleading, at least several planes should be analysed also for wild type and BNIP3-KO, and not only for stx17 RNAi and the double mutant. 

In response to the comment, we quantified the TEM images of wild-type and BNIP3-KO DIOMs and added the resulting graph to Figure 4C. The corresponding raw data have also been provided (Supplementary File 2).

(5) How was Figure 5D, 5D' quantified? What corresponds to "regular", "medium", "high"? A statistical test is missing. I would rather conclude that MIR and LIR are redundant as double mutant appears to be stronger than both singles. This is also concluded in some sections of the text, so the authors seem to contradict themselves. Why not measure the mitochondria areas as done in Figure 6A' instead? 

In the previous version, we manually categorized pooled, blinded images from different genotypes. However, as the reviewer pointed out, this approach was not quantitative. In the revised version, we analyzed the images using ImageJ to quantify the mitochondrial area per cell. Statistical significance was assessed using the Kruskal-Wallis test. Accordingly, we have revised Figure 5D, the method section, and the figure legend.

(6) Figure 6B data seem to come from a single image per genotype only. At least 3 or 4 animals should be measured and the values reported. 

We analyzed Pearson’s correlation coefficients (R values) from at least five images per genotype and performed statistical analysis. The resulting quantification is presented in Figure 6B’, and the corresponding text has been revised accordingly.

(7) As BNIP3 mutants are viable, it would be interesting to report if they can fly and how long they live. 

Additional data on adult lifespan, climbing ability, and elapsed time for eclosion in BNIP3 KO flies have been included as supplemental information (Figure 3-figure supplement 2). No significant differences were observed in those assays under our experimental conditions.

(8) The transcriptomics data are not well linked to the autophagy mechanism. In particular, the mutant transcriptomics data are confusing, as the abstract seems to suggest that blocking autophagy impacts transcriptomics, which is not (strongly) the case. I would at least re-write this part, as it is currently misleading and sparks wrong expectations to the reader. Also throughout the text, the authors need to make clear if there are transcriptomic changes or not and if there are, how these are linked to autophagy. 

In the abstract, we described the findings as “transcriptional dynamics independent of autophagy” (line 49) because the loss of autophagy had only a minimal effect on transcriptional changes. This conclusion is supported by the data presented in our manuscript. In the result section, we state: “In contrast to our prediction, the knockdown of Atg18a, FIP200, or Stx17 only had a slight impact on transcriptomic dynamics in DIOM remodeling (Fig. 2C), with only minor changes detected (Fig. 2-figure supplement 2G)” (lines 199-201). In the Discussion section, we further note: “The transcriptional dynamics associated with DIOM remodeling are largely independent of autophagy (Fig.2). Instead, our RNA-seq data suggest that it is regulated primarily by ecdysone signaling, with minimal influence from autophagy inhibition” (lines 326-328).

(9) No table with the measured data is provided. 

We have provided the raw data files corresponding to all quantified results as Supplementary File 2.

Minor points: 

(1) To my knowledge, it is standard to indicate the time after puparium formation in hours, instead of days, (e.g. 24h, 48h etc.). 

Thank you for the comments. In our previous publications on DIOM remodeling during metamorphosis (PMID: 28063257 and 33077556), we used days rather than hours to indicate developmental time points. To maintain consistency across our studies, we have chosen to continue using days in the present manuscript.

(2) "Myofibrils typically form beneath the sarcolemma (Mao et al., 2022; Sanger et al., 2010); therefore, when mitochondria accumulate, myofibrils are restricted to the cell periphery." This is quite a general statement that does not always hold, in particular not in Drosophila flight muscles and likely also not in abdominal muscles (see PMIDs 29846170, 28174246). 

Thank you for pointing that out. We rewrote the sentence as follows: In the absence of BNIP3, mitochondria derived from the larval muscle accumulate and cluster in the cell center, physically obstructing myofibril formation during hypertrophy and restricting myofibrils to the cell periphery (Fig. 6E) (lines 392-394).

Reviewer #2 (Recommendations for the authors): 

Suggestions for improved or additional experiments, data or analyses. 

The authors should test, by a co-IP experiment, whether BNIP3 mutants lose the interaction with HA-Atg18a. 

