eLife Assessment

This important study explores how the phase of neural oscillations in the alpha band affects visual perception, indicating that perceptual performance varies due to changes in sensory precision rather than decision bias. The evidence is solid in its experimental design and analytical approach, although the limited sample size restricts the generalizability of the findings. This work should interest cognitive neuroscientists who study perception and decision-making.

Reviewer #1 (Public review):

Summary:

In their paper entitled "Alpha-Band Phase Modulates Perceptual Sensitivity by Changing Internal Noise and Sensory Tuning," Pilipenko et al. investigate how pre-stimulus alpha phase influences near-threshold visual perception. The authors aim to clarify whether alpha phase primarily shifts the criterion, multiplicatively amplifies signals, or changes the effective variance and tuning of sensory evidence. Six observers completed many thousands of trials in a double-pass Gabor-in-noise detection task while an EEG was recorded. The authors combine signal detection theory, phase-resolved analyses, and reverse correlation to test mechanistic predictions. The experimental design and analysis pipeline provide a clear conceptual scaffold, with SDT-based schematic models that make the empirical results accessible even for readers who are not specialists in classification-image methods.

Strengths:

The study presents a coherent and well-executed investigation with several notable strengths. First, the main behavioral and EEG results in Figure 2 demonstrate robust pre-stimulus coupling between alpha phase and d′ across a substantial portion of the pre-stimulus interval, with little evidence that the criterion is modulated to a comparable extent. The inverse phasic relationship between hit and false-alarm rates maps clearly onto the variance-reduction account, and the response-consistency analysis offers an intuitive behavioral complement: when two identical stimuli are both presented at the participant's optimal phase, responses are more consistent than when one or both occur at suboptimal phases. The frontal-occipital phase-difference result suggests a coordinated rather than purely local phase mechanism, supporting the central claim that alpha phase is linked to changes in sensitivity that behave like changes in internal variability rather than simple gain or criterion shifts. Supplementary analyses showing that alpha power has only a limited relationship with d′ and confidence reassure readers that the main effects are genuinely phase-linked rather than a recasting of amplitude differences.

Second, the reverse-correlation results in Figure 3 extend this story in a satisfying way. The classification images and their Gaussian fits show that at the optimal phase, the weighting of stimulus energy is more sharply concentrated around target-relevant spatial frequencies and orientations, and the bootstrapped parameter distributions indicate that the suboptimal phase is best described by broader tuning and a modest change in gain rather than a pure criterion account. The authors' interpretation that optimal-phase perception reflects both reduced effective internal noise and sharpened sensory tuning is reasonable and well-supported. Overall, the data and figures largely achieve the stated aims, and the work is likely to have an impact both by clarifying the interpretation of alpha-phase effects and by illustrating a useful analytic framework that other groups can adopt.

Weaknesses:

The weaknesses are limited and relate primarily to framing and presentation rather than to the substance of the work. First, because contrast was titrated to maintain moderate performance (d′ between 1.2 and 1.8), the phase-linked changes in sensitivity appear modest in absolute terms, which could benefit from explicit contextualization. Second, a coding error resulted in unequal numbers of double-pass stimulus pairs across participants, which affects the interpretability of the response-consistency results. Third, several methodological details could be stated more explicitly to enhance transparency, including stimulus timing specifications, electrode selection criteria, and the purpose of phase alignment in group averaging. Finally, some mechanistic interpretations in the Discussion could be phrased more conservatively to clearly distinguish between measurement and inference, particularly regarding the relationship between reduced internal noise and sharpened tuning, and the physiological implementation of the frontal-occipital phase relationship.

Reviewer #2 (Public review):

Summary:

The study of Pilipenko et al evaluated the role of alpha phase in a visual perception paradigm using the framework of signal detection theory and reverse correlation. Their findings suggest that phase-related modulations in perception are mediated by a reduction in internal noise and a moderate increase in tuning to relevant features of the stimuli in specific phases of the alpha cycle. Interestingly, the alpha phase did not affect the criterion. Criterion was related to modulations in alpha power, in agreement with previous research.

Strengths:

The experiment was carefully designed, and the analytical pipeline is original and suited to answer the research question. The authors frame the research question very well and propose several models that account for the possible mechanisms by which the alpha phase can modulate perception. This study can be very valuable for the ongoing discussion about the role of alpha activity in perception.

Weaknesses:

The sample size collected (N = 6) is, in my opinion, too small for the statistical approach adopted (group level). It is well known that small sample sizes result in an increased likelihood of false positives; even in the case of true positives, effect sizes are inflated (Button et al., 2013; Tamar and Orban de Xivry, 2019), negatively affecting the replicability of the effect.

Although the experimental design allows for an accurate characterization of the effects at the single-subject level, conclusions are drawn from group-level aggregated measures. With only six subjects, the estimation of between-subject variability is not reliable. The authors need to acknowledge that the sample size is too small; therefore, results should be interpreted with caution.

Conclusion:

This study addresses an important and timely question and proposes an original and well-thought-out analytical framework to investigate the role of alpha phase in visual perception. While the experimental design and theoretical motivation are strong, the very limited sample size substantially constrains the strength of the conclusions that can be drawn at the group level.

Bibliography:

Button, K., Ioannidis, J., Mokrysz, C. et al. Power failure: why small sample size undermines the reliability of neuroscience. Nat Rev Neurosci 14, 365-376 (2013). https://doi.org/10.1038/nrn3475

Tamar R Makin, Jean-Jacques Orban de Xivry (2019) Science Forum: Ten common statistical mistakes to watch out for when writing or reviewing a manuscript eLife 8:e48175 https://doi.org/10.7554/eLife.48175

Author response:

We would like to thank the reviewers for their helpful feedback. We appreciate their recognition of many positive features from our study and plan to address the weaknesses with the following set of changes:

Reviewer #1 rightly points out that the titration of performance throughout the experiment could reduce the overall size of the phasic effect we observed by compressing the overall range of d’. In our revision, we plan to acknowledge the potential consequence of stimulus titration as well as emphasize that the resultant vector length approach we took to quantify phase-behavior coupling is a better reflection of the effect size than the plot of phase-binned d’. Next, we will include language cautioning the certainty of our double-pass statistics since half of our participants had much fewer double-pass trials due to a coding error. Finally, we can gladly clarify methodological details requested and revise the discussions by phrasing several of our interpretations more conservatively: specifically discussing the possibility that the frontal-occipital phase difference could also arise from two counter-phase sources, and including the possibility that sensory noise reduction and sharpened tuning may be two separate mechanisms.

Reviewer #2 raises concerns about performing group-level statistical analyses on a small sample size. We acknowledge this as a reasonable concern and will include the single-subject effects of our main analysis in the Supplementary Materials as well as discuss that although the sample size is a limitation of our study, there are several justifications for taking a small-n, large-trial approach given our research question. We would also like to highlight that we feel more confident in the reproducibility of our results given the convergence of evidence across multiple measures (phase-d’ coupling, counter-phasic hit and false alarm rates, response consistency, and classification images) which are all pointing towards a consistent interpretation of a phase effect on internal variability.

eLife Assessment

IL21R, being a key cytokine receptor for shaping the T follicular helper and B cell functions, utilizes two STAT family members, STAT1 and STAT3. The authors utilize the IL21R ENU-induced mutant, together with relevant in vitro and in vivo experiments, to dissect the function of STAT1 and STAT3. The approach by itself sounds reasonable, but the main conclusions are incompletely supported by the data presented in this manuscript.

Reviewer #1 (Public review):

Summary:

King and colleagues generated a mouse with a point mutation in IL21R and investigated the influence on IL-21-mediated T and B cell activation and differentiation. They found that mutant mice show a reduced T and B cell response, with CD4 T cell differentiation into T follicular helper cells being primarily affected.

Strengths:

The authors combined in vitro and in vivo analysis, including bone-marrow chimeric mice.

Weaknesses:

The effect of the IL21R EINS mutant does not specifically affect STAT1, as clearly shown in Figure 1 H, I. Particularly at lower doses of IL21, which may be more relevant in vivo, the effects are very similar. A second key weakness is the very small Tfh response, a not very clear PD-1 and CXCR5 staining to identify Tfh, and a lack of a steady-state (prior to immunisation) comparison of Tfh numbers in the different mouse strains. The latter makes it impossible to know what fraction of the response is antigen-specific.

Reviewer #2 (Public review):

Summary:

In the manuscript, "An IL-21R hypomorph circumvents functional redundancy to define STAT1 signaling in germinal center responses," Cecile King and colleagues identify a cytoplasmic site of the IL-21 receptor that differentially regulates STAT1 and STAT3 activation upon IL-21 stimulation. They further examine the immunological consequences of this site-specific alteration on Tfh differentiation and Tfh-dependent humoral immunity, raising important questions about how gene-knockout models may obscure nuanced functional roles of signaling molecules.

Strengths:

The study convincingly highlights a non-redundant role for STAT1 downstream of IL-21-IL-21R signaling in the Tfh differentiation pathway. This conclusion is supported by in vitro analyses of STAT1 and STAT3 activation in CD4 T cells stimulated with IL-21 or IL-6; by in vivo assessments of Tfh and germinal center B cell responses in WT and IL21R-EINS mutant mice, including bone-marrow chimera systems; and by investigating the expression of Tfh-related molecules in WT versus IL21R-EINS CD4 T cells.

Weaknesses:

Although the experiments were carefully executed with appropriate controls, a key question remains unresolved: whether the Tfh differentiation defect in IL21R-EINS mice is directly attributable to reduced STAT1 activation. Rescue experiments that restore STAT1 signaling in IL21R-EINS TCR-transgenic CD4 T cells would provide strong evidence linking the mutation to impaired STAT1 activation and, consequently, defective Tfh differentiation. Without such evidence, it remains formally possible that additional, uncharacterized mutations introduced during ENU mutagenesis contribute to the phenotypes observed, particularly given the discrepancies between IL21R knockout and IL21R-EINS mutant mice.

eLife Assessment

This is a useful study presenting solid data indicating that the bacterial GTPases EngA and ObgE enable single-step reconstitution of functional 50S ribosomal subunits under near-physiological conditions. The study elegantly bridges the gap between the non-physiological aspects of the previous two-step reconstitution method and the extract-dependent iSAT system to enable ribosome assembly under translation-compatible conditions; however, it is limited by reliance on rRNA and proteins extracted from native ribosomes and does not achieve a true bottom-up reconstruction from all synthetic components. The evidence is incomplete in not characterizing the spectrum of reporter polypeptides produced and not comparing their rate and yield of synthesis from reconstituted ribosomes to that obtained with pure native ribosomes; and the impact of the study is limited by not including reporters to examine the fidelity of initiation, elongation or termination achieved with the reconstituted ribosomes.

Reviewer #1 (Public review):

Summary:

This study presents evidence that the addition of the two GTPases EngA and ObgE to reactions comprised of rRNAs and total ribosomal proteins purified from native bacterial ribosomes can bypass the requirements for non-physiological temperature shifts and Mg⁺² ion concentrations for in vitro reconstitution of functional E. coli ribosomes.

Strengths:

This advance allows ribosome reconstitution in a fully reconstituted protein synthesis system containing individually purified recombinant translation factors, with the reconstituted ribosomes substituting for native purified ribosomes to support protein synthesis. This work potentially represents an important development in the long-term effort to produce synthetic cells.

Weaknesses:

While much of the evidence is solid, the analysis is incomplete in certain respects that detract from the scientific quality and significance of the findings:

(1) The authors do not describe how the native ribosomal proteins (RPs) were purified, and it is unclear whether all subassemblies of RPs have been disrupted in the purification procedure. If not, additional chaperones might be required beyond the two GTPases described here for functional ribosome assembly from individual RPs.

(2) Reconstitution studies in the past have succeeded by using all recombinant, individually purified RPs, which would clearly address the issue in the preceding comment and also eliminate the possibility that an unknown ribosome assembly factor that co-purifies with native ribosomes has been added to the reconstitution reactions along with the RPs.

(3) They never compared the efficiency of the reconstituted ribosomes to native ribosomes added to the "PURE" in vitro protein synthesis system, making it unclear what proportion of the reconstituted ribosomes are functional, and how protein yield per mRNA molecule compares to that given by the PURE system programmed with purified native ribosomes.

(4) They also have not examined the synthesized GFP protein by SDS-PAGE to determine what proportion is full-length.

(5) The previous development of the PURE system included examinations of the synthesis of multiple proteins, one of which was an enzyme whose specific activity could be compared to that of the native enzyme. This would be a significant improvement to the current study. They could also have programmed the translation reactions containing reconstituted ribosomes with (i) total native mRNA and compared the products in SDS-PAGE to those obtained with the control PURE system containing native ribosomes; (ii) with specifc reporter mRNAs designed to examine dependence on a Shine-Dalgarno sequence and the impact of an in-frame stop codon in prematurely terminating translation to assess the fidelity of initiation and termination events; and (iii) an mRNA with a programmed frameshift site to assess elongation fidelity displayed by their reconstituted ribosomes.

Reviewer #2 (Public review):

This study presents a significant advance in the field of in vitro ribosome assembly by demonstrating that the bacterial GTPases EngA and ObgE enable single-step reconstitution of functional 50S ribosomal subunits under near-physiological conditions-specifically at 37 {degree sign}C and with total Mg²⁺ concentrations below 10 mM.

This achievement directly addresses a long-standing limitation of the traditional two-step in vitro assembly protocol (Nierhaus & Dohme, PNAS 1974), which requires non-physiological temperatures (44-50 {degree sign}C), and high Mg²⁺ concentrations (~20 mM). Inspired by the integrated Synthesis, Assembly, and Translation (iSAT) platform (Jewett et al., Mol Syst Biol 2013), leveraging E. coli S150 crude extract, which supplies essential assembly factors, the authors hypothesize that specific ribosome biogenesis factors-particularly GTPases present in such extracts-may be responsible for enabling assembly under mild conditions. Through systematic screening, they identify EngA and ObgE as the minimal pair sufficient to replace the need for temperature and Mg²⁺ shifts when using phenol-extracted (i.e., mature, modified) rRNA and purified TP70 proteins.

However, several important concerns remain:

(1) Dependence on Native rRNA Limits Generalizability

The current system relies on rRNA extracted from native ribosomes via phenol, which retains natural post-transcriptional modifications. As the authors note (lines 302-304), attempts to assemble active 50S subunits using in vitro transcribed rRNA, even in the presence of EngA and ObgE, failed. This contrasts with iSAT, where in vitro transcribed rRNA can yield functional (though reduced-activity, ~20% of native) ribosomes, presumably due to the presence of rRNA modification enzymes and additional chaperones in the S150 extract. Thus, while this study successfully isolates two key GTPase factors that mimic part of iSAT's functionality, it does not fully recapitulate iSAT's capacity for de novo assembly from unmodified RNA. The manuscript should clarify that the in vitro assembly demonstrated here is contingent on using native rRNA and does not yet achieve true bottom-up reconstruction from synthetic parts. Moreover, given iSAT's success with transcribed rRNA, could a similar systematic omission approach (e.g., adding individual factors) help identify the additional components required to support unmodified rRNA folding?

(2) Imprecise Use of "Physiological Mg²⁺ Concentration"

The abstract states that assembly occurs at "physiological Mg²⁺ concentration" (<10 mM). However, while this total Mg²⁺ level aligns with optimized in vitro translation buffers (e.g., in PURE or iSAT systems), it exceeds estimates of free cytosolic [Mg²⁺] in E. coli (~1-2 mM). The authors should clarify that they refer to total Mg²⁺ concentrations compatible with cell-free protein synthesis, not necessarily intracellular free ion levels, to avoid misleading readers about true physiological relevance.

In summary, this work elegantly bridges the gap between the two-step method and the extract-dependent iSAT system by identifying two defined GTPases that capture a core functionality of cellular extracts: enabling ribosome assembly under translation-compatible conditions. However, the reliance on native rRNA underscores that additional factors - likely present in iSAT's S150 extract - are still needed for full de novo reconstitution from unmodified transcripts. Future work combining the precision of this defined system with the completeness of iSAT may ultimately realize truly autonomous synthetic ribosome biogenesis.

Author response

Public Reviews:

Reviewer #1 (Public review):

This study presents evidence that the addition of the two GTPases EngA and ObgE to reactions comprised of rRNAs and total ribosomal proteins purified from native bacterial ribosomes can bypass the requirements for non-physiological temperature shifts and Mg⁺² ion concentrations for in vitro reconstitution of functional E. coli ribosomes.

Strengths:

This advance allows ribosome reconstitution in a fully reconstituted protein synthesis system containing individually purified recombinant translation factors, with the reconstituted ribosomes substituting for native purified ribosomes to support protein synthesis. This work potentially represents an important development in the long-term effort to produce synthetic cells.

Weaknesses:

While much of the evidence is solid, the analysis is incomplete in certain respects that detract from the scientific quality and significance of the findings:

(1) The authors do not describe how the native ribosomal proteins (RPs) were purified, and it is unclear whether all subassemblies of RPs have been disrupted in the purification procedure. If not, additional chaperones might be required beyond the two GTPases described here for functional ribosome assembly from individual RPs.

Native ribosomal proteins (RPs) were prepared from native ribosomes, according to the well-established protocol described by Dr. Knud H. Nierhaus [Nierhaus, K. H. Reconstitution of ribosomes in Ribosomes and protein synthesis: A Practical Approach (Spedding G. eds.) 161-189, IRL Press at Oxford University Press, New York (1990)]. In this method, ribosome proteins are subjected to dialysis in 6 M urea buffer, a strong denaturing condition that may completely disrupt ribosomal structure and dissociate all ribosomal protein subassemblies. To make this point clear, we will describe the ribosomal protein (RP) preparation procedure in the manuscript, rather than merely referring to the book.

In addition, we would like to clarify one point related to this comment. The focus of the present study is to show that the presence of two factors is required for single-step ribosome reconstitution under translation-compatible, cell-free conditions. We do not intend to claim that these two factors are absolutely sufficient for ribosome reconstitution. Hence, we will revise the manuscript to more explicitly state what this work does and does not conclude.

(2) Reconstitution studies in the past have succeeded by using all recombinant, individually purified RPs, which would clearly address the issue in the preceding comment and also eliminate the possibility that an unknown ribosome assembly factor that co-purifies with native ribosomes has been added to the reconstitution reactions along with the RPs.

As noted in the response to the Comment (1), the focus of the present study is the requirement of the two factors for functional ribosome assembly. Therefore, we consider that it is not necessary to completely exclude the possibility that unknown ribosome assembly factors are present in the RP preparation. Nevertheless, we agree that it is important to clarify what factors, if any, are co-present in the RP fraction. To address this, we plan to add proteomic analysis results of the TP70 preparation.

We also agree that additional, as-yet-unidentified components, including factors involved in rRNA modification, could plausibly further improve assembly efficiency. We will explicitly note this possibility in the Discussion.

Finally, extending the system to the use of in vitro-transcribed rRNA and fully recombinant ribosomal proteins could be essentially a next step of this study, and we are currently exploring these directions in our laboratory. However, we consider them beyond the scope of the present study and will provide them as future perspectives of this study in the Discussion.

(3) They never compared the efficiency of the reconstituted ribosomes to native ribosomes added to the "PURE" in vitro protein synthesis system, making it unclear what proportion of the reconstituted ribosomes are functional, and how protein yield per mRNA molecule compares to that given by the PURE system programmed with purified native ribosomes.

We consider that it is feasible to estimate the GFP synthesis rate from the increase in fluorescence over time under conditions where the template mRNA is in excess, and to compare this rate directly between reconstituted and native ribosomes. We will therefore consider performing this experiment. This comparison should provide insight into what fraction of ribosomes reconstituted in our system are functionally active.

By contrast, quantifying protein yield per mRNA molecule is substantially more challenging. The translation system is complex, and the apparent yield per mRNA can vary depending on factors such as differences in polysome formation efficiency. In addition, the PURE system is a coupled transcription–translation setup that starts from DNA templates, which further complicates rigorous normalization on a per-mRNA basis. Because the main focus of this study is to determine how many functionally active ribosomes can be reconstituted under translation-compatible conditions, we plan to address this comment by carrying out the former experiment.

(4) They also have not examined the synthesized GFP protein by SDS-PAGE to determine what proportion is full-length.

Because we can add an affinity tag to the GFP reporter, it should be feasible to selectively purify the synthesized protein from the reaction mixture and analyze it by SDS–PAGE. We therefore plan to perform this experiment.

(5) The previous development of the PURE system included examinations of the synthesis of multiple proteins, one of which was an enzyme whose specific activity could be compared to that of the native enzyme. This would be a significant improvement to the current study. They could also have programmed the translation reactions containing reconstituted ribosomes with (i) total native mRNA and compared the products in SDS-PAGE to those obtained with the control PURE system containing native ribosomes; (ii) with specifc reporter mRNAs designed to examine dependence on a Shine-Dalgarno sequence and the impact of an in-frame stop codon in prematurely terminating translation to assess the fidelity of initiation and termination events; and (iii) an mRNA with a programmed frameshift site to assess elongation fidelity displayed by their reconstituted ribosomes.

Following the recommendation, we plan to test the synthesis of at least one additional protein with enzymatic activity, in addition to GFP, so that the activity of the translated product can be assessed.

We agree that comparing translation products using total mRNA, testing dependence on the Shine–Dalgarno sequence, and performing dedicated assays to evaluate initiation/elongation/termination fidelity are all attractive and valuable studies. However, we consider these to be beyond the scope of the present manuscript. We will therefore describe them explicitly as future directions in the Discussion.

At the same time, we anticipate that mass spectrometric (MS) analysis of GFP and the enzyme product(s) that we attempt to synthesize could partially address concerns related to product integrity (e.g., truncations) and, to some extent, translational fidelity. We therefore plan to carry out MS analysis of these translated products.

Reviewer #2 (Public review):

This study presents a significant advance in the field of in vitro ribosome assembly by demonstrating that the bacterial GTPases EngA and ObgE enable single-step reconstitution of functional 50S ribosomal subunits under near-physiological conditions-specifically at 37 {degree sign}C and with total Mg²⁺ concentrations below 10 mM.

This achievement directly addresses a long-standing limitation of the traditional two-step in vitro assembly protocol (Nierhaus & Dohme, PNAS 1974), which requires non-physiological temperatures (44-50 {degree sign}C), and high Mg²⁺ concentrations (~20 mM). Inspired by the integrated Synthesis, Assembly, and Translation (iSAT) platform (Jewett et al., Mol Syst Biol 2013), leveraging E. coli S150 crude extract, which supplies essential assembly factors, the authors hypothesize that specific ribosome biogenesis factors-particularly GTPases present in such extracts-may be responsible for enabling assembly under mild conditions. Through systematic screening, they identify EngA and ObgE as the minimal pair sufficient to replace the need for temperature and Mg²⁺ shifts when using phenol-extracted (i.e., mature, modified) rRNA and purified TP70 proteins.

However, several important concerns remain:

(1) Dependence on Native rRNA Limits Generalizability

The current system relies on rRNA extracted from native ribosomes via phenol, which retains natural post-transcriptional modifications. As the authors note (lines 302-304), attempts to assemble active 50S subunits using in vitro transcribed rRNA, even in the presence of EngA and ObgE, failed. This contrasts with iSAT, where in vitro transcribed rRNA can yield functional (though reduced-activity, ~20% of native) ribosomes, presumably due to the presence of rRNA modification enzymes and additional chaperones in the S150 extract. Thus, while this study successfully isolates two key GTPase factors that mimic part of iSAT's functionality, it does not fully recapitulate iSAT's capacity for de novo assembly from unmodified RNA. The manuscript should clarify that the in vitro assembly demonstrated here is contingent on using native rRNA and does not yet achieve true bottom-up reconstruction from synthetic parts. Moreover, given iSAT's success with transcribed rRNA, could a similar systematic omission approach (e.g., adding individual factors) help identify the additional components required to support unmodified rRNA folding?

We fully recognize the reviewer’s point that our current system has not yet achieved a true bottom-up reconstruction. Although we intended to state this clearly in the manuscript, the fact that this concern remains indicates that our description was not sufficiently explicit. We will therefore revisit the organization and wording of the manuscript and revise it to ensure that this limitation is clearly communicated to readers.

(2) Imprecise Use of "Physiological Mg²⁺ Concentration"

The abstract states that assembly occurs at "physiological Mg²⁺ concentration" (<10 mM). However, while this total Mg²⁺ level aligns with optimized in vitro translation buffers (e.g., in PURE or iSAT systems), it exceeds estimates of free cytosolic [Mg²⁺] in E. coli (~1-2 mM). The authors should clarify that they refer to total Mg²⁺ concentrations compatible with cell-free protein synthesis, not necessarily intracellular free ion levels, to avoid misleading readers about true physiological relevance.

We agree that this is a very reasonable point. We will therefore revise the manuscript to clarify that we are referring to the total Mg²⁺ concentration compatible with cell-free protein synthesis, rather than the intracellular free Mg²⁺ level under physiological conditions.

In summary, this work elegantly bridges the gap between the two-step method and the extract-dependent iSAT system by identifying two defined GTPases that capture a core functionality of cellular extracts: enabling ribosome assembly under translation-compatible conditions. However, the reliance on native rRNA underscores that additional factors - likely present in iSAT's S150 extract - are still needed for full de novo reconstitution from unmodified transcripts. Future work combining the precision of this defined system with the completeness of iSAT may ultimately realize truly autonomous synthetic ribosome biogenesis.

eLife Assessment

This important study reports characterisation of hepatocyte molecular pathways affected by a glycyrrhizin derivative in both in vivo and in vitro mouse models of alcohol-associated liver disease. The authors show convincing evidence indicating that IPP delta isomerase 1 (Idi1) is an intermediate in these pharmacological effects, via the binding of the glycyrrhizin derivative to an upstream regulator of Idi1, HSD11B1, although some more quantitative analyses and better organisation of data would strengthen the study. The findings would be of interest to immunologists and pharmacologists interested in liver inflammation and its amelioration.

Reviewer #1 (Public review):

Summary:

In this article by Xiao et al., the authors aimed to identify the precise targets by which magnesium isoglycyrrhizinate (MgIG) functions to improve liver injury in response to ethanol treatment. The authors found through a series of in vivo and molecular approaches that MgIG treatment attenuates alcohol-induced liver injury through a potential SREBP2-IdI1 axis. This manuscript adds to a previous set of literature showing MgIG improves liver function across a variety of etiologies, and also provides mechanistic insight into its mechanism of action.

Strengths:

(1) The authors use a combination of approaches from both in-vivo mouse models to in-vitro approaches with AML12 hepatocytes to support the notion that MgIG does improve liver function in response to ethanol treatment.

(2) The authors use both knockdown and overexpression approaches, in vivo and in vitro, to support most of the claims provided.

(3) Identification of HSD11B1 as the protein target of MgIG, as well as confirmation of direct protein-protein interactions between HSD11B1/SREBP2/IDI1, is novel.

Weaknesses:

Major weaknesses can be classified into 3 groups:

(1) The results do not support some claims made.

(2) Qualitative analyses of some of the lipid measures, as opposed to more quantitative analyses.

(3) There are no appropriate readouts of Srebp2 translocation and/or activity.

More specific comments:

(1) A few of the claims made are not supported by the references provided. For instance, line 76 states MgIG has hepatoprotective properties and improved liver function, but the reference provided is in the context of myocardial fibrosis.

(2) MgIG is clinically used for the treatment of liver inflammatory disease in China and Japan. In the first line of the abstract, the authors noted that MgIG is clinically approved for ALD. In which countries is MgIG approved for clinical utility in this space?

(3) Serum TGs are not an indicator of liver function. Alterations in serum TGs can occur despite changes in liver function.

(4) There are discrepancies in the results section and the figure legends. For example, line 302 states Idil is upregulated in alcohol fed mice relative to the control group. The figure legend states that the comparison for Figure 2A is that of ALD+MgIG and ALD only.

(5) Oil Red O staining provided does not appear to be consistent with the quantification in Figure 1D. ORO is nonspecific and can be highly subjective. The representative image in Figure 1C appears to have a much greater than 30% ORO (+) area.

(6) The connection between Idil expression in response to EtOH/PA treatment in AML12 cells with viability and apoptosis isn't entirely clear. MgIG treatment completely reduces Idi1 expression in response to EtOH/PA, but only moderate changes, at best, are observed in viability and apoptosis. This suggests the primary mechanism related to MgIG treatment may not be via Idi1.

(7) The nile red stained images also do not appear representative with its quantification. Several claims about more or less lipid accumulation across these studies are not supported by clear differences in nile red.

(8) The authors make a comment that Hsd11b1 expression is quite low in AML12 cells. So why did the authors choose to knockdown Hsd11b1 in this model?

(9) Line 380 - the claim that MGIG weakens the interaction between HSD11b1 and SREBP2 cannot be made solely based on one Western blot.

(10) It's not clear what the numbers represent on top of the Western blots. Are these averages over the course of three independent experiments?

(11) The claim in line 382 that knockdown of Hsd11b1 resulted in accumulation of pSREBP2 is not supported by the data provided in Figure 6D.

(12) None of the images provided in Figure 6E support the claims stated in the results. Activation of SREBP2 leads to nuclear translocation and subsequent induction of genes involved in cholesterol biosynthesis and uptake. Manipulation of Hsd11b1 via OE or KD does not show any nuclear localization with DAPI.

(13) The entire manuscript is focused on this axis of MgIG-Hsd11b1-Srebp2, but no Srebp2 transcriptional targets are ever measured.

(14) Acc1 and Scd1 are Srebp1 targets, not Srebp2.

(15) A major weakness of this manuscript is the lack of studies providing quantitative assessments of Srebp2 activation and true liver lipid measurements.

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors investigated magnesium isoglycyrrhizinate (MgIG)'s hepatoprotective actions in chronic-binge alcohol-associated liver disease (ALD) mouse models and ethanol/palmitic acid-challenged AML-12 hepatocytes. They found that MgIG markedly attenuated alcohol-induced liver injury, evidenced by ameliorated histological damage, reduced hepatic steatosis, and normalized liver-to-body weight ratios. RNA sequencing identified isopentenyl diphosphate delta isomerase 1 (IDI1) as a key downstream effector. Hepatocyte-specific genetic manipulations confirmed that MgIG modulates the SREBP2-IDI1 axis. The mechanistic studies suggested that MgIG could directly target HSD11B1 and modulate the HSD11B1-SREBP2-IDI1 axis to attenuate ALD. This manuscript is of interest to the research field of ALD.

Strengths:

The authors have performed both in vivo and in vitro studies to demonstrate the action of magnesium isoglycyrrhizinate on hepatocytes and an animal model of alcohol-associated liver disease.

Weaknesses:

The data were not well-organised, and the paper needs proofreading again, with a focus on the use of scientific language throughout.

Here are several comments:

(1) In Supplemental Figure 1A, all the treatment arms (A-control, MgIG-25 mg/kg, MgIG-50 mg/kg) showed body weight loss compared to the untreated controls. However, Figure 1E showed body weight gain in the treatment arms (A-control and MgIG-25 mg/kg), why? In Supplemental Figure 1A, the mice with MgIG (25 mg/kg) showed the lowest body weight, compared to either A-control or MgIG (50 mg/kg) treatment. Can the authors explain why MgIG (25 mg/kg) causes bodyweight loss more than MgIG (50 mg/kg)? What about the other parameters (ALT, ALS, NAS, etc.) for the mice with MgIG (50 mg/kg)?

(2) IL-6 is a key pro-inflammatory cytokine significantly involved in ALD, acting as a marker of ALD severity. Can the authors explain why MgIG 1.0 mg/ml shows higher IL-6 gene expression than MgIG (0.1-0.5 mg/ml)? Same question for the mRNA levels of lipid metabolic enzymes Acc1 and Scd1.

(3) For the qPCR results of Hsd11b1 knockdown (siRNA) and Hsd11b1 overexpression (plasmid) in AML-12 cells (Figure 5B), what is the description for the gene expression level (Y axis)? Fold changes versus GAPDH? Hsd11b1 overexpression showed non-efficiency (20-23, units on Y axis), even lower than the Hsd11b1 knockdown (above 50, units on Y axis). The authors need to explain this. For the plasmid-based Hsd11b1 overexpression, why does the scramble control inhibit Hsd11b1 gene expression (less than 2, units on the Y axis)? Again, this needs to be explained.

Author response:

Thank you for your letter and for the constructive feedback from the reviewers on our manuscript (eLife-RP-RA-2025-109174). We appreciate the time and expertise you and the reviewers have dedicated to improving our work.

We have carefully considered all comments and have developed a comprehensive revision plan. To address the primary concerns, we will conduct several new experiments designed to provide robust support for our key conclusions. Other points will be addressed through textual revisions, including the addition of existing ADMET data and an expanded discussion section.

We are confident that these revisions will fully satisfy the reviewers' concerns and significantly strengthen the manuscript. Our detailed experimental plan and point-by-point responses are provided below.

(1) Addressing "Qualitative analyses of some of the lipid measures, as opposed to more quantitative analyses"

Supplementary experiments and analyses

We will add the assessment of hepatic triglyceride and total cholesterol levels in liver tissues from control, experimental, and drug-treated mice, thereby providing further quantitative validation.

(2) Addressing "SREBP2"

Supplementary experiments and analyses

We will include a luciferase assay to determine whether alcohol plus PA induces SREBP2 activation in AML-12 cells.

As suggested, we will assess the expression levels of SREBP2 downstream target genes (Hmgcr, Hmgcs, Ldlr, and Lcn2) in both in vitro and in vivo models.

(3) Timeline and process arrangement of supplementary experiments

To comprehensively address these issues, we plan to purchase the following required reagents and have formulated the following experimental plan:

Author response table 1.

Given the time required for reagent acquisition and the execution of these in vitro and in vivo experiments, we kindly request an extension of the revision deadline by 8 weeks. This will ensure the comprehensive and high-quality completion of all necessary studies.

We will fully commit to delivering a thoroughly revised manuscript that robustly addresses all reviewer comments and aligns with the high standards of eLife. We greatly appreciate your guidance and flexibility.

eLife Assessment

This important study examines how mismatched light and temperature cycles shape Drosophila locomotor timing and temperature-dependent timeless splicing, and leverages long-term early/late selection lines to probe evolutionary plasticity. The strength of evidence is incomplete at present, mainly because startle/masking under step cues could confound the behavioural readouts, and tim's involvement remains correlative. The authors should address masking in the behaviour analyses and provide causal support for tim's role.

Reviewer #1 (Public review):

Summary:

This manuscript addresses an important question: how do circadian clocks adjust to a complex rhythmic environment with multiple daily rhythms? The focus is on the temperature and light cycles (TC and LD) and their phase relationship. In nature, TC usually lags the LD cycle, but the phase delay can vary depending on seasonal and daily weather conditions. The authors present evidence that circadian behavior adjusts to different TC/LD phase relationships, that temperature-sensitive tim splicing patterns might underlie some of these responses, and that artificial selection for preferential evening or morning eclosion behavior impacts how flies respond to different LD/TC phase relationship

Strength:

Experiments are conducted on control strains and strains that have been selected in the laboratory for preferential morning or evening eclosion phenotypes. This study is thus quite unique as it allows us to probe whether this artificial selection impacted how animals respond to different environmental conditions, and thus gives hints on how evolution might shape circadian oscillators and their entrainment. The authors focused on circadian locomotor behavior and timeless (tim) splicing because warm and cold-specific transcripts have been described as playing an important role in determining temperature-dependent circadian behavior. Not surprisingly, the results are complex, but there are interesting observations. In particular, the "late" strain appears to be able to adjust more efficiently its evening peak in response to changes in the phase relationship between temperature and light cycles, but the morning peak seems less responsive in this strain. Differences in the circadian pattern of expression of different tim mRNA isoforms are found under specific LD/TC conditions.

Weaknesses:

These observations are interesting, but in the absence of specific genetic manipulations, it is difficult to establish a causative link between tim molecular phenotypes and behavior. The study is thus quite descriptive. It would be worth testing available tim splicing mutants, or mutants for regulators of tim splicing, to understand in more detail and more directly how tim splicing determines behavioral adaptation to different phase relationships between temperature and light cycles. Also, I wonder whether polymorphisms in or around tim splicing sites, or in tim splicing regulators, were selected in the early or late strains.

I also have a major methodological concern. The authors studied how the evening and morning phases are adjusted under different conditions and different strains. They divided the daily cycle into 12h morning and 12h evening periods, and calculated the phase of morning and evening activity using circular statistics. However, the non-circadian "startle" responses to light or temperature transitions should have a very important impact on phase calculation, and thus at least partially obscure actual circadian morning and evening peak phase changes. Moreover, the timing of the temperature-up startle drifts with the temperature cycles, and will even shift from the morning to the evening portion of the divided daily cycle. Its amplitude also varies as a function of the LD/TC phase relationship. Note that the startle responses and their changes under different conditions will also affect SSD quantifications.

For the circadian phase, these issues seem, for example, quite obvious for the morning peak in Figure 1. According to the phase quantification on panel D, there is essentially no change in the morning phase when the temperature cycle is shifted by 6 hours compared to the LD cycle, but the behavior trace on panel B clearly shows a phase advance of morning anticipation. Comparison between the graphs on panels C and D also indicates that there are methodological caveats, as they do not correlate well.

Because of the various masking effects, phase quantification under entrainment is a thorny problem in Drosophila. I would suggest testing other measurements of anticipatory behavior to complement or perhaps supersede the current behavior analysis. For example, the authors could employ the anticipatory index used in many previous studies, measure the onset of morning or evening activity, or, if more reliable, the time at which 50% of anticipatory activity is reached. Termination of activity could also be considered. Interestingly, it seems there are clear effects on evening activity termination in Figure 3. All these methods will be impacted by startle responses under specific LD/TC phase relationships, but their combination might prove informative.

Reviewer #2 (Public review):

Summary:

The authors aimed to dissect the plasticity of circadian outputs by combining evolutionary biology with chronobiology. By utilizing Drosophila strains selected for "Late" and "Early" adult emergence, they sought to investigate whether selection for developmental timing co-evolves with plasticity in daily locomotor activity. Specifically, they examined how these diverse lines respond to complex, desynchronized environmental cues (temperature and light cycles) and investigated the molecular role of the splicing factor Psi and timeless isoforms in mediating this plasticity.

Major strengths and weaknesses:

The primary strength of this work is the novel utilization of long-term selection lines to address fundamental questions about how organisms cope with complex environmental cues. The behavioral data are compelling, clearly demonstrating that "Late" and "Early" flies possess distinct capabilities to track temperature cycles when they are desynchronized from light cycles.

However, a significant weakness lies in the causal links proposed between the molecular findings and these behavioral phenotypes. The molecular insights (Figures 2, 4, 5, and 6) rely on mRNA extracted from whole heads. As head tissue is dominated by photoreceptor cells and glia rather than the specific pacemaker neurons (LNv, LNd) driving these behaviors, this approach introduces a confound. Differential splicing observed here may reflect the state of the compound eye rather than the central clock circuit, a distinction highlighted by recent studies (e.g., Ma et al., PNAS 2023).

Furthermore, while the authors report that Psi mRNA loses rhythmicity under out-of-sync conditions, this correlation does not definitively prove that Psi oscillation is required for the observed splicing patterns or behavioral plasticity. The amplitude of the reported Psi rhythm is also low (~1.5 fold) and variable, raising questions about its functional significance in the absence of manipulation experiments (such as constitutive expression) to test causality.

Appraisal of aims and conclusions:

The authors successfully demonstrate the co-evolution of emergence timing and activity plasticity, achieving their aim on the behavioral level. However, the conclusion that the specific molecular mechanism involves the loss of Psi rhythmicity driving timeless splicing changes is not yet fully supported by the data. The current evidence is correlative, and without spatial resolution (specific clock neurons) or causal manipulation, the mechanistic model remains speculative.

This study is likely to be of significant interest to the chronobiology and evolutionary biology communities as it highlights the "enhanced plasticity" of circadian clocks as an adaptive trait. The findings suggest that plasticity to phase lags - common in nature where temperature often lags light - may be a key evolutionary adaptation. Addressing the mechanistic gaps would significantly increase the utility of these findings for understanding the molecular basis of circadian plasticity.

Reviewer #3 (Public review):

Summary:

This study attempts to mimic in the laboratory changing seasonal phase relationships between light and temperature and determine their effects on Drosophila circadian locomotor behavior and on the underlying splicing patterns of a canonical clock gene, timeless. The results are then extended to strains that have been selected over many years for early or late circadian phase phenotypes.

Strengths:

A lot of work, and some results showing that the phasing of behavioral and molecular phenotypes is slightly altered in the predicted directions in the selected strains.

Weaknesses:

The experimental conditions are extremely artificial, with immediate light and temperature transitions compared to the gradual changes observed in nature. Studies in the wild have shown how the laboratory reveals artifacts that are not observed in nature. The behavioral and molecular effects are very small, and some of the graphs and second-order analyses of the main effects appear contradictory. Consequently, the Discussion is very speculative as it is based on such small laboratory effects

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

This manuscript addresses an important question: how do circadian clocks adjust to a complex rhythmic environment with multiple daily rhythms? The focus is on the temperature and light cycles (TC and LD) and their phase relationship. In nature, TC usually lags the LD cycle, but the phase delay can vary depending on seasonal and daily weather conditions. The authors present evidence that circadian behavior adjusts to different TC/LD phase relationships, that temperature-sensitive tim splicing patterns might underlie some of these responses, and that artificial selection for preferential evening or morning eclosion behavior impacts how flies respond to different LD/TC phase relationship

Strength:

Experiments are conducted on control strains and strains that have been selected in the laboratory for preferential morning or evening eclosion phenotypes. This study is thus quite unique as it allows us to probe whether this artificial selection impacted how animals respond to different environmental conditions, and thus gives hints on how evolution might shape circadian oscillators and their entrainment. The authors focused on circadian locomotor behavior and timeless (tim) splicing because warm and cold-specific transcripts have been described as playing an important role in determining temperature-dependent circadian behavior. Not surprisingly, the results are complex, but there are interesting observations. In particular, the "late" strain appears to be able to adjust more efficiently its evening peak in response to changes in the phase relationship between temperature and light cycles, but the morning peak seems less responsive in this strain. Differences in the circadian pattern of expression of different tim mRNA isoforms are found under specific LD/TC conditions.

We sincerely thank the reviewer for this generous assessment and for recognizing several key strengths of our study. We are particularly gratified that the reviewer values our use of long-term laboratory-selected chronotype lines (350+ generations), which provide a unique evolutionary perspective on how artificial selection reshapes circadian responses to complex LD/TC phase relationships—precisely our core research question.

Weaknesses:

These observations are interesting, but in the absence of specific genetic manipulations, it is difficult to establish a causative link between tim molecular phenotypes and behavior. The study is thus quite descriptive. It would be worth testing available tim splicing mutants, or mutants for regulators of tim splicing, to understand in more detail and more directly how tim splicing determines behavioral adaptation to different phase relationships between temperature and light cycles. Also, I wonder whether polymorphisms in or around tim splicing sites, or in tim splicing regulators, were selected in the early or late strains.

We thank the reviewer for this insightful comment. We agree that our current data do not establish a direct causal link between tim splicing (or Psi) and behaviour, and we appreciate that some of our wording (e.g. “linking circadian gene splicing to behavioural plasticity” or describing tim splicing as a “pivotal node”) may have suggested unintended causal links. In the revision, we will (i) explicitly state in the Abstract, Introduction, and early Discussion that the main aim was to test whether selection for timing of eclosion is accompanied by correlated evolution of temperature‑dependent tim splicing patterns and evening activity plasticity under complex LD/TC regimes, and (ii) consistently describe the molecular findings as correlational and hypothesis‑generating rather than causal. We will also add phrases throughout the text to point the reader more clearly to existing passages where we already emphasize “correlated evolution” and explicitly label our mechanistic ideas as “we speculate” / “we hypothesize” and as future experiments.

We fully agree that studies using tim splicing mutants or manipulations of splicing regulators under in‑sync and out‑of‑sync LD/TC regimes will be essential to ascertain what role tim variants play under such environmental conditions, and we will highlight this as a key future direction. At the same time, we emphasize that the long‑term selection lines provide a complementary perspective to classical mutant analyses by revealing how behavioural and molecular phenotypes can exhibit correlated evolution under a specific, chronobiologically relevant selection pressure (timing of emergence).

Finally, we appreciate the suggestion regarding polymorphisms. Whole‑genome analyses of these lines in a PhD thesis from our group (Ghosh, 2022, unpublished, doctoral dissertation) reveal significant SNPs in intronic regions of timeless in both Early and Late populations, as well as SNPs in CG7879, a gene implicated in alternative mRNA splicing, in the Late line. Because these analyses are ongoing and not yet peer‑reviewed, we do not present them as main results.

I also have a major methodological concern. The authors studied how the evening and morning phases are adjusted under different conditions and different strains. They divided the daily cycle into 12h morning and 12h evening periods, and calculated the phase of morning and evening activity using circular statistics. However, the non-circadian "startle" responses to light or temperature transitions should have a very important impact on phase calculation, and thus at least partially obscure actual circadian morning and evening peak phase changes. Moreover, the timing of the temperature-up startle drifts with the temperature cycles, and will even shift from the morning to the evening portion of the divided daily cycle. Its amplitude also varies as a function of the LD/TC phase relationship. Note that the startle responses and their changes under different conditions will also affect SSD quantifications.

We thank the reviewer for this perceptive methodological concern, which we had anticipated and systematically quantified but had not included in the original submission. The reviewer is absolutely correct that non-circadian startle responses to zeitgeber transitions could confound both circular phase (CoM) calculations and SSD quantifications, particularly as TC drift creates shifting startle locations across morning/evening windows.

We will be including startle response quantification (previously conducted but unpublished) as new a Supplementary figure, systematically measuring SSD in 1-hour windows immediately following each of the four environmental transitions (lights-ON, lights-OFF, temperature rise and temperature fall) across all six LDTC regimes (2-12hr TC-LD lags) for all 12 selection lines (early_1-4, control_1-4, late_1-4).

Author response image 1.

Startle responses in selection lines under LDTC regimes: SSD calculated to assess startle response to each of the transitions (1-hour window after the transition used for calculations). Error bars are 95% Tukey’s confidence intervals for the main effect of selection in a two-factor ANOVA design with block as a random factor. Non-overlapping error bars indicate significant differences among the values. SSD values between in-sync and out-of-sync regimes for a range of phase relationships between LD and TC cycles (A) LDTC 2-hr, (B) LDTC 4-hr, (C) LDTC 6-hr, (D) LDTC 8-hr, (E) LDTC 10-hr, (F) LDTC 12-hr.

Key findings directly addressing the reviewer's concerns:

(1) Morning phase advances in LDTC 8-12hr regimes are explained by quantified nocturnal startle activity around temperature rise transitions occurring within morning windows. Critically, these startles show no selection line differences, confirming they represent equivalent non-circadian confounds across lines.

(2) Early selection lines exhibit significantly heightened startle responses specifically to temperature rise in LDTC 4hr and 6hr regimes (early > control ≥ late), demonstrating that startle responses themselves exhibit correlated evolution with emergence timing—an important novel finding that strengthens our evolutionary story.

(3) Startle responses differed among selection lines only for the temperature rise transition under two of the regimes used, LDTC 4 hr and 6 hr regimes. Under LDTC 4 hr, temperature rise transition falls in the morning window and despite early having significantly greater startle than late, the overall morning SSD (over 12 hours morning window) did not differ significantly among the selection lines for this regime. Thus, eliminating the startle window would make the selection lines more similar to one another. On the other hand, under LDTC 6 hour regime, the startle response to temperature rise falls in the evening 12 hour window. In this case too, early showed higher startle than control and late. A higher startle in early would thus, contribute to the observed differences among selection lines. We agree with the reviewer that eliminating this startle peak would lead to a clearer interpretation of the change in circadian evening activity.

We deliberately preserved all behavioural data without filtering out startle windows since it would require arbitrary cutoffs like 1 hr, 2 hr or 3 hours post transitions or until the startle peaks declines in different selection lines under different regimes. In the revised version, we will add complementary analyses excluding the startle windows to obtain mean phase and SSD values which are unaffected by the startle responses.

For the circadian phase, these issues seem, for example, quite obvious for the morning peak in Figure 1. According to the phase quantification on panel D, there is essentially no change in the morning phase when the temperature cycle is shifted by 6 hours compared to the LD cycle, but the behavior trace on panel B clearly shows a phase advance of morning anticipation. Comparison between the graphs on panels C and D also indicates that there are methodological caveats, as they do not correlate well.

Because of the various masking effects, phase quantification under entrainment is a thorny problem in Drosophila. I would suggest testing other measurements of anticipatory behavior to complement or perhaps supersede the current behavior analysis. For example, the authors could employ the anticipatory index used in many previous studies, measure the onset of morning or evening activity, or, if more reliable, the time at which 50% of anticipatory activity is reached. Termination of activity could also be considered. Interestingly, it seems there are clear effects on evening activity termination in Figure 3. All these methods will be impacted by startle responses under specific LD/TC phase relationships, but their combination might prove informative.

We agree that phase quantification under entrained conditions in Drosophila is challenging and that anticipatory indices, onset/offset measures, and T50 metrics each have particular strengths and weaknesses. In designing our analysis, we chose to avoid metrics that require arbitrary or subjective criteria (e.g. defining activity thresholds or durations for anticipation, or visually marking onset/offset), because these can substantially affect the estimated phase and reduce comparability across regimes and genotypes. Instead, we used two fully quantitative, parameter-free measures applied to the entire waveform within defined windows: (i) SSD to capture waveform change in shape/amplitude and (ii) circular mean phase of activity (CoM) restricted to the 12 h morning and 12 h evening windows. By integrating over the entire window, these measures are less sensitive to the exact choice of threshold and to short-lived, high-amplitude startles at transitions, and they treat all bins within the window in a consistent, reproducible way across all LDTC regimes and lines. Panels C (SSD) and D (CoM) are intentionally complementary, not redundant: SSD reflects how much the waveform changes in shape and amplitude, whereas CoM reflects the timing of the center of mass of activity. Under conditions where masking alters amplitude and introduces short-lived bouts without a major shift of the main peak, it is expected that SSD and CoM will not correlate linearly across regimes.

We will be including a detailed calculation of how CoM is obtained in our methods for the revised version.  

Reviewer #2 (Public review):

Summary:

The authors aimed to dissect the plasticity of circadian outputs by combining evolutionary biology with chronobiology. By utilizing Drosophila strains selected for "Late" and "Early" adult emergence, they sought to investigate whether selection for developmental timing co-evolves with plasticity in daily locomotor activity. Specifically, they examined how these diverse lines respond to complex, desynchronized environmental cues (temperature and light cycles) and investigated the molecular role of the splicing factor Psi and timeless isoforms in mediating this plasticity.

Major strengths and weaknesses:

The primary strength of this work is the novel utilization of long-term selection lines to address fundamental questions about how organisms cope with complex environmental cues. The behavioral data are compelling, clearly demonstrating that "Late" and "Early" flies possess distinct capabilities to track temperature cycles when they are desynchronized from light cycles.

We sincerely thank the reviewer for this enthusiastic recognition of our study's core strengths. We are particularly gratified that the reviewer highlights our novel use of long-term selection lines (350+ generations) as the primary strength, enabling us to address fundamental evolutionary questions about circadian plasticity under complex environmental cues. We thank them for identifying our behavioral data as compelling (Figs 1, 3), which robustly demonstrate selection-driven divergence in temperature cycle tracking.

However, a significant weakness lies in the causal links proposed between the molecular findings and these behavioral phenotypes. The molecular insights (Figures 2, 4, 5, and 6) rely on mRNA extracted from whole heads. As head tissue is dominated by photoreceptor cells and glia rather than the specific pacemaker neurons (LNv, LNd) driving these behaviors, this approach introduces a confound. Differential splicing observed here may reflect the state of the compound eye rather than the central clock circuit, a distinction highlighted by recent studies (e.g., Ma et al., PNAS 2023).

We thank the reviewer for highlighting this important methodological consideration. We fully agree that whole-head extracts do not provide spatial resolution to distinguish central pacemaker neurons (~100-200 total) from compound eyes and glia, and that cell-type-specific profiling represents the critical next experimental step. As mentioned in our response to Reviewer 1, we appreciate the issue with our phrasing and will be revising it accordingly to more clearly describe that we do not claim any causal connections between expression of the tim splice variants in particular circadian neurons and their contribution of the phenotype observed.

We chose whole-head extracts for practical reasons aligned with our study's specific goals:

(1) Fly numbers: Our artificially selected populations are maintained at large numbers (~1000s per line). Whole-head extracts enabled sampling ~150 flies per time point = ~600 flies per genotype per environmental, providing means to faithfully sample the variation that may exist in such randomly mating populations.

(2) Established method for characterizing splicing patterns: The majority of temperature-dependent period/timeless splicing studies have successfully used whole-head extracts (Majercak et al., 1999; Shakhmantsir et al., 2018; Martin Anduaga et al., 2019) to characterize splicing dynamics under novel conditions.

(3) Novel environmental regimes: Our primary molecular contribution was documenting timeless splicing patterns under previously untested LDTC phase relationships (TC 2-12hr lags relative to LD) and testing whether these exhibit selection-dependent differences consistent with behavioral divergence.

Furthermore, while the authors report that Psi mRNA loses rhythmicity under out-of-sync conditions, this correlation does not definitively prove that Psi oscillation is required for the observed splicing patterns or behavioral plasticity. The amplitude of the reported Psi rhythm is also low (~1.5 fold) and variable, raising questions about its functional significance in the absence of manipulation experiments (such as constitutive expression) to test causality.

We thank the reviewer for this insightful comment and appreciate that our phrasing has been misleading. We will especially pay attention to this issue, raised by two reviewers, and clearly highlight our results as correlated evolution and hypothesis-generating.

We appreciate the reviewer highlighting these points and would like to draw attention to the following points in our Discussion section:

“Psi and levels of tim-cold and tim-sc (Foley et al., 2019). We observe that this correlation is most clearly upheld under temperature cycles wherein tim-medium and Psi peak in-phase while the cold-induced transcripts start rising when Psi falls (Figure 8A1&2). Under LDTC in-sync conditions this relationship is weaker, even though Psi is rhythmic, potentially due to light-modulated factors influencing timeless splicing (Figure 8B1&2). This is in line with Psi’s established role in regulating activity phasing under TC 12:12 but not LD 12:12 (Foley et al., 2019). This is also supported by the fact that while tim-medium and tim-cold are rhythmic under LD 12:12 (Shakhmantsir et al., 2018), Psi is not (datasets from Kuintzle et al., 2017; Rodriguez et al., 2013). Assuming this to be true across genetic backgrounds and sexes and combined with our similar findings for these three transcripts under LDTC out-of-sync (Figure 2B3, D3&E3), we speculate that Psi rhythmicity may not be essential for tim-medium or tim-cold rhythmicity especially under conditions wherein light cycles are present along with temperature cycles (Figure 8C1&2). Our study opens avenues for future experiments manipulating PSI expression under varying light-temperature regimes to dissect its precise regulatory interactions. We hypothesize that flies with Psi knocked down in the clock neurons should exhibit a less pronounced shift of the evening activity under the range LDTC out-of-sync conditions for which activity is assayed in our study. On the other hand, its overexpression should cause larger delays in response to delayed temperature cycles due to the increased levels of tim-medium translating into delay in TIM protein accumulation.”

Appraisal of aims and conclusions:

The authors successfully demonstrate the co-evolution of emergence timing and activity plasticity, achieving their aim on the behavioral level. However, the conclusion that the specific molecular mechanism involves the loss of Psi rhythmicity driving timeless splicing changes is not yet fully supported by the data. The current evidence is correlative, and without spatial resolution (specific clock neurons) or causal manipulation, the mechanistic model remains speculative.

This study is likely to be of significant interest to the chronobiology and evolutionary biology communities as it highlights the "enhanced plasticity" of circadian clocks as an adaptive trait. The findings suggest that plasticity to phase lags - common in nature where temperature often lags light - may be a key evolutionary adaptation. Addressing the mechanistic gaps would significantly increase the utility of these findings for understanding the molecular basis of circadian plasticity.

Thank you for this thoughtful appraisal affirming our successful demonstration of co-evolution between emergence timing and circadian activity plasticity.

Reviewer #3 (Public review):

Summary:

This study attempts to mimic in the laboratory changing seasonal phase relationships between light and temperature and determine their effects on Drosophila circadian locomotor behavior and on the underlying splicing patterns of a canonical clock gene, timeless. The results are then extended to strains that have been selected over many years for early or late circadian phase phenotypes.

Strengths:

A lot of work, and some results showing that the phasing of behavioural and molecular phenotypes is slightly altered in the predicted directions in the selected strains.

We thank the reviewer for acknowledging the substantial experimental effort across 7 environmental regimes (6 LDTC phase relationships + LDTC in-phase), 12 replicate populations (early_1-4, control_1-4, late_1-4), and comprehensive behavioural + molecular phenotyping.

Weaknesses:

The experimental conditions are extremely artificial, with immediate light and temperature transitions compared to the gradual changes observed in nature. Studies in the wild have shown how the laboratory reveals artifacts that are not observed in nature. The behavioural and molecular effects are very small, and some of the graphs and second-order analyses of the main effects appear contradictory. Consequently, the Discussion is very speculative as it is based on such small laboratory effects.

We thank the reviewer for these important points regarding ecological validity, effect sizes, and interpretation scope.

(1) Behavioural effects are robust across population replicates in selection lines (not small/weak)

Our study assayed 12  populations total (4 replicate populations each of early, control, and late selection lines) under 7 LDTC regimes. Critically, selection effects were consistent across all 4 replicate populations within each selection line for every condition tested. In these randomly mating large populations, the mixed model ANOVA reveals highly significant selection×regime interactions [F(5,45)=4.1, p=0.003; Fig 3E, Table S2], demonstrating strong, replicated evolutionary divergence in evening temperature sensitivity.

(2) Molecular effects test critical evolutionary hypothesis

As stated in our Introduction, "selection can shape circadian gene splicing and temperature responsiveness" (Low et al., 2008, 2012). Our laboratory-selected chronotype populations—known to exhibit evolved temperature responsiveness (Abhilash et al., 2019, 2020; Nikhil et al., 2014; Vaze et al., 2012)—provide an apt system to test whether selection for temporal niche leads to divergence in timeless splicing. With ~600 heads per environmental regime per selection line, we detect statistically robust, selection line-specific temporal profiles [early4 advanced timeless phase (Fig 4A4); late4 prolonged tim-cold (Fig 5A4); significant regime×selection×time interactions (Tables S3-S5)], providing initial robust evidence of correlated molecular evolution under novel LDTC regimes.

(3) Systematic design fills critical field gap

Artificial conditions like LD/DD have been useful in revealing fundamental zeitgeber principles. Our systematic 2-12hr TC-LD lags directly implement Pittendrigh & Bruce (1959) + Oda & Friesen (2011) validated design, which discuss how such experimental designs can provide a more comprehensive understanding of zeitgeber integration compared to studies with only one phase jump between two zeitgebers.

(4) Ramping regimes as essential next step

Gradual ramping regimes better mimic nature and represent critical future experiments. New Discussion addition in the revised version: "Ramping LDTC regimes can test whether selection-specific zeitgeber hierarchy persists under naturalistic gradients." While ramping experiments are essential, we would like to emphasize that we aimed to use this experimental design as a tool to test if evening activity exhibits greater temperature sensitivity and if this property of the circadian system can undergo correlated evolution upon selection for timing of eclosion/emergence.

(5) New startle quantification addresses masking

Our startle quantification (which will be added as a new supplementary figure) confirms circadian evening tracking persists despite quantified, selection-independent masking in most of the regimes.

eLife Assessment

The study presents a valuable resource of proline hydroxylation proteins for molecular biology studies in oxygen-sensing and cell signaling with the characterization of Repo-man proline hydroxylation site. The evidence supporting the claim of the authors is solid, although further clarification of the overall efficiency of the HILIC analysis, the specificity/sensitivity of immonium ion analysis, as well as quantification of proline hydroxylation identifications will be helpful. The work will be of interest to researchers studying post-translational modification, oxygen sensing, and cell signaling.

Reviewer #1 (Public review):

Summary:

The manuscript by Hao Jiang et al described a systematic approach to identify proline hydroxylation proteins. The authors implemented a proteomic strategy with HILIC-chromatographic separation and reported an identification with high confidence of 4993 sites from HEK293 cells (4 replicates) and 3247 sites from RCC4 cells with 1412 sites overlapping between the two cell lines. A small fraction of about 200 sites from each cell line were identified with HyPro immonium ion. The authors investigated the conditions and challenges of using HyPro immonium ions as a diagnostic tool. The study focused the validation analysis of Repo-man (CDCA2) proline hydroxylation comparing MS/MS spectra, retention time and diagnostic ions of purified proteins with corresponding synthetic peptides. Using SILAC analysis and recombinant enzyme assay, the study evaluated Repo-man HyPro604 as a target of PHD1 enzyme.

Strengths:

The study involved extensive LCMS runs for in-depth characterization of proline hydroxylation proteins including four replicated analysis of 293 cells and three replicated analysis of RCC4 cells with 32 HILIC fractions in each analysis. The identification of over 4000 confident proline hydroxylation sites from the two cell lines would be a valuable resource for the community. The characterization of Repo-man proline hydroxylation is a novel finding.

Weaknesses:

As a study mainly focused on methodology, there are some potential technical weaknesses discussed below.

(1) The study applied HILIC-based chromatographic separation with a goal to enrich and separate hydroxyproline containing peptides. The separation effects for peptides from 293 cells and RCC4 cells seems somewhat different (Figure 2A and Figure S1A), which may indicate that the application efficiency of the strategy may be cell line dependent.

(2) The study evaluated the HyPro immonium ion as a diagnostic ion for HyPro identification showcasing multiple influential factors and potential challenges. It is important to note that with only around 5% of the identifications had HyPro immonium ion, it would be very challenging to implement this strategy in a global LCMS analysis to either validate or invalidate HyPro identifications. In comparison, acetyllysine immonium ion was previously reported to be a useful marker for acetyllysine peptides (PMID: 18338905) and the strategy offered a sensitivity of 70% with a specificity of 98%.

(3) The authors aimed to identify potential PHD targets by comparing the HyPro proteins identified with or without PHD inhibitor FG-4592 treatment. The workflow followed a classification strategy, rather than a typical quantitative proteomics approach for comprehensive analysis.

(4) The authors performed inhibitor treatment and in vitro PHD1 enzyme assay to validate that Repo-man can be hydroxylated by PHD1. It remains unknown if PHD1 expression in cells is sufficient to stimulate Repo-man hydroxylation.

Reviewer #2 (Public review):

Summary:

In this manuscript, Jiang et al. developed a robust workflow for identifying proline hydroxylation sites in proteins. They identified proline hydroxylation sites in HEK293 and RCC4 cells, respectively. The authors found that the more hydrophilic HILIC fractions were enriched in peptides containing hydroxylated proline residues. These peptides showed differences in charge and mass distribution compared to unmodified or oxidized peptides. The intensity of the diagnostic hydroxyproline iminium ion depended on parameters including MS collision energy, parent peptide concentration, and the sequence of amino acids adjacent to the modified proline residue. Additionally, they demonstrate that a combination of retention time in LC and optimized MS parameter settings reliably identifies proline hydroxylation sites in peptides, even when multiple proline residues are present

Strengths:

Overall, the manuscript presents an advanced, standardized protocol for identifying proline hydroxylation. The experiments were well designed, and the developed protocol is straightforward, which may help resolve confusion in the field.

Comments on revisions:

All of my concerns have been resolved by the authors. It is ready for publication.

Reviewer #3 (Public review):

Summary:

The authors present a new method for detecting and identifying proline hydroxylation sites within the proteome. This tool utilizes traditional LC-MS technology with optimized parameters, combined with HILIC-based separation techniques. The authors show that they pick up known hydroxy-proline sites and also validate a new site discovered through their pipeline.

Strengths:

The manuscript utilizes state-of-the-art mass spectrometric techniques with optimized collision parameters to ensure proper detection of the immonium ions, which is an advance compared to other similar approaches before. The use of synthetic control peptides on the HILIC separation step clearly demonstrates the ability of the method to reliably distinguish hydroxy-proline from oxidized methionine - containing peptides. Using this method, they identify a site on CDCA2, which they go on to validate in vitro and also study its role in regulation of mitotic progression in an associated manuscript.

Weaknesses:

Despite the authors claim about the specificity of this method in picking up the intended peptides, there is a good amount of potential false positives that also happen to get picked (owing to the limitations of MS-based readout), and the authors' criteria for downstream filtering of such peptides requires further clarification. In the same vein, greater and more diverse cell-based validation approach will be helpful to substantiate the claims regarding enrichment of peptides in the described pathway analyses. Experiments must show reproducibility and contain appropriate controls wherever necessary.

Comments on revisions:

I thank the authors for their clarifications and opinions on my questions and suggestions. Based on the response, the following points are important while considering the significance of this manuscript:

- The manuscript provides a novel method to detect and identify proline hydroxylation residues in the proteome. While this provides several advances over previous methods, the probability of false positives, loss of true positives and incomplete removal of the interference of methionine oxidation in this strategy need to be addressed clearly in the discussion section of the manuscript, so that the strengths and limitations of this method are made aware to the reader.

- Going by the standards of publication in eLife, reproducibility is very important in the experiments done. Hence, I strongly recommend that the authors perform the experiments in triplicate with error bars to confirm reproducibility. Graphs with single data points do not convey that, and this is very important for eLife.

- As for Figure 9C, the authors have rejected the request for a control lane in the figure. It may sound trivial to the authors, but for completeness of the experiment, all applicable controls must be performed and shown alongside the main data. It is essential to show the PHD1 only control to rule out the possibility of the contribution of any non-specific signal in the dot blot by PHD1.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

The manuscript by Hao Jiang et al described a systematic approach to identify proline hydroxylation proteins. The authors implemented a proteomic strategy with HILIC-chromatographic separation and reported an identification of 4993 sites from HEK293 cells (4 replicates) and 3247 sites from RCC4 sites (3 replicates) with 1412 sites overlapping between the two cell lines. From the analysis, the authors identified 225 sites and 184 sites respectively from 293 and RCC4 cells with HyPro diagnostic ion. The identifications were validated by analyzing a few synthetic peptides, with a specific focus on Repo-man (CDCA2) through comparing MS/MS spectra, retention time, and diagnostic ions. With SILAC analysis and recombinant enzyme assay, the study showed that Repo-man HyPro604 is a target of the PHD1 enzyme.

Strengths:

The study involved extensive LC-MS analysis and was carefully implemented. The identification of over 4000 confident proline hydroxylation sites would be a valuable resource for the community. The characterization of Repo-man proline hydroxylation is a novel finding.

Weaknesses:

However, as a study mainly focused on methodology, the findings from the experimental data did not convincingly demonstrate the sensitivity and specificity of the workflow for site-specific identification of proline hydroxylation in global studies.

Proline hydroxylation is an enzymatic post translational protein modification, catalysed by prolyl Hydroxylases (PHDs), which can have profound biological significance, e.g. altering protein half-life and/or the stability of protein-protein interactions. Furthermore, there has been controversy in the field as to the true number of protein targets for PHDs in cells. Thus, there is a clear need for methods to enable the robust identification of genuine PHD targets and to reliably map sites of PHD-catalysed proline hydroxylation in proteins. We believe, therefore, that our methodology, as reported here in Jiang et al., is an important contribution towards this goal. We note that our methodology has already been used successfully by others

(https://doi.org/10.1016/j.mcpro.2025.100969). While further improvements in this methodology may of course be developed in future, we are not currently aware of any superior methods that have been reported previously in the literature. The criticism made by the reviewer notably does not include reference to any such alternative published methodology that interested researchers can use which would offer superior results to the approach we document in this study.

Major concerns:

(1) The study applied HILIC-based chromatographic separation with a goal of enriching and separating hydroxyproline-containing peptides. However, as the authors mentioned, such an approach is not specific to proline hydroxylation. In addition, many other chromatography techniques can achieve deep proteome fractionation such as high pH reverse phase fractionation, strong-cation exchange etc. There was no data in this study to demonstrate that the strategy offered improved coverage of proline hydroxylation proteins, as the identifications of the HyPro sites could be achieved through deep fractionation and a highly sensitive LCMS setup. The data of Figure 2A and S1A were somewhat confusing without a clear explanation of the heat map representations. 

The data we present in this study demonstrate clearly that peptides with hydroxylated prolines are enriched in specific HILIC fractions (F10-F18), in comparison with total unfractionated peptides derived from cell extracts. We also refer the reviewer to our previously published study by Bensaddek et al (International Journal of Mass Spectrometry: doi:10.1016/j.ijms.2015.07.029), which was reference 41 in this study, in which we compared directly the performance of both HILIC and strong anionic exchange chromatography, (hSAX). This showed that HILIC provided superior enrichment to hSAX for enrichment of peptides containing hydroxylated proline residues. To clarify this point for readers, we have now included a specific reference to our previous study at the start of the Results section in our current revision. Currently, we use HILIC to provide a degree of enrichment for proline hydroxylated peptides because we are not aware of alternative chromatographic methods that in our hands provide better results.

We have included descriptions of the information shown in the heatmaps in the associated figure legends and captions.

(2) The study reported that the HyPro immonium ion is a diagnostic ion for HyPro identification. However, the data showed that only around 5% of the identifications had such a diagnostic ion. In comparison, acetyl-lysine immonium ion was previously reported to be a useful marker for acetyllysine peptides (PMID: 18338905), and the strategy offered a sensitivity of 70% with a specificity of 98%. In this study, the sensitivity of HyPro immonium ion was quite low. The authors also clearly demonstrated that the presence of immonium ion varied significantly due to MS settings, peptide sequence, and abundance. With further complications from L/I immonium ions, it became very challenging to implement this strategy in a global LC-MS analysis to either validate or invalidate HyPro identifications.

The reviewer appears to have misunderstood the point we make with regard to the identification of the immonium ion and its use as a diagnostic marker for proline hydroxylation in MS analyses. We do not claim that this immonium ion is an essential diagnostic marker for proline hydroxylation. As the reviewer notes, with respect to the acetyl-lysine modification, the corresponding immonium ion is often used in MS studies as a diagnostic for identification of specific post translational modifications. Previous studies have reported that the immonium ion for hydroxylated proline is detected when the transcription factor HIF is analysed, but is often absent with other putative PHD targets, which has been used as an argument that these targets are not genuine proline hydroxylation sites. We are not, therefore, introducing the idea in this study that the hydroxy-proline immonium ion is a required diagnostic marker for proline hydroxylation, but instead demonstrating that detection of this ion, at least in some peptide sequences, may require the use of higher MS collision energies than are typically required for routine peptide identification. We believe that this is an interesting observation that can help to clear up discussions in the literature regarding the true prevalence of PHD-catalysed proline hydroxylation in different target proteins. Our data suggest that, in future MS studies analysing suspected PHD target proteins, two different collision energy might need to be used, i.e., normal collision energy for the routine identification of a peptide, combined with use of a higher collision energy if the hydroxy-proline immonium ion was not already detected.

(3) The study aimed to apply the HILIC-based proteomics workflow to identify HyPro proteins regulated by the PHD enzyme. However, the quantification strategy was not rigorous. The study just considered the HyPro proteins not identified by FG-4592 treatment as potential PHD targeted proteins. There are a few issues. First, such an analysis was not quantitative without reproducibility or statistical analysis. Second, it did not take into consideration that data-dependent LC-MS analysis was not comprehensive and some peptide ions may not be identified due to background interferences. Lastly, FG-4592 treatment for 24 hrs could lead to wide changes in gene expressions and protein abundances. Therefore, it is not informative to draw conclusions based on the data for bioinformatic analysis.

We refer the reviewer to the data we present in this study using SILAC analysis, combined with our MS workflow. to achieve a more accurate quantitative picture of proline hydroxylation levels. While we agree that the point the reviewer makes is valid, regarding our data dependent LC-MS/MS analysis potentially not being comprehensive, this means, however, that we are potentially underestimating the true prevalence of proline hydroxylated peptides, not overestimating the level of these modified peptides. We also refer the reviewer to the accompanying study by Druker et al., (eLife 2025; doi.org/10.7554/eLife.108131.1)  in which we present a detailed follow-on study demonstrating the functional significance of the novel proline hydroxylation site we detected in the protein RepoMan (CDCA2). Therefore, even if we have not achieved a fully comprehensive analysis of all proline hydroxylated peptides catalysed by PHD enzymes, we believe that we have advanced the field by documenting a workflow that is able to identify and validate novel PHD targets.

(4) The authors performed an in vitro PHD1 enzyme assay to validate that Repo-man can be hydroxylated by PHD1. However, Figure 9 did not show quantitatively PHD1-induced increase in Repo-man HyPro abundance and it is difficult to assess its reaction efficiency to compare with HIF1a HyPro.

The analysis shown in Figure 9 was not intended to quantify the efficiency of in vitro hydroxylation of RepoMan by PHD1, but rather to answer the question, ‘Can recombinant PHD1 alone hydroxylate P604 on RepoMan in vitro, yes or no?’. The data show that the answer here is ‘yes’. Clearly, the HIF peptide is a more efficient substrate in vitro for recombinant PHD1 than the RepoMan peptide and we have now included a statement in the Discussion that addresses the significance of this observation more directly.

Reviewer #2 (Public review):

Summary:

In this manuscript, Jiang et al. developed a robust workflow for identifying proline hydroxylation sites in proteins. They identified proline hydroxylation sites in HEK293 and RCC4 cells, respectively. The authors found that the more hydrophilic HILIC fractions were enriched in peptides containing hydroxylated proline residues. These peptides showed differences in charge and mass distribution compared to unmodified or oxidized peptides. The intensity of the diagnostic hydroxyproline iminium ion depended on parameters including MS collision energy, parent peptide concentration, and the sequence of amino acids adjacent to the modified proline residue. Additionally, they demonstrate that a combination of retention time in LC and optimized MS parameter settings reliably identifies proline hydroxylation sites in peptides, even when multiple proline residues are present.