As requested, we tested the effect of MER deletion on the interaction between BNIP3 and Atg18a in co-IP experiment. As shown in the new Fig. 5C, the deletion of MER weakened the interaction. This result was confirmed in three independent experiments. Its corresponding text has also been revised as follows: “We confirmed that HA-tagged Drosophila Atg18a co-immunoprecipitated with GFP-tagged full-length Drosophila BNIP3, and that this interaction was attenuated by the deletion of the MER (residues 42-53) (Fig. 5C)” (lines 270-273).

Minor corrections to the text and figures 

(1) In the list of authors, Kawaguchi Kohei could be Kohei Kawaguchi_._ 

Thank you very much. It has been corrected.

(2) In Fig3D, other receptors (Zonda, CG12511, Key, Ref2P) should be mentioned briefly. 

Thank you for the suggestion. We have revised the sentences as follows: “The time course RNA-seq data (Fig. 1 and 2) indicated that, among the known mitophagy regulators, only BNIP3 was robustly expressed in 1 d APF DIOMs. In contrast, Zonda, CG12511, Pink1, Park, Key, Ref(2)P, and IKKe—the Drosophila orthologs of FKBP8, FUNDC1, PINK1, Parkin, Optineurin, p62, and TBK1, respectively—showed little or undetectable expression at this stage (Fig. 3D).” (lines 230-234).

Reviewer #3 (Recommendations for the authors): 

Remarks: 

(1) What is the consequence of impaired muscle remodeling on the organismal level? Is the eclosion of adult flies impaired? One could think of assays for this, such as quantifying failed eclosions and/or video microscopy of the eclosion process. Is muscle function impaired? One could measure the contractile force of isolated fibers during electrical stimulation as well, etc. I believe that showing the physiological importance of muscle remodeling would be the biggest advantage that could arise from using a complete animal model.

We appreciate the comments. We have added data on adult lifespan, climbing ability, and the elapsed time for eclosion in BNIP3 KO flies as supplemental information (Figures 3-figure supplement 2). In BNIP3 KO DIOMs, despite the massive accumulation of mitochondria, an organized peripheral myofibril layer with contractile function is retained. However, we have not measured the contractile force of isolated muscle cells due to technical limitations. We plan to address this in future studies.

A related note is that I missed the proper discussion of the function and fate of these short-lived adult muscles (please see references in my summary). 

We have added a sentence regarding the function and fate of DIOMs in the introduction (lines 80-82) as follows: “The remodeled adult DIOMs function during eclosion, persist for approximately 12 hours, and are subsequently eliminated via programmed cell death (Kimura and Truman, 1990; J Neurosci. 1990;10:403-1)”.

(2) I don't think that "data not shown" should be used these days, when supplemental data allow the inclusion of not-so-critical results. 

We have added the data as Figure 5-figure supplement 2. As shown in the figure, overexpression of GFP-BNIP3 in 3IL BWMs did not induce the formation of tdTomato-positive autolysosomes, which are abundantly accumulated in DIOMs at 1 and 2 d APF.

(3) The term "naked mitochondria" does not sound scientific enough to this reviewer. I suggest "cytosolic mitochondria" or "unengulfed mitochondria". 

In accordance with the reviewer’s suggestion, we have replaced “naked mitochondria” with “unengulfed mitochondria” (lines 251 and 670).

eLife Assessment

Understanding how neural circuits mediate decision-making is a core problem in neuroscience. In this interesting and important work, the authors use detailed behavioral analysis and rigorous quantitative modeling to convincingly support the idea that the nematode C. elegans uses an "accept-reject" behavioral strategy, based on learned features of its environment, to make decisions upon encountering food patches. The work expands our understanding of the behavioral repertoire of this species, providing a foundation for future mechanistic studies in this powerful model system.

Reviewer #1 (Public review):

Summary:

This work uses a novel, ethologically relevant behavioral task to explore decision-making paradigms in C. elegans foraging behavior. By rigorously quantifying multiple features of animal behavior as they navigate in a patch food environment, the authors provide strong evidence that worms exhibit one of three qualitatively distinct behavioral responses upon encountering a patch: (1) "search", in which the encountered patch is below the detection threshold; (2) "sample", in which animals detect a patch encounter and reduce their motor speed, but do not stay to exploit the resource and are therefore considered to have "rejected" it; and (3) "exploit", in which animals "accept" the patch and exploit the resource for tens of minutes. Interestingly, the probability of these outcomes varies with the density of the patch as well as the prior experience of the animal. Together, these experiments provide an interesting new framework for understanding the ability of the C. elegans nervous system to use sensory information and internal state to implement behavioral state decisions.