Strengths:

Overall, the manuscript presents an advanced, standardized protocol for identifying proline hydroxylation. The experiments were well designed, and the developed protocol is straightforward, which may help resolve confusion in the field.

Weaknesses:

(1) The authors should provide a summary of the standard protocol for identifying proline hydroxylation sites in proteins that can easily be followed by others.

This is a good suggestion and we have now included a figure (Figure 10) with a summary of our workflow in the current revision.

(2) Cockman et al. proposed that HIF-α is the only physiologically relevant target for PHDs. Their approach is considered the gold standard for identifying PHD targets. Therefore, the authors should discuss the major progress they made in this manuscript that challenges Cockman's conclusion.

While we had mentioned the Cockman et al., paper in the Introduction, we had not focussed on this somewhat controversial issue. However, in response to the Reviewer’s request, we have now added a comment in the Discussion section in the current revision of how our new data address the proposal discussed previously by Cockman et al. In brief, we believe that our findings are not consistent with a model in which PHDs have no protein targets other than HIFs.

Reviewer #3 (Public review): 

Summary:

The authors present a new method for detecting and identifying proline hydroxylation sites within the proteome. This tool utilizes traditional LC-MS technology with optimized parameters, combined with HILIC-based separation techniques. The authors show that they pick up known hydroxy-proline sites and also validate a new site discovered through their pipeline.

Strengths:

The manuscript utilizes state-of-the-art mass spectrometric techniques with optimized collision parameters to ensure proper detection of the immonium ions, which is an advance compared to other similar approaches before. The use of synthetic control peptides on the HILIC separation step clearly demonstrates the ability of the method to reliably distinguish hydroxy-proline from oxidized methionine - containing peptides. Using this method, they identify a site on CDCA2, which they go on to validate in vitro and also study its role in regulation of mitotic progression in an associated manuscript.

Weaknesses:

Despite the authors' claim about the specificity of this method in picking up the intended peptides, there is a good amount of potential false positives that also happen to get picked (owing to the limitations of MS-based readout), and the authors' criteria for downstream filtering of such peptides require further clarification. In the same vein, greater and more diverse cell-based validation approach will be helpful to substantiate the claims regarding enrichment of peptides in the described pathway analyses.

We of course agree that false positives may arise, as is true for essentially all PTM studies. There are two issues here; first, are identified sites technically correct? (i.e. not misidentifications from the MS data) and second, are the identified modifications of biological significance? We have addressed this using the popular MaxQuant software suite to evaluate the modifications identified and to control the false discovery rate (FDR) at both the precursor and protein level, as described in the manuscript. We are aware that false positives could arise from confusing oxidation of methionine with hydroxylation of proline. Therefore, to address the issue as to whether we could identify bona fide PHD protein targets outside of the HIF family, we adopted a conservative approach by simply filtering out peptides where there was a methionine residue within three amino acids of the predicted proline hydroxylation site. This was a pragmatic decision made to reduce the likelihood of false positives in our dataset and we recognise that this likely results in us overlooking some genuine proline hydroxylation sites that occur nearby methionine residues. To address the potential biological relevance of the proline hydroxylation sites identified, we analysed extracts from cells treated with FG inhibitors. Of course a detailed understanding of biological significance relies upon follow-on experimental analyses for each site, which we have performed for P604 on RepoMan in accompanying study by Druker et al., (eLife 2025; doi.org/10.7554/eLife.108131.1).

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) The finding that the immonium ion intensities of L/I did not increase with increasing collision energy was surprising. Was this specific to this synthetic peptide?

We agree this is an interesting and unexpected finding. We have no reason to believe that it is specific to synthetic peptides per se, but rather think this reflects an effect of amino acid composition in the peptides analysed. It will be interesting to explore this phenomenon in more detail in future.

(2) The sequence logos in Figure 4 seemed to lack any amino acid enrichment in most positions except for collagen peptides. Have these findings been tested with statistical analysis?

The results we show for sequence logo analysis were generated using WebLogo (10.1101/gr.849004) and correspond to an analysis of all proline hydroxylated peptides we detected across all cell lines and replicates analysed. The fact that collagens are highly abundant proteins with very high levels of proline hydroxylation likely explains why collagen peptides dominated the outcome of the sequence logo analysis. There is clearly scope for more detailed follow up analysis in future of the sequence specificity of proline hydroxylation sites in no- collagen proteins that are validated PHD targets.

(3) Overall figure quality was not ideal. The resolution and font sizes of figures should be carefully evaluated and adjusted. The figure legend should contain a title for the figure. Annotations of the figures were somewhat confusing. 

We agree with the criticism of the figure resolution in the review copies - the lower resolution appears to have been generated after we had uploaded higher resolution original images. We are providing again higher resolution versions of all figures for the current revision.

Reviewer #3 (Recommendations for the authors):

Certain concerns regarding portions of the manuscript that need addressing:

(1) " These data show that two different cell lines show unique profiles of proteins with hydroxylated peptides." - It is difficult to conclusively say this statement after profiling the prolyl hydroxy proteome from just two cell lines, especially since the amino acids with the highest frequency in the most enriched peptides are similar in both cell lines.

We agree with this point and have changed the current revision to state instead, “This shows that each of the two cell lines analysed have distinct profiles.”

(2) "We noted that there was a high frequency of a methionine residues appearing either at the first, second, or even third positions after the HyPro site.." - according to the authors, claim, the advantage of their method was that they were able to overcome the limitation of older methods that couldn't separate methionine oxidation from proline hydroxylation. However, in this statement, they say that the high frequency of methionine residues may be because of the similar mass shift. These statements are contradictory. The authors should either tone down the claim or prove that those are indeed hydroxyproline sites. Is it possible that in the filtering step of excluding these high-frequency of methionine - containing peptides, we are losing potential positive hits for hydroxy-proline sites? What is the authors' take on this?

We respectfully do not agree that our, “statements are contradictory”, with respect to the potential confusion between identification of methionine oxidation and proline hydroxylation, but acknowledge that we have not explained this issue clearly enough. It is a fact that the similar mass shift resulting from proline hydroxylation and methionine oxidation is a technical challenge that can potentially lead to misidentifications in MS studies and that is what we state clearly in the manuscript. We have addressed this issue head on experimentally in this study and show using synthetic peptides how detailed analysis of specific proline hydroxylation sites in target proteins can be distinguished from methionine oxidation, based upon differential chromatographic behaviour of peptides with either hydroxylated proline or oxidised methionine, as well as by detailed analysis of fragmentation spectra. However, in the case of our global analysis, as we were not able to perform synthetic peptide comparisons for every putative site identified, we took the pragmatic approach of filtering out examples of peptides where a methionine residue was present within three residues of a potential proline hydroxylation site. This was done simply to reduce the possibility of misidentification in the set of novel proline hydroxylated peptides identified and we accept that as a consequence we are likely filtering out peptides that include bona fide proline hydroxylation sites. We have clarified this point in the current revision and hope to be able to address this issue more comprehensively in future studies.

(3) "Accordingly, a score cut-off of 40 for hydroxylated peptides and a localisation probability cut-off of more than 0.5 for hydroxylated peptides was performed." Could the authors shed more light and clarify what was the basis for this value of cut-off to be used in this filtering step? Is this sample dependent? What should be the criteria to determine this value?

We used MaxQuant software (10.1016/j.cell.2006.09.026), for PTM analysis, in which a localization probability score of 0.75 and score cut-off of 40 is a commonly used threshold to define high confidence. The reason that we used 0.5 at the first step was to investigate how likely it might be that the misassignment of delta m/z +16 Da (oxidation) on Methionine would affect the identification of hydroxylation on Proline. However, we note that in the final results set used for analysis, all putative proline hydroxylated peptides that had a Methionine residue near to the hydroxylated proline were disregarded as a pragmatic step to reduce the probability of false identifications.

(4) The authors are requested to kindly make the HPLC and MS traces more legible and use highresolution images, with clearly labeled values on the peaks. Kindly extract coordinates from the underlying data files to plot the curves if needed to make it clearer.

We have reviewed the clarity of all images and figures in the current revision.

(5) There seems to be no error bars in Figure 3, Figure 7E, and panels of Figure 8 with bar graphs. Are those single replicate data?

These specific figures are from single replicate data.

(6) For Figure 9C, the control with only PHD1 (no peptide) is missing. 

The ‘no peptide control’ was not included in the figure because it is simply a blank lane and there is nothing to see.

eLife Assessment

This valuable study presents findings on how prokaryotic antibiotics affect translation in mitochondrial ribosomes. Using mitoribosome profiling, the authors provide solid evidence that most tested antibiotics act similarly on bacterial and mitochondrial translation. Additionally, this work shows that alternative translation initiation events might exist in two specific mt-mRNAs (MT-ND1 and MT-ND5). However, additional biochemical and structural experiments are needed to support these findings.

Reviewer #1 (Public review):

Summary:

This study aimed to determine whether bacterial translation inhibitors affect mitochondria through the same mechanisms. Using mitoribosome profiling, the authors found that most antibiotics, except telithromycin, act similarly in both systems. These insights could help in the development of antibiotics with reduced mitochondrial toxicity.

They also identified potential novel mitochondrial translation events, proposing new initiation sites for MT-ND1 and MT-ND5. These insights not only challenge existing annotations but also open new avenues for research on mitochondrial function.

Strengths:

Ribosome profiling is a state-of-the-art method for monitoring the translatome at very high resolution. Using mitoribosome profiling, the authors convincingly demonstrate that most of the analyzed antibiotics act in the same way on both bacterial and mitochondrial ribosomes, except for telithromycin. Additionally, the authors report possible alternative translation events, raising new questions about the mechanisms behind mitochondrial initiation and start codon recognition in mammals.

Weaknesses:

All the weaknesses I previously highlighted were adequately addressed.

Reviewer #3 (Public review):

Summary:

Recently, the off-target activity of antibiotics on human mitoribosome has been paid more attention in the mitochondrial field. Hafner et al applied mitoribosome profilling to study the effect of antibiotics on protein translation in mitochondria as there are similarities between bacterial ribosome and mitoribosome. The authors conclude that some antibiotics act on mitochondrial translation initiation by the same mechanism as in bacteria. On the other hand, the authors showed that chloramphenicol, linezolid and telithromycin trap mitochondrial translation in a context-dependent manner. More interesting, during deep analysis of 5' end of ORF, the authors reported the alternative start codon for ND1 and ND5 proteins instead of previously known one. This is a novel finding in the field and it also provide another application of the technique to further study on mitochondrial translation.

Strengths:

This is the first study which applied mitoribosome profiling method to analyze mutiple antibiotics treatment cells. The mitoribosome profiling method had been optimized carefully and has been suggested to be a novel method to study translation events in mitochondria. The manuscript is constructive and well-written.

Weaknesses:

This is a novel and interesting study, however, most of conclusion comes from mitoribosome profiling analysis, as the result, the manuscript lacks the cellular biochemical data to provide more evidence and support the findings.

Comments on revisions:

The authors addressed most of my concerns and comments, although there is still no biochemical assay which should be performed to support mitoribsome profiling data.

The author also carefully investigated the structure of complex I, however, I am surprised that the author chose to analyse a low resolution structure (3.7 A). Recently, there are more high resolution structures of mammalian complex I published (7R41, 7V2C, 7QSM, 9I4I). Furthermore, the authors should not only respond to the reviewers but also (somehow) discuss these points in the manuscript.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

This study aimed to determine whether bacterial translation inhibitors affect mitochondria through the same mechanisms. Using mitoribosome profiling, the authors found that most antibiotics, except telithromycin, act similarly in both systems. These insights could help in the development of antibiotics with reduced mitochondrial toxicity.

They also identified potential novel mitochondrial translation events, proposing new initiation sites for MT-ND1 and MT-ND5. These insights not only challenge existing annotations but also open new avenues for research on mitochondrial function.

Strengths:

Ribosome profiling is a state-of-the-art method for monitoring the translatome at very high resolution. Using mitoribosome profiling, the authors convincingly demonstrate that most of the analyzed antibiotics act in the same way on both bacterial and mitochondrial ribosomes, except for telithromycin. Additionally, the authors report possible alternative translation events, raising new questions about the mechanisms behind mitochondrial initiation and start codon recognition in mammals.

Weaknesses:

The main weaknesses of this study are:

While the authors highlight an interesting difference in the inhibitory mechanism of telithromycin on bacterial and mitochondrial ribosomes, mechanistic explanations or hypotheses are lacking.

We acknowledge that we were not able to present a clear explanation for potential mechanistic differences of telithromycin inhibition between mitochondrial and bacterial ribosomes. In future work, structural analyses in collaboration with experts will provide these insights.

The assignment of alternative start codons in MT-ND1 and MT-ND5 is very interesting but does not seem to fully align with structural data.

We appreciate the reviewer’s comment and consulted a cryo-EM expert to review our findings in the context of the available structural data. We downloaded the density map and reviewed the N-termini of MT-ND1 and MT-ND5. We only observed the density of the N-terminus of MT-ND1 at low confidence. At an RMSD of 2, we could not observe density for the side chains of Met and Pro, and there are gaps in the density for what is modeled as the main chain. The assignment of these residues may have been overlooked due to the expectation that they should be present in the peptide.

For MT-ND5, we did observe some density that could be part of the main chain; however, it did not fill out until we reduced the stringency, and we did not observe density mapping to side chain residues. To summarize, we do not confidently see density for either the side chain or the main chain for either peptide.

The newly proposed translation events in the ncRNAs are preliminary and should be further substantiated with additional evidence or interpreted with more caution.

We agree with the reviewer that we did not provide conclusive evidence that our phased ribosome footprinting data on mitochondrial non-coding RNAs are proof of novel translation events. We do acknowledge this in the main text:” Due to both the short ORFs, minimal read coverage, and lack of a detectable peptide we could not determine if translation elongation occurred on the mitochondrial tRNAs. These sites may be unproductive mitoribosome binding events or simply from tRNAs partially digesting during MNase treatment.”

Reviewer #2 (Public review):

In this study, the authors set out to explore how antibiotics known to inhibit bacterial protein synthesis also affect mitoribosomes in HEK cells. They achieved this through mitoribosome profiling, where RNase I and Mnase were used to generate mitoribosome-protected fragments, followed by sequencing to map the regions where translation arrest occurs. This profiling identified the codon-specific impact of antibiotics on mitochondrial translation.

The study finds that most antibiotics tested inhibit mitochondrial translation similarly to their bacterial counterparts, except telithromycin, which exhibited distinct stalling patterns. Specifically, chloramphenicol and linezolid selectively inhibited translation when certain amino acids were in the penultimate position of the nascent peptide, which aligns with their known bacterial mechanism. Telithromycin stalls translation at an R/K-X-R/K motif in bacteria, and the study demonstrated a preference for arresting at an R/K/A-X-K motif in mitochondria. Additionally, alternative translation initiation sites were identified in MT-ND1 and MT-ND5, with non-canonical start codons. Overall, the paper presents a comprehensive analysis of antibiotics in the context of mitochondrial translation toxicity, and the identification of alternative translation initiation sites will provide valuable insights for researchers in the mitochondrial translation field.

From my perspective as a structural biologist working on the human mitoribosome, I appreciate the use of mitoribosome profiling to explore off-target antibiotic effects and the discovery of alternative mitochondrial translation initiation sites. However, the description is somewhat limited by a focus on this single methodology. The authors could strengthen their discussion by incorporating structural approaches, which have contributed significantly to the field. For example, antibiotics such as paromomycin and linezolid have been modeled in the human mitoribosome (PMID: 25838379), while streptomycin has been resolved (10.7554/eLife.77460), and erythromycin was previously discussed (PMID: 24675956). The reason we can now describe off-target effects more meaningfully is due to the availability of fully modified human mitoribosome structures, including mitochondria-specific modifications and their roles in stabilizing the decoding center and binding ligands, mRNA, and tRNAs (10.1038/s41467-024-48163-x).

These and other relevant studies should be acknowledged throughout the paper to provide additional context.

We appreciate the work that has previously revealed how different antibiotics bind the mitochondrial ribosome. We have included these references in the manuscript to provide background and context for this work in relationship to the field.

Reviewer #3 (Public review):

Summary:

Recently, the off-target activity of antibiotics on human mitoribosome has been paid more attention in the mitochondrial field. Hafner et al applied mitoribosome profilling to study the effect of antibiotics on protein translation in mitochondria as there are similarities between bacterial ribosome and mitoribosome. The authors conclude that some antibiotics act on mitochondrial translation initiation by the same mechanism as in bacteria. On the other hand, the authors showed that chloramphenicol, linezolid and telithromycin trap mitochondrial translation in a context-dependent manner. More interesting, during deep analysis of 5' end of ORF, the authors reported the alternative start codon for ND1 and ND5 proteins instead of previously known one. This is a novel finding in the field and it also provides another application of the technique to further study on mitochondrial translation.

Strengths:

This is the first study which applied mitoribosome profiling method to analyze mutiple antibiotics treatment cells.

The mitoribosome profiling method had been optimized carefully and has been suggested to be a novel method to study translation events in mitochondria. The manuscript is constructive and written well.

Weaknesses:

This is a novel and interesting study, however, most of the conclusion comes from mitoribosome profiling analysis, as a result, the manuscript lacks the cellular biochemical data to provide more evidence and support the findings.

We thank the reviewer for the positive assessment of our work. We agree that future biochemical and structural experiments will strengthen the conclusions we derive from the ribosome profiling.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

In Fig. 1A, the quality of the Western blot for the sucrose gradient is suboptimal. I recommend enhancing the quality of the Western blot image and providing the sucrose gradient sedimentation patterns for both the mtSSU and mtLSU to confirm the accurate selection of the monosome fraction. Additionally, to correctly assign the A260 peaks to mitochondrial and cytosolic ribosomes, it would be helpful to include markers for both the cytoribosomal LSU and SSU, too. Furthermore, do the authors observe mitochondrial polysomes in their sucrose gradient? If so, were those fractions fully excluded from the analysis?

We repeated our sucrose gradient and Western blotting with antibodies for the large and small subunits of the mitoribosome. We did not repeat western blotting for the cytoribosomes as the 40S, 60S, and 80S peaks are present in their canonical heights and locations on a sucrose gradient. Western blotting indicates that the large and small subunits of the mitoribosome are located in the fraction taken for mitoribo-seq. We do see trace amounts of mitoribosome in fractions past the 55S site. Those fractions were excluded from library preparation.

The MNase footprints exhibited a bimodal distribution, which the authors suggest may indicate that "MNase-treatment may have captured two distinct conformations of the ribosome." It would be relevant to clarify whether an enzyme titration was performed, as excessive MNase could lead to ribosomal RNA degradation, potentially influencing the footprints.

We did not perform a titration and instead based our concentration on the protocol from Rooijers et al, 2013. We included a statement of this and a reference to the concentration in the methods.

Is there an explanation for why RNase I footprinting reveals a very high peak at the 5'-end of the MT-CYB transcript, whereas this is not observed with MNase footprinting?

It is not clear. The intensity of peaks at the 5’ end of the transcripts varies. We do observe that the relative intensity of the 5’ peak is greater for RNase I footprinted samples than MNase-treated samples.

I understand that throughout the manuscript, the authors use MT-CYB as an example to illustrate the effects of the antibiotics on mitochondrial translation. However, to strengthen the generality of the conclusions, it would be beneficial to provide the read distribution across the entire mitochondrial transcriptome, possibly in the supplementary material. Additionally, I suggest including the read distribution for MT-CYB in untreated cells to improve data interpretation and enhance the clarity of figures (e.g., Figs. 1B, 2B, 3B).

As these experiments were generated across multiple mitoribo-seq experiments, each was done with its own control experiment. It would be inaccurate to show a single trace as representative of all experiments. Instead, we include Supplementary Figure 1, which shows the untreated MT-CYB trace for all control samples and indicates which treatment they pair with.

It would be very valuable to label each individual data point in the read phasing shown in Fig. 1D with the corresponding transcripts. For improved data visualization, I suggest assigning distinct colors to each transcript.

We are concerned that including the name of each gene in the main figure would be too difficult for the reader to accurately interpret. Instead, we have added a Supplementary Table with those values.

How do the authors explain the significant peak (approx. 10,000 reads) at the 5' end of the transcript in the presence of tiamulin (Fig. 2B)? Does this peak correspond to the start codon, and how does it relate to the quantification reported in Fig. 2C?

Yes, this represents the start codon. These reads are likely derived from the start codon as they are mapping to the 5’ end of the transcript. There are differences in sequencing depth depending on the experiment, so what is critical is the relative distribution of reads on the transcript rather than comparing absolute reads between experiments. MT-CYB has 54% of the reads at the start site, which is representative of what we see across all genes.

Throughout the manuscript, I found the usage of the terms "5' end" and "start codon" somewhat confusing, as they appear to be used synonymously in some instances. For example, in Fig. 2C, the y-axis label states "ribosomes at start codon," while the figure caption mentions "...percentage of reads that map to the 5' end of mitochondrial transcripts." Given the size of the graphs, it is also challenging for the reader to determine whether the peaks correspond specifically to the start codon or if multiple peaks accumulate at the initial codons.

We were selected for this language because two different types of analysis are being carried out. Ribosome profiling carried out in Figures 2 and 3 is carried out with RNase I, which poorly maps the ribosomes at the start codon when we do the read length analysis in Figure 4. Ribosome footprint at the 5’ end may include ribosomes that are on the 2-4 codons following the start codon, so it would not be accurate to label those as “ribosomes at a start codon.” We have renamed the axis to “Ribosomes at 5’ end”. Wig files are available online for all mitoribosome profiling experiments. In this case, the assigned “P-site” is several codons after the start codon due to the offset applied and the minimal 5’ UTR. Thus, it is less important to see which codon density is assigned to, but rather the general distribution of the reads.

The authors state, "Cells treated with telithromycin did show a slight increase in MRPF abundance at the 5' end of MT-CYB" and "the cumulative distribution of MRPFs suggested that ribosome density was biased towards the 5' end of the gene for chloramphenicol and telithromycin, but not significantly for linezolid." Could this observation be linked to the presence of specific stalling motifs in that region? If so, it would be beneficial to display such motifs on the graphs of the read distribution across the transcriptome to substantiate the context-dependent inhibition.

Thank you for this suggestion. For chloramphenicol and linezolid, alanine, serine, and threonine make up nearly 25% of the mitochondrial proteome. As such, there are numerous stall sites across the transcript. Given their identical stalling motifs, the difference between chloramphenicol and linezolid is due to sequence-specific differences. Potentially, this could be due to conditions such as the final concentration of antibiotic inside the mitochondria and the on/off rate of an inhibitor with the translating mitoribosome. Both may affect the kinetics of stalling and allow mitoribosomes to evade early stall sites.

We have also included the sites of all A/K/R-X-K motifs located in the genome and the calculated fold change for each position. As a note, this includes sites that do not pass the minimum filter set by our analysis and we note this in the text.

The comment raises an additional question: Does the increased density at the 5’ end derive from stalled mitoribosomes or queued mitoribosomes behind a stalling event? Recent work by Iwasaki’s group shows that mitoribosomes can form disomes and queue behind each other. However, we could not observe 30 aa periodicities behind stalling events that would be indicative of collided mitoribosomes.

In Fig. 3E, the authors report an additional and very interesting observation that is not discussed. Linezolid treatment causes reduced ribosome occupancy when proline or glycine codons occupy the P-site, or when the amino acids have been incorporated into the polypeptide chain and occupy the -1 position. It is known that the translation of proline and glycine frequently leads to ribosome stalling due to the physicochemical properties of these amino acids. Has this effect of linezolid been reported in the bacterial translation system? Additionally, can the authors propose hypotheses for the mechanism behind this observation? A similar observation is noted for telithromycin when glycine occupies the same positions, as well as when aspartate occupies the P- and A-sites.

In bacteria, Linezolid does have an “anti-stalling” motif when glycine is present in the A-site. However, this is due to the size of the residue being compatible with antibiotic binding.

The most likely cause of this effect is a redistribution of ribosome footprints. As the antibiotics introduce new arrest sites, ribosome density at other sites relatively decreases. This is likely an artifact from mitoribosomes redistributing from endogenously slow codons to new arrest sites. When looking at carrying out our disome profiling in the presence of anisomycin, we see a similar effect. Cytoribosomes are redistributed from endogenous stalling sites, such as proline, and are redistributed throughout the gene. As a result, translation at proline appears “more efficient” upon treatment with an inhibitor but is instead an artifact of analysis.

Figure 3F could benefit from indicating which mtDNA-encoded protein corresponds to each of the strongest stalling motifs.

We have included a supplementary figure to highlight which mitochondrially-encoded genes containing the R/K/A-X-K motif and noted in the text that mitochondrial translation may be unevenly inhibited.

The legend "increasing mRPF abundance" in Fig. 4C may be missing the corresponding colors.

The legend applies to all sections of the figure. We double-checked the range of the colors in the tables, and they do match the legend.

The observation that the start codons in MT-ND1 and MT-ND5 might differ from the annotated canonical ones is intriguing. While the ribosome profiling data appear clear, mass spectrometry (MS) analysis may be misleading. The absence of evidence does not necessarily imply evidence of absence. How does this proposed conclusion correlate with the structural data obtained from HEK cells? For instance, the cryo-EM structural model of a complex I-containing human supercomplex (PDB: 5XTD, PMID: 28844695) shows the presence of Pro2 in MT-ND1 and the full-length MT-ND5 protein. The authors should carefully examine structural data to ascertain whether alternative forms of MT-ND1 and MT-ND5 are actually observed in the assembled complex I.

We really appreciate this comment. We sat down with an expert in cryo-EM and reviewed the figure. We downloaded the density map and reviewed the N-termini of MT-ND1 and MT-ND5. We only observed the density of the N-terminus of MT-ND1 at low confidence. At an RMSD of 2, we could not observe density for the side chains of Met and Pro, and there are gaps in the density for what is modeled as the main chain. The assignment of these residues may have been overlooked due to the expectation that they should be present in the peptide.

For MT-ND5, we did observe some density that could be part of the main chain; however, it did not fill out until we reduced the stringency, and we did not observe density mapping to side chain residues. To summarize, we do not confidently see density for either the side chain or the main chain for either peptide.

Given that ribosome profiling is based on the assumption that ribosomes protect mRNA fragments from RNase digestion, interpreting the data related to Fig. 5 and the proposed existence of translation events involving ncRNAs is challenging. Most importantly, tRNAs and rRNAs are highly folded RNA molecules and, by definition, are protected by ribosomal proteins. Simultaneously, as the authors point out, "These reads could either be products of random digestion of the abundant background of ncRNAs or be genuine MRPFs." RNase I preferentially digests single-stranded RNA (ssRNA), but excess enzyme can still lead to degradation. Consequently, many random tRNA/rRNA fragments may be generated by RNase digestion, potentially resulting in artifacts. I suggest that the authors examine what happens to these reads when mitochondrial translation is inhibited.

We have low-quality mitoribo-seq with initiation inhibitors and Mnase showing footprints of the same size. We do not have a small-molecule inhibitor that is able to completely ablate translation, as they instead stabilize mitoribosomes at different steps in translation. We have considered alternative ways of capturing a background rRNA and tRNA digestion pattern; however, these have their own drawbacks. Dissociation with EDTA prior to digestion or carrying out library prep on the small and large subunits may capture mitoribosomes no longer in the process of translation; however, dissociated subunits would have different surfaces now available for digestion and may not capture tRNAs.

Regarding the statement, "While the ORF on MT-TS1 is longer, MRPF density was low and we did not observe read phasing and thus it is likely not translated (not shown)," the data should not be excluded unless a clear explanation is provided for why translation would not occur from this specific RNA.

We have included this value in the graph as well as in Supplementary Figure 1.

The graph in Fig. 5B shows the periodicity of only the putative RNR1 ORF, but not that of the other proposed ORFs. What is the reason for this?

We have included the MT-TS1 putative ORF in Figure 5 and Figure S1. Other ORFs did not have density in the ORF. If these are real mitoribosome footprints at these start codons, it may be due to them being transient binding events that never result in elongation. Alternatively, they may be due to tRNA degradation during library preparation.

The assumption that the UUG codon can serve as a start site for mitochondrial translation has not been substantiated. Recent data have identified translation initiation events from non-ATG/ATA codons (near-cognate and sub-cognate) using retapamulin, but UUG was not among them. Can the authors detect such events in their ribosome profiling data collected in the presence of retapamulin, tiamulin, or josamycin?

The report of translation initiation at non-ATG/ATA codons strongly disagrees with our findings. We report that sites of translation initiation observed within annotated coding regions in mitochondria occur at the annotated start sites, while the other report finds frequent alternative initiation events. We have looked for those arrest sites and did not observe them.

In the section "Mitoribosome profiling reveals novel translation events," the title may be misleading given the preliminary nature of the results. To support such a claim, the authors should provide experimental evidence demonstrating that the proposed translation events genuinely exist and result in the synthesis of previously unidentified polypeptides. Alternatively, the interpretation should be approached with greater caution and more clearly indicated as preliminary.

We agree with the reviewers that a distinction should be made between reporting truly novel translation events, like the recently reported MT-ND5-dORF, and sites we suspect mitoribosomes may be binding and that require detailed follow-up. We altered the section title to suggest that this may be showing novel translation events. Additionally, we included a statement in the discussion that these MRPFs may be simply tRNA digestion by RNase I.

Although located at the 5' end of RNR1, the newly identified ORF is situated 79 nt downstream. According to current knowledge, this appears to be a lengthened 5' UTR that may hinder mitoribosome loading. The authors should speculate on potential initiation mechanisms.

The start of the putative ORF is not located 79 nts down, but at the 8^th nucleotide. The reviewer may be including the tRNA-Phe in their calculation, which is cleaved from MT-RNR1. This start site is closer to the 5’ end than our findings with MT-ND5.

To enhance the interpretation of the mitoribosome profiling data, the authors could complement their findings with classical metabolic labeling using (35)S-methionine. This approach would allow for a different assessment of the stringency of the inhibition under the tested experimental conditions.

We are currently working on these experiments using mito-funcats. A future direction we are taking this work is to understand how the cell responds to different mechanisms of translation inhibition. For example, we are trying to understand if telithromycin, which appears highly selective, only partially inhibits translation of the mtDNA-encoded proteome.

Reviewer #2 (Recommendations for the authors):

Other small editorial comments:

Line 24: "translate proteins"?

Revised for clarity

Line 24: The sentence describing mitochondrial translation as "closely resembling the one in prokaryotes" could be reformulated. While the core of the mitoribosome is conserved, the entire apparatus has many mitochondria-specific features.

Since this is the abstract, we simplified the point by saying that mitoribosomes are more similar to prokaryotic than cytosolic ribosomes.

Clarified to highlight that the mitochondrial system is more similar to the bacterial system than the eukaryotic system.

Line 33: "novel" or "previously unrecognized" ?

Rewritten for clarity.

Lines 33-35: The claim made here is not shown in the paper.

We removed the more aspirational goal of this paper and focused on the main findings of the paper.

Lines 44, 47, 89 (and elsewhere): "cytoplasmic" or "cytosolic" ?

Both terms are used in the literature. We opted for cytoplasmic as it can also include ribosomes not free in the cytosol, such as those bound to the ER.

Reviewer #3 (Recommendations for the authors):

(1) The authors should state why they chose these antibiotics for mitoribosome profiling analysis over other antibiotics from same group. Did they screen multiple antibiotics to determine the candidates for next step?

We selected antibiotics that had a known stalling motif in bacteria (initiation or context-dependent elongation inhibitors). In addition, we carried out mitoribosome profiling with erythromycin, azithromycin, thiostrepton, and kanamycin in this work. However, we did not see any effect from these drugs in mitoribosome profiling. We are currently testing other inhibitors, such as doxycycline and tigecycline, and looking at optimizing treatment conditions to identify stalling motifs in samples that previously showed no difference.

(2) What is the reason for choosing the concentration of antibiotics retapamulin, tiamulin and josamycin, this is IC50 value or above this value? On the other hand, none of this information has been provided for the antibiotics in the next part. The authors should provide biochemical study for the effect of these antibiotics on cell survival and/or protein translation such as S35 assay or steady state level of mtDNA-encoded proteins upon cell treatment with these antibiotics.

Prior to mitoribo-seq, we carried out time and concentration assays with all antibiotics. 100 µg/ml and a 30-minute treatment was tolerable for all antibiotics except retapamulin. We aimed to treat cells with a relatively high concentration of inhibitor in order to capture actively translating mitoribosomes. We were concerned that longer treatments may lead to decreased translation initiation, leading to the capture of fewer mitoribosomes. These concentrations were nearly identical to contemporary conditions carried out in Bibel et al, RNA 2025.

(3) Why did the authors choose MT-CYB as the representative for further analysis in the second and third parts of the manuscript?

We chose MT-CYB because its length allowed for easy visualization. Some mitochondrial genes, such as MT-ND6, had a propensity for stronger stalling at initiation. While coverage was throughout the genes, it was difficult to visualize the changes within the ORF. Also, MT-CYB was less visually complex than polycistronic transcripts. All wigs were uploaded to GEO.

(4) Page 11, line 233-234: the authors state that telithromycin induces stalling at R/K/A-X-K motif. The authors should do further analysis on mitochondrial genome which proteins contain this motif. Furthermore, same as comment 2: the authors should confirm by 35S assay or WB to know which mtDNA-encoded proteins are affected.

We have included a supplementary figure showing which mitochondrial genes contain these motifs.

(5) The results and conclusion from the fourth paragraph are very interesting. The authors suggest alternative start codon for two mtDNA encoded proteins: ND1 and ND5 based on ribosome profiling analysis. Again, I have several comments on this part: <br /> (a) For the accumulation of the alternative start codon of ND1 and ND5 as suggested in the manuscript, do the authors observe this trend with the initiation inhibitors used in the second paragraphs of the manuscript?

We did not observe similar read lengths with retapamulin, tiamulin, or josamycin, which produced read lengths that were consistent with other RNase I footprinted samples.

(b) This observation was further confirmed by MS with a peptide form ND1 protein, the authors should show MS peak indicating MW of the peptide and MS/MS data for the peptide which supports this hypothesis.

We are including the MS/MS report for this peptide.

(c) Interestingly, several high-resolution structures of mammalian complex I have been reported so far (PMID: 7614227, 10396290, 38870289), ND1 and ND5 protein express full sequences with fMet at the distal N-terminal. This is different to the suggestion from the manuscript. Could the author discuss or comment on that?

This point was brought up by another reviewer. We have carefully analyzed the density map of PMID: 28844695. We sat down with an expert in cryo-EM and reviewed the figure. We downloaded the density map and reviewed the N-termini of MT-ND1 and MT-ND5. We only observed the density of the N-terminus of MT-ND1 at low confidence. At an RMSD of 2, we could not observe density for the sidechains of Met and Pro, and there is a gap in density for what is modeled as the main chain. The assignment of these residues may have been overlooked due to the expectation that they should be present in the peptide.

For MT-ND5, we did observe some density that could be part of the main chain; however, it did not fill out until we reduced the stringency, and we did not observe density mapping to side chain residues. To summarize, we do not confidently see density for either the side chain or the main chain for either peptide.

Minor comments:

The method should be written more accurately for easily repeating experiments by other groups. For example:

(1) The authors should indicate what was exact HEK293 cell line used in this study.

We have indicated the exact cell line.

(2) Page 22, line 471: which (number) fractions had been collected. The Western Blot analysis shown in Figure 1A should be repeated with both proteins from small and large subunits.

We have repeated the Western blot with antibodies for large and small subunits. We took fractions 8 and 9, which are now indicated in the text and figure.

(3) Page 23, line 502: is this number of cells used for MS experiment is correct? Or is this number of cells per mL?

This is correct and is based on the kit protocol. It is not cells per mL. We have clarified the kit being used in the methods.

eLife Assessment

This work provides an important resource identifying 72 proteins as novel candidates for plasma membrane and/or cell wall damage repair in budding yeast, and describes the temporal coordination of exocytosis and endocytosis during the repair process. The data are convincing; however, additional experimental validation will better support the claim that repair proteins shuttle between the bud tip and the damage site.

Reviewer #1 (Public review):

Summary:

In this manuscript, Yamazaki et al. conducted multiple microscopy-based GFP localization screens, from which they identified proteins that are associated with PM/cell wall damage stress response. Specifically, the authors identified that bud-localized TMD-containing proteins and endocytotic proteins are associated with PM damage stress. The authors further demonstrated that polarized exocytosis and CME are temporally coupled in response to PM damage, and CME is required for polarized exocytosis and the targeting of TMD-containing proteins to the damage site. From these results, the authors proposed a model that CME delivers TMD-containing repair proteins between the bud tip and the damage site.

Strengths:

Overall, this is a well-written manuscript, and the experiments are overall well-conducted. The authors identified many repair proteins and revealed the temporal coordination of different categories of repair proteins. Furthermore, the authors demonstrated that CME is required for targeting of repair proteins to the damage site, as well as cellular survival in response to stress related to PM/cell wall damage. Although the roles of CME and bud-localized proteins in damage repair are not completely new to the field, this work does have conceptual advances by identifying novel repair proteins and proposing the intriguing model that the repairing cargoes are shuttled between the bud tip and the damaged site through coupled exocytosis and endocytosis.

Weaknesses:

While the results presented in this manuscript are convincing, they might not be sufficient to support some of the authors' claims. Especially in the last two result sessions, the authors claimed CME delivers TMD-containing repair proteins from the bud tip to the damage site. The model is no doubt highly possible based on the date, but caveats still exist. For example, the repair proteins might not be transported from one localization to another localization, but are degraded and re-synthesized. Although the Gal-induced expression system can further support the model to some extent, I think more direct verification (such as FLIP or photo-convertible fluorescence tags to distinguish between pre-existing and newly synthesized proteins) would significantly improve the strength of evidence.

Review on revised version:

The authors addressed most of concerns that were originally raised, primarily by revising the text and figures and expanding the discussion, which improves the clarity of the manuscript. Although the authors did not address my major concern on the shuttling/trafficking model experimentally, I do understand the limitation of resources and time. The authors noted that they planned to do these experiments for their future work, and such studies would be more definitive evaluations for the proposed model. Overall I think this is a very interesting and well-conducted study and I enjoyed reading this manuscript. I look forward to their following research of this study.

Reviewer #2 (Public review):

This paper remarkably reveals the identification of plasma membrane repair proteins, revealing spatiotemporal cellular responses to plasma membrane damage. The study highlights a combination of sodium dodecyl sulfate (SDS) and lase for identifying and characterizing proteins involved in plasma membrane (PM) repair in Saccharomyces cerevisiae. From 80 PM, repair proteins that were identified, 72 of them were novel proteins. The use of both proteomic and microscopy approaches provided a spatiotemporal coordination of exocytosis and clathrin-mediated endocytosis (CME) during repair. Interestingly, the authors were able to demonstrate that exocytosis dominates early and CME later, with CME also playing an essential role in trafficking transmembrane-domain (TMD) containing repair proteins between the bud tip and the damage site.

Weaknesses/limitations:

- Still, there is a lack of clarity about mentioning Pkc1 as the best characterized repair protein, or why is Pkc1 mentioned only as it is changing the localization?!

- The use of a C-terminal GFP-tagged library for the laser damage assay may have limited the identification of proteins whose localization or function depends on an intact N-terminus. N-terminal regions might contain targeting or regulatory elements; therefore, some relevant repair factors may have been missed. Analysis of endogenously N-terminally tagged strains, at least for selected candidates, could help address this limitation.

- The authors appropriately discuss the limitations of SDS- and laser-induced plasma membrane damage, including the possibility that these approaches may not capture proteins involved in other forms of membrane injury, such as mechanical or osmotic stress.

Reviewer #3 (Public review):

Summary:

This work aims to understand how cells repair damage to the plasma membrane (PM). This is important as failure to do so will result in cell lysis and death. Therefore, this is an important fundamental question with broad implications for all eukaryotic cells. Despite this importance, there are relatively few proteins known to contribute to this repair process. This study expands the number of experimentally validated PM from 8 to 80. Further, they use precise laser-induced damage of the PM/cell wall and use live-cell imaging to track the recruitment of repair proteins to these damage sites. They focus on repair proteins that are involved in either exocytosis or clathrin-mediated endocytosis (CME) to understand how these membrane remodeling processes contribute to PM repair. Through these experiments, they find that while exocytosis and CME both occur at the sites of PM damage, exocytosis predominates the early stages of repairs, while CME predominates in the later stages of repairs. Lastly, they propose that CME is responsible for diverting repair proteins localized to the growing bud cell to the site of PM damage.

Strengths:

The manuscript is very well written and the experiments presented flow logically. The use of laser-induced damage and live-cell imaging to validate the proteome-wide screen using SDS induced damage strengthen the role of the identified candidates in PM/cell wall repair.

Comments on revisions:

The authors have very nicely addressed my previous comments and I have no further concerns.

Author response:

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

eLife Assessment

This work provides an important resource identifying 72 proteins as novel candidates for plasma membrane and/or cell wall damage repair in budding yeast, and describes the temporal coordination of exocytosis and endocytosis during the repair process. The data are convincing; however, additional experimental validation will better support the claim that repair proteins shuttle between the bud tip and the damage site.

We thank the editors and reviewers for their positive assessment of our work and the constructive feedback to improve our manuscript. We agree with the assessment that additional validation of repair protein shuttling between the bud tip and the damage site is required to further support the model.

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this manuscript, Yamazaki et al. conducted multiple microscopy-based GFP localization screens, from which they identified proteins that are associated with PM/cell wall damage stress response. Specifically, the authors identified that budlocalized TMD-containing proteins and endocytotic proteins are associated with PM damage stress. The authors further demonstrated that polarized exocytosis and CME are temporally coupled in response to PM damage, and CME is required for polarized exocytosis and the targeting of TMD-containing proteins to the damage site. From these results, the authors proposed a model that CME delivers TMD-containing repair proteins between the bud tip and the damage site.

Strengths:

Overall, this is a well-written manuscript, and the experiments are well-conducted. The authors identified many repair proteins and revealed the temporal coordination of different categories of repair proteins. Furthermore, the authors demonstrated that CME is required for targeting of repair proteins to the damage site, as well as cellular survival in response to stress related to PM/cell wall damage. Although the roles of CME and bud-localized proteins in damage repair are not completely new to the field, this work does have conceptual advances by identifying novel repair proteins and proposing the intriguing model that the repairing cargoes are shuttled between the bud tip and the damaged site through coupled exocytosis and endocytosis.

Weaknesses:

While the results presented in this manuscript are convincing, they might not be sufficient to support some of the authors' claims. Especially in the last two result sessions, the authors claimed CME delivers TMD-containing repair proteins from the bud tip to the damage site. The model is no doubt highly possible based on the data, but caveats still exist. For example, the repair proteins might not be transported from one localization to another localization, but are degraded and resynthesized. Although the Gal-induced expression system can further support the model to some extent, I think more direct verification (such as FLIP or photo-convertible fluorescence tags to distinguish between pre-existing and newly synthesized proteins) would significantly improve the strength of evidence.

Major experiment suggestions:

(1) The authors may want to provide more direct evidence for "protein shuttling" and for excluding the possibility that proteins at the bud are degraded and synthesized de novo near the damage site. For example, if the authors could use FLIP to bleach budlocalized fluorescent proteins, and the damaged site does not show fluorescent proteins upon laser damage, this will strongly support the authors' model. Alternatively, the authors could use photo-convertible tags (e.g., Dendra) to differentiate between preexisting repair proteins and newly synthesized proteins.

We thank the reviewer for evaluating our work and giving us important feedback. We agree that the FLIP and photo-convertible experiments will further confirm our model. Here, due to time and resource constraints, we decided not to perform this experiment. Instead, we have discussed this limitation in 363-366. Our proposed model of repair protein shuttling should be further tested in our future work.

(2) In line with point 1, the authors used Gal-inducible expression, which supported their model. However, the author may need to show protein abundance in galactose, glucose, and upon PM damage. Western blot would be ideal to show the level of fulllength proteins, or whole-cell fluorescence quantification can also roughly indicate the protein abundance. Otherwise, we cannot assume that the tagged proteins are only expressed when they are growing in galactose-containing media.

Thank you very much for raising the concern and suggesting the important experiments.We agree that the Western blot experiment to confirm the mNG-Snc1 expression in each medium will further strengthen our conclusion. Along with point (1), further investigation of repair protein shuttling between the bud tip and the damage site and the mechanisms underlying it will be an important future direction. As described above, we have discussed this limitation in 363-366.

(3) Similarly, for Myo2 and Exo70 localization in CME mutants (Figure 4), it might be worth doing a western or whole-cell fluorescence quantification to exclude the caveat that CME deficiency might affect protein abundance or synthesis.

We thank the reviewer for suggesting the point. Following the reviewer’s suggestion, we quantified the whole-cell fluorescence of WT and CME mutants and verified that the effect of the CME deletion on the expression levels of Myo2-sfGFP and Exo70-mNG is minimal ( Figure S6). We added the description in lines 211-212.

(4) From the authors' model in Figure 7, it looks like the repair proteins contribute to bud growth. Does laser damage to the mother cell prevent bud growth due to the reduction of TMD-containing repair proteins at the bud? If the authors could provide evidence for that, it would further support the model.

Thank you very much for raising the important point. We speculate that the reduction of TMD-containing proteins at the bud by CME is one of the causes of cell growth arrest after PM damage (1). This is because TMD-containing repair proteins at the bud tip, including phospholipid flippases (Dnf1/Dnf2), Snc1, and Dfg5, are involved in polarized cell growth (2-4). This will be an important future direction as well.

(5) Is the PM repair cell-cycle-dependent? For example, would the recruitment of repair proteins to the damage site be impaired when the cells are under alpha-factor arrest?

Thank you for raising this interesting point. Indeed, the senior author Kono previously performed this experiment when she was in David Pellman’s lab. The preliminary results suggest that Pkc1 can be targeted to the damage site, without any impairment, under alpha-factor arrest. A more comprehensive analysis in the future will contribute to concluding the relation between PM repair and the cell cycle.

Reviewer #2 (Public review):

This paper remarkably reveals the identification of plasma membrane repair proteins, revealing spatiotemporal cellular responses to plasma membrane damage. The study highlights a combination of sodium dodecyl sulfate (SDS) and lase for identifying and characterizing proteins involved in plasma membrane (PM) repair in Saccharomyces cerevisiae. From 80 PM, repair proteins that were identified, 72 of them were novel proteins. The use of both proteomic and microscopy approaches provided a spatiotemporal coordination of exocytosis and clathrin-mediated endocytosis (CME) during repair. Interestingly, the authors were able to demonstrate that exocytosis dominates early and CME later, with CME also playing an essential role in trafficking transmembrane-domain (TMD)containing repair proteins between the bud tip and the damage site.

Weaknesses/limitations:

(1) Why are the authors saying that Pkc1 is the best characterized repair protein? What is the evidence?

We would like to thank the reviewer for taking his/her time to evaluate our work and for valuable suggestions. We described Pkc1 as “best characterized” because it was the first protein reported to accumulate at the laser damage site in budding yeast (5). However, as the reviewer suggested, we do not have enough evidence to describe Pkc1 as “best characterized”. We therefore used “one of the known repair proteins” to mention Pkc1 in the manuscript (lines 90-91).

(2) It is unclear why the authors decided on the C-terminal GFP-tagged library to continue with the laser damage assay, exclusively the C-terminal GFP-tagged library. Potentially, this could have missed N-terminal tag-dependent localizations and functions and may have excluded functionally important repair proteins

Thank you very much for the comments. We decided to use the C-terminal GFP-tagged library for the laser damage assay because we intended to evaluate the proteins of endogenous expression levels. The N-terminal sfGFP-tagged library is expressed by the NOP1 promoter, while the C-terminal GFP-tagged library is expressed by the endogenous promoters. We clarified these points in lines 114-118. We agree with the reviewer on that we may have missed some portion of repair proteins in the N-terminaldependent localization and functions by this approach. Therefore, in our manuscript, we discussed these limitations in lines 281-289.

(3) The use of SDS and laser damage may bias toward proteins responsive to these specific stresses, potentially missing proteins involved in other forms of plasma membrane injuries, such as mechanical, osmotic, etc.). SDS stress is known to indirectly induce oxidative stress and heat-shock responses.

Thank you very much for raising this point. We agree that the combination of SDS and laser may be biased to identify PM repair proteins. Therefore, in the manuscript, we discussed this point as a limitation of this work in lines 292-298.

(4) It is unclear what the scale bars of Figures 3, 5, and 6 are. These should be included in the figure legend.

We apologize for the missing scale bars. We added them to the legends of the figures in the manuscript.

(5) Figure 4 should be organized to compare WT vs. mutant, which would emphasize the magnitude of impairment.

Thank you for raising this point. Following the suggestion, we updated Figure 4. In the Figure 4, we compared WT vs mutant in the manuscript. We clarified it in the legends in the manuscript. 

(6) It would be interesting to expand on possible mechanisms for CME-mediated sorting and retargeting of TMD proteins, including a speculative model.

Thank you very much for this important suggestion. We think it will be very important to characterize the mechanism of CME-mediated TMD protein trafficking between the bud tip and the damage site. In the manuscript, we discussed the possible mechanism for CME activation at the damage site in lines 328-333. We speculate that the activation of the CME may facilitate the retargeting of the TMD proteins from the damage site to the bud tip.

We do not have a model of how CMEs activate at the bud tip to sort and target the TMD proteins to the damage site. One possibility is that the cell cycle arrest after PM damage (1) may affect the localization of CME proteins because the cell cycle affects the localization of some of the CME proteins (6). We will work on the mechanism of repair protein sorting from the bud tip to the damage site in our future work.

Reviewer #3 (Public review):

Summary:

This work aims to understand how cells repair damage to the plasma membrane (PM). This is important, as failure to do so will result in cell lysis and death. Therefore, this is an important fundamental question with broad implications for all eukaryotic cells. Despite this importance, there are relatively few proteins known to contribute to this repair process. This study expands the number of experimentally validated PM from 8 to 80. Further, they use precise laser-induced damage of the PM/cell wall and use livecell imaging to track the recruitment of repair proteins to these damage sites. They focus on repair proteins that are involved in either exocytosis or clathrin-mediated endocytosis (CME) to understand how these membrane remodeling processes contribute to PM repair. Through these experiments, they find that while exocytosis and CME both occur at the sites of PM damage, exocytosis predominates in the early stages of repairs, while CME predominates in the later stages of repairs. Lastly, they propose that CME is responsible for diverting repair proteins localized to the growing bud cell to the site of PM damage.

Strengths:

The manuscript is very well written, and the experiments presented flow logically. The use of laser-induced damage and live-cell imaging to validate the proteome-wide screen using SDS-induced damage strengthens the role of the identified candidates in PM/cell wall repair.

Weaknesses:

(1) Could the authors estimate the fraction of their candidates that are associated with cell wall repair versus plasma membrane repair? Understanding how many of these proteins may be associated with the repair of the cell wall or PM may be useful for thinking about how these results are relevant to systems that do or do not have a cell wall. Perhaps this is already in their GO analysis, but I don't see it mentioned in the manuscript.

We would like to thank the reviewer for taking his/her time to evaluate our work and valuable suggestions. We agree that this is important information to include. Although it may be difficult to completely distinguish the PM repair and cell wall repair proteins, we have identified at least six proteins involved in cell wall synthesis (Flc1, Dfg5, Smi1, Skg1, Tos7, and Chs3). We included this information in lines 142-146 in the manuscript.

(2) Do the authors identify actin cable-associated proteins or formin regulators associated with sites of PM damage? Prior work from the senior author (reference 26) shows that the formin Bnr1 relocalizes to sites of PM damage, so it would be interesting if Bnr1 and its regulators (e.g., Bud14, Smy1, etc) are recruited to these sites as well. These may play a role in directing PM repair proteins (see more below).

Thank you for the suggestion. We identified several Bnr1-interacting proteins, including Bud6, Bil1, and Smy1 (Table S2), although Bnr1 itself was not identified in our screening. This could be attributed to the fact that (1) C-terminal GFP fusion impaired the function of Bnr1, and (2) a single GFP fusion is not sufficient to visualize the weak signal at the damage site. Indeed, in reference 26, 3GFP-Bnr1 (N-terminal 3xGFP fusion) was used.

(3) Do the authors suspect that actin cables play a role in the relocalization of material from the bud tip to PM damage sites? They mention that TMD proteins are secretory vesicle cargo (lines 134-143) and that Myo2 localizes to damage sites. Together, this suggests a possible role for cable-based transport of repair proteins. While this may be the focus of future work, some additional discussion of the role of cables would strengthen their proposed mechanism (steps 3 and 4 in Figure 7).

Thank you very much for the suggestion. We agree that actin cables may play a role in the targeting of vesicles and repair proteins to the damage site. Following the reviewer’s suggestion, we discussed the roles of Bnr1 and actin cables for repair protein trafficking in lines 309-313 in the manuscript.

(4) Lines 248-249: I find the rationale for using an inducible Gal promoter here unclear. Some clarification is needed.

Thank you for raising this point. We clarified this as possible as we could in lines 249255 in the manuscript.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) The N-terminal GFP collection screen is interesting but seems irrelevant to the rest of the results. The authors discussed that in the discussion part, but it might be worth showing how many hits from the laser damage screen (in Figure 2) overlap with the Nterminal GFP screen hits.

Thank you for the suggestion. We found that 48 out of 80 repair proteins are hits in the N-terminal GFP library (Table S1 and S2). This result suggested that the N-terminal library is also a useful resource for identifying repair proteins. In the manuscript, we discussed it in lines 288-289.

(2) SDS treatment seems a harsh stressor. As the authors mentioned, the overlapped hits from the N- and C-terminal GFP screen might be more general stress factors. Thus, I think Line 84 (the subtitle) might be overclaiming, and the authors might need to tone down the sentence.

Thank you for the suggestion. Following the reviewer’s suggestion, we changed the sentence to “Proteome-scale identification of SDS-responsive proteins” in the manuscript. We believe that the new sentence describes our findings more precisely.

(3) Line 103-106, it does not seem obvious to me that the protein puncta in the cytoplasm are due to endocytosis. The authors might need to provide more experimental evidence for the conclusion, or at least provide more reasoning/references on that aspect (e.g.,several specific protein hits belonging to that group have been shown to be endocytosed).

Thank you very much for raising this point. We agree with the reviewer and deleted the description that these puncta are due to endocytosis in the manuscript.

(4) For Figure 1D and S1C, the authors annotated some of the localization changes clearly, but some are confusing to me. For example," from bud tip/neck" to where? And from where to "Puncta/foci"? A clearer annotation might help the readers to understand the categorization.

Thank you very much for the suggestion. These annotations were defined because it is difficult to conclusively describe the protein localization after SDS treatment. To convincingly identify the destination of the GFP fusion proteins, the dual color imaging of proteins with organelle markers or deep learning-based localization estimation is required. We feel that this might be out of the scope of this work. Therefore, as criteria, we used the localization of protein localization in normal/non-stressed conditions reported in (7) and the Saccharomyces Genome Database (SGD). We clarified this annotation definition in the manuscript (lines 413-436).

(5) For localization in Figure 2C, as I understand, does it refer to6 the "before damage/normal" localization? If so, I think it would be helpful to state that these localizations are based on the untreated/normal conditions in the text.

Yes, it refers to the “before damage/normal localization”. Following the reviewer’s suggestion, we stated that these localizations are based on these conditions in the manuscript (line 130).

(6) The authors mentioned "four classes" in Line 120, but did not mention the "PM to cytoplasm" class in the text. It would be helpful to discuss/speculate why these transporters might contribute to PM damage repair.

Thank you very much for this suggestion. We speculated that these transporters are endocytosed after PM damage because endocytosis of PM proteins contributes to cell adaptation to environmental stress (8). We mentioned it in the manuscript (lines 120-122).

(7) Line 175-180 My understanding of the text is that the signals of Exo70-mNG/Dnf1mNG peak before the Ede1-mSc-I peaks. They occur simultaneously, but their dominating phase are different. It is clearer when looking at the data, but I think the conclusion sentences themselves are confusing to me. The authors might consider rewriting the sentences to make them more straightforward.

Thank you very much for pointing this out. Following the reviewer’s suggestion, we revised the sentence (lines 177-182 in the manuscript).

Reviewer #2 (Recommendations for the authors):

It would be interesting to expand on the functional characterization of the 72 novel candidates and explore possible mechanisms for CME-mediated sorting and retargeting of TMD proteins by including a speculative model.

Thank you very much for the comment. We agree that the further characterization of novel repair proteins and exploration of the possible mechanisms for CME-mediated TMD protein sorting and retargeting are truly important. This should be our important future direction.

Reviewer #3 (Recommendations for the authors):

The x-axis in Figure 1C is labeled 'Ratio' - what is this a ratio of?

Thank you for raising this point. It is the ratio of the number of proteins associated with a GO term to the total number of proteins in the background. We clarified it in the legend of Figure 1C in the manuscript.

References

(1) K. Kono, A. Al-Zain, L. Schroeder, M. Nakanishi, A. E. Ikui, Plasma membrane/cell wall perturbation activates a novel cell cycle checkpoint during G1 in Saccharomyces cerevisiae. Proc Natl Acad Sci U S A 113, 6910-6915 (2016).

(2) A. Das et al., Flippase-mediated phospholipid asymmetry promotes fast Cdc42 recycling in dynamic maintenance of cell polarity. Nat Cell Biol 14, 304-310 (2012).

(3) M. Adnan et al., SNARE Protein Snc1 Is Essential for Vesicle Trafficking, Membrane Fusion and Protein Secretion in Fungi. Cells 12 (2023).

(4) H.-U. Mösch, G. R. Fink, Dissection of Filamentous Growth by Transposon Mutagenesis in Saccharomyces cerevisiae. Genetics 145, 671-684 (1997).

(5) K. Kono, Y. Saeki, S. Yoshida, K. Tanaka, D. Pellman, Proteasomal degradation resolves competition between cell polarization and cellular wound healing. Cell 150, 151-164 (2012).

(6) A. Litsios et al., Proteome-scale movements and compartment connectivity during the eukaryotic cell cycle. Cell 187, 1490-1507.e1421 (2024).

(7) W.-K. Huh et al., Global analysis of protein localization in budding yeast.Nature 425, 686-691 (2003).

(8) T. López-Hernández, V. Haucke, T. Maritzen, Endocytosis in the adaptation to cellular stress. Cell Stress 4, 230-247 (2020).

Reviewer #2 (Public review):

Summary:

Feng, Jing-Xin et al. studied the hemogenic capacity of the endothelial cells in the adult mouse bone marrow. Using Cdh5-CreERT2 in vivo inducible system, though rare, they characterized a subset of endothelial cells expressing hematopoietic markers that were transplantable. They suggested that the endothelial cells need the support of stromal cells to acquire blood-forming capacity ex vivo. These endothelial cells were transplantable and contributed to hematopoiesis with ca. 1% chimerism in a stress hematopoiesis condition (5-FU) and recruited to the peritoneal cavity upon Thioglycolate treatment. Ultimately, the authors detailed the blood lineage generation of the adult endothelial cells in a single cell fashion, suggesting a predominant HSPCs-independent blood formation by adult bone marrow endothelial cells, in addition to the discovery of Col1a2+ endothelial cells with blood-forming potential, corresponding to their high Runx1 expressing property.

The conclusion regarding the characterization of hematopoietic-related endothelial cells in adult bone marrow is well supported by data. However, the paper would be more convincing, if the function of the endothelial cells were characterized more rigorously.

(1) Ex vivo culture of CD45-VE-Cadherin+ZsGreen EC cells generated CD45+ZsGreen+ hematopoietic cells. However, given that FACS sorting can never achieve 100% purity, there is a concern that hematopoietic cells might arise from the ones that got contaminated into the culture at the time of sorting. The sorting purity and time course analysis of ex vivo culture should be shown to exclude the possibility.

(2) Although it was mentioned in the text that the experimental mice survived up to 12 weeks after lethal irradiation and transplantation, the time-course kinetics of donor cell repopulation (>12 weeks) would add a precise and convincing evaluation. This would be absolutely needed as the chimerism kinetics can allow us to guess what repopulation they were (HSC versus progenitors). Moreover, data on either bone marrow chimerism assessing phenotypic LT-HSC and/or secondary transplantation would dramatically strengthen the manuscript.

(3) The conclusion by the authors, which says "Adult EHT is independent of pre-existing hematopoietic cell progenitors", is not fully supported by the experimental evidence provided (Figure 4 and Figure S3). More recipients with ZsGreen+ LSK must be tested.

Strengths:

The authors used multiple methods to characterize the blood-forming capacity of the genetically - and phenotypically - defined endothelial cells from several reporter mouse systems. The polylox barcoding method to trace the adult bone marrow endothelial cell contribution to hematopoiesis is a strong insight to estimate the lineage contribution.

Weaknesses:

It is unclear what the biological significance of the blood cells de novo generated from the adult bone marrow endothelial cells is. Moreover, since the frequency is very rare (<1% bone marrow and peripheral blood CD45+), more data regarding its identity (function, morphology, and markers) are needed to clearly exclude the possibility of contamination/mosaicism of the reporter mice system used.

Reviewer #1 (Public review):

Summary:

This manuscript by Feng et al. uses mouse models to study the embryonic origins of HSPCs. Using multiple types of genetic lineage tracing, the authors aimed to identify whether BM-resident endothelial cells retain hematopoietic capacity in adult organisms. Through an important mix of various labeling methodologies (and various controls), they reach the conclusion that BM endothelial cells contribute up to 3% of hematopoietic cells in young mice.

Strengths:

The major strength of the paper lies in the combination of various labeling strategies, including multiple Cdh5-CreER transgenic lines, different CreER lines (col1a2), and different reporters (ZsGreen, mTmG), including a barcoding-type reporter (PolyLox). This makes it highly unlikely that the results are driven by a rare artifact due to one random Cre line or one leaky reporter. The transplantation control (where the authors show no labeling of transplanted LSKs from the Cdh5 model) is also very supportive of their conclusions.

Weaknesses:

We believe that the work of ruling out alternative hypotheses, though initiated, was left incomplete. We specifically think that the authors need to properly consider whether there is specific, sparse labeling of HSPCs (in their native, non-transplant, model, in young animals). Polylox experiments, though an exciting addition, are also incomplete without additional controls. Some additional killer experiments are suggested.

eLife Assessment

The study proposed hemogenic endothelium in adult BM using lineage tracing. Though the study is potentially valuable, the data is incomplete due to the lack of control and insufficient analysis. There is potential for the study to be improved by further revision.

eLife Assessment

This important study demonstrates that paternal diet influences not only testicular morphology but also placental and fetal development, supporting a role for paternal contributions to offspring health. The authors combine transcriptomic and histological analyses across multiple tissues, and the evidence supporting the central conclusions is convincing. While aspects of the paternal gut phenotype remain largely descriptive, and the paternal and fetoplacental findings are discussed separately, clearer integration of these elements and additional methodological clarification would strengthen interpretation.

Reviewer #1 (Public review):

Summary:

Morgan et al. studied how paternal dietary alteration influenced testicular phenotype, placental and fetal growth using a mouse model of paternal low protein diet (LPD) or Western Diet (WD) feeding, with or without supplementation of methyl-donors and carriers (MD). They found diet- and sex-specific effects of paternal diet alteration. All experimental diets decreased paternal body weight and the number of spermatogonial stem cells, while fertility was unaffected. WD males (irrespective of MD) showed signs of adiposity and metabolic dysfunction, abnormal seminiferous tubules, and dysregulation of testicular genes related to chromatin homeostasis. Conversely, LPD induced abnormalities in the early placental cone, fetal growth restriction, and placental insufficiency, which were partly ameliorated by MD. The paternal diets changed the placental transcriptome in a sex-specific manner and led to a loss of sexual dimorphism in the placental transcriptome. These data provide a novel insight into how paternal health can affect the outcome of pregnancies, which is often overlooked in prenatal care.

Strengths:

The authors have performed a well-designed study using commonly used mouse models of paternal underfeeding (low protein) and overfeeding (Western diet). They performed comprehensive phenotyping at multiple timepoints, including the fathers, the early placenta, and the late gestation feto-placental unit. The inclusion of both testicular and placental morphological and transcriptomic analysis is a powerful, non-biased tool for such exploratory observational studies. The authors describe changes in testicular gene expression revolving around histone (methylation) pathways that are linked to altered offspring development (H3.3 and H3K4), which is in line with hypothesised paternal contributions to offspring health. The authors report sex differences in control placentas that mimic those in humans, providing potential for translatability of the findings. The exploration of sexual dimorphism (often overlooked) and its absence in response to dietary modification is novel and contributes to the evidence-base for the inclusion of both sexes in developmental studies.

Weaknesses:

The data are overall consistent with the conclusions of the authors. The paternal and pregnancy data are discussed separately, instead of linking the paternal phenotype to offspring outcomes. Some clarifications regarding the methods and the model would improve the interpretation of the findings.

(1) The authors insufficiently discuss their rationale for studying methyl-donors and carriers as micronutrient supplementation in their mouse model. The impact of the findings would be better disseminated if their role were explained in more detail.

(2) It is unclear from the methods exactly how long the male mice were kept on their respective diets at the time of mating and culling. Male mice were kept on the diet between 8 and 24 weeks before mating, which is a large window in which the males undergo a considerable change in body weight (Figure 1A). If males were mated at 8 weeks but phenotyped at 24 weeks, or if there were differences between groups, this complicates the interpretation of the findings and the extrapolation of the paternal phenotype to changes seen in the fetoplacental unit. The same applies to paternal age, which is an important known factor affecting male fertility and offspring outcomes.

(3) The male mice exhibited lower body weights when fed experimental diets compared to the control diet, even when placed on the hypercaloric Western Diet. As paternal body weight is an important contributor to offspring health, this is an important confounder that needs to be addressed. This may also have translational implications; in humans, consumption of a Western-style diet is often associated with weight gain. The cause of the weight discrepancy is also unaddressed. It is mentioned that the isocaloric LPD was fed ad libitum, while it is unclear whether the WD was also fed ad libitum, or whether males under- or over-ate on each experimental diet.

(4) The description and presentation of certain statistical analyses could be improved.

(i) It is unclear what statistical analysis has been performed on the time-course data in Figure 1A (if any). If one-way ANOVA was performed at each timepoint (as the methods and legend suggest), this is an inaccurate method to analyse time-course data.

(ii) It is unclear what methods were used to test the relative abundance of microbiome species at the family level (Figure 2L), whether correction was applied for multiple testing, and what the stars represent in the figure. 3) Mentioning whether siblings were used in any analyses would improve transparency, and if so, whether statistical correction needed to be applied to control for confounding by the father.

Reviewer #2 (Public review):

Summary:

The authors investigated the effects of a low-protein diet (LPD) and a high sugar- and fat-rich diet (Western diet, WD) on paternal metabolic and reproductive parameters and feto-placental development and gene expression. They did not observe significant effects on fertility; however, they reported gut microbiota dysbiosis, alterations in testicular morphology, and severe detrimental effects on spermatogenesis. In addition, they examined whether the adverse effects of these diets could be prevented by supplementation with methyl donors. Although LPD and WD showed limited negative effects on paternal reproductive health (with no impairment of reproductive success), the consequences on fetal and placental development were evident and, as reported in many previous studies, were sex-dependent.

Strengths:

This study is of high quality and addresses a research question of great global relevance, particularly in light of the growing concern regarding the exponential increase in metabolic disorders, such as obesity and diabetes, worldwide. The work highlights the importance of a balanced paternal diet in regulating the expression of metabolic genes in the offspring at both fetal and placental levels. The identification of genes involved in metabolic pathways that may influence offspring health after birth is highly valuable, strengthening the manuscript and emphasizing the need to further investigate long-term outcomes in adult offspring.

The histological analyses performed on paternal testes clearly demonstrate diet-induced damage. Moreover, although placental morphometric analyses and detailed histological assessments of the different placental zones did not reveal significant differences between groups, their inclusion is important. These results indicate that even in the absence of overt placental phenotypic changes, placental function may still be altered, with potential consequences for fetal programming.

Weaknesses:

Overall, this manuscript presents a rich and comprehensive dataset; however, this has resulted in the analysis of paternal gut dysbiosis remaining largely descriptive. While still valuable, this raises questions regarding why supplementation with methyl donors was unable to restore gut microbial balance in animals receiving the modified diets.

Author response:

Public Reviews: 

Reviewer #1 (Public review):

Summary:

Morgan et al. studied how paternal dietary alteration influenced testicular phenotype, placental and fetal growth using a mouse model of paternal low protein diet (LPD) or Western Diet (WD) feeding, with or without supplementation of methyl-donors and carriers (MD). They found diet- and sex-specific effects of paternal diet alteration. All experimental diets decreased paternal body weight and the number of spermatogonial stem cells, while fertility was unaffected. WD males (irrespective of MD) showed signs of adiposity and metabolic dysfunction, abnormal seminiferous tubules, and dysregulation of testicular genes related to chromatin homeostasis. Conversely, LPD induced abnormalities in the early placental cone, fetal growth restriction, and placental insufficiency, which were partly ameliorated by MD. The paternal diets changed the placental transcriptome in a sex-specific manner and led to a loss of sexual dimorphism in the placental transcriptome. These data provide a novel insight into how paternal health can affect the outcome of pregnancies, which is often overlooked in prenatal care.

Strengths:

The authors have performed a well-designed study using commonly used mouse models of paternal underfeeding (low protein) and overfeeding (Western diet). They performed comprehensive phenotyping at multiple timepoints, including the fathers, the early placenta, and the late gestation feto-placental unit. The inclusion of both testicular and placental morphological and transcriptomic analysis is a powerful, non-biased tool for such exploratory observational studies. The authors describe changes in testicular gene expression revolving around histone (methylation) pathways that are linked to altered offspring development (H3.3 and H3K4), which is in line with hypothesised paternal contributions to offspring health. The authors report sex differences in control placentas that mimic those in humans, providing potential for translatability of the findings. The exploration of sexual dimorphism (often overlooked) and its absence in response to dietary modification is novel and contributes to the evidence-base for the inclusion of both sexes in developmental studies.

Weaknesses:

The data are overall consistent with the conclusions of the authors. The paternal and pregnancy data are discussed separately, instead of linking the paternal phenotype to offspring outcomes. Some clarifications regarding the methods and the model would improve the interpretation of the findings.

(1) The authors insufficiently discuss their rationale for studying methyl-donors and carriers as micronutrient supplementation in their mouse model. The impact of the findings would be better disseminated if their role were explained in more detail.

We acknowledge the Reviewer’s comments regarding the amount of detail in support of the inclusion of methyl carriers and donors within our diet. Therefore, we will revise the manuscript to include more justification, especially within the Introduction section, for their inclusion.

(2) It is unclear from the methods exactly how long the male mice were kept on their respective diets at the time of mating and culling. Male mice were kept on the diet between 8 and 24 weeks before mating, which is a large window in which the males undergo a considerable change in body weight (Figure 1A). If males were mated at 8 weeks but phenotyped at 24 weeks, or if there were differences between groups, this complicates the interpretation of the findings and the extrapolation of the paternal phenotype to changes seen in the fetoplacental unit. The same applies to paternal age, which is an important known factor affecting male fertility and offspring outcomes.

We thank the Reviewer for their comments regarding the ages of the males analysed. We will provide more detailed descriptions of the males in our manuscript. However, all male ages were balanced across all groups.

(3) The male mice exhibited lower body weights when fed experimental diets compared to the control diet, even when placed on the hypercaloric Western Diet. As paternal body weight is an important contributor to offspring health, this is an important confounder that needs to be addressed. This may also have translational implications; in humans, consumption of a Western-style diet is often associated with weight gain. The cause of the weight discrepancy is also unaddressed. It is mentioned that the isocaloric LPD was fed ad libitum, while it is unclear whether the WD was also fed ad libitum, or whether males under- or over-ate on each experimental diet.

We agree with the Reviewer that the general trend towards a lighter body weight for our experimental animals is unexpected. We can confirm that all diets were fed ad libitum. However, as males were group housed, we were unable to measure food consumption for individual males. We also observed that for males fed the high fat diets, they often shredded significant quantities of their diet, rather than eating it, so preventing accurate measurement of food intake.

We also agree with the Reviewer that body weight can be a significant confounder for many paternal and offspring parameters. However, while the experimental males did become lighter, there were no statistical differences between groups in mean body weight. As such, body weight was not included as a variable within our statistical analysis.

(4) The description and presentation of certain statistical analyses could be improved.

(i) It is unclear what statistical analysis has been performed on the time-course data in Figure 1A (if any). If one-way ANOVA was performed at each timepoint (as the methods and legend suggest), this is an inaccurate method to analyse time-course data.

(ii) It is unclear what methods were used to test the relative abundance of microbiome species at the family level (Figure 2L), whether correction was applied for multiple testing, and what the stars represent in the figure. 3) Mentioning whether siblings were used in any analyses would improve transparency, and if so, whether statistical correction needed to be applied to control for confounding by the father.

We apologize for the lack of clarity regarding the statistical analyses. Going forward, we will revise the manuscript and include a more detailed description of the different analyses, the inclusion of siblings, and the correction for multiple testing.

Reviewer #2 (Public review):

Summary:

The authors investigated the effects of a low-protein diet (LPD) and a high sugar- and fat-rich diet (Western diet, WD) on paternal metabolic and reproductive parameters and fetoplacental development and gene expression. They did not observe significant effects on fertility; however, they reported gut microbiota dysbiosis, alterations in testicular morphology, and severe detrimental effects on spermatogenesis. In addition, they examined whether the adverse effects of these diets could be prevented by supplementation with methyl donors. Although LPD and WD showed limited negative effects on paternal reproductive health (with no impairment of reproductive success), the consequences on fetal and placental development were evident and, as reported in many previous studies, were sex-dependent.

Strengths:

This study is of high quality and addresses a research question of great global relevance, particularly in light of the growing concern regarding the exponential increase in metabolic disorders, such as obesity and diabetes, worldwide. The work highlights the importance of a balanced paternal diet in regulating the expression of metabolic genes in the offspring at both fetal and placental levels. The identification of genes involved in metabolic pathways that may influence offspring health after birth is highly valuable, strengthening the manuscript and emphasizing the need to further investigate long-term outcomes in adult offspring.