Strengths:

The work uses a novel, neuroethologically-inspired approach to studying foraging behavior

The studies are carried out with an exceptional level of quantitative rigor and attention to detail

Powerful quantitative modeling approaches including GLMs are used to study the behavioral states that worms enter upon encountering food, and the parameters that govern the decision about which state to enter

The work provides strong evidence that C. elegans can make 'accept-reject' decisions upon encountering a food resource

Accept-reject decisions depend on the quality of the food resource encountered as well as on internally represented features that provide measurements of multiple dimensions of internal state, including feeding status and time.

Reviewer #2 (Public review):

This study provides an experimental and computational framework to examine and understand how C. elegans make decisions while foraging environments with patches of food. The authors show that C. elegans reject or accept food patches depending on a number of internal and external factors.

The key novelty of this paper is the explicit demonstration of behavior analysis and quantitative modeling to elucidate decision-making processes. In particular, the description of the exploring vs. exploiting phases, and sensing vs. non-sensing categories of foraging behavior based on the clustering of behavioral states defined in a multi-dimensional behavior-metrics space, and the implementation of a generalized linear model (GLM) whose parameters can provide quantitative biological interpretations.

The work builds on the literature of C. elegans foraging by adding the reject/accept framework.

Reviewer #3 (Public review):

Summary:

In this study by Haley et al, the authors investigated explore-exploit foraging using C. elegans as a model system. Through an elegant set of patchy environment assays, the authors built a GLM based on past experience that predicts whether an animal will decide to stay on a patch to feed and exploit that resource, instead of choosing to leave and explore other patches.

Strengths:

I really enjoyed reading this paper. The experiments are simple and elegant, and address fundamental questions of foraging theory in a well-defined system. The experimental design is thoroughly vetted, and the authors provide a considerable volume of data to prove their points.

Weakness:

History-dependence of the GLM. The logistic GLM seems like a logical way to model a binary choice, and I think the parameters you chose are certainly important. However, the framing of them seem odd to me. I do not doubt the animals are assessing the current state of the patch with an assessment of past experience; that makes perfect logical sense. However, it seems odd to reduce past experience to the categories of recently exploited patch, recently encountered patch, and time since last exploitation. This implies the animals have some way of discriminating these past patch experiences and committing them to memory. Also, it seems logical that the time on these patches, not just their density, should also matter, just as the time without food matters. Time is inherent to memory. This model also imposes a prior categorization in trying to distinguish between sensed vs. not-sensed patches, which I criticized earlier. Only "sensed" patches are used in the model, but it is questionable whether worms genuinely do not "sense" these patches.

It seems more likely the worm simply has some memory of chemosensation and relative satiety, both of which increase on patches, and decrease while off of patches. The magnitudes are likely a function of patch density. That being said, I leave it up to the reader to decide how best to interpret the data.

Impact:

I think this work will have a solid impact on the field, as it provides tangible variables to test how animals assess their environment and decide to exploit resources. I think the strength of this research could be strengthened by a reassessment of their model that would both simplify it and provide testable timescales of satiety/starvation memory.

Author Response:

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

Reviewer #1 (Public review):

Summary:

This work uses a novel, ethologically relevant behavioral task to explore decision-making paradigms in C. elegans foraging behavior. By rigorously quantifying multiple features of animal behavior as they navigate in a patch food environment, the authors provide strong evidence that worms exhibit one of three qualitatively distinct behavioral responses upon encountering a patch: (1) "search", in which the encountered patch is below the detection threshold; (2) "sample", in which animals detect a patch encounter and reduce their motor speed, but do not stay to exploit the resource and are therefore considered to have "rejected" it; and (3) "exploit", in which animals "accept" the patch and exploit the resource for tens of minutes. Interestingly, the probability of these outcomes varies with the density of the patch as well as the prior experience of the animal. Together, these experiments provide an interesting new framework for understanding the ability of the C. elegans nervous system to use sensory information and internal state to implement behavioral state decisions.