The histological analyses performed on paternal testes clearly demonstrate diet-induced damage. Moreover, although placental morphometric analyses and detailed histological assessments of the different placental zones did not reveal significant differences between groups, their inclusion is important. These results indicate that even in the absence of overt placental phenotypic changes, placental function may still be altered, with potential consequences for fetal programming.

Weaknesses:

Overall, this manuscript presents a rich and comprehensive dataset; however, this has resulted in the analysis of paternal gut dysbiosis remaining largely descriptive. While still valuable, this raises questions regarding why supplementation with methyl donors was unable to restore gut microbial balance in animals receiving the modified diets.

We thank the Reviewer for their considered thoughts on the gut dysbiosis induced in our models the minimal impact of the methyl donors and carriers. We will include additional text within the Discussion to acknowledge this. However, at this point in time, we are unsure as to why the methyl donors had minimal impact. It could be that the macronutrients (i.e. protein, fat, carbohydrates) have more of an influence on gut bacterial profiles than micronutrients. Alternatively, due to the prolonged nature of our feeding regimens, any initial influences of the methyl donors may become diluted out over time. We will amend the text to reflect these potential factors.

eLife Assessment

This valuable paper describes the regulation of the association of meiotic chromosome axis proteins on chromosome ends with sub-telomeric elements in budding yeast. The genome-wide analyses of binding of chromosome components as well as chromatin regulators, complemented with the mapping of meiotic DNA double-strand breaks on chromosome ends, provided incomplete evidence to support the authors' conclusion. The results in the paper are of interest to researchers in meiotic recombination and the structure of genomes and chromosomes.

Reviewer #1 (Public review):

Meiotic recombination at chromosome ends can be deleterious, and its initiation-the programmed formation of DSBs-has long been known to be suppressed. However, the underlying mechanisms of this suppression remained unclear. A bottleneck has been the repetitive sequences embedded within chromosome ends, which make them challenging to analyze using genomic approaches. The authors addressed this issue by developing a new computational pipeline that reliably maps ChIP-seq reads and other genomic data, enabling exploration of previously inaccessible yet biologically important regions of the genome.

In budding yeast, chromosome ends (~20 kb) show depletion of axis proteins (Red1 and Hop1) important for recruiting DSB-forming proteins. Using their newly developed pipeline, the authors reanalyzed previously published datasets and data generated in this study, revealing heretofore unseen details at chromosome ends. While axis proteins are depleted at chromosome ends, the meiotic cohesin component Rec8 is not. Y' elements play a crucial role in this suppression. The suppression does not depend on the physical chromosome ends but on cis-acting elements. Dot1 suppresses Red1 recruitment at chromosome ends but promotes it in interior regions. Sir complex renders subtelomeric chromatin inaccessible to the DSB-forming machinery.

The high-quality data and extensive analyses provide important insights into the mechanisms that suppress meiotic DSB formation at chromosome ends. To fully realise this value, several aspects of data presentation and interpretation should be clarified to ensure that the conclusions are stated with appropriate precision and that remaining future issues are clearly articulated.

(1) To assess the chromosome fusion effects on overall subtelomeric suppression, authors should guide how to look at the data presented in Figure 2b-c. Based on the authors' definition of the terminal 20 kb as the suppressed region, SK1 chrIV-R and S288c chrI-L would be affected by the chromosome fusion, if any. In addition, I find it somewhat challenging to draw clear conclusions from inspecting profiles to compare subtelomeric and internal regions. Perhaps, applying a quantitative approach - such as a bootstrap-based analysis similar to those presented earlier-would be easier to interpret.

(2) The relationship between coding density and Red1 signal needs clarification. An important conclusion from Figure 3 is that the subtelomeric depletion of Red1 primarily reflects suppression of the Rec8-dependent recruitment pathway, whereas Rec8-independent recruitment appears similar between ends and internal regions. Based on the authors' previous papers (referencess 13, 16), I thought coding (or nucleosome) density primarily influences the Rec8-independent pathway. However, the correlations presented in Figure 2d-e (also implied in Figure 3a) appear opposite to my expectation. Specifically, differences in axis protein binding between chromosome ends and internal regions (or within chromosome ends), where the Rec8-dependent pathway dominates, correlate with coding density. In contrast, no such correlation is evident in rec8Δ cells, where only the Rec8-independent pathway is active and end-specific depletion is absent. One possibility is that masking coding regions within Y' elements influences the correlation analysis. Additional analysis and a clearer explanation would be highly appreciated.

(3) The Dot1-Sir3 section staring from L266 should be clarified. I found this section particularly difficult to follow. It begins by stating that dot1∆ leads to Sir complex spreading, but then moves directly to an analysis of Red1 ChIP in sir3∆ without clearly articulating the underlying hypothesis. I wonder if this analysis is intended to explain the differences observed between dot1∆ and H3K79R mutants in the previous section. I also did not get the concluding statement - Dot1 counteracts Sir3 activity. As sir3Δ alone does not affect subtelomeric suppression, it is unclear what Dot1 counteracts. Perhaps, explicitly stating the authors' working model at the outset of this section would greatly clarify the rationale, results, and conclusions.

Reviewer #2 (Public review):

Summary:

In this manuscript, Raghavan and his colleagues sought to identify cis-acting elements and/or protein factors that limit meiotic crossover at chromosome ends. This is important for avoiding chromosome rearrangements and preventing chromosome missegregation.

By reanalyzing published ChIP datasets, the researchers identified a correlation between low levels of protein axis binding - which are known to modulate homologous recombination - and the presence of cis-acting elements such as the subtelomeric element Y' and low gene density. Genetic analyses coupled with ChIP experiments revealed that the differential binding of the Red1 protein in subtelomeric regions requires the methyltransferase Dot1. Interestingly, Red1 depletion in subtelomeric regions does not impact DSB formation. Another surprising finding is that deleting DOT1 has no effect on Red1 loading in the absence of the silencing factor Sir3. Unlike Dot1, Sir3 directly impacts DSB formation, probably by limiting promoter access to Spo11. However, this explains only a small part of the low levels of DSBs forming in subtelomeric regions.

Strengths:

(1) This work provides intriguing observations, such as the impact of Dot1 and Sir3 on Red1 loading and the uncoupling of Red1 loading and DSB induction in subtelomeric regions.

(2) The separation of axis protein deposition and DSB induction observed in the absence of Dot1 is interesting because it rules out the possibility that the binding pattern of these proteins is sufficient to explain the low level of DSB in subtelomeric regions.

(3) The demonstration that Sir3 suppresses the induction of DSBs by limiting the openness of promoters in subtelomeric regions is convincing.

Weaknesses:

(1) The impact of the cis-encoded signal is not demonstrated. Y' containing subtelomeres behave differently from X-only, but this is only correlative. No compelling manipulation has been performed to test the impact of these elements on protein axis recruitment or DSB formation.

(2) The mechanism by which Dot1 and Sir3 impact Red1 loading is missing.

(3) Sir3's impact on DSB induction is compelling, yet it only accounts for a small proportion of DSB depletion in subtelomeric regions. Thus, the main mechanisms suppressing crossover close to the ends of chromosomes remain to be deciphered.

Reviewer #3 (Public review):

Summary:

The paper by Raghavan et. al. describes pathways that suppress the formation of meiotic DNA double-strand breaks (DSBs) for interhomolog recombination at the end of chromosomes. Previously, the authors' group showed that meiotic DSB formation is suppressed in a ~20kb region of the telomeres in S. cerevisiae by suppressing the binding of meiosis-specific axis proteins such as Red1 and Hop1. In this study, by precise genome-wide analysis of binding sites of axis proteins, the authors showed that the binding of Red1 and Hop1 to sub-telomeric regions with X and Y' elements is dependent on Rec8 (cohesin) and/or Hop1's chromatin-binding region (CBR). Furthermore, Dot1 functions in a histone H3K79 trimethylation-independent manner, and the silencing proteins Sir2/3 also regulate the binding of Red1 and Hop1 and also the distribution of DSBs in sub-telomeres.

Strengths:

The experiments were conducted with high quality and included nice bioinformatic analyses, and the results were mostly convincing. The text is easy to read.

Weaknesses:

The paper did not provide any new mechanistic insights into how DSB formation is suppressed at sub-telomeres.

eLife Assessment

This important study reveals intriguing connections between chromosome breakage and DNA elimination during programmed genome rearrangement in the ciliate Tetrahymena thermophila. By developing a novel FISH approach that distinguishes germline and somatic telomeres, the authors provide compelling evidence that chromosome breakage removes germline telomeres along with hundreds of kilobases of germline-limited sequences. By disrupting a single chromosome breakage site, they further showed that DNA elimination was globally affected, which opens up a new direction for mechanistic studies. Thus, this work reveals additional similarity between the programmed DNA elimination in ciliates and nematodes that underlies the transition from germline to somatic telomeres.

Reviewer #1 (Public review):

Summary:

In this study, Nagao and Mochizuki examine the fate of germline chromosome ends during somatic genome differentiation in the ciliate Tetrahymena thermophila. During sexual reproduction, a new somatic genome is created from a zygotic, germline-derived genome by extensive programmed DNA elimination events. It has been known for some time that the termini of the germline chromosomes are eliminated, but the exact process and kinetics of the elimination events have not been thoroughly investigated. The authors first use germline-specific telomere probes to show that the loss of these chromosome ends occurs with similar timing as other DNA elimination events. By comparative analysis of the assembled germline and somatic genomes, the authors find that the ends of each of the germline chromosomes are composed of a few hundred kilobases of micronuclear limited sequences (MLS) that are removed starting around 14 hours after the start of conjugation, which initiates sexual development. They then develop an in situ hybridization assay to track the fate of one end of chromosome 4 while simultaneously following the adjacent macronuclear destined sequence (MDS) retained in the new somatic genome. This allows the authors to more clearly show that these adjacent chromosomal segments are initially amplified in the developing genome before the terminal MLS is eliminated. Finally, they mutate the chromosome breakage sequence (CBS) that normally separates the MLS terminus from the adjacent MDS region, to show that strains that develop with only one mutant chromosome can produce viable sexual progeny, but it appears that both the MLS and the MDS from the mutant chromosome are lost. If both chromosome copies have the CBS mutation, the cells arrest during development and do not eliminate many germline-limited sequences and fail to produce viable progeny. Overall, this study provides many new insights into the fate of germline chromosome ends during somatic genome remodeling and suggests extensive coordination of different DNA elimination events in Tetrahymena.

Strengths:

Overall, the experiments were well executed with appropriate controls. The findings are generally robust. Importantly, the study provides several novel findings. First, the authors provide a fairly comprehensive characterization of the size of the MLS at the end of each germline chromosome. I'm not sure whether this has been published elsewhere. Second, the authors develop a novel method to study the fate of chromosome termini during development and use it to conclusively track the elimination of these termini. Third, the authors show that the elimination of these termini appears to occur concurrently with most other DNA elimination events during somatic genome differentiation. And fourth, the authors show that failure to separate these eliminated sequences from the normally retained chromosome alters the fate of these adjacent MDS and the loss of the cells' ability to produce viable progeny.

Weaknesses:

It appears the authors did extensive analysis of the MLS chromosome ends, but did not provide too much information related to their composition. If this has not been published elsewhere, it would be useful to describe the proportion of unique and repetitive sequences and provide more information about the general composition of the chromosome ends. Such information would help the reader understand the nature of these MLS and how they may or may not differ from other eliminated sequences. Although the development of the novel FISH probes for large chromosome ends allowed for these novel discoveries, the signal in several images was visible, but often quite faint. I'm not sure there is anything the authors could do to improve the signal-to-noise ratio, but one needs to stare at the images carefully to understand the findings. One main weakness in the opinion of this reviewer is that the authors did very little to understand why, when a terminal MLS and the adjacent MDS fail to get separated because of failure in chromosome breakage, both segments are eliminated. The authors propose that possibly essential genes in the MDS get silenced, and the resulting lack of gene expression is the issue, but this and other possibilities were not tested. The study would provide more mechanistic insight if they had tried to assess whether the MDS on the CBS mutant chromosome becomes enriched in silencing modifications (e.g., H3K9me3). Alternatively, the authors could have examined changes in gene expression for some of the loci on the neighbouring MDS. The other main weakness is that since the authors only mutated the end of one germline chromosome, it is not clear whether the elimination of the MDS adjacent to the terminal MLS on chromosome 4 when the CBS is mutated is a general phenomenon, i.e., would happen at all chromosome ends, or is unique to the situation at Chromosome 4R. Knowing whether it is a general phenomenon or not would provide important insight into the authors' findings.

Reviewer #2 (Public review):

Summary:

Nagao and Mochizuki investigated how the germline (MIC) telomere was removed during programmed genome rearrangement in the developing somatic nucleus (MAC). Using an optimized oligo-FISH procedure, the authors demonstrated that MIC telomeres were co-eliminated with a large region of MIC-limited sequences (MLS) demarcated on the opposite side by a sub-telomeric chromosome breakage site (CBS). This conclusion was corroborated by the latest assembly of the Tetrahymena MIC genome. They further employed CRISPR-Cas9 mutagenesis to disrupt a specific sub-telomeric CBS (4R-CBS). In uniparental progeny (mutant X WT), DNA elimination of the sub-telomeric MLS was not affected, but the adjacent MAC-destined sequence (MDS) may be co-eliminated. However, in biparental progeny (mutant X mutant), global DNA elimination was arrested, revealing previously unrecognized connections between chromosome breakage and DNA elimination. It also paves the way for future studies into the underlying molecular mechanisms. The work is rigorous, well-controlled, and offers important insights into how eukaryotic genomes demarcate genic regions (retained DNA) and regions derived from transposable elements (TE; eliminated DNA) during differentiation. The identification of chromosome breakage sequences as barriers preventing the spread of silencing (and ultimately, DNA elimination) from TE-derived regions into functional somatic genes is a key conceptual contribution.

Strengths:

New method development: Oligo-FISH in Tetrahymena. This allows high-resolution visualization of critical genome rearrangement events during MIC-to-MAC differentiation. This method will be a very powerful tool in this area of study.

Integration of cytological and genomic data. The conclusion is strongly supported by both analyses.

Rigorous genetic analysis of the role played by 4R-CBS in separating the fate of sub-telomeric MLS (elimination) and MDS (retention). DNA elimination in ciliates has long been regarded as an extreme form of gene silencing. Now, chromosome breakage sequences can be viewed as an extreme form of gene insulators.

Weaknesses:

The finding of global disruption of DNA elimination in 4R-CBS mutant progeny is highly intriguing, but it's mostly presented as a hypothesis in the Discussion. The authors propose that the failure to separate MLS from MDS allows aberrant heterochromatin spreading from the former into the latter, potentially silencing genes required for DNA elimination itself. While supported by prior literature on heterochromatin feedback loops, the specific targets silenced are not identified. While results from ChIP-seq and small RNA-seq can greatly strengthen the paper, the reviewer understands that direct molecular characterization may be beyond the scope of the current work.

Reviewer #3 (Public review):

Programmed DNA elimination (PDE) is a process that removes a substantial amount of genomic DNA during development. While it contradicts the genome constancy rule, an increasing number of organisms have been found to undergo PDE, indicating its potential biological function. Single-cell ciliates have been used as a prominent model system for studying PDE, providing important mechanistic insights into this process. Many of those studies have focused on the excision of internally eliminated sequences (IES) and the subsequent repair using non-homologous end joining (NHEJ). These studies have led to the identification of small RNAs that mark retained or eliminated regions and the transposons that generate double-strand breaks.

In this manuscript, Nagao and Mochizuki examined the other type of breaks in ciliates that were healed with telomere addition. They specifically focused on the sequences at the ends of the germline (MIC) chromosomes, which have received relatively less attention due to the technical challenges associated with the highly repetitive nature of the sequences. The authors used the Tetrahymena model and developed a set of new tools. They used a novel FISH strategy that enables the distinction between germline and somatic telomeres, as well as the retained and eliminated DNA near the chromosome ends. This allows them to track these sequences at the cellular level throughout the development process, where PDE occurs. They also analyzed the more comprehensive germline and somatic genomes and determined at the sequence level the loss of subtelomeric and telomere sequences at all chromosome ends. Their result is reminiscent of the PDE observed in nematodes, where all germline chromosome ends are removed and remodeled. Thus, the finding connects two independent PDE systems, a protozoan and a metazoan, and suggests the convergent evolution of chromosome end removal and remodeling in PDE.

The majority of sites (8/10) at the junctions of retained and eliminated DNA at the chromosome ends contain a chromosome breakage sequence (CBS). The authors created a set of mutants that modify the CBS at the ends of chromosome 4R. CBS regions are challenging for CRISPR due to their AT-rich sequences, making the creation of the 4R-CBS mutants a significant breakthrough. They used the FISH assay to determine if PDE still occurs in these mutant strains with compromised CBS. Surprisingly, they found that instead of blocking PDE, its adjacent retained DNA is now eliminated, suggesting a co-elimination event when the breakage is impaired. Furthermore, in biparental mutant crosses, no PDE occurred, and no viable progeny were produced, indicating that the removal of chromosome ends is crucial for proper PDE and sexual progeny development. Overall, the work demonstrates a critical role for 4R-CBS in separating retained and eliminated DNA.

eLife Assessment

This important study presents new insights into the post-transcriptional mechanisms that govern cortical development. Through state-of-the-art methodology to track neuronal birth order, the data provide compelling evidence that Imp1 (Igf2bp1/Zbp1) orchestrates radial glia fate transitions and cortical neurogenesis. The findings establish a new framework for understanding how post-transcriptional mechanisms integrate with transcriptional and epigenetic regulatory layers to control cortical temporal patterning.

Reviewer #1 (Public review):

Summary:

A hallmark of cortical development is the temporal progression of lineage programs in radial glia progenitors (RGs) that orderly generate a large set of glutamatergic projection neuron types, which are deployed to the cortex in a largely inside-out sequence. This process is thought to contribute to the formation of proper cortical circuitry, but the underlying cellular and molecular mechanisms remain poorly understood. To a large extent, this is due to technical limitations that can fate map RGs and their progeny with cell type resolution, and manipulate gene expression with proper cell and temporal resolution. Building on the TEMPO technique that Tsumin Lee group developed, here Azur et al show that the RNA binding protein Imp1 functions as a dosage- and stage-dependent post-transcriptional mechanism that orchestrates developmental stage transitions in radial glial progenitors, and controls neuronal fate decisions and spatial organization of neuronal and glial cell progeny. Their results suggest that while transcriptional regulators define available cellular states and gate major transitions, post-transcriptional mechanisms like Imp1 provide an additional layer of control by modulating stage-specific transcript stability. Imp1 thus acts as a temporal coordinator whose dosage and timing determine whether developmental transitions are temporarily delayed or blocked. These findings establish a new framework for understanding how post-transcriptional mechanisms integrate with transcriptional and epigenetic regulatory layers to control cortical temporal patterning.

Strengths:

The authors apply a novel genetic fate mapping and gene manipulation technology (TEMPO) with cellular resolution. This reveals a dosage- and stage-dependent post-transcriptional mechanism that orchestrates developmental stage transitions in radial glial progenitors, and controls neuronal fate decisions and spatial organization of neuronal and glial cell/astrocyte progeny.

Weaknesses:

The endogenous developmental expression pattern of Imp1 and TEMPO-mediated overexpression are not well described or characterized with cellular resolution (whether only in radial glial cells or also in post-mitotic neurons). Thus, the interpretations of the overexpression phenotypes are not always clear.

Reviewer #2 (Public review):

Summary:

In this manuscript, Azur et al seek to determine the role of Imp1/Igf2bp1 in regulating the temporal generation of cortical neuron types. The authors showed that overexpression of Imp1 changes the laminar distribution of cortical neurons and suggest that Imp1 plays a temporal role in specifying cell fates.

Strengths:

The study uniquely used TEMPO to investigate the temporal effects of Imp1/Igf2bp1 in cortical development. The disrupted laminar distribution and delayed fate transition are interesting. The results are presented with proper quantification, they are generally well interpreted, and suggest important roles for Imp1.

Weaknesses:

(1) While the results suggest Imp1 is important in regulating cortical neurogenesis, it remains unclear when and where it is expressed to execute such temporal functions. For instance, where is Imp1 expressed in the developing brain? Is it specific to the radial glial cells or ubiquitous in progenitors and neurons? Does it show temporal expression in RGCs?

(2) The advantage and interpretation of TEMPO need further clarification. TEMPO is an interesting method and appears useful in simultaneously labelling cells and controlling gene expression. Since the reporter, Cas9, and gRNA triggers are all driven by ubiquitous promoters and integrated into the genome using piggyBac, it appears logical that the color transition should happen in all cells over time. The color code appears to track the time when the plasmids got integrated instead of the birthday of neurons. Is this logically true? If the TEMPO system is introduced into postmitotic neurons and the CAG promoter is not silenced, would the tri-color transition happen?

(3) The accumulation of neurons at the subplate region would benefit from showing larger views of the affected hemisphere. IUE is invasive. The glass pipette may consistently introduce focal damages and truncate RGCs. It is important to examine slices covering the whole IUE region.

Reviewer #3 (Public review):

Summary:

The work by Azur and colleagues makes use of the TEMPO (Temporal Encoding and Manipulation in a Predefined Order) methodology to trace cortical neurogenesis in combination with overexpression of Imp1. Imp1 is a mammalian homologue of the Drosophila Imp, which has been shown to control temporal identity in a stem cell context. In their work, they show that overexpression of Imp1 in radial glia, which generate neurons and macroglia in a sequential manner during cortical development, leads to a disruption of faithful neuron/glia generation. They show that continuous overexpression leads to a distinct phenotypic outcome when compared to paradigms where Imp1 was specifically overexpressed in defined temporal windows, enabled by the unique TEMPO approach. Interestingly, the observed phenotype with 'ectopic' generation of mainly lower cortical layer neurons appears not to be due to migration deficits. Strikingly, the overexpression of Imp1 specifically at later stages also leads to ectopic glia-like foci throughout the developing cortical plate. Altogether, the new data provide new insights regarding the role of the post-transcriptional Imp1 regulator in controlling temporal fate in radial glia for the faithful generation of neurons and glia during cortical development.

Strengths:

The TEMPO approach provides excellent experimental access to probe Imp1 gene function at defined temporal windows. The data is very robust and convincing. The overexpression paradigm and its associated phenotypes match very well the expected outcome based on Imp1 loss-of-function. Overall, the study contributes significantly to our understanding of the molecular cues that are associated with the temporal progression of radial glia fate potential during cortical development.

Weaknesses:

The authors provide some experimental evidence, including live imaging, that deficits related to Imp1 overexpression and subsequent overabundance of lower-layer neurons, or accumulation at the subplate, appear to evolve independently of neuronal migration deficits. However, the analysis at the population level might not suffice to make the claim robust. To analyze neuronal migration in more depth, the authors could trace individual neurons and establish speed and directional parameters for comparison.

In their analysis, the authors mainly rely on temporal parameters/criteria to associate the generation of certain neuron fates. While two markers were used to identify the neuronal fate, the variance seems quite high. The authors could consider utilizing an antibody against Satb2, which would provide additional data points that could help to establish statistical significance in some of the analyses.

The analysis of glia was done at postnatal day 10, although gliogenesis and, in particular, astrocyte maturation last at least until postnatal day 28. The authors could consider extending their analysis to capture the full spectrum of their astrocyte phenotype.

eLife Assessment

This is a well-executed intrathecal MRI tracer study that provides valuable early in vivo evidence for CSF drainage into human skull bone marrow and explores clinically relevant associations using robust imaging methodology and regional analyses. However, the evidence supporting the interpretation of early (4 h) tracer signal as impaired clearance is incomplete, and appears difficult to reconcile with established CSF tracer kinetics. They also note that the reported links to sleep and cognitive performance are weakened by reliance on subjective, retrospective questionnaires rather than objective physiological measurements.

Reviewer #1 (Public review):

Summary:

This manuscript examines the passage of an intrathecal CSF tracer into skull bone marrow, cortex, and venous compartments using serial MRI at multiple time points. The study builds on recent anatomical and imaging work suggesting direct communication between CSF spaces and bone marrow in the skull. It extends these observations to a larger, clinically heterogeneous human cohort. The imaging methodology is carefully executed, and the dataset is rich. The findings are potentially important for understanding CSF drainage pathways and their associations with inflammation, sleep quality, and cognition. However, key aspects of the interpretation - particularly regarding tracer kinetics and the definition of "clearance" - require clarification and, in my view, reconsideration.

Strengths:

(1) The study employs a well-established intrathecal contrast-enhanced MRI approach with multiple post-injection time points, enabling the assessment of regional tracer dynamics.

(2) The analysis of skull bone marrow in distinct anatomical regions (near the superior sagittal sinus, lateral fissure, and cisterna magna) is novel and informative.

(3) The cohort size is relatively large for an intrathecal tracer study in humans, and the authors make commendable efforts to relate imaging findings to clinical variables such as inflammation, sleep quality, and cognitive performance.

(4) The manuscript is clearly written, the figures are informative, and the discussion is well grounded in recent anatomical and experimental literature on skull-meningeal connections.

Weaknesses:

The central interpretation that a higher percentage increase in skull bone marrow tracer signal at 4.5 hours reflects reduced clearance is not convincingly justified. Based on the existing CSF tracer literature, the 4-6 hour time window is generally considered an enrichment or inflow phase rather than a clearance phase. Later time points (15 and 39 hours) are more likely to reflect clearance or washout. An alternative interpretation - that a higher signal at 4.5 hours reflects more pronounced tracer entry - should be considered and discussed.

Relatedly, the manuscript lacks a clear conceptual separation between tracer enrichment and clearance phases across time points. If 4.5 hours is intended to represent clearance, this assumption requires more vigorous justification and alignment with prior work.

CSF passage via the nasal/olfactory pathway is insufficiently discussed. Previous human imaging studies have questioned the importance of peri-olfactory CSF clearance, yet the present findings suggest delayed enrichment in the nasal turbinates. This discrepancy should be explicitly addressed, including a discussion of potential methodological limitations (e.g., timing of acquisitions, ROI definition, or sensitivity to slow drainage pathways).

More generally, given the descriptive nature of the study and the limited temporal sampling, some conclusions regarding directionality and efficiency of "drainage" may be overstated and would benefit from more cautious framing.

Reviewer #2 (Public review):

Summary

Zhou et al. utilize longitudinal, intrathecal contrast-enhanced MRI to investigate a novel physiological pathway: the drainage of cerebrospinal fluid (CSF) into the human skull bone marrow. By mapping tracer enrichment across 87 patients at multiple time points, the authors identify regional variations in drainage speed and link these dynamics to systemic factors like aging, hypertension, and diabetes. Most notably, the study suggests that this drainage function serves as a significant mediator between sleep quality and cognitive performance.

Strengths

(1) The study provides a significant transition from murine models to human subjects, showing that CSF-to-marrow communication is a broader phenomenon in clinical cohorts.

(2) The use of four imaging time points (0h to 39h) allows for a precise characterization of tracer kinetics, revealing that the parietal region near the superior sagittal sinus (SSS) is a rapid exit route.

(3) The statistical finding that skull bone marrow drainage accounts for approximately 38% of the link between sleep and cognition provides a provocative new target for neurodegenerative research.

Weaknesses

(1) Figure 1: The figure relies on a single representative brain to illustrate a process that likely varies significantly across different skull anatomies and disease states. In the provided grayscale MRI scans, the tracer enrichment is essentially imperceptible to the naked eye. Without heatmaps or digital subtraction maps (Post-injection minus Baseline) for the entire cohort, it is difficult to substantiate the quantitative "percentage change" data visually.

Reliance on a single, manually placed circular Region of Interest (ROI) is susceptible to sampling bias. A more robust approach would involve averaging multiple ROIs per region (multi-sampling) to ensure the signal is representative of the whole marrow compartment.

(2) Methodological Rigor of Sleep Analysis: The study relies exclusively on the self-reported Pittsburgh Sleep Quality Index (PSQI), which is retrospective and highly prone to recall bias, particularly in a cohort with cognitive impairment. There is no objective verification of sleep (e.g., actigraphy or polysomnography). Since waste clearance is physiologically tied to specific stages, such as Slow-Wave Sleep, subjective scores cannot determine whether drainage is linked to sleep physiology or reflects a higher general disease burden. The MRI captures an acute state during hospitalization, whereas the sleep quality reported covers the month preceding admission. This mismatch complicates the claim that the current drainage function directly reflects historical sleep quality.

Appraisal and Impact

The authors demonstrate the feasibility of monitoring CSF-to-skull marrow drainage in humans. However, the strength of the associations with sleep and cognition is currently attenuated by a lack of visual "proof" in the raw data and a reliance on subjective behavioral metrics. If these technical gaps are explicitly addressed through the use of population heatmaps and more rigorous multi-ROI sampling, this work will significantly advance our understanding of the brain's waste-clearance systems and their role in systemic health.

Reviewer #3 (Public review):

Summary:

In this study, the authors injected a contrast agent into patients and followed the induced signal change with MRI. Doing so, they observed cerebrospinal fluid (CSF) drainage whose magnitude and dynamics varied by anatomical location and scaled with a range of cognitive and socio-demographic metrics, including sleep scores and sex.

Strengths:

I would first like to stress that I am not a specialist in the topic of that paper; so my comments should be taken with a grain of salt, and feedback from the other reviewers should also be carefully considered.

I found the text concise and the figures straightforward to understand. Although they are manually defined, the authors compared drainage across different anatomical locations, which is a positive feature. Albeit purely correlative, the attempt to connect these otherwise 'peripheral' measures to cognitive variables is quite interesting. I also particularly liked the last paragraph of the discussion, which listed the main limitations of the study.

Weaknesses:

In the paragraph starting at line 446, the authors interpret poor sleep quality as being a cause and a consequence of impaired CSF clearance, but their approach is purely correlational. In other words, a third variable could be driving both of these parameters (correct?), thereby explaining their correlation. Later, they also proposed that therapeutically altering CSF clearance could improve cognitive symptoms, but, again, if there's a hidden cause of the correlation, that does not seem like a valid possibility. I believe there were other instances of this sort of inferential problem in the Discussion. It seems essential, particularly in clinical research, to precisely identify what the available evidence supports (correlation) and what is speculation (causation).

Assuming I did not miss it, the approach for testing and reporting correlations is not specified. In particular, the authors report correlation with CSF drainage and a variety of other metrics. But how many tests did the authors perform? They solely mention that they used the Benjamini-Hochberg method to correct for multiple comparisons. How were the decisions to test for this or that effect determined? Or did they test all the metrics they had? Also, that particular correction method is limited when statistics are negatively correlated. It would be helpful to validate findings with another approach.

I assume many of the metrics the authors use are also correlated with one another. Is it possible that a single principal component is driving the different correlations they see? Performing dimensionality reduction across available metrics and relating the resulting principal components to CSF drainage would help clarify the forces at play here.

In their interpretations, the authors claim that the CSF drainage they observe occurs through the bone marrow of the skull. How confident can we be in that claim? Is it that there are no other likely possibilities? It might be an unnecessary question, but given there seems to be no causal intervention (which is fine), and no consideration of alternatives, I am wondering whether this is because other possibilities are improbable or whether they were not adequately considered.

eLife Assessment

This valuable work describes a computational and experimental workflow that turns a moderately stable α-helical bundle into a very stable fold. The authors advance our understanding of α-helix stabilization and provide a convenient framework with implications for the protein design field. The main claims are supported by convincing evidence through sound and well-validated methods, yet further characterization would strengthen specific conclusions for the design of mechanically, thermally, and chemically stable α-helical bundles.

Reviewer #1 (Public review):

Summary:

In the work from Qiu et al., a workflow aimed at obtaining the stabilization of a simple small protein against mechanical and chemical stressors is presented.

Strengths:

The workflow makes use of state-of-the-art AI-driven structure generation and couples it with more classical computational and experimental characterizations in order to measure its efficacy. The work is well presented, and the results are thorough and convincing.

Weaknesses:

I will comment mostly on the MD results due to my expertise.

The Methods description is quite precise, but is missing some important details:

(1) Version of GROMACS used.

(2) The barostat used.

(3) pH at which the system is simulated.

(4) The pulling is quite fast (but maybe it is not a problem)

(5) What was the value for the harmonic restraint potential? 1000 is mentioned for the pulling potential, but it is not clear if the same value is used for the restraint, too, during pulling.

(6) The box dimensions.

From this last point, a possible criticism arises: Do the unfolded proteins really still stay far enough away from themselves to not influence the result? This might not be the major influence, but for correctness, I would indicate the dimensions of the box in all directions and plot the minimum distance of the protein from copies of itself across the boundary conditions over time.

Additionally, no time series are shown for the equilibration phases (e.g., RMSD evolution over time), which would empower the reader to judge the equilibration of the system before either steered MD or annealing MD is performed.

Reviewer #2 (Public review):

Summary:

Qiu, Jun et. al., developed and validated a computational pipeline aimed at stabilizing α-helical bundles into very stable folds. The computational pipeline is a hierarchical computational methodology tasked to generate and filter a pool of candidates, ultimately producing a manageable number of high-confidence candidates for experimental evaluation. The pipeline is split into two stages. In stage I, a large pool of candidate designs is generated by RFdiffusion and ProteinMPNN, filtered down by a series of filters (hydropathy score, foldability assessed by ESMFold and AlphaFold). The final set is chosen by running a series of steered MD simulations. This stage reached unfolding forces above 100pN. In stage II, targeted tweaks are introduced - such as salt bridges and metal ion coordination - to further enhance the stability of the α-helical bundle. The constructs undergo validation through a series of biophysical experiments. Thermal stability is assessed by CD, chemical stability by chemical denaturation, and mechanical stability by AFM.

Strengths:

A hierarchical computational approach that begins with high-throughput generation of candidates, followed by a series of filters based on specific goal-oriented constraints, is a powerful approach for a rapid exploration of the sequence space. This type of approach breaks down the multi-objective optimization into manageable chunks and has been successfully applied for protein design purposes (e.g., the design of protein binders). Here, the authors nicely demonstrate how this design strategy can be applied to successfully redesign a moderately stable α-helical bundle into an ultrastable fold. This approach is highly modular, allowing the filtering methods to be easily swapped based on the specific optimization goals or the desired level of filtering.

Weaknesses:

Assessing the change in stability relative to the WT α-helical bundle is challenging because an additional helix has been introduced, resulting in a comparison between a three-helix bundle and a four-helix bundle. Consequently, the appropriate reference point for comparison is unclear. A more direct and informative approach would have been to redesign the original α-helical bundle of the human spectrin repeat R15, allowing for a more straightforward stability comparison.

While the authors have shown experimentally that stage II constructs have increased the mechanical stability by AFM, they did not show that these same constructs have increased the thermal and chemical stabilities. Since the effects of salt bridges on stability are highly context dependent (orientation, local environment, exposed vs buried, etc.), it is difficult to assess the magnitude of the effect that this change had on other types of stabilities.

The three constructs chosen are 60-70% identical to each other, either suggesting overconstrained optimization of the sequence or a physical constraint inherent to designing ultrastable α-helical bundles. It would be interesting to explore these possible design principles further.

While the use of steered MD is an elegant approach to picking the top N most stable designs, its computational cost may become prohibitive as the number of designs increases or as the protein size grows, especially since it requires simulating a water box that can accommodate a fully denatured protein.

Reviewer #3 (Public review):

Summary:

Qiu et al. present a hierarchical framework that combines AI and molecular dynamics simulation to design an α-helical protein with enhanced thermal, chemical, and mechanical stability. Strategically, chemical modification by incorporating additional α-helix, site-specific salt bridges, and metal coordination further enhanced the stability. The experimental validation using single-molecule force spectroscopy and CD melting measurements provides fundamental physical chemical insights into the stabilization of α-helices. Together with the group's prior work on super-stable β strands (https://www.nature.com/articles/s41557-025-01998-3), this research provides a comprehensive toolkit for protein stabilization. This framework has broad implications for designing stable proteins capable of functioning under extreme conditions.

Strengths:

The study represents a complete framework for stabilizing the fundamental protein elements, α-helices. A key strength of this work is the integration of AI tools with chemical knowledge of protein stability.<br /> The experimental validation in this study is exceptional. The single-molecule AFM analysis provided a high-resolution look at the energy landscape of these designed scaffolds. This approach allows for the direct observation of mechanical unfolding forces (exceeding 200 pN) and the precise contribution of individual chemical modifications to global stability. These measurements offer new, fundamental insights into the physicochemical principles that govern α-helix stabilization.

Weaknesses:

(1) The authors report that appending an additional helix increases the overcall stability of the α-helical protein. Could the author provide a more detailed structural explanation for this? Why does the mechanical stability increase as the number of helixes increase? Is there a reported correlation between the number of helices (or the extent of the hydrophobic core) and the stability?

(2) The author analyzed both thermal stability and mechanical stability. It would be helpful for the author to discuss the relationship between these two parameters in the context of their design. Since thermal melting probes equilibrium stability (ΔG), while mechanical stability probes the unfolding energy barriers along the pulling coordinate.

(3) While the current study demonstrates a dramatic increase in global stability, the analysis focuses almost exclusively on the unfolding (melting) process. However, thermodynamic stability is a function of both folding (kf) and unfolding (ku) rates. It remains unclear whether the observed ultrastability is primarily driven by a drastic decrease in the unfolding rate (ku) or if the design also maintains or improves the folding rate (kf)?

(4) The authors chose the spectrin repeat R15 as the starting scaffold for their design. R15 is a well-established model known for its "ultra-fast" folding kinetics, with folding rates (kf ~105s), near three orders of magnitude faster than its homologues like R17 (Scott et.al., Journal of molecular biology 344.1 (2004): 195-205). Does the newly designed protein, with its additional fourth helix and site-specific chemical modifications, retain the exceptionally high folding rate of the parent R15?

eLife Assessment

This study provides valuable findings on how the activity of the E3 ubiquitin ligase Highwire (Hiw/Phr1) is regulated and its impact on synaptic growth. The authors propose that impaired endocytosis leads to condensation of Hiw, resulting in increased synaptic growth. They also integrate such a mechanism within the known JNK (c-JUN N-terminal Kinase) and BMP (Bone Morphogenetic Protein) signalling pathways involved in synapse regulation. While the work raises an interesting mechanistic framework, several aspects of the experimental design and methodology are incomplete, and key conclusions, particularly those regarding the liquid-liquid phase separation of the E3 ubiquitin ligase, are not fully supported by the presented data.

Joint Public Review:

Pippadpally et al. investigate how the conserved E3 ubiquitin ligase Highwire (Hiw/Phr1), a well-established negative regulator of synaptic growth, is functionally and spatially regulated. Using a GFP-tagged Hiw transgene in Drosophila, the authors report that disruption of endocytosis via loss of AP-2, synaptojanin, or Rab11-mediated recycling endosome function leads to accumulation of Hiw in neuronal cell bodies as enlarged foci, altogether accompanied by synaptic overgrowth. Provided that the Hiw foci are sensitive to aliphatic alcohol treatment, the authors propose that impaired endocytosis promotes liquid-liquid phase separation of the E3 ubiquitin ligase, reducing its ability to degrade the MAPKKK Wallenda and thereby activating JNK signalling. Crosstalk with BMP signalling and roles for autophagy are also explored within this framework.

Strengths

The work provides a novel tool, the GFP-tagged Hiw transgene, to study the spatio-temporal regulation of the E3 ubiquitin ligase Highwire (Hiw/Phr1) in Drosophila, and its impact on synaptic growth. The results presented point to a potentially thought-provoking connection between endocytic defects, Hiw condensation, Hiw down-regulation and synaptic overgrowth. The specific effects of the endocytic mutants on the redistribution of the Hiw to the neuronal cell body and the genetic interactions between the endocytosis and JNK pathway mutants are convincing.

Weaknesses

Several conclusions are insufficiently supported at this point. For example, evidence that the Hiw foci represent bona fide liquid-liquid phase (LLP) separated condensates is limited. Sensitivity to 1,6-hexanediol is not definitive proof of their liquid condensate nature, and their recovery kinetics after 1,6-hexanediol wash-out and their morphology are inconsistent with a pure liquid behaviour. Furthermore, the claim that the Hiw foci are non-vesicular is not strongly supported, as it is only based on the lack of colocalization with a handful of endosomal proteins.

Importantly, the appearance of the putative condensates is correlative rather than causative for synaptic overgrowth, and in the absence of a mechanistic link between endocytosis and Hiw condensation, the causality is difficult to address. Of note is that the putative condensates are already present (albeit to a lesser extent) in the absence of endocytic defects and that the conclusions rely heavily on overexpressed GFP-Hiw, which may perturb normal protein behaviour and artificially induce condensation or aggregation.

The use of hypomorphic mutants in genetic experiments also introduces some ambiguity in their interpretation, as the results may reflect dosage effects from multiple pathways rather than pathway order. Finally, the manuscript would benefit from a more comprehensive reference to relevant literature on JNKKKs and BMP signalling, as well as on the recycling endosome function in synaptic growth and the regulation of the aforementioned pathways.

Overall, while the work presents thought-provoking observations and a potentially interesting regulatory model, additional experimental rigor and broader contextualization are needed to substantiate the proposed mechanism and its biological relevance.

Author response:

Weaknesses:

(1) Several conclusions are insufficiently supported at this point. For example, evidence that the Hiw foci represent bona fide liquid-liquid phase (LLP) separated condensates is limited. Sensitivity to 1,6-hexanediol is not definitive proof of their liquid condensate nature, and their recovery kinetics after 1,6-hexanediol wash-out and their morphology are inconsistent with a pure liquid behaviour. Furthermore, the claim that the Hiw foci are non-vesicular is not strongly supported, as it is only based on the lack of colocalization with a handful of endosomal proteins.

We agree that, at the current stage of the manuscript, we have presented data only on Hiw foci in the VNC and shown that they are sensitive to 1,6-HD but not to 2,5-HD. To further provide definitive proof that these are bona fide condensates, we will now perform in vitro analysis of different domains of Hiw and the Hiw IDR region. In addition, we will also investigate the Hiw-GFP behavior in non-neuronal and transiently transfected cell lines using FRAP and other protocols previously applied to condensate-forming proteins.

Finally, we will perform an in-depth analysis of the Hiw condensates for their colocalization with endocytic proteins and cellular compartments and determine whether they are part of any known vesicular structures.

(2) Importantly, the appearance of the putative condensates is correlative rather than causative for synaptic overgrowth, and in the absence of a mechanistic link between endocytosis and Hiw condensation, the causality is difficult to address. Of note is that the putative condensates are already present (albeit to a lesser extent) in the absence of endocytic defects and that the conclusions rely heavily on overexpressed GFP-Hiw, which may perturb normal protein behaviour and artificially induce condensation or aggregation.

To investigate the formation of condensates and their relation to synaptic growth, we will perform a time-course analysis of changes at the NMJ and correlate with the Hiw condensate appearance in the VNC of shi^ts expressing GFP-Hiw, along with appropriate controls. The GFP transgene used is a functional transgene and well established for studying Hiw behaviour. The Hiw condensates do not form when expressed on an otherwise wild-type background. We will further assess the formation of Hiw condensates in other endocytic mutants with appropriate controls.

(3) The use of hypomorphic mutants in genetic experiments also introduces some ambiguity in their interpretation, as the results may reflect dosage effects from multiple pathways rather than pathway order. Finally, the manuscript would benefit from a more comprehensive reference to relevant literature on JNKKKs and BMP signalling, as well as on the recycling endosome function in synaptic growth and the regulation of the aforementioned pathways.

We will perform genetic analysis using homozygous mutants of the wit and saxophone genes to further support epistatic interactions between the BMP signaling pathway and synaptic growth. We will strengthen the discussion part.

eLife Assessment

The authors use sequencing of nascent DNA (DNA linked to an RNA primer, “SNS-Seq”) to localise DNA replication origins in Trypanosoma brucei, so this work will be of interest to those studying either Kinetoplastids or DNA replication. The paper presents the SNS-seq results for only part of the genome, and there are significant discrepancies between the SNS-Seq results and those from other, previously-published results obtained using other origin mapping methods. The reasons for the differences are unknown and from the data available, it is not possible to assess which origin-mapping method is most suitable for origin mapping in T. brucei. Thus at present, the evidence that origins are distributed as the authors claim - and not where previously mapped - is inadequate.

Reviewer #1 (Public review):

In this paper, Stanojcic and colleagues attempt to map sites of DNA replication initiation in the genome of the African trypanosome, Trypanosoma brucei. Their approach to this mapping is to isolate 'short-nascent strands' (SNSs), a strategy adopted previously in other eukaryotes (including in the related parasite Leishmania major), which involves isolation of DNA molecules whose termini contain replication-priming RNA. By mapping the isolated and sequenced SNSs to the genome (SNS-seq), the authors suggest that they have identified origins, which they localise to intergenic (strictly, inter-CDS) regions within polycistronic transcription units and suggest display very extensive overlap with previously mapped R-loops in the same loci. Finally, having defined locations of SNS-seq mapping, they suggest they have identified G4 and nucleosome features of origins, again using previously generated data. Though there is merit in applying a new approach to understand DNA replication initiation in T. brucei, where previous work has used MFA-seq and ChIP of a subunit of the Origin Replication Complex (ORC), there are two significant deficiencies in the study that must be addressed to ensure rigour and accuracy.

(1) The suggestion that the SNS-seq data is mapping DNA replication origins that are present in inter-CDS regions of the polycistronic transcription units of T. brucei is novel and does not agree with existing data on the localisation of ORC1/CDC6, and it is very unclear if it agrees with previous mapping of DNA replication by MFA-seq due to the way the authors have presented this correlation. For these reasons, the findings essentially rely on a single experimental approach, which must be further tested to ensure SNS-seq is truly detecting origins. Indeed, in this regard, the very extensive overlap of SNS-seq signal with RNA-DNA hybrids should be tested further to rule out the possibility that the approach is mapping these structures and not origins.

(2) The authors' presentation of their SNS-seq data is too limited and therefore potentially provides a misleading view of DNA replication in the genome of T. brucei. The work is presented through a narrow focus on SNS-seq signal in the inter-CDS regions within polycistronic transcription units, which constitute only part of the genome, ignoring both the transcription start and stop sites at the ends of the units and the large subtelomeres, which are mainly transcriptionally silent. The authors must present a fuller and more balanced view of SNS-seq mapping across the whole genome to ensure full understanding and clarity.

Reviewer #2 (Public review):

Summary:

Stanojcic et al. investigate the origins of DNA replication in the unicellular parasite Trypanosoma brucei. They perform two experiments, stranded SNS-seq and DNA molecular combing. Further, they integrate various publicly available datasets, such as G4-seq and DRIP-seq, into their extensive analysis. Using this data, they elucidate the structure of the origins of replication. In particular, they find various properties located at or around origins, such as polynucleotide stretches, G-quadruplex structures, regions of low and high nucleosome occupancy, R-loops, and that origins are mostly present in intergenic regions. Combining their population-level SNS-seq and their single-molecule DNA molecular combing data, they elucidate the total number of origins as well as the number of origins active in a single cell.

Strengths:

(1) A very strong part of this manuscript is that the authors integrate several other datasets and investigate a large number of properties around origins of replication. Data analysis clearly shows the enrichment of various properties at the origins, and the manuscript concludes with a very well-presented model that clearly explains the authors' understanding and interpretation of the data.

(2) The DNA combing experiment is an excellent orthogonal approach to the SNS-seq data. The authors used the different properties of the two experiments (one giving location information, one giving single-molecule information) well to extract information and contrast the experiments.

(3) The discussion is exemplary, as the authors openly discuss the strengths and weaknesses of the approaches used. Further, the discussion serves its purpose of putting the results in both an evolutionary and a trypanosome-focused context.

Weaknesses:

I have major concerns about the origin of replication sites determined from the SNS-seq data. As a caveat, I want to state that, before reading this manuscript, SNS-seq was unknown to me; hence, some of my concerns might be misplaced.

(1) I do not understand why SNS-seq would create peaks. Replication should originate in one locus, then move outward in both directions until the replication fork moving outward from another origin is encountered. Hence, in an asynchronous population average measurement, I would expect SNS data to be broad regions of + and -, which, taken together, cover the whole genome. Why are there so many regions not covered at all by reads, and why are there such narrow peaks?

(2) I am concerned that up to 96% percent of all peaks are filtered away. If there is so much noise in the data, how can one be sure that the peaks that remain are real? Specifically, if the authors placed the same number of peaks as was measured randomly in intergenic regions, would 4% of these peaks pass the filtering process by chance?

(3) There are 3 previous studies that map origins of replication in T. brucei. Devlin et al. 2016, Tiengwe et al. 2012, and Krasiļņikova et al. 2025 (https://doi.org/10.1038/s41467-025-56087-3), all with a different technique: MFA-seq. All three previous studies mostly agree on the locations and number of origins. The authors compared their results to the first two, but not the last study; they found that their results are vastly different from the previous studies (see Supplementary Figure 8A). In their discussion, the authors defend this discrepancy mostly by stating that the discrepancy between these methods has been observed in other organisms. I believe that, given the situation that the other studies precede this manuscript, it is the authors' duty to investigate the differences more than by merely pointing to other organisms. A conclusion should be reached on why the results are different, e.g., by orthogonally validating origins absent in the previous studies.

(4) Some patterns that were identified to be associated with origins of replication, such as G-quadruplexes and nucleosomes phasing, are known to be biases of SNS-seq (see Foulk et al. Characterizing and controlling intrinsic biases of lambda exonuclease in nascent strand sequencing reveals phasing between nucleosomes and G-quadruplex motifs around a subset of human replication origins. Genome Res. 2015;25(5):725-735. doi:10.1101/gr.183848.114).

Are the claims well substantiated?:

My opinion on whether the authors' results support their conclusions depends on whether my concerns about the sites determined from the SNS-seq data can be dismissed. In the case that these concerns can be dismissed, I do think that the claims are compelling.

Impact:

If the origins of replication prove to be distributed as claimed, this study has the potential to be important for two fields. Firstly, in research focused on T. brucei as a disease agent, where essential processes that function differently than in mammals are excellent drug targets. Secondly, this study would impact basic research analyzing DNA replication over the evolutionary tree, where T. brucei can be used as an early-divergent eukaryotic model organism.

Author response:

eLife Assessment

The authors use sequencing of nascent DNA (DNA linked to an RNA primer, "SNS-Seq") to localise DNA replication origins in Trypanosoma brucei, so this work will be of interest to those studying either Kinetoplastids or DNA replication. The paper presents the SNS-seq results for only part of the genome, and there are significant discrepancies between the SNS-Seq results and those from other, previously-published results obtained using other origin mapping methods. The reasons for the differences are unknown and from the data available, it is not possible to assess which origin-mapping method is most suitable for origin mapping in T. brucei. Thus at present, the evidence that origins are distributed as the authors claim - and not where previously mapped - is inadequate.

We would like to clarify a few points regarding our study. Our primary objective was to characterise the topology and genome-wide distribution of short nascent-strand (SNS) enrichments. The stranded SNS-seq approach provides the high strand-specific resolution required to analyse origins. The observation that SNS-seq peaks (potential origins) are most frequently found in intergenic regions is not an artefact of analysing only part of the genome; rather, it is a result of analysing the entire genome.

We agree that orthogonal validation is necessary. However, neither MFA-seq nor TbORC1/CDC6 ChIP-on-chip has yet been experimentally validated as definitive markers of origin activity in T. brucei, nor do they validate each other. 

Public Reviews:

Reviewer #1 (Public review):

In this paper, Stanojcic and colleagues attempt to map sites of DNA replication initiation in the genome of the African trypanosome, Trypanosoma brucei. Their approach to this mapping is to isolate 'short-nascent strands' (SNSs), a strategy adopted previously in other eukaryotes (including in the related parasite Leishmania major), which involves isolation of DNA molecules whose termini contain replication-priming RNA. By mapping the isolated and sequenced SNSs to the genome (SNS-seq), the authors suggest that they have identified origins, which they localise to intergenic (strictly, inter-CDS) regions within polycistronic transcription units and suggest display very extensive overlap with previously mapped R-loops in the same loci. Finally, having defined locations of SNS-seq mapping, they suggest they have identified G4 and nucleosome features of origins, again using previously generated data.

Though there is merit in applying a new approach to understand DNA replication initiation in T. brucei, where previous work has used MFA-seq and ChIP of a subunit of the Origin Replication Complex (ORC), there are two significant deficiencies in the study that must be addressed to ensure rigour and accuracy.

(1) The suggestion that the SNS-seq data is mapping DNA replication origins that are present in inter-CDS regions of the polycistronic transcription units of T. brucei is novel and does not agree with existing data on the localisation of ORC1/CDC6, and it is very unclear if it agrees with previous mapping of DNA replication by MFA-seq due to the way the authors have presented this correlation. For these reasons, the findings essentially rely on a single experimental approach, which must be further tested to ensure SNS-seq is truly detecting origins. Indeed, in this regard, the very extensive overlap of SNS-seq signal with RNA-DNA hybrids should be tested further to rule out the possibility that the approach is mapping these structures and not origins.

(2) The authors' presentation of their SNS-seq data is too limited and therefore potentially provides a misleading view of DNA replication in the genome of T. brucei. The work is presented through a narrow focus on SNS-seq signal in the inter-CDS regions within polycistronic transcription units, which constitute only part of the genome, ignoring both the transcription start and stop sites at the ends of the units and the large subtelomeres, which are mainly transcriptionally silent. The authors must present a fuller and more balanced view of SNS-seq mapping across the whole genome to ensure full understanding and clarity.

Regarding comparisons with previous work:

Two other attempts to identify origins in T. brucei —ORC1/CDC6 binding sites (ChIP-on-chip, PMID: 22840408) and MFA-seq (PMID: 22840408, 27228154)—were both produced by the McCulloch group. These methods do not validate each other; in fact, MFA-seq origins overlap with only 4.4% of the 953 ORC1/CDC6 sites (PMID: 29491738). Therefore, low overlap between SNS-seq peaks and ORC1/CDC6 sites cannot disqualify our findings. Similar low overlaps are observed in other parasites (PMID: 38441981, PMID: 38038269, PMID: 36808528) and in human cells (PMID: 38567819).

We also would like to emphasize that the ORC1/CDC6 dataset originally published (PMID: 22840408) is no longer available; only a re-analysis by TritrypDB exists, which differs significantly from the published version (personal communication from Richard McCulloch). While the McCulloch group reported a predominant localization of ORC1/CDC6 sites within SSRs at transcription start and termination regions, our re-analysis indicates that only 10.3% of TbORC1/CDC6-12Myc sites overlapped with 41.8% of SSRs.

MFA-seq does not map individual origins, it rather detects replicated genomic regions by comparing DNA copy number between S- and G1-phases of the cell cycle (PMID: 36640769; PMID: 37469113; PMID: 36455525). The broad replicated regions (0.1–0.5 Mbp) identified by MFA-seq in T. brucei are likely to contain multiple origins, rather than just one. In that sense we disagree with the McCulloch's group who claimed that there is a single origin per broad peak. Our analysis shows that up to 50% of the origins detected by stranded SNS-seq locate within broad MFA-seq regions. The methodology used by McCulloch’s group to infer single origins from MFA-seq regions has not been published or made available, as well as the precise position of these regions, making direct comparison difficult.

Finally, the genomic features we describe—poly(dA/dT) stretches, G4 structures and nucleosome occupancy patterns—are consistent with origin topology described in other organisms.

On the concern that SNS-seq may map RNA-DNA hybrids rather than replication origins: Isolation and sequencing of short nascent strands (SNS) is a well-established and widely used technique for high-resolution origin mapping. This technique has been employed for decades in various laboratories, with numerous publications documenting its use. We followed the published protocol for SNS isolation (Cayrou et al., Methods, 2012, PMID: 22796403). RNA-DNA hybrids cannot persist through the multiple denaturation steps in our workflow, as they melt at 95°C (Roberts and Crothers, Science, 1992; PMID: 1279808). Even in the unlikely event that some hybrids remained, they would not be incorporated into libraries prepared using a single-stranded DNA protocol and therefore would not be sequenced (see Figure 1B and Methods).

Furthermore, our analysis shows that only a small proportion (1.7%) of previously reported RNA-DNA hybrids overlap with SNS-seq origins. It is important to note that RNA-primed nascent strands naturally form RNA-DNA hybrids during replication initiation, meaning the enrichment of RNA-DNA hybrids near origins is both expected and biologically relevant.

On the claim that our analysis focuses narrowly on inter-CDS regions and ignores other genomic compartments: this is incorrect. We mapped and analyzed stranded SNS-seq data across the entire genome of T. brucei 427 wild-type strain (Müller et al., Nature, 2018; PMID: 30333624), including both core and subtelomeric regions. Our findings indicate that most origins are located in intergenic regions, but all analyses were performed using the full set of detected origins, regardless of location.

We did not ignore transcription start and stop sites (TSS/TTS). The manuscript already includes origin distribution across genomic compartments as defined by TriTrypDB (Fig. 2C) and addresses overlap with TSS, TTS and HT in the section “Spatial coordination between the activity of the origin and transcription”. While this overlap is minimal, we have included metaplots in the revised manuscript for clarity.

Reviewer #2 (Public review):

Summary: 

Stanojcic et al. investigate the origins of DNA replication in the unicellular parasite Trypanosoma brucei. They perform two experiments, stranded SNS-seq and DNA molecular combing. Further, they integrate various publicly available datasets, such as G4-seq and DRIP-seq, into their extensive analysis. Using this data, they elucidate the structure of the origins of replication. In particular, they find various properties located at or around origins, such as polynucleotide stretches, G-quadruplex structures, regions of low and high nucleosome occupancy, R-loops, and that origins are mostly present in intergenic regions. Combining their population-level SNS-seq and their single-molecule DNA molecular combing data, they elucidate the total number of origins as well as the number of origins active in a single cell.

Strengths:

(1) A very strong part of this manuscript is that the authors integrate several other datasets and investigate a large number of properties around origins of replication. Data analysis clearly shows the enrichment of various properties at the origins, and the manuscript concludes with a very well-presented model that clearly explains the authors' understanding and interpretation of the data.

We sincerely thank you for this positive feedback.

(2) The DNA combing experiment is an excellent orthogonal approach to the SNS-seq data. The authors used the different properties of the two experiments (one giving location information, one giving single-molecule information) well to extract information and contrast the experiments.

Thank you very much for this remark.

(3) The discussion is exemplary, as the authors openly discuss the strengths and weaknesses of the approaches used. Further, the discussion serves its purpose of putting the results in both an evolutionary and a trypanosome-focused context.

Thank you for appreciating our discussion.

Weaknesses:

I have major concerns about the origin of replication sites determined from the SNS-seq data. As a caveat, I want to state that, before reading this manuscript, SNS-seq was unknown to me; hence, some of my concerns might be misplaced.

(1) I do not understand why SNS-seq would create peaks. Replication should originate in one locus, then move outward in both directions until the replication fork moving outward from another origin is encountered. Hence, in an asynchronous population average measurement, I would expect SNS data to be broad regions of + and -, which, taken together, cover the whole genome. Why are there so many regions not covered at all by reads, and why are there such narrow peaks?

Thank you for asking these questions. As you correctly point out, replication forks progress in both directions from their origins and ultimately converge at termination sites. However, the SNS-seq method specifically isolates short nascent strands (SNSs) of 0.5–2.5 kb using a sucrose gradient. These short fragments are generated immediately after origin firing and mark the sites of replication initiation, rather than the entire replicated regions. Consequently: (i) SNS-seq does not capture long replication forks or termination regions, only the immediate vicinity of origins. (ii) The narrow peaks indicate the size of selected SNSs (0.5–2.5 kb) and the fact that many cells initiate replication at the same genomic sites, leading to localized enrichment. (iii) Regions without coverage refer to genomic areas that do not serve as efficient origins in the analyzed cell population. Thus, SNS-seq is designed to map origin positions, but not the entire replicated regions.

(2) I am concerned that up to 96% percent of all peaks are filtered away. If there is so much noise in the data, how can one be sure that the peaks that remain are real? Specifically, if the authors placed the same number of peaks as was measured randomly in intergenic regions, would 4% of these peaks pass the filtering process by chance?

Maintaining the strandness of the sequenced DNA fibres enabled us to filter the peaks, thereby increasing the probability that the filtered peak pairs corresponded to origins. Two SNS peaks must be oriented in a way that reflects the topology of the SNS strands within an active origin: the upstream peak must be on the minus strand and followed by the downstream peak on the plus strand.

As suggested by the reviewer, we tested whether randomly placed plus and minus peaks could reproduce the number of filter-passing peaks using the same bioinformatics workflow. Only 1–6% of random peaks passed the filters, compared with 4–12% in our experimental data, resulting in about 50% fewer selected regions (origins). Moreover, the “origins” from random peaks showed 0% reproducibility across replicates, whereas the experimental data showed 7–64% reproducibility. These results indicate that the retainee peaks are highly unlikely to arise by chance and support the specificity of our approach. Thank you for this suggestion.

(3) There are 3 previous studies that map origins of replication in T. brucei. Devlin et al. 2016, Tiengwe et al. 2012, and Krasiļņikova et al. 2025 (https://doi.org/10.1038/s41467-025-56087-3), all with a different technique: MFA-seq. All three previous studies mostly agree on the locations and number of origins. The authors compared their results to the first two, but not the last study; they found that their results are vastly different from the previous studies (see Supplementary Figure 8A). In their discussion, the authors defend this discrepancy mostly by stating that the discrepancy between these methods has been observed in other organisms. I believe that, given the situation that the other studies precede this manuscript, it is the authors' duty to investigate the differences more than by merely pointing to other organisms. A conclusion should be reached on why the results are different, e.g., by orthogonally validating origins absent in the previous studies.

The MFA-seq data for T. brucei were published in two studies by McCulloch’s group: Tiengwe et al. (2012) using TREU927 PCF cells, and Devlin et al. (2016) using PCF and BSF Lister427 cells. In Krasilnikova et al. (2025), previously published MFA-seq data from Devlin et al. were remapped to a new genome assembly without generating new MFA-seq data, which explains why we did not include that comparison.

Clarifying the differences between MFA-seq and our stranded SNS-seq data is essential. MFA-seq and SNS-seq interrogate different aspects of replication. SNS-seq is a widely used, high-resolution method for mapping individual replication origins, whereas MFA-seq detects replicated regions by comparing DNA copy number between S and G1 phases. MFA-seq identified broad replicated regions (0.1–0.5 Mb) that were interpreted by McCulloch’s group as containing a single origin. We disagree with this interpretation and consider that there are multiple origins in each broad peaks; theoretical considerations of replication timing indicate that far more origins are required for complete genome duplication during the short S-phase. Once this assumption is reconsidered, MFA-seq and SNS-seq results become complementary: MFA-seq identifies replicated regions, while SNS-seq pinpoints individual origins within those regions. Our analysis revealed that up to 50% of the origins detected by stranded SNS-seq were located within the broad MFA peaks. This pattern—broad MFA-seq regions containing multiple initiation sites—has also recently been found in Leishmania by McCulloch’s team using nanopore sequencing (PMID: 26481451). Nanopore sequencing showed numerous initiation sites within MFA-seq regions and additional numerous sites outside these regions in asynchronous cells, consistent with what we observed using stranded SNS-seq in T. brucei. We will expand our discussion and conclude that the discrepancy arises from methodological differences and interpretation. The two approaches provide complementary insights into replication dynamics, rather than ‘vastly different’ results.

We recognize the importance of validating our results in future using an alternative mapping method and functional assays. However, it is important to emphasize that stranded SNS-seq is an origin mapping technique with a very high level of resolution. This technique can detect regions between two divergent SNS peaks, which should represent regions of DNA replication initiation. At present, no alternative technique has been developed that can match this level of resolution.

(4) Some patterns that were identified to be associated with origins of replication, such as G-quadruplexes and nucleosomes phasing, are known to be biases of SNS-seq (see Foulk et al. Characterizing and controlling intrinsic biases of lambda exonuclease in nascent strand sequencing reveals phasing between nucleosomes and G-quadruplex motifs around a subset of human replication origins. Genome Res. 2015;25(5):725-735. doi:10.1101/gr.183848.114).

It is important to note that the conditions used in our study differ significantly from those applied in the Foulk et al. Genome Res. 2015. We used SNS isolation and enzymatic treatments as described in previous reports (Cayrou, C. et al. Genome Res, 2015 and Cayrou, C et al. Methods, 2012). Here, we enriched the SNS by size on a sucrose gradient and then treated this SNS-enriched fraction with high amounts of repeated λ-exonuclease treatments (100u for 16h at 37oC - see Methods). In contrast, Foulk et al. used sonicated total genomic DNA for origin mapping, without enrichment of SNS on a sucrose gradient as we did, and then they performed a λ-exonuclease treatment. A previous study (Cayrou, C. et al. Genome Res, 2015, Figure S2, which can be found at https://genome.cshlp.org/content/25/12/1873/suppl/DC1) has shown that complete digestion of G4-rich DNA sequences is achieved under the conditions we used.

Furthermore, the SNS depleted control (without RNA) was included in our experimental approach. This control represents all molecules that are difficult to digest with lambda exonuclease, including G4 structures. Peak calling was performed against this background control, with the aim of removing false positive peaks resulting from undigested DNA structures. We explained better this step in the revised manuscript.

The key benefit of our study is that the orientation of the enrichments (peaks) remains consistent throughout the sequencing process. We identified an enrichment of two divergent strands synthesised on complementary strands containing G4s. These two divergent strands themselves do not, however, contain G4s (see Fig. 8 for the model). Therefore, the enriched molecules detected in our study do not contain G4s. They are complementary to the strands enriched with G4s. This means that the observed enrichment of

G4s cannot be an artefact of the enzymatic treatments used in this study. We added this part in the discussion of the revised manuscript.

We also performed an additional control which is not mentioned in the manuscript. In parallel with replicating cells, we isolated the DNA from the stationary phase of growth, which primarily contains non-replicating cells. Following the three λ-exonuclease treatments, there was insufficient DNA remaining from the stationary phase cells to prepare the libraries for sequencing. This control strongly indicated that there was little to no contaminating DNA present with the SNS molecules after λ-exonuclease enrichment.

eLife Assessment

This study offers valuable insights into how humans detect and adapt to regime shifts, highlighting dissociable contributions of the frontoparietal network and ventromedial prefrontal cortex to sensitivity to signal diagnosticity and transition probabilities. The combination of an innovative instructed-probability task, Bayesian behavioural modeling, and model-based fMRI analyses provides a solid foundation for the main claims; however, major interpretational limitations remain, particularly a potential confound between posterior switch probability and time in the neuroimaging results. At the behavioural level, reliance on explicitly instructed conditional probabilities leaves open alternative explanations that complicate attribution to a single computational mechanism, such that clearer disambiguation between competing accounts and stronger control of temporal and representational confounds would further strengthen the evidence.

Reviewer #1 (Public review):

Summary:

The study examines human biases in a regime-change task, in which participants have to report the probability of a regime change in the face of noisy data. The behavioral results indicate that humans display systematic biases, in particular, overreaction in stable but noisy environments and underreaction in volatile settings with more certain signals. fMRI results suggest that a frontoparietal brain network is selectively involved in representing subjective sensitivity to noise, while the vmPFC selectively represents sensitivity to the rate of change.

Strengths:

The study relies on a task that measures regime-change detection primarily based on descriptive information about the noisiness and rate of change. This distinguishes the study from prior work using reversal-learning or change-point tasks in which participants are required to learn these parameters from experiences. The authors discuss these differences comprehensively.

The study uses a simple Bayes-optimal model combined with model fitting, which seems to describe the data well. The model is comprehensively validated.

The authors apply model-based fMRI analyses that provide a close link to behavioral results, offering an elegant way to examine individual biases.

Weaknesses:

The authors have adequately addressed my prior concerns.

Reviewer #3 (Public review):

This study concerns how observers (human participants) detect changes in the statistics of their environment, termed regime shifts. To make this concrete, a series of 10 balls are drawn from an urn that contains mainly red or mainly blue balls. If there is a regime shift, the urn is changed over (from mainly red to mainly blue) at some point in the 10 trials. Participants report their belief that there has been a regime shift as a % probability. Their judgement should (mathematically) depend on the prior probability of a regime shift (which is set at one of three levels) and the strength of evidence (also one of three levels, operationalized as the proportion of red balls in the mostly-blue urn and vice versa). Participants are directly instructed of the prior probability of regime shift and proportion of red balls, which are presented on-screen as numerical probabilities. The task therefore differs from most previous work on this question in that probabilities are instructed rather than learned by observation, and beliefs are reported as numerical probabilities rather than being inferred from participants' choice behaviour (as in many bandit tasks, such as Behrens 2007 Nature Neurosci).

The key behavioural finding is that participants over-estimate the prior probability of regime change when it is low, and under estimate it when it is high; and participants over-estimate the strength of evidence when it is low and under-estimate it when it is high. In other words participants make much less distinction between the different generative environments than an optimal observer would. This is termed 'system neglect'. A neuroeconomic-style mathematical model is presented and fit to data.

Functional MRI results how that strength of evidence for a regime shift (roughly, the surprise associated with a blue ball from an apparently red urn) is associated with activity in the frontal-parietal orienting network. Meanwhile at time-points where the probability of a regime shift is high, there is activity in another network including vmPFC. Both networks show individual differences effects, such that people who were more sensitive to strength of evidence and prior probability show more activity in the frontal-parietal and vmPFC-linked networks respectively.

Strengths

(1) The study provides a different task for looking at change-detection and how this depends on estimates of environmental volatility and sensory evidence strength, in which participants are directly and precisely informed of the environmental volatility and sensory evidence strength rather than inferring them through observation as in most previous studies

(2) Participants directly provide belief estimates as probabilities rather than experimenters inferring them from choice behaviour as in most previous studies

(3) The results are consistent with well-established findings that surprising sensory events activate the frontal-parietal orienting network whilst updating of beliefs about the word ('regime shift') activates vmPFC.

Weaknesses

(1) The use of numerical probabilities (both to describe the environments to participants, and for participants to report their beliefs) may be problematic because people are notoriously bad at interpreting probabilities presented in this way, and show poor ability to reason with this information (see Kahneman's classic work on probabilistic reasoning, and how it can be improved by using natural frequencies). Therefore the fact that, in the present study, people do not fully use this information, or use it inaccurately, may reflect the mode of information delivery.

In the response to this comment the authors have pointed out their own previous work showing that system neglect can occur even when numerical probabilities are not used. This is reassuring but there remains a large body of classic work showing that observers do struggle with conditional probabilities of the type presented in the task.

(2) Although a very precise model of 'system neglect' is presented, many other models could fit the data.

For example, you would get similar effects due to attraction of parameter estimates towards a global mean - essentially application of a hyper-prior in which the parameters applied by each participant in each block are attracted towards the experiment-wise mean values of these parameters. For example, the prior probability of regime shift ground-truth values [0.01, 0.05, 0.10] are mapped to subjective values of [0.037, 0.052, 0.069]; this would occur if observers apply a hyper-prior that the probability of regime shift is about 0.05 (the average value over all blocks). This 'attraction to the mean' is a well-established phenomenon and cannot be ruled out with the current data (I suppose you could rule it out by comparing to another dataset in which the mean ground-truth value was different).

More generally, any model in which participants don't fully use the numerical information they were given would produce apparent 'system neglect'. Four qualitatively different example reasons are: 1. Some individual participants completely ignored the probability values given. 2. Participants did not ignore the probability values given, but combined them with a hyperprior as above. 3. Participants had a reporting bias where their reported beliefs that a regime-change had occurred tend to be shifted towards 50% (rather than reporting 'confident' values such 5% or 95%). 4. Participants underweighted probability outliers, resulting in underweighting of evidence in the 'high signal diagnosticity' environment (10.1016/j.neuron.2014.01.020 )

In summary I agree that any model that fits the data would have to capture the idea that participants don't differentiate between the different environments as much as they should, but I think there are a number of qualitatively different reasons why they might do this - of which the above are only examples - hence I find it problematic that the authors present the behaviour as evidence for one extremely specific model.

(3) Despite efforts to control confounds in the fMRI study, including two control experiments, I think some confounds remain.

For example, a network of regions is presented as correlating with the cumulative probability that there has been a regime shift in this block of 10 samples (Pt). However, regardless of the exact samples shown, Pt always increases with sample number (as by the time of later samples, there have been more opportunities for a regime shift)? To control for this the authors include, in a supplementary analysis, an 'intertemporal prior.' I would have preferred to see the results of this better-controlled analysis presented in the main figure. From the tables in the SI it is very difficult to tell how the results change with the includion of the control regressors.

On the other hand, two additional fMRI experiments are done as control experiments and the effect of Pt in the main study is compared to Pt in these control experiments. Whilst I admire the effort in carrying out control studies, I can't understand how these particular experiment are useful controls. For example, in experiment 3 participants simply type in numbers presented on the screen - how can we even have an estimate of Pt from this task?

(4) The Discussion is very long, and whilst a lot of related literature is cited, I found it hard to pin down within the discussion, what the key contributions of this study are. In my opinion it would be better to have a short but incisive discussion highlighting the advances in understanding that arise from the current study, rather than reviewing the field so broadly.

Author response:

The following is the authors’ response to the current reviews

eLife Assessment

This study offers valuable insights into how humans detect and adapt to regime shifts, highlighting dissociable contributions of the frontoparietal network and ventromedial prefrontal cortex to sensitivity to signal diagnosticity and transition probabilities. The combination of an innovative instructed-probability task, Bayesian behavioural modeling, and model-based fMRI analyses provides a solid foundation for the main claims; however, major interpretational limitations remain, particularly a potential confound between posterior switch probability and time in the neuroimaging results. At the behavioural level, reliance on explicitly instructed conditional probabilities leaves open alternative explanations that complicate attribution to a single computational mechanism, such that clearer disambiguation between competing accounts and stronger control of temporal and representational confounds would further strengthen the evidence.