Strengths:

The work uses a novel, neuroethologically-inspired approach to studying foraging behavior

The studies are carried out with an exceptional level of quantitative rigor and attention to detail

Powerful quantitative modeling approaches including GLMs are used to study the behavioral states that worms enter upon encountering food, and the parameters that govern the decision about which state to enter

The work provides strong evidence that C. elegans can make 'accept-reject' decisions upon encountering a food resource

Accept-reject decisions depend on the quality of the food resource encountered as well as on internally represented features that provide measurements of multiple dimensions of internal state, including feeding status and time

Reviewer #2 (Public review):

This study provides an experimental and computational framework to examine and understand how C. elegans make decisions while foraging environments with patches of food. The authors show that C. elegans reject or accept food patches depending on a number of internal and external factors.

The key novelty of this paper is the explicit demonstration of behavior analysis and quantitative modeling to elucidate decision-making processes. In particular, the description of the exploring vs. exploiting phases, and sensing vs. non-sensing categories of foraging behavior based on the clustering of behavioral states defined in a multi-dimensional behavior-metrics space, and the implementation of a generalized linear model (GLM) whose parameters can provide quantitative biological interpretations.

The work builds on the literature of C. elegans foraging by adding the reject/accept framework.

Reviewer #3 (Public review):

Summary:

In this study by Haley et al, the authors investigated explore-exploit foraging using C. elegans as a model system. Through an elegant set of patchy environment assays, the authors built a GLM based on past experience that predicts whether an animal will decide to stay on a patch to feed and exploit that resource, instead of choosing to leave and explore other patches.

Strengths:

I really enjoyed reading this paper. The experiments are simple and elegant, and address fundamental questions of foraging theory in a well-defined system. The experimental design is thoroughly vetted, and the authors provide a considerable volume of data to prove their points. My only criticisms have to do with the data interpretation, which I think are easily addressable.

Weaknesses:

History-dependence of the GLM

The logistic GLM seems like a logical way to model a binary choice, and I think the parameters you chose are certainly important. However, the framing of them seem odd to me. I do not doubt the animals are assessing the current state of the patch with an assessment of past experience; that makes perfect logical sense. However, it seems odd to reduce past experience to the categories of recently exploited patch, recently encountered patch, and time since last exploitation. This implies the animals have some way of discriminating these past patch experiences and committing them to memory. Also, it seems logical that the time on these patches, not just their density, should also matter, just as the time without food matters. Time is inherent to memory. This model also imposes a prior categorization in trying to distinguish between sensed vs. not-sensed patches, which I criticized earlier. Only "sensed" patches are used in the model, but it is questionable whether worms genuinely do not "sense" these patches.

It seems more likely that the worm simply has some memory of chemosensation and relative satiety, both of which increase on patches and decrease while off of patches. The magnitudes are likely a function of patch density. That being said, I leave it up to the reader to decide how best to interpret the data.

Model design: We agree with the reviewer that past experience is not likely to be discretized into the exact parameters of our model. We have added to our manuscript to further clarify this point (lines 645-647). Investigating the mechanisms behind this behavior is beyond the scope of this project but is certainly an exciting trajectory for future C. elegans research.

osm-6

The argument is that osm-6 animals can't sense food very well, so when they sense it, they enter the exploitation state by default. That is what they appear to do, but why? Clearly they are sensing the food in some other way, correct? Are ciliated neurons the only way worms can sense food? Don't they also actively pump on food, and can therefore sense the food entering their pharynx? I think you could provide further insight by commenting on this. Perhaps your decision model is dependent on comparing environmental sensing with pharyngeal sensing? Food intake certainly influences their decision, no? Perhaps food intake triggers exploitation behavior, which can be over-run by chemo/mechanosensory information?

osm-6 behavior: We thank the reviewer for pointing out the need to further elaborate on a mechanistic hypothesis to explain the behavior of osm-6 sensory mutants. We agree with the reviewer’s speculation that post-ingestive and other non-ciliary sensory cues likely drive detection of food. We have added additional commentary to our manuscript to state this (lines 529-538).

Impact

I think this work will have a solid impact on the field, as it provides tangible variables to test how animals assess their environment and decide to exploit resources. I think the strength of this research could be strengthened by a reassessment of their model that would both simplify it and provide testable timescales of satiety/starvation memory.