Thank you. In this revision, we will focus on addressing Reviewer 3’s concern on the potential confound between posterior probability and time in neuroimaging results. First, we will present whole-brain results of subjects’ probability estimates (their subjective posterior probability of switch) after controlling for the effect of time on probability of switch (the intertemporal prior). Second, we will compare the effect of probability estimates (Pt) on vmPFC and ventral striatum activity—which we found to correlate with Pt—with and without including intertemporal prior in the GLM. Third, to address Reviewer 3’s comment that from the Tables of activation in the supplement vmPFC and ventral striatum cannot be located, we will add slice-by-slice image of the whole-brain results on Pt in the Supplemental Information in addition to the Tables of Activation.

Public Reviews:

Reviewer #1 (Public review):<br /> Summary:

The study examines human biases in a regime-change task, in which participants have to report the probability of a regime change in the face of noisy data. The behavioral results indicate that humans display systematic biases, in particular, overreaction in stable but noisy environments and underreaction in volatile settings with more certain signals. fMRI results suggest that a frontoparietal brain network is selectively involved in representing subjective sensitivity to noise, while the vmPFC selectively represents sensitivity to the rate of change.

Strengths:

The study relies on a task that measures regime-change detection primarily based on descriptive information about the noisiness and rate of change. This distinguishes the study from prior work using reversal-learning or change-point tasks in which participants are required to learn these parameters from experiences. The authors discuss these differences comprehensively.

The study uses a simple Bayes-optimal model combined with model fitting, which seems to describe the data well. The model is comprehensively validated.

The authors apply model-based fMRI analyses that provide a close link to behavioral results, offering an elegant way to examine individual biases.

Weaknesses:

The authors have adequately addressed my prior concerns.

Thank you for reviewing our paper and providing constructive comments that helped us improve our paper.

Reviewer #3 (Public review):

Thank you again for reviewing the manuscript. In this revision, we will focus on addressing your concern on the potential confound between posterior probability and time in neuroimaging results. First, we will present whole-brain results of subjects’ probability estimates (Pt, their subjective posterior probability of switch) after controlling for the effect of time on probability of switch (the intertemporal prior). Second, we will compare the effect of probability estimates (Pt) on vmPFC and ventral striatum activity—which we found to correlate with Pt—with and without including intertemporal prior in the GLM. These results will be summarized in a new figure (Figure 4).

Finally, to address that you were not able to locate vmPFC and ventral striatum from the Tables of activation, we will add slice-by-slice image of the whole-brain results on Pt in the supplement in addition to the Tables of Activation.

This study concerns how observers (human participants) detect changes in the statistics of their environment, termed regime shifts. To make this concrete, a series of 10 balls are drawn from an urn that contains mainly red or mainly blue balls. If there is a regime shift, the urn is changed over (from mainly red to mainly blue) at some point in the 10 trials. Participants report their belief that there has been a regime shift as a % probability. Their judgement should (mathematically) depend on the prior probability of a regime shift (which is set at one of three levels) and the strength of evidence (also one of three levels, operationalized as the proportion of red balls in the mostly-blue urn and vice versa). Participants are directly instructed of the prior probability of regime shift and proportion of red balls, which are presented on-screen as numerical probabilities. The task therefore differs from most previous work on this question in that probabilities are instructed rather than learned by observation, and beliefs are reported as numerical probabilities rather than being inferred from participants' choice behaviour (as in many bandit tasks, such as Behrens 2007 Nature Neurosci).

The key behavioural finding is that participants over-estimate the prior probability of regime change when it is low, and under estimate it when it is high; and participants over-estimate the strength of evidence when it is low and under-estimate it when it is high. In other words participants make much less distinction between the different generative environments than an optimal observer would. This is termed 'system neglect'. A neuroeconomic-style mathematical model is presented and fit to data.

Functional MRI results how that strength of evidence for a regime shift (roughly, the surprise associated with a blue ball from an apparently red urn) is associated with activity in the frontal-parietal orienting network. Meanwhile at time-points where the probability of a regime shift is high, there is activity in another network including vmPFC. Both networks show individual differences effects, such that people who were more sensitive to strength of evidence and prior probability show more activity in the frontal-parietal and vmPFC-linked networks respectively.

Strengths

(1) The study provides a different task for looking at change-detection and how this depends on estimates of environmental volatility and sensory evidence strength, in which participants are directly and precisely informed of the environmental volatility and sensory evidence strength rather than inferring them through observation as in most previous studies

(2) Participants directly provide belief estimates as probabilities rather than experimenters inferring them from choice behaviour as in most previous studies

(3) The results are consistent with well-established findings that surprising sensory events activate the frontal-parietal orienting network whilst updating of beliefs about the word ('regime shift') activates vmPFC.

Weaknesses

(1) The use of numerical probabilities (both to describe the environments to participants, and for participants to report their beliefs) may be problematic because people are notoriously bad at interpreting probabilities presented in this way, and show poor ability to reason with this information (see Kahneman's classic work on probabilistic reasoning, and how it can be improved by using natural frequencies). Therefore the fact that, in the present study, people do not fully use this information, or use it inaccurately, may reflect the mode of information delivery.

In the response to this comment the authors have pointed out their own previous work showing that system neglect can occur even when numerical probabilities are not used. This is reassuring but there remains a large body of classic work showing that observers do struggle with conditional probabilities of the type presented in the task.

Thank you. Yes, people do struggle with conditional probabilities in many studies. However, as our previous work suggested (Massey and Wu, 2005), system-neglect was likely not due to response mode (having to enter probability estimates or making binary predictions, and etc.).

(2) Although a very precise model of 'system neglect' is presented, many other models could fit the data.

For example, you would get similar effects due to attraction of parameter estimates towards a global mean - essentially application of a hyper-prior in which the parameters applied by each participant in each block are attracted towards the experiment-wise mean values of these parameters. For example, the prior probability of regime shift ground-truth values [0.01, 0.05, 0.10] are mapped to subjective values of [0.037, 0.052, 0.069]; this would occur if observers apply a hyper-prior that the probability of regime shift is about 0.05 (the average value over all blocks). This 'attraction to the mean' is a well-established phenomenon and cannot be ruled out with the current data (I suppose you could rule it out by comparing to another dataset in which the mean ground-truth value was different).

We thank the reviewer for this comment. We do not disagree that there are alternative models that can describe over- and underreactions seen in the dataset. However, we do wish to point out that since we began with the normative Bayesian model, the natural progression in case the normative model fails to capture data is to modify the starting model. It is under this context that we developed the system-neglect model. It was a simple extension (a parameterized version) of the normative Bayesian model.

Regarding the hyperprior idea, even if the participants have a hyperprior, there has to be some function that describes/implements attraction to the mean. Having a hyperprior itself does not imply attraction to this hyperprior. We therefore were not sure why the hyperprior itself can produce attraction to the mean.

We do look further into the possibility of attraction to the mean. First, as suggested by the reviewer, we looked into another dataset with different mean ground-truth value. In Massey and Wu (2005), the transition probabilities were [0.02 0.05 0.1 0.2], which is different from the current study [0.01 0.05 0.1], and there they also found over- and underreactions as well. Second, we reason that for the attraction to the mean idea to work subjects need to know the mean of the system parameters. This would take time to develop because we did not tell subjects about the mean. If this is caused by attraction to the mean, subjects’ behavior would be different in the early stage of the experiment where they had little idea about the mean, compared with the late stage of the experiment where they knew about the mean. We will further analyze and compare participants’ data at the beginning of the experiment with data at the end of the experiment.

More generally, any model in which participants don't fully use the numerical information they were given would produce apparent 'system neglect'. Four qualitatively different example reasons are: 1. Some individual participants completely ignored the probability values given. 2. Participants did not ignore the probability values given, but combined them with a hyperprior as above. 3. Participants had a reporting bias where their reported beliefs that a regime-change had occurred tend to be shifted towards 50% (rather than reporting 'confident' values such 5% or 95%). 4. Participants underweighted probability outliers, resulting in underweighting of evidence in the 'high signal diagnosticity' environment (10.1016/j.neuron.2014.01.020 )

We thank the reviewer for pointing out these potential explanations. Again, we do not disagree that any model in which participants don’t fully use numerical information they were given would produce system neglect. It is hard to separate ‘not fully using numerical information’ from ‘lack of sensitivity to the numerical information’. We will respond in more details to the four example reasons later.

In summary I agree that any model that fits the data would have to capture the idea that participants don't differentiate between the different environments as much as they should, but I think there are a number of qualitatively different reasons why they might do this - of which the above are only examples - hence I find it problematic that the authors present the behaviour as evidence for one extremely specific model.

Again, we do not disagree with the reviewer on the modeling statement. However, we also wish to point out that the system-neglect model we had is a simple extension of the normative Bayesian model. Had we gone to a non-Bayesian framework, we would have faced the criticism of why we simply do not consider a simple extension of the starting model. In response, we will add a section in Discussion summarizing our exchange on this matter.

(3) Despite efforts to control confounds in the fMRI study, including two control experiments, I think some confounds remain.

For example, a network of regions is presented as correlating with the cumulative probability that there has been a regime shift in this block of 10 samples (Pt). However, regardless of the exact samples shown, Pt always increases with sample number (as by the time of later samples, there have been more opportunities for a regime shift)? To control for this the authors include, in a supplementary analysis, an 'intertemporal prior.' I would have preferred to see the results of this better-controlled analysis presented in the main figure. From the tables in the SI it is very difficult to tell how the results change with the includion of the control regressors.

Thank you. In response, we will add a new figure, now Figure 4, showing the results of Pt and delta Pt from GLM-2 where we added the intertemporal prior as a regressor to control for temporal confounds. We compared Pt and delta Pt results in vmPFC and ventral striatum between GLM-1 and GLM-2. We also will show the results of intertemporal prior on vmPFC and ventral striatum under GLM-2.

On the other hand, two additional fMRI experiments are done as control experiments and the effect of Pt in the main study is compared to Pt in these control experiments. Whilst I admire the effort in carrying out control studies, I can't understand how these particular experiment are useful controls. For example, in experiment 3 participants simply type in numbers presented on the screen - how can we even have an estimate of Pt from this task?

We thank the reviewer for this comment. On the one hand, the effect of Pt we see in brain activity can be simply due to motor confounds and the purpose of Experiment 3 was to control for them. Our question was, if subjects saw the similar visual layout and were just instructed to press buttons to indicate two-digit numbers, would we observe the vmPFC, ventral striatum, and the frontoparietal network like what we did in the main experiment (Experiment 1)?

On the other hand, the effect of Pt can simply reflect probability estimates of that the current regime is the blue regime, and therefore not particularly about change detection. In Experiment 2, we tested that idea, namely whether what we found about Pt was unique to change detection. In Experiment 2, subjects estimated the probability that the current regime is the blue regime (just as they did in Experiment 1) except that there were no regime shifts involved. In other words, it is possible that the regions we identified were generally associated with probability estimation and not particularly about probability estimates of change. We used Experiment 2 to examine whether this were true.

To make the purpose of the two control experiments clearer, we updated the paragraph describing the control experiments on page 9:

“To establish the neural representations for regime-shift estimation, we performed three fMRI experiments ( subjects for each experiment, 90 subjects in total). Experiment 1 was the main experiment, while Experiments 2 to 3 were control experiments that ruled out two important confounds (Fig. 1E). The control experiments were designed to clarify whether any effect of subjects’ probability estimates of a regime shift, , in brain activity can be uniquely attributed to change detection. Here we considered two major confounds that can contribute to the effect of . First, since subjects in Experiment 1 made judgments about the probability that the current regime is the blue regime (which corresponded to probability of regime change), the effect of  did not particularly have to do with change detection. To address this issue, in Experiment 2 subjects made exactly the same judgments as in Experiment 1 except that the environments were stationary (no transition from one regime to another was possible), as in Edwards (1968) classic “bookbag-and-poker chip” studies. Subjects in both experiments had to estimate the probability that the current regime is the blue regime, but this estimation corresponded to the estimates of regime change only in Experiment 1. Therefore, activity that correlated with probability estimates in Experiment 1 but not in Experiment 2 can be uniquely attributed to representing regime-shift judgments. Second, the effect of  can be due to motor preparation and/or execution, as subjects in Experiment 1 entered two-digit numbers with button presses to indicate their probability estimates. To address this issue, in Experiment 3 subjects performed a task where they were presented with two-digit numbers and were instructed to enter the numbers with button presses. By comparing the fMRI results of these experiments, we were therefore able to establish the neural representations that can be uniquely attributed to the probability estimates of regime-shift.”

To further make sure that the probability-estimate signals in Experiment 1 were not due to motor confounds, we implemented an action-handedness regressor in the GLM, as we described below on page 19:

“Finally, we note that in GLM-1, we implemented an “action-handedness” regressor to directly address the motor-confound issue, that higher probability estimates preferentially involved right-handed responses for entering higher digits. The action-handedness regressor was parametric, coding -1 if both finger presses involved the left hand (e.g., a subject pressed “23” as her probability estimate when seeing a signal), 0 if using one left finger and one right finger (e.g., “75”), and 1 if both finger presses involved the right hand (e.g., “90”). Taken together, these results ruled out motor confounds and suggested that vmPFC and ventral striatum represent subjects’ probability estimates of change (regime shifts) and belief revision.”

(4) The Discussion is very long, and whilst a lot of related literature is cited, I found it hard to pin down within the discussion, what the key contributions of this study are. In my opinion it would be better to have a short but incisive discussion highlighting the advances in understanding that arise from the current study, rather than reviewing the field so broadly.

Thank you. We thank the reviewer for pushing us to highlight the key contributions. In response, we added a paragraph at the beginning of Discussion to better highlight our contributions:

“In this study, we investigated how humans detect changes in the environments and the neural mechanisms that contribute to how we might under- and overreact in our judgments. Combining a novel behavioral paradigm with computational modeling and fMRI, we discovered that sensitivity to environmental parameters that directly impact change detection is a key mechanism for under- and overreactions. This mechanism is implemented by distinct brain networks in the frontal and parietal cortices and in accordance with the computational roles they played in change detection. By introducing the framework in system neglect and providing evidence for its neural implementations, this study offered both theoretical and empirical insights into how systematic judgment biases arise in dynamic environments.”

**Recommendations for the authors:

Reviewer #3 (Recommendations for the authors):**

Thank you for pointing out the inclusion of the intertemporal prior in glm2, this seems like an important control that would address my criticism. Why not present this better-controlled analysis in the main figure, rather than the results for glm1 which has no effective control of the increasing posterior probability of a reversal with time?

Thank you for this suggestion. We added a new figure (Figure 4) that showed results from GLM-2. In this new figure, we showed whole-brain results on Pt and delta Pt, ROI results of vmPFC and ventral striatum on Pt, delta Pt, and intertemporal prior.

The reason we kept results from GLM-1 (Figure 3) was primarily because we wanted to compare the effect of Pt between experiments under identical GLM. In other words, the regressors in GLM-1 was identical across all 3 experiments. In Experiments 1 and 2, Pt and delta Pt were respectively probability estimates and belief updates that current regime was the Blue regime. In Experiment 3, Pt and delta Pt were simply the number subjects were instructed to press (Pt) and change in number between successive periods (delta Pt).

As a further point I could not navigate the tables of fMRI activations in SI and recommend replacing or supplementing these with images. For example I cannot actually find a vmPFC or ventral striatum cluster listed for the effect of Pt in GLM1 (version in table S1), which I thought were the main results? Beyond that, comparing how much weaker (or not) those results are when additional confound regressors are included in GLM2 seems impossible.

The vmPFC and ventral striatum were part of the cluster labeled as Central Opercular cortex. In response, we will provide information about coordinates on the local maxima within the cluster. We will also add slice-by-slice images showing the effect of Pt.

The following is the authors’ response to the original reviews

eLife Assessment

This study offers valuable insights into how humans detect and adapt to regime shifts, highlighting distinct contributions of the frontoparietal network and ventromedial prefrontal cortex to sensitivity to signal diagnosticity and transition probabilities. The combination of an innovative task design, behavioral modeling, and model-based fMRI analyses provides a solid foundation for the conclusions; however, the neuroimaging results have several limitations, particularly a potential confound between the posterior probability of a switch and the passage of time that may not be fully controlled by including trial number as a regressor. The control experiments intended to address this issue also appear conceptually inconsistent and, at the behavioral level, while informing participants of conditional probabilities rather than requiring learning is theoretically elegant, such information is difficult to apply accurately, as shown by well-documented challenges with conditional reasoning and base-rate neglect. Expressing these probabilities as natural frequencies rather than percentages may have improved comprehension. Overall, the study advances understanding of belief updating under uncertainty but would benefit from more intuitive probabilistic framing and stronger control of temporal confounds in future work.

We thank the editors for the assessment and we appreciate your efforts in reviewing the paper. The editors added several limitations in the assessment based on the new reviewer 3 in this round, which we would like to clarify below.

With regard to temporal confounds, we clarified in the main text and response to Reviewer 3 that we had already addressed the potential confound between posterior probability of a switch and passage of time in GLM-2 with the inclusion of intertemporal prior. After adding intertemporal prior in the GLM, we still observed the same fMRI results on probability estimates. In addition, we did two other robustness checks, which we mentioned in the manuscript.

With regard to response mode (probability estimation rather than choice or indicating natural frequencies), we wish to point out that the in previous research by Massey and Wu (2005), which the current study was based on, the concern of participants showing system-neglect tendencies due to the mode of information delivery, namely indicating beliefs through reporting probability estimates rather than through choice or other response mode was addressed. Massy and Wu (2005, Study 3) found the same biases when participants performed a choice task that did not require them to indicate probability estimates.

With regard to the control experiments, the control experiments in fact were not intended to address the confounds between posterior probability and passage of time. Rather, they aimed to address whether the neural findings were unique to change detection (Experiment 2) and to address visual and motor confounds (Experiment 3). These and the results of the control experiments were mentioned on page 18-19.

We also wish to highlight that we had performed detailed model comparisons after reviewer 2’s suggestions. Although reviewer 2 was unable to re-review the manuscript, we believe this provides insight into the literature on change detection. See “Incorporating signal dependency into system-neglect model led to better models for regime-shift detection” (p.27-30). The model comparison showed that system-neglect models that incorporate signal dependency are better models than the original system-neglect model in describing participants probability estimates. This suggests that people respond to change-consistent and change-inconsistent signals differently when judging whether the regime had changed. This was not reported in previous behavioral studies and was largely inspired by the neural finding on signal dependency in the frontoparietal cortex. It indicates that neural findings can provide novel insights into computational modeling of behavior.

To better highlight and summarize our key contributions, we added a paragraph at the beginning of Discussion:

“In this study, we investigated how humans detect changes in the environments and the neural mechanisms that contribute to how we might under- and overreact in our judgments. Combining a novel behavioral paradigm with computational modeling and fMRI, we discovered that sensitivity to environmental parameters that directly impact change detection is a key mechanism for under- and overreactions. This mechanism is implemented by distinct brain networks in the frontal and parietal cortices and in accordance with the computational roles they played in change detection. By introducing the framework in system neglect and providing evidence for its neural implementations, this study offered both theoretical and empirical insights into how systematic judgment biases arise in dynamic environments.”    

Public Reviews:

Reviewer #1 (Public review):

Summary:

The study examines human biases in a regime-change task, in which participants have to report the probability of a regime change in the face of noisy data. The behavioral results indicate that humans display systematic biases, in particular, overreaction in stable but noisy environments and underreaction in volatile settings with more certain signals. fMRI results suggest that a frontoparietal brain network is selectively involved in representing subjective sensitivity to noise, while the vmPFC selectively represents sensitivity to the rate of change.

Strengths:

- The study relies on a task that measures regime-change detection primarily based on descriptive information about the noisiness and rate of change. This distinguishes the study from prior work using reversal-learning or change-point tasks in which participants are required to learn these parameters from experiences. The authors discuss these differences comprehensively.

- The study uses a simple Bayes-optimal model combined with model fitting, which seems to describe the data well. The model is comprehensively validated.

- The authors apply model-based fMRI analyses that provide a close link to behavioral results, offering an elegant way to examine individual biases.

We thank the reviewer for the comments.

Weaknesses:

The authors have adequately addressed most of my prior concerns.

We thank the reviewer for recognizing our effort in addressing your concerns.

My only remaining comment concerns the z-test of the correlations. I agree with the non-parametric test based on bootstrapping at the subject level, providing evidence for significant differences in correlations within the left IFG and IPS.

However, the parametric test seems inadequate to me. The equation presented is described as the Fisher z-test, but the numerator uses the raw correlation coefficients (r) rather than the Fisher-transformed values (z). To my understanding, the subtraction should involve the Fisher z-scores, not the raw correlations.

More importantly, the Fisher z-test in its standard form assumes that the correlations come from independent samples, as reflected in the denominator (which uses the n of each independent sample). However, in my opinion, the two correlations are not independent but computed within-subject. In such cases, parametric tests should take into account the dependency. I believe one appropriate method for the current case (correlated correlation coefficients sharing a variable [behavioral slope]) is explained here:

Meng, X.-l., Rosenthal, R., & Rubin, D. B. (1992). Comparing correlated correlation coefficients. Psychological Bulletin, 111(1), 172-175. https://doi.org/10.1037/0033-2909.111.1.172

It should be implemented here:

Diedenhofen B, Musch J (2015) cocor: A Comprehensive Solution for the Statistical Comparison of Correlations. PLoS ONE 10(4): e0121945. https://doi.org/10.1371/journal.pone.0121945

My recommendation is to verify whether my assumptions hold, and if so, perform a test that takes correlated correlations into account. Or, to focus exclusively on the non-parametric test.

In any case, I recommend a short discussion of these findings and how the authors interpret that some of the differences in correlations are not significant.

Thank you for the careful check. Yes. This was indeed a mistake from us. We also agree that the two correlations are not independent. Therefore, we modified the test that accounts for dependent correlations by following Meng et al. (1992) suggested by the reviewer. We updated in the Methods section on p.56-57:

“In the parametric test, we adopted the approach of Meng et al. (1992) to statistically compare the two correlation coefficients. This approach specifically tests differences between dependent correlation coefficients according to the following equation

Where N is the number of subjects, z_ri is the Fisher z-transformed value of r_i,(r₁ = r_blue and r₂ = r_red), and r_x is the correlation between the neural sensitivity at change-consistent signals and change-inconsistent signals. The computation of h is based on the following equations

Where is the mean of the , and f should be set to 1 if > 1.”

We updated on the Results section on p.29:

“Since these correlation coefficients were not independent, we compared them using the test developed in Meng et al. (1992) (see Methods). We found that among the five ROIs in the frontoparietal network, two of them, namely the left IFG and left IPS, the difference in correlation was significant (one-tailed z test; left IFG: z = 1.8908, p = 0.0293; left IPS: z = 2.2584, p = 0.0049). For the remaining three ROIs, the difference in correlation was not significant (dmPFC: z = 0.9522, p = 0.1705; right IFG: z = 0.9860, p = 0.1621; right IPS: z = 1.4833, p = 0.0690).”

We added a Discussion on these results on p.41:

“Interestingly, such sensitivity to signal diagnosticity was only present in the frontoparietal network when participants encountered change-consistent signals. However, while most brain areas within this network responded in this fashion, only the left IPS and left IFG showed a significant difference in coding individual participants’ sensitivity to signal diagnosticity between change-consistent and change-inconsistent signals. Unlike the left IPS and left IFG, we observed in dmPFC a marginally significant correlation with behavioral sensitivity at change-inconsistent signals as well. Together, these results indicate that while different brain areas in the frontoparietal network responded similarly to change-consistent signals, there was a greater degree of heterogeneity in responding to change-inconsistent signals.”

Reviewer #3 (Public review):

This study concerns how observers (human participants) detect changes in the statistics of their environment, termed regime shifts. To make this concrete, a series of 10 balls are drawn from an urn that contains mainly red or mainly blue balls. If there is a regime shift, the urn is changed over (from mainly red to mainly blue) at some point in the 10 trials. Participants report their belief that there has been a regime shift as a % probability. Their judgement should (mathematically) depend on the prior probability of a regime shift (which is set at one of three levels) and the strength of evidence (also one of three levels, operationalized as the proportion of red balls in the mostly-blue urn and vice versa). Participants are directly instructed of the prior probability of regime shift and proportion of red balls, which are presented on-screen as numerical probabilities. The task therefore differs from most previous work on this question in that probabilities are instructed rather than learned by observation, and beliefs are reported as numerical probabilities rather than being inferred from participants' choice behaviour (as in many bandit tasks, such as Behrens 2007 Nature Neurosci).

The key behavioural finding is that participants over-estimate the prior probability of regime change when it is low, and under estimate it when it is high; and participants over-estimate the strength of evidence when it is low and under-estimate it when it is high. In other words participants make much less distinction between the different generative environments than an optimal observer would. This is termed 'system neglect'. A neuroeconomic-style mathematical model is presented and fit to data.

Functional MRI results how that strength of evidence for a regime shift (roughly, the surprise associated with a blue ball from an apparently red urn) is associated with activity in the frontal-parietal orienting network. Meanwhile, at time-points where the probability of a regime shift is high, there is activity in another network including vmPFC. Both networks show individual differences effects, such that people who were more sensitive to strength of evidence and prior probability show more activity in the frontal-parietal and vmPFC-linked networks respectively.

We thank the reviewer for the overall descriptions of the manuscript.

Strengths

(1) The study provides a different task for looking at change-detection and how this depends on estimates of environmental volatility and sensory evidence strength, in which participants are directly and precisely informed of the environmental volatility and sensory evidence strength rather than inferring them through observation as in most previous studies

(2) Participants directly provide belief estimates as probabilities rather than experimenters inferring them from choice behaviour as in most previous studies

(3) The results are consistent with well-established findings that surprising sensory events activate the frontal-parietal orienting network whilst updating of beliefs about the word ('regime shift') activates vmPFC.

Thank you for these assessments.

Weaknesses

(1) The use of numerical probabilities (both to describe the environments to participants, and for participants to report their beliefs) may be problematic because people are notoriously bad at interpreting probabilities presented in this way, and show poor ability to reason with this information (see Kahneman's classic work on probabilistic reasoning, and how it can be improved by using natural frequencies). Therefore the fact that, in the present study, people do not fully use this information, or use it inaccurately, may reflect the mode of information delivery.

We appreciate the reviewer’s concern on this issue. The concern was addressed in Massey and Wu (2005) as participants performed a choice task in which they were not asked to provide probability estimates (Study 3 in Massy and Wu, 2005). Instead, participants in Study 3 were asked to predict the color of the ball before seeing a signal. This was a more intuitive way of indicating his or her belief about regime shift. The results from the choice task were identical to those found in the probability estimation task (Study 1 in Massey and Wu). We take this as evidence that the system-neglect behavior the participants showed was less likely to be due to the mode of information delivery.

(2) Although a very precise model of 'system neglect' is presented, many other models could fit the data.

For example, you would get similar effects due to attraction of parameter estimates towards a global mean - essentially application of a hyper-prior in which the parameters applied by each participant in each block are attracted towards the experiment-wise mean values of these parameters. For example, the prior probability of regime shift ground-truth values [0.01, 0.05, 0.10] are mapped to subjective values of [0.037, 0.052, 0.069]; this would occur if observers apply a hyper-prior that the probability of regime shift is about 0.05 (the average value over all blocks). This 'attraction to the mean' is a well-established phenomenon and cannot be ruled out with the current data (I suppose you could rule it out by comparing to another dataset in which the mean ground-truth value was different).

We thank the reviewer for this comment. It is true that the system-neglect model is not entirely inconsistent with regression to the mean, regardless of whether the implementation has a hyper prior or not. In fact, our behavioral measure of sensitivity to transition probability and signal diagnosticity, which we termed the behavioral slope, is based on linear regression analysis. In general, the modeling approach in this paper is to start from a generative model that defines ideal performance and consider modifying the generative model when systematic deviations in actual performance from the ideal is observed. In this approach, a generative Bayesian model with hyper priors would be more complex to begin with, and a regression to the mean idea by itself does not generate a priori predictions.

More generally, any model in which participants don't fully use the numerical information they were given would produce apparent 'system neglect'. Four qualitatively different example reasons are: 1. Some individual participants completely ignored the probability values given. 2. Participants did not ignore the probability values given, but combined them with a hyperprior as above. 3. Participants had a reporting bias where their reported beliefs that a regime-change had occurred tend to be shifted towards 50% (rather than reporting 'confident' values such 5% or 95%). 4. Participants underweighted probability outliers resulting in underweighting of evidence in the 'high signal diagnosticity' environment (10.1016/j.neuron.2014.01.020)

In summary I agree that any model that fits the data would have to capture the idea that participants don't differentiate between the different environments as much as they should, but I think there are a number of qualitatively different reasons why they might do this - of which the above are only examples - hence I find it problematic that the authors present the behaviour as evidence for one extremely specific model.

Thank you for raising this point. The modeling principle we adopt is the following. We start from the normative model—the Bayesian model—that defined what normative behavior should look like. We compared participants’ behavior with the Bayesian model and found systematic deviations from it. To explain those systematic deviations, we considered modeling options within the confines of the same modeling framework. In other words, we considered a parameterized version of the Bayesian model, which is the system-neglect model and examined through model comparison the best modeling choice. This modeling approach is not uncommon in economics and psychology. For example, Kahneman and Tversky adopted this approach when proposing prospect theory, a modification of expected utility theory where expected utility theory can be seen as one specific model for how utility of an option should be computed.

(3) Despite efforts to control confounds in the fMRI study, including two control experiments, I think some confounds remain.

For example, a network of regions is presented as correlating with the cumulative probability that there has been a regime shift in this block of 10 samples (Pt). However, regardless of the exact samples shown, doesn't Pt always increase with sample number (as by the time of later samples, there have been more opportunities for a regime shift)? Unless this is completely linear, the effect won't be controlled by including trial number as a co-regressor (which was done).

Thank you for raising this concern. Yes, Pt always increases with sample number regardless of evidence (seeing change-consistent or change-inconsistent signals). This is captured by the ‘intertemporal prior’ in the Bayesian model, which we included as a regressor in our GLM analysis (GLM-2), in addition to Pt. In short, GLM-1 had Pt and sample number. GLM-2 had Pt, intertemporal prior, and sample number, among other regressors. And we found that, in both GLM-1 and GLM-2, both vmPFC and ventral striatum correlated with Pt.

To make this clearer, we updated the main text to further clarify this on p.18:

“We examined the robustness of P_t representations in these two regions in several follow-up analyses. First, we implemented a GLM (GLM-2 in Methods) that, in addition to P_t, included various task-related variables contributing to P_t as regressors (Fig. S7 in SI). Specifically, to account for the fact that the probability of regime change increased over time, we included the intertemporal prior as a regressor in GLM-2. The intertemporal prior is the natural logarithm of the odds in favor of regime shift in the t-th period, where q is transition probability and t = 1,…,10 is the period (see Eq. 1 in Methods). It describes normatively how the prior probability of change increased over time regardless of the signals (blue and red balls) the subjects saw during a trial. Including it along with P_t would clarify whether any effect of P_t can otherwise be attributed to the intertemporal prior. Second, we implemented a GLM that replaced P_t with the log odds of P_t, ln (P_t/(1-P_t)) (Fig. S8 in SI). Third, we implemented a GLM that examined  separately on periods when change-consistent (blue balls) and change-inconsistent (red balls) signals appeared (Fig. S9 in SI). Each of these analyses showed the same pattern of correlations between P_t and activation in vmPFC and ventral striatum, further establishing the robustness of the P_t findings.”

On the other hand, two additional fMRI experiments are done as control experiments and the effect of Pt in the main study is compared to Pt in these control experiments. Whilst I admire the effort in carrying out control studies, I can't understand how these particular experiment are useful controls. For example in experiment 3 participants simply type in numbers presented on the screen - how can we even have an estimate of Pt from this task?

We thank the reviewer for this comment. On the one hand, the effect of Pt we see in brain activity can be simply due to motor confounds and the purpose of Experiment 3 was to control for them. Our question was, if subjects saw the similar visual layout and were just instructed to press buttons to indicate two-digit numbers, would we observe the vmPFC, ventral striatum, and the frontoparietal network like what we did in the main experiment (Experiment 1)?

On the other hand, the effect of Pt can simply reflect probability estimates of that the current regime is the blue regime, and therefore not particularly about change detection. In Experiment 2, we tested that idea, namely whether what we found about Pt was unique to change detection. In Experiment 2, subjects estimated the probability that the current regime is the blue regime (just as they did in Experiment 1) except that there were no regime shifts involved. In other words, it is possible that the regions we identified were generally associated with probability estimation and not particularly about probability estimates of change. We used Experiment 2 to examine whether this were true.

To make the purpose of the two control experiments clearer, we updated the paragraph describing the control experiments on page 9:

“To establish the neural representations for regime-shift estimation, we performed three fMRI experiments (n\=30 subjects for each experiment, 90 subjects in total). Experiment 1 was the main experiment, while Experiments 2 to 3 were control experiments that ruled out two important confounds (Fig. 1E). The control experiments were designed to clarify whether any effect of subjects’ probability estimates of a regime shift, P_t, in brain activity can be uniquely attributed to change detection. Here we considered two major confounds that can contribute to the effect of . First, since subjects in Experiment 1 made judgments about the probability that the current regime is the blue regime (which corresponded to probability of regime change), the effect of P_t did not particularly have to do with change detection. To address this issue, in Experiment 2 subjects made exactly the same judgments as in Experiment 1 except that the environments were stationary (no transition from one regime to another was possible), as in Edwards (1968) classic “bookbag-and-poker chip” studies. Subjects in both experiments had to estimate the probability that the current regime is the blue regime, but this estimation corresponded to the estimates of regime change only in Experiment 1. Therefore, activity that correlated with probability estimates in Experiment 1 but not in Experiment 2 can be uniquely attributed to representing regime-shift judgments. Second, the effect of P_t can be due to motor preparation and/or execution, as subjects in Experiment 1 entered two-digit numbers with button presses to indicate their probability estimates. To address this issue, in Experiment 3 subjects performed a task where they were presented with two-digit numbers and were instructed to enter the numbers with button presses. By comparing the fMRI results of these experiments, we were therefore able to establish the neural representations that can be uniquely attributed to the probability estimates of regime-shift.”

To further make sure that the probability-estimate signals in Experiment 1 were not due to motor confounds, we implemented an action-handedness regressor in the GLM, as we described below on page 19:

“Finally, we note that in GLM-1, we implemented an “action-handedness” regressor to directly address the motor-confound issue, that higher probability estimates preferentially involved right-handed responses for entering higher digits. The action-handedness regressor was parametric, coding -1 if both finger presses involved the left hand (e.g., a subject pressed “23” as her probability estimate when seeing a signal), 0 if using one left finger and one right finger (e.g., “75”), and 1 if both finger presses involved the right hand (e.g., “90”). Taken together, these results ruled out motor confounds and suggested that vmPFC and ventral striatum represent subjects’ probability estimates of change (regime shifts) and belief revision.”

(4) The Discussion is very long, and whilst a lot of related literature is cited, I found it hard to pin down within the discussion, what the key contributions of this study are. In my opinion it would be better to have a short but incisive discussion highlighting the advances in understanding that arise from the current study, rather than reviewing the field so broadly.

Thank you. We thank the reviewer for pushing us to highlight the key contributions. In response, we added a paragraph at the beginning of Discussion to better highlight our contributions:

“In this study, we investigated how humans detect changes in the environments and the neural mechanisms that contribute to how we might under- and overreact in our judgments. Combining a novel behavioral paradigm with computational modeling and fMRI, we discovered that sensitivity to environmental parameters that directly impact change detection is a key mechanism for under- and overreactions. This mechanism is implemented by distinct brain networks in the frontal and parietal cortices and in accordance with the computational roles they played in change detection. By introducing the framework in system neglect and providing evidence for its neural implementations, this study offered both theoretical and empirical insights into how systematic judgment biases arise in dynamic environments.”

Recommendations for the authors:

Reviewer #3 (Recommendations for the authors):

Many of the figures are too tiny - the writing is very small, as are the pictures of brains. I'd suggest adjusting these so they will be readable without enlarging.

Thank you. We apologize for the poor readability of the figures. We had enlarged the figures (Fig. 5 in particular) and their font size to make them more readable.

eLife Assessment

This article reports an algorithm for inferring the presence of synaptic connection between neurons based on naturally occurring spiking activity of a neuronal network. One key improvement is to combine self-supervised and synthetic approaches to learn to focus on features that generalize to the conditions of the observed network. This valuable contribution is currently supported by incomplete evidence.

Reviewer #1 (Public review):

Summary:

The authors proposed a new method to infer connectivity from spike trains whose main novelty relies on their approach to mitigate the problem of model mismatch. The latter arises when the inference algorithm is trained or based on a model that does not accurately describe the data. They propose combining domain adaptation with a deep neural architecture and in an architecture called DeepDAM. They apply DeepDAM to an in vivo ground-truth dataset previously recorded in mouse CA1, show that it performs better than methods without domain adaptation, and evaluate its robustness. Finally, they show that their approach can also be applied to a different problem i.e., inferring biophysical properties of individual neurons.