Reviewer #2 (Recommendations for the authors):

The authors have addressed most of my concerns.

Reviewer #3 (Recommendations for the authors):

The authors provide a considerable amount of processed data (great, thank you!), but it would be even better if they provided the raw data of the worm coordinates, and when and where these coordinates overlapped with patches. This is the raw data that was ultimately used for all the quantifications in the paper, and would be incredibly useful to readers who are interested in modeling the data themselves.

This should not be prohibitive.

Data Availability: We thank the reviewer for pointing out this need. We are uploading all processed data (e.g. worm coordinates relative to the arena and patches) to a curated data storage server. We have updated our data availability statement to state this (lines 684-688).

Search vs. sample & sensing vs. non-sensing.

The different definitions of behaviors in Figures 2H-K are a bit confusing. I think the confusion stems in part from the changing terms and color associations in Figures 2 H-K. Essentially the explore density in Figure 2 H is split into two densities based on the two densities (sensing vs. non-responding) observed in Figure 2I. In turn, the sensing density in Figure 2I is split into two densities (explore vs exploit) based on the two densities observed in Figure 2 H. But the way the figures are colored, yellow means search (Figure 2H) and non-responding (Figure 2I), green means exploit (Figure 2H) which includes sensing and non-responding, but also exclusively sensing (Figure 2I), and blue consistently means exploit in both figures. It might help to use two different color codes for Figures 2H and 2I, and then in 2J you define search as explore AND non-responding, sample as explore AND sensing, and exploit as exploit.

Color schema: While we understand the confusion, we believe that introducing additional colors may also present some misunderstandings. We have decided to leave the figure as it is.

eLife Assessment

This is a well-written study that presents a solid genetic screen to identify regulators of adipose morphology and remodeling in zebrafish. The authors generated a rigorous screening platform based on live, whole animal imaging and statistical methods that revealed both novel and known genes critical for adipose regulation. This work is valuable because it provides several candidate genes relevant to metabolic health and a quantitative screening pipeline that will be beneficial for future studies. A limitation of the study is that it precludes a definitive distinction between developmental and remodeling effects.

Joint Public Review:

In this manuscript, Wafer and Tandon et al. present a thoughtful and well-designed genetic screen for regulators of adipose remodeling using zebrafish as a model system. The authors cross-referenced several human adipocyte-related transcriptomic and genetic association datasets to identify candidate genes, which they then tested in zebrafish. Importantly, the authors devised an unbiased microscopy-based screening platform to document quantitative adipose phenotypes with whole animal imaging, while also employing rigorous statistical methods. From their screen, the authors identified 6 genes that resulted in robust adipose phenotypes out of a total of 25 that were tested. Overall, this work will be a useful resource for the field because of both the genes identified and the quantitative, rigorous screening pipeline. However, there are limitations that preclude a definitive distinction between developmental and remodeling effects that should be acknowledged and discussed, or addressed with new experiments.

Strengths:

(1) This work combines multiple omic datasets to identify candidate genes that informed a CRISPR-based screen to identify genes underlying adipose tissue development and adaptation. This approach offers a new avenue to improve our understanding and testing of new genetic mechanisms underlying the development of obesity.

(2) Using a clever screening approach, this study identifies new genes that are associated with adipose tissue lipid droplet size change. Importantly, the study provides further validation using a stable CRISPR line to show the phenotype in basal and high-fat diet conditions.

(3) The experiments are well-designed and rigorous. Sample sizes are large. Statistical analyses are highly rigorous, contributing to a high-quality study.

Weaknesses:

(1) The image quantification established in Figures 3 and 4 and used in CRISPR screening showed the relationship among zebrafish development, adipose tissue size, and lipid droplet size. Although adipose tissue development patterning is linked with adipose tissue adaptation, as shown by the evidence provided in this paper, it will be more powerful if the imaging method and pipeline were established to directly access the adipose tissue plasticity rather than just the developmental patterning. Furthermore, the authors should perform additional analysis of their existing data to more accurately determine lipid droplet size along the AP axis in response to HFD.

(2) In the absence of tissue-specific manipulations, definitively establishing the mechanisms underlying the genetic regulation of adipose tissue physiology presents limitations.