Strengths:

(1) The problem of inferring connectivity from extracellular recording is a very timely one: as the yield of silicon probes steadily increases, the number of simultaneously recorded pairs does so quadratically, drastically increasing the possibility of detecting connected pairs.

(2) Using domain adaptation to address model mismatch is a clever idea, and the way the authors introduced it into the larger architecture seems sensible.

(3) The authors clearly put a great effort into trying to communicate the intuitions to the reader.

Weaknesses:

(1) The validation of the approach is incomplete: due to its very limited size, the single ground-truth dataset considered does not provide a sufficient basis to draw a strong conclusion. While the authors correctly note that this is the only dataset of its kind, the value of this validation is limited compared to what could be done by carefully designing in silico experiments.

(2) Surprisingly, the authors fail to compare their method to the approach originally proposed for the data they validate on (English et al., 2017).

(3) The authors make a commendable effort to study the method's robustness by pushing the limits of the dataset. However, the logic of the robustness analysis is often unclear, and once again, the limited size of the dataset poses major limitations to the authors.

(4) The lack of details concerning both the approach and the validation makes it challenging for the reader to establish the technical soundness of the study.

Although in the current form this study does not provide enough basis to judge the impact of DeepDAM in the broader neuroscience community, it nevertheless puts forward a valuable and novel idea: using domain adaptation to mitigate the problem of model mismatch. This approach might be leveraged in future studies and methods to infer connectivity.

Reviewer #2 (Public review):

The article is very well written, and the new methodology is presented with care. I particularly appreciated the step-by-step rationale for establishing the approach, such as the relationship between K-means centers and the various parameters. This text is conveniently supported by the flow charts and t-SNE plots. Importantly, I thought the choice of state-of-the-art method was appropriate and the choice of dataset adequate, which together convinced me in believing the large improvement reported. I thought that the crossmodal feature-engineering solution proposed was elegant and seems exportable to other fields. Here are a few notes.<br /> While the validation data set was well chosen and of high quality, it remains a single dataset and also remains a non-recurrent network. The authors acknowledge this in the discussion, but I wanted to chime in to say that for the method to be more than convincing, it would need to have been tested on more datasets. It should be acknowledged that the problem becomes more complicated in a recurrent excitatory network, and thus the method may not work as well in the cortex or in CA3.

While the data is shown to work in this particular dataset (plus the two others at the end), I was left wondering when the method breaks. And it should break if the models are sufficiently mismatched. Such a question can be addressed using synthetic-synthetic models. This was an important intuition that I was missing, and an important check on the general nature of the method that I was missing.

While the choice of state-of-the-art is good in my opinion, I was looking for comments on the methods prior to that. For instance, methods such based on GLMs have been used by the Pillow, Paninski, and Truccolo groups. I could not find a decent discussion of these methods in the main text and thought that both their acknowledgement and rationale for dismissing were missing.

While most of the text was very clear, I thought that page 11 was odd and missing much in terms of introductions. Foremost is the introduction of the dataset, which is never really done. Page 11 refers to 'this dataset', while the previous sentence was saying that having such a dataset would be important and is challenging. The dataset needs to be properly described: what's the method for labeling, what's the brain area, what were the spike recording methodologies, what is meant by two labeling methodologies, what do we know about the idiosyncrasies of the particular network the recording came from (like CA1 is non-recurrent, so which connections)? I was surprised to see 'English et al.' cited in text only on page 13 since their data has been hailed from the beginning.

Further elements that needed definition are the Nsyn and i, which were not defined in the cortex of Equation 2-3: I was not sure if it referred to different samples or different variants of the synthetic model. I also would have preferred having the function f defined earlier, as it is defined for Equation 3, but appears in Equation 2.

When the loss functions are described, it would be important to define 'data' and 'labels' here. This machine learning jargon has a concrete interpretation in this context, and making this concrete would be very important for the readership.

While I appreciated that there was a section on robustness, I did not find that the features studied were the most important. In this context, I was surprised that the other datasets were relegated to supplementary, as these appeared more relevant.

Some of the figures have text that is too small. In particular, Figure 2 has text that is way too small. It seemed to me that the pseudo code could stand alone, and the screenshot of the equations did not need to be repeated in a figure, especially if their size becomes so small that we can't even read them.

Author response:

General Response

We thank the reviewers for their positive assessment of our work and for acknowledging the timeliness of the problem and the novelty of using domain adaptation to address model mismatch. We appreciate the constructive feedback regarding validation and clarity. In the revised manuscript, we will address these points as follows:

(1) Systematic Validation: We will design and perform systematic in silico experiments to evaluate the method beyond the single in vivo dataset , including robustness tests regarding recording length and network synchrony.

(2) Recurrent Networks & Failure Analysis: We will test our method on synthetic datasets generated from highly recurrent networks and analyze exactly when the method breaks as a function of mismatch magnitude.

(3) Method Comparisons: We will report the Matthews Correlation Coefficient (MCC) for the approach by English et al. (2017) and expand our comparison and discussion of GLM-based methods.

(4) Clarifications: We will rigorously define the dataset details (labeling, recording methodology), mathematical notation, and machine learning terminology ('data', 'labels').

(5) Discussion of Limitations: We will explicitly discuss the challenges and limitations inherent in generalizing to more recurrently connected regions.

Below are our more detailed responses:

Public Reviews:

Reviewer #1 (Public review):

Weaknesses:

(1) The validation of the approach is incomplete: due to its very limited size, the single ground-truth dataset considered does not provide a sufficient basis to draw a strong conclusion. While the authors correctly note that this is the only dataset of its kind, the value of this validation is limited compared to what could be done by carefully designing in silico experiments.

We thank the reviewer for acknowledging the scarcity of suitable in vivo ground-truth datasets and the limitations this poses. We agree that additional validation is necessary to draw strong conclusions. In the revised manuscript, we will systematically design and perform in silico experiments for evaluations beyond the single in vivo dataset.

(2) Surprisingly, the authors fail to compare their method to the approach originally proposed for the data they validate on (English et al., 2017).

We agree that this is an essential comparison. We will report the Matthews Correlation Coefficient (MCC) result of the approach by English et al. (2017) on the spontaneous period of the recording.

(3) The authors make a commendable effort to study the method's robustness by pushing the limits of the dataset. However, the logic of the robustness analysis is often unclear, and once again, the limited size of the dataset poses major limitations to the authors.

We appreciate the reviewer recognizing our initial efforts to evaluate robustness. In our original draft, we tested recording length, network model choices, and analyzed failure cases. However, we agree that the limited real data restricts the scope of these tests. To address this, we will perform more systematic robustness tests on the newly generated synthetic datasets in the revised version, allowing us to evaluate performance under a wider range of conditions.

(4) The lack of details concerning both the approach and the validation makes it challenging for the reader to establish the technical soundness of the study.

We will revise the manuscript thoroughly to better present the methodology of our framework and the validation pipelines. We will ensure that the figures and text clearly articulate the technical details required to assess the soundness of the study.

Although in the current form this study does not provide enough basis to judge the impact of DeepDAM in the broader neuroscience community, it nevertheless puts forward a valuable and novel idea: using domain adaptation to mitigate the problem of model mismatch. This approach might be leveraged in future studies and methods to infer connectivity.

We thank the reviewer again for acknowledging the novelty and importance of our work.

Reviewer #2 (Public review):

While the validation data set was well chosen and of high quality, it remains a single dataset and also remains a non-recurrent network. The authors acknowledge this in the discussion, but I wanted to chime in to say that for the method to be more than convincing, it would need to have been tested on more datasets. It should be acknowledged that the problem becomes more complicated in a recurrent excitatory network, and thus the method may not work as well in the cortex or in CA3.

We will carefully revise our text to specifically discuss this limitation and the challenges inherent in generalizing to more recurrently connected regions. Furthermore, to empirically address this concern, we will test our method extensively on synthetic datasets generated from highly recurrent networks to quantify performance in these regimes.

While the data is shown to work in this particular dataset (plus the two others at the end), I was left wondering when the method breaks. And it should break if the models are sufficiently mismatched. Such a question can be addressed using synthetic-synthetic models. This was an important intuition that I was missing, and an important check on the general nature of the method that I was missing.

We thank the reviewer for this insight regarding the general nature of the method. While we previously analyzed failure cases regarding strong covariation and low spike counts, we agree that a systematic analysis of mismatch magnitude is missing. Building on our planned experiments with synthetic data, we will analyze and discuss exactly when the method breaks as a function of the mismatch magnitude between datasets.

While the choice of state-of-the-art is good in my opinion, I was looking for comments on the methods prior to that. For instance, methods such based on GLMs have been used by the Pillow, Paninski, and Truccolo groups. I could not find a decent discussion of these methods in the main text and thought that both their acknowledgement and rationale for dismissing were missing.

As the reviewer noted, we extensively compared our method with a GLM-based method (GLMCC) and CoNNECT, whose superiority over other GLM-based methods, such as extend GLM method (Ren et al., 2020, J Neurophysiol), have already been demonstrated in their papers (Endo et al., Sci Rep, 2021). However, we acknowledge that the discussion of the broader GLM literature was insufficient. To make the comparison more thorough, we will conduct comparisons with additional GLM-based methods and include a detailed discussion of these approaches.

Endo, D., Kobayashi, R., Bartolo, R., Averbeck, B. B., Sugase-Miyamoto, Y., Hayashi, K., ... & Shinomoto, S. (2021). A convolutional neural network for estimating synaptic connectivity from spike trains. Scientific Reports, 11(1), 12087.

Ren, N., Ito, S., Hafizi, H., Beggs, J. M., & Stevenson, I. H. (2020). Model-based detection of putative synaptic connections from spike recordings with latency and type constraints. Journal of Neurophysiology, 124(6), 1588-1604.

While most of the text was very clear, I thought that page 11 was odd and missing much in terms of introductions. Foremost is the introduction of the dataset, which is never really done. Page 11 refers to 'this dataset', while the previous sentence was saying that having such a dataset would be important and is challenging. The dataset needs to be properly described: what's the method for labeling, what's the brain area, what were the spike recording methodologies, what is meant by two labeling methodologies, what do we know about the idiosyncrasies of the particular network the recording came from (like CA1 is non-recurrent, so which connections)? I was surprised to see 'English et al.' cited in text only on page 13 since their data has been hailed from the beginning.

Further elements that needed definition are the Nsyn and i, which were not defined in the cortex of Equation 2-3: I was not sure if it referred to different samples or different variants of the synthetic model. I also would have preferred having the function f defined earlier, as it is defined for Equation 3, but appears in Equation 2.

When the loss functions are described, it would be important to define 'data' and 'labels' here. This machine learning jargon has a concrete interpretation in this context, and making this concrete would be very important for the readership.

We thank the reviewer for these constructive comments on the writing. We will clarify the introduction of the dataset (labeling method, brain area, recording methodology) and ensure all mathematical terms (such as Nsyn, i, and function f) and machine learning terminology (definitions of 'data' and 'labels' in this context) are rigorously defined upon first use in the revised manuscript.

While I appreciated that there was a section on robustness, I did not find that the features studied were the most important. In this context, I was surprised that the other datasets were relegated to supplementary, as these appeared more relevant.

Robustness is an important aspect of our framework to demonstrate its applicability to real experimental scenarios. We specifically analyzed how synchrony between neurons, the number of recorded spikes and the choice of the network influence the performance of our method. We also agree that these aspects are limited by the one dataset we evaluated on. Therefore, we will test the robustness of our method more systematically on synthetic datasets.

With more extensive analysis on synthetic datasets, we believe that the results on inferring biophysical properties of single neuron and microcircuit models remain in the supplement, such that the main figures focus purely on synaptic connectivity inference.

Some of the figures have text that is too small. In particular, Figure 2 has text that is way too small. It seemed to me that the pseudo code could stand alone, and the screenshot of the equations did not need to be repeated in a figure, especially if their size becomes so small that we can't even read them.

We will remove the pseudo-code and equations from Figure 2 to improve readability. The pseudo-code will be presented as a distinct box in the main text.

eLife Assessment

This useful paper describes a software tool, "DrosoMating", which allows automated, high-throughput quantification of 6 common metrics of courtship and mating behaviors in Drosophila melanogaster. The validity of the tool is quite convincingly demonstrated by comparing expert human assessments with those made by DrosoMating. The work, however, does not address how DrosoMating compares with or advances on other existing tools for exactly the same purpose, whether it can be used for studies of other Drosophila species, and/or whether finer aspects of courtship response timing - which depend on proximal female signals to the male - could be extracted with more detailed analyses. Some additional statistical analyses would also help further strengthen the authors' current conclusions.

Reviewer #1 (Public review):

Summary:

The study of Drosophila mating behaviors has offered a powerful entry point for understanding how complex innate behaviors are instantiated in the brain. The effectiveness of this behavioral model stems from how readily quantifiable many components of the courtship ritual are, facilitating the fine-scale correlations between the behaviors and the circuits that underpin their implementation. Detailed quantification, however, can be both time-consuming and error-prone, particularly when scored manually. Song et al. have sought to address this challenge by developing DrosoMating, software that facilitates the automated and high-throughput quantification of 6 common metrics of courtship and mating behaviors. Compared to a human observer, DrosoMating matches courtship scoring with high fidelity. Further, the authors demonstrate that the software effectively detects previously described variations in courtship resulting from genetic background or social conditioning. Finally, they validate its utility in assaying the consequences of neural manipulations by silencing Kenyon cells involved in memory formation in the context of courtship conditioning.

Strengths:

(1) The authors demonstrate that for three key courtship/mating metrics, DrosoMating performs virtually indistinguishably from a human observer, with differences consistently within 10 seconds and no statistically significant differences detected. This demonstrates the software's usefulness as a tool for reducing bias and scoring time for analyses involving these metrics.

(2) The authors validate the tool across multiple genetic backgrounds and experimental manipulations to confirm its ability to detect known influences on male mating behavior.

(3) The authors present a simple, modular chamber design that is integrated with DrosoMating and allows for high-throughput experimentation, capable of simultaneously analyzing up to 144 fly pairs across all chambers.

Weaknesses:

(1) DrosoMating appears to be an effective tool for the high-throughput quantification of key courtship and mating metrics, but a number of similar tools for automated analysis already exist. FlyTracker (CalTech), for instance, is a widely used software that offers a similar machine vision approach to quantifying a variety of courtship metrics. It would be valuable to understand how DrosoMating compares to such approaches and what specific advantages it might offer in terms of accuracy, ease of use, and sensitivity to experimental conditions.

(2) The courtship behaviors of Drosophila males represent a series of complex behaviors that unfold dynamically in response to female signals (Coen et al., 2014; Ning et al., 2022; Roemschied et al., 2023). While metrics like courtship latency, courtship index, and copulation duration are useful summary statistics, they compress the complexity of actions that occur throughout the mating ritual. The manuscript would be strengthened by a discussion of the potential for DrosoMating to capture more of the moment-to-moment behaviors that constitute courtship. Even without modifying the software, it would be useful to see how the data can be used in combination with machine learning classifiers like JAABA to better segment the behavioral composition of courtship and mating across genotypes and experimental manipulations. Such integration could substantially expand the utility of this tool for the broader Drosophila neuroscience community.

(3) While testing the software's capacity to function across strains is useful, it does not address the "universality" of this method. Cross-species studies of mating behavior diversity are becoming increasingly common, and it would be beneficial to know if this tool can maintain its accuracy in Drosophila species with a greater range of morphological and behavioral variation. Demonstrating the software's performance across species would strengthen claims about its broader applicability.

Reviewer #2 (Public review):

This paper introduces "DrosoMating," an integrated hardware and software solution for automating the analysis of male Drosophila courtship. The authors aim to provide a low-cost, accessible alternative to expensive ethological rigs by utilizing a custom acrylic chamber and smartphone-based recording. The system focuses on quantifying key temporal metrics-Courtship Index (CI), Copulation Latency (CL), and Mating Duration (MD)-and is applied to behavioral paradigms involving memory mutants (orb2, rut).

The development of open-source behavioral tools is a significant contribution to neuroethology, and the authors successfully demonstrate a system that simplifies the setup for large-scale screens. A major strength of the work is the specific focus on automating Copulation Latency and Mating Duration, metrics that are often labor-intensive to score manually.

However, there are several limitations in the current analysis and validation that affect the strength of the conclusions:

First, the statistical rigor requires substantial improvement. The analysis of multi-group experiments (e.g., comparing four distinct strains or factorial designs with genotype and training) currently relies on multiple independent Student's t-tests. This approach is statistically invalid for these experimental designs as it inflates the family-wise Type I error rate. To support the claims of strain-specific differences or learning deficits, the data must be analyzed using Analysis of Variance (ANOVA) to properly account for multiple comparisons and to explicitly test for interaction effects between genotype and training conditions.

Second, the biological validation using w1118 and y1 mutants entails a potential confound. The authors attribute the low Courtship Index in these strains to courtship-specific deficits. However, both strains are known to exhibit general locomotor sluggishness (due to visual or pigmentation/behavioral defects). Since "following" behavior is likely a component of the Courtship Index, a reduction in this metric could reflect a general motor deficit rather than a specific lack of reproductive motivation. Without controlling for general locomotion, the interpretation of these behavioral phenotypes remains ambiguous.

Third, the benchmarking of the system is currently limited to comparisons against manual scoring. Given that the field has largely adopted sophisticated open-source tracking tools (e.g., Ctrax, FlyTracker, JAABA), the utility of DrosoMating would be better contextualized by comparing its performance - in terms of accuracy, speed, or identity maintenance - against these existing automated standards, rather than solely against human observation.

Finally, the visual presentation of the data hinders the assessment of the system's temporal precision. While the system is designed to capture time-resolved metrics, the results are presented primarily as aggregate bar plots. The absence of behavioral ethograms or raster plots makes it difficult to verify the software's ability to accurately detect specific transitions, such as the exact onset of copulation.

Author response:

Thank you very much for the constructive feedback on our manuscript, "Simple Methods to Acutely Measure Multiple Timing Metrics among Sexual Repertoire of Male Drosophila," and for the opportunity to address the reviewers' comments. We appreciate the time and effort the reviewers have invested in evaluating our work, and we agree that their suggestions will significantly strengthen the manuscript.

We are currently working diligently to address all the concerns raised in the public reviews and recommendations. Below is an outline of the major revisions we plan to implement in the revised version:

(1) Statistical Rigor and Analysis

We acknowledge the statistical limitations pointed out by Reviewer #2. We will re-analyze the multi-group data in Figures 3 and 4 using One-way and Two-way ANOVA with appropriate post-hoc tests (e.g., Tukey's HSD), respectively, to properly account for multiple comparisons and interaction effects between genotype and training conditions.

(2) Comparison with Existing Tools

As suggested by both reviewers, we will provide a detailed comparison of DrosoMating with established automated tracking systems (e.g., FlyTracker, JAABA, Ctrax)，and specific use cases where DrosoMating offers distinct advantages in terms of cost, accessibility, and ease of use for high-throughput screening.

(3) Control for Locomotor Activity

To address the potential confound of general locomotor deficits in w1118 and y1 mutants, we will calculate and present general locomotion metrics (e.g., average velocity, total distance traveled) from our tracking data to dissociate motor defects from specific courtship deficits.

(4) Software Capabilities and Cross-Species Applicability

We will clarify how DrosoMating handles fly identification during mating (including occlusion management). We will also discuss or test the software's applicability across different *Drosophila* species, as requested.

(5) Minor Corrections

We will address all textual errors, standardize terminology (e.g., "Mating Duration" vs. "Copulation Duration"), improve figure legibility, and provide complete statistical details for all figures.

We believe these revisions will substantially improve the rigor, clarity, and utility of our manuscript. We aim to resubmit the revised version within the standard timeframe and will ensure the preprint is updated accordingly.

eLife Assessment

This valuable study provides convincing evidence that MgdE, a conserved mycobacterial nucleomodulin, downregulates inflammatory gene transcription by interacting with the histone methyltransferase COMPASS complex and altering histone H3 lysine methylation. This work will interest microbiologists as well as cell and cancer biologists.

Reviewer #1 (Public review):

Summary:

This fundamental study identifies a new mechanism that involves a mycobacterial nucleomodulin manipulation of the host histone methyltransferase COMPASS complex to promote infection. Although other intracellular pathogens are known to manipulate histone methylation, this is the first report demonstrating specific targeting the COMPASS complex by a pathogen. The rigorous experimental design using of state-of-the art bioinformatic analysis, protein modeling, molecular and cellular interaction and functional approaches, culminating with in vivo infection modeling provide convincing, unequivocal evidence that supports the authors claims. This work will be of particular interest to cellular microbiologist working on microbial virulence mechanisms and effectors, specifically nucleomodulins, and cell/cancer biologists that examine COMPASS dysfunction in cancer biology.

Strengths:

(1) The strengths of this study include the rigorous and comprehensive experimental design that involved numerous state-of-the-art approaches to identify potential nucleomodulins, define molecular nucleomodulin-host interactions, cellular nucleomodulin localization, intracellular survival, and inflammatory gene transcriptional responses, and confirmation of the inflammatory and infection phenotype in a small animal model.

(2) The use of bioinformatic, cellular and in vivo modeling that are consistent and support the overall conclusions is a strengthen of the study. In addition, the rigorous experimental design and data analysis including the supplemental data provided, further strengthens the evidence supporting the conclusions.

Weaknesses:

(1) This work could be stronger if the MgdE-COMPASS subunit interactions that negatively impact COMPASS complex function were more well defined. Since the COMPASS complex consists of many enzymes, examining functional impact on each of the components would be interesting.

(2) Examining the impact of WDR5 inhibitors on histone methylation, gene transcription and mycobacterial infection could provide additional rigor and provide useful information related to mechanisms and specific role of WDR5 inhibition on mycobacteria infection.

(3) The interaction between MgdE and COMPASS complex subunit ASH2L is relatively undefined and studies to understand the relationship between WDR5 and ASH2L in COMPASS complex function during infection could provide interesting molecular details that are undefined in this study.

(4) The AlphaFold prediction results for all the nuclear proteins examined could be useful. Since the interaction predictions with COMPASS subunits range from 0.77 for WDR5 and 0.47 for ASH2L, it is not clear how the focus on COMPASS complex over other nuclear proteins was determined.

Comments on revisions:

The authors have addressed the weaknesses that were identified by this reviewer by providing rational explanation and specific references that support the findings and conclusions.

Reviewer #2 (Public review):

Summary:

The manuscript by Chen et al addresses an important aspect of pathogenesis for mycobacterial pathogens, seeking to understand how bacterial effector proteins disrupt the host immune response. To address this question the authors sought to identify bacterial effectors from M. tuberculosis (Mtb) that localize to the host nucleus and disrupt host gene expression as a means of impairing host immune function. Their revised manuscript has strengthened their observations by performing additional experiments with BCG strains expressing tagged MgdE.

Strengths:

The researchers conducted a rigorous bioinformatic analysis to identify secreted effectors containing mammalian nuclear localization signal (NLS) sequences, which formed the basis of quantitative microscopy analysis to identify bacterial proteins that had nuclear targeting within human cells. The study used two complementary methods to detect protein-protein interaction: yeast two-hybrid assays and reciprocal immunoprecipitation (IP). The combined use of these techniques provides strong evidence of interactions between MgdE and SET1 components and suggests the interactions are in fact direct. The authors also carried out rigorous analysis of changes in gene expression in macrophages infected with MgdE mutant BCG. They found strong and consistent effects on key cytokines such as IL6 and CSF1/2, suggesting that nuclear-localized MgdE does in fact alter gene expression during infection of macrophages. The revised manuscript contains additional biochemical analyses of BCG strains expressing tagged MgdE that further supports their microscopy findings.

Weaknesses:

There are some drawbacks in this study that limit the application of the findings to M. tuberculosis (Mtb) pathogenesis. Much of the study relies on transfected/ overexpressed proteins in non-immune cells (HEK293T) or in yeast using 2-hybrid approaches, and pathogenesis is studied using the BCG vaccine strain rather than virulent Mtb. In addition, the magnitude of some of the changes they observe are quite small. However, overall the key findings of the paper - that MgdE interacts with COMPASS and alters gene expression are well-supported.

Comments on revisions:

The authors have performed additional experiments that have addressed several important concerns from the original manuscript and they now include an analysis of BCG strains expressing FLAG-tagged MgdE that supports their model. However here are still a few areas where the data are difficult to interpret or do not support their claims.

Reviewer #3 (Public review):

In this study, Chen L et al. systematically analyzed the mycobacterial nucleomodulins and identified MgdE as a key nucleomodulin in pathogenesis. They found that MgdE enters into host cell nucleus through two nuclear localization signals, KRIR108-111 and RLRRPR300-305, and then interacts with COMPASS complex subunits ASH2L and WDR5 to suppress H3K4 methylation-mediated transcription of pro-inflammatory cytokines, thereby promoting mycobacterial survival.

Comments on revisions:

The authors have adequately addressed previous concerns through additional experimentation. The revised data robustly support the main conclusions, demonstrating that MgdE engages the host COMPASS complex to suppress H3K4 methylation, thereby repressing pro-inflammatory gene expression and promoting mycobacterial survival. This work represents a significant conceptual advance.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

This fundamental study identifies a new mechanism that involves a mycobacterial nucleomodulin manipulation of the host histone methyltransferase COMPASS complex to promote infection. Although other intracellular pathogens are known to manipulate histone methylation, this is the first report demonstrating the specific targeting of the COMPASS complex by a pathogen. The rigorous experimental design using state-of-the art bioinformatic analysis, protein modeling, molecular and cellular interaction, and functional approaches, culminating with in vivo infection modeling, provides convincing, unequivocal evidence that supports the authors' claims. This work will be of particular interest to cellular microbiologists working on microbial virulence mechanisms and effectors, specifically nucleomodulins, and cell/cancer biologists that examine COMPASS dysfunction in cancer biology.

Strengths:

(1) The strengths of this study include the rigorous and comprehensive experimental design that involved numerous state-of-the-art approaches to identify potential nucleomodulins, define molecular nucleomodulin-host interactions, cellular nucleomodulin localization, intracellular survival, and inflammatory gene transcriptional responses, and confirmation of the inflammatory and infection phenotype in a small animal model.

(2) The use of bioinformatic, cellular, and in vivo modeling that are consistent and support the overall conclusions is a strength of the study. In addition, the rigorous experimental design and data analysis, including the supplemental data provided, further strengthen the evidence supporting the conclusions.

Weaknesses:

(1) This work could be stronger if the MgdE-COMPASS subunit interactions that negatively impact COMPASS complex function were better defined. Since the COMPASS complex consists of many enzymes, examining the functional impact on each of the components would be interesting.

We thank the reviewer for this insightful comment. A biochemistry assays could be helpful to interpret the functional impact on each of the components by MgdE interaction. However, the purification of the COMPASS complex could be a hard task itself due to the complexity of the full COMPASS complex along with its dynamic structural properties and limited solubility.

(2) Examining the impact of WDR5 inhibitors on histone methylation, gene transcription, and mycobacterial infection could provide additional rigor and provide useful information related to the mechanisms and specific role of WDR5 inhibition on mycobacterial infection.

We thank the reviewer for the comment. A previous study showed that WIN-site inhibitors, such as compound C6, can displace WDR5 from chromatin, leading to a reduction in global H3K4me3 levels and suppression of immune-related gene expression (Hung et al., Nucleic Acids Res, 2018; Bryan et al., Nucleic Acids Res, 2020). These results closely mirror the functional effects we observed for MgdE, suggesting that MgdE may act as a functional mimic of WDR5 inhibition. This supports our proposed model in which MgdE disrupts COMPASS activity by targeting WDR5, thereby dampening host pro-inflammatory responses.

(3) The interaction between MgdE and COMPASS complex subunit ASH2L is relatively undefined, and studies to understand the relationship between WDR5 and ASH2L in COMPASS complex function during infection could provide interesting molecular details that are undefined in this study.

We thank the reviewer for the comment. In this study, we constructed single and multiple point mutants of MgdE at residues S⁸⁰, D²⁴⁴, and H²⁴⁷ to identify key amino acids involved in its interaction with ASH2L (Figure 5A and B; New Figure S4C). However, these mutations did not interrupt the interaction with MgdE, suggesting that more residues are involved in the interaction.

ASH2L and WDR5 function cooperatively within the WRAD module to stabilize the SET domain and promote H3K4 methyltransferase activity with physiological conditions (Couture and Skiniotis, Epigenetics, 2013; Qu et al., Cell, 2018; Rahman et al., Proc Natl Acad Sci U S A, 2022). ASH2L interacts with RbBP5 via its SPRY domain, whereas WDR5 bridges MLL1 and RbBP5 through the WIN and WBM motifs (Chen et al., Cell Res, 2012; Park et al., Nat Commun, 2019). The interaction status between ASH2L and WDR5 during mycobacterial infection could not be determined in our current study.

(4) The AlphaFold prediction results for all the nuclear proteins examined could be useful. Since the interaction predictions with COMPASS subunits range from 0.77 for WDR5 and 0.47 for ASH2L, it is not clear how the focus on COMPASS complex over other nuclear proteins was determined.

We thank the reviewer for the comment. We employed AlphaFold to predict the interactions between MgdE and the major nuclear proteins. This screen identified several subunits of the SET1/COMPASS complex as high-confidence candidates for interaction with MgdE (Figure S4A). This result is consistent with a proteomic study by Penn et al. which reported potential interactions between MgdE and components of the human SET1/COMPASS complex based on affinity purification-mass spectrometry analysis (Penn et al., Mol Cell, 2018).

Reviewer #2 (Public review):

Summary:

The manuscript by Chen et al addresses an important aspect of pathogenesis for mycobacterial pathogens, seeking to understand how bacterial effector proteins disrupt the host immune response. To address this question, the authors sought to identify bacterial effectors from M. tuberculosis (Mtb) that localize to the host nucleus and disrupt host gene expression as a means of impairing host immune function.

Strengths:

The researchers conducted a rigorous bioinformatic analysis to identify secreted effectors containing mammalian nuclear localization signal (NLS) sequences, which formed the basis of quantitative microscopy analysis to identify bacterial proteins that had nuclear targeting within human cells. The study used two complementary methods to detect protein-protein interaction: yeast two-hybrid assays and reciprocal immunoprecipitation (IP). The combined use of these techniques provides strong evidence of interactions between MgdE and SET1 components and suggests that the interactions are, in fact, direct. The authors also carried out a rigorous analysis of changes in gene expression in macrophages infected with the mgdE mutant BCG. They found strong and consistent effects on key cytokines such as IL6 and CSF1/2, suggesting that nuclear-localized MgdE does, in fact, alter gene expression during infection of macrophages.

Weaknesses:

There are some drawbacks in this study that limit the application of the findings to M. tuberculosis (Mtb) pathogenesis. The first concern is that much of the study relies on ectopic overexpression of proteins either in transfected non-immune cells (HEK293T) or in yeast, using 2-hybrid approaches. Some of their data in 293T cells is hard to interpret, and it is unclear if the protein-protein interactions they identify occur during natural infection with mycobacteria. The second major concern is that pathogenesis is studied using the BCG vaccine strain rather than virulent Mtb. However, overall, the key findings of the paper - that MgdE interacts with SET1 and alters gene expression are well-supported.

We thank the reviewer for the comment. We agree that the ectopic overexpression could not completely reflect a natural status, although these approaches were adopted in many similar experiments (Drerup et al., Molecular plant, 2013; Chen et al., Cell host & microbe, 2018; Ge et al., Autophagy, 2021). Further, the MgdE localization experiment using Mtb infected macrophages will be performed to increase the evidence in the natural infection.

We agree with the reviewer that BCG strain could not fully recapitulate the pathogenicity or immunological complexity of M. tuberculosis infection. We employed BCG as a biosafe surrogate model since it was acceptable in many related studies (Wang et al., Nat Immunol, 2025; Wang et al., Nat Commun, 2017; Péan et al., Nat Commun, 2017; Li et al., J Biol Chem, 2020).

Reviewer #3 (Public review):

In this study, Chen L et al. systematically analyzed the mycobacterial nucleomodulins and identified MgdE as a key nucleomodulin in pathogenesis. They found that MgdE enters into host cell nucleus through two nuclear localization signals, KRIR^108-111 and RLRRPR^300-305, and then interacts with COMPASS complex subunits ASH2L and WDR5 to suppress H3K4 methylation-mediated transcription of pro-inflammatory cytokines, thereby promoting mycobacterial survival. This study is potentially interesting, but there are several critical issues that need to be addressed to support the conclusions of the manuscript.

(1) Figure 2: The study identified MgdE as a nucleomodulin in mycobacteria and demonstrated its nuclear translocation via dual NLS motifs. The authors examined MgdE nuclear translocation through ectopic expression in HEK293T cells, which may not reflect physiological conditions. Nuclear-cytoplasmic fractionation experiments under mycobacterial infection should be performed to determine MgdE localization.

We thank the reviewer for this insightful comment. In the revised manuscript, we addressed this concern by performing nuclear-cytoplasmic fractionation experiments using M. bovis BCG-infected macrophages to assess the subcellular localization of MgdE (New Figure 2F) (Lines 146–155). Nuclear-cytoplasmic fractionation experiments showed that WT MgdE and the NLS single mutants (MgdE^ΔNLS1 and MgdE^ΔNLS2) could be detected both in the cytoplasm and in the nucleus, while the double mutant MgdE^ΔNLS1-2 was detectable only in the cytoplasm. These findings strongly indicate that MgdE is capable of translocating into the host cell nucleus during BCG infection, and that this nuclear localization relies on the dual NLS motifs.

(2) Figure 2F: The authors detected MgdE-EGFP using an anti-GFP antibody, but EGFP as a control was not detected in its lane. The authors should address this technical issue.

We thank the reviewer for this question. In the revised manuscript, we have included the uncropped immunoblot images, which clearly show the EGFP band in the corresponding lane. These have been provided in the New Figure 2E.

(3) Figure 3C-3H: The data showing that the expression of all detected genes in 24 h is comparable to that in 4 h (but not 0 h) during WT BCG infection is beyond comprehension. The issue is also present in Figure 7C, Figure 7D, and Figure S7. Moreover, since Il6, Il1β (pro-inflammatory), and Il10 (anti-inflammatory) were all upregulated upon MgdE deletion, how do the authors explain the phenomenon that MgdE deletion simultaneously enhanced these gene expressions?

We thank the reviewer for the comment. A relative quantification method was used in our qPCR experiments to normalize the WT expression levels in Figure 3C–3H, Figure 7C, 7D, and New Figure S6.

The concurrent induction of both types of cytokines likely represents a dynamic host strategy to fine-tune immune responses during infection. This interpretation is supported by previous studies (Podleśny-Drabiniok et al., Cell Rep, 2025; Cicchese et al., Immunological Reviews, 2018).

(4) Figure 5: The authors confirmed the interactions between MgdE and WDR5/ASH2L. How does the interaction between MgdE and WDR5 inhibit COMPASS-dependent methyltransferase activity? Additionally, the precise MgdE-ASH2L binding interface and its functional impact on COMPASS assembly or activity require clarification.

We thank the reviewer for this insightful comment. We cautiously speculate that the MgdE interaction inhibits COMPASS-dependent methyltransferase activity by interfering with the integrity and stability of the COMPASS complex. Accordingly, we have incorporated the following discussion into the revised manuscript (Lines 303-315):

“The COMPASS complex facilitates H3K4 methylation through a conserved assembly mechanism involving multiple core subunits. WDR5, a central scaffolding component, interacts with RbBP5 and ASH2L to promote complex assembly and enzymatic activity (Qu et al., 2018; Wysocka et al., 2005). It also recognizes the WIN motif of methyltransferases such as MLL1, thereby anchoring them to the complex and stabilizing the ASH2L-RbBP5 dimer (Hsu et al., Cell, 2018). ASH2L further contributes to COMPASS activation by interacting with both RbBP5 and DPY30 and by stabilizing the SET domain, which is essential for efficient substrate recognition and catalysis (Qu et al., Cell, 2018; Park et al., Nat Commun, 2019). Our work shows that MgdE binds both WDR5 and ASH2L and inhibits the methyltransferase activity of the COMPASS complex. Site-directed mutagenesis revealed that residues D²²⁴ and H²⁴⁷ of MgdE are critical for WDR5 binding, as the double mutant MgdE-D²²⁴A/H²⁴⁷A fails to interact with WDR5 and shows diminished suppression of H3K4me3 levels (Figure 5D).”

Regarding the precise MgdE-ASH2L binding interface, we attempted to identify the key interaction site by introducing point mutations into ASH2L. However, these mutations did not disrupt the interaction (Figure 5A and B; New Figure S4C), suggesting that more residues are involved in the interaction.

(5) Figure 6: The authors proposed that the MgdE-regulated COMPASS complex-H3K4me3 axis suppresses pro-inflammatory responses, but the presented data do not sufficiently support this claim. H3K4me3 inhibitor should be employed to verify cytokine production during infection.

We thank the reviewer for the comment. We have now revised the description in lines 220-221 and lines 867-868 "MgdE suppresses host inflammatory responses probably by inhibition of COMPASS complex-mediated H3K4 methylation."

(6) There appears to be a discrepancy between the results shown in Figure S7 and its accompanying legend. The data related to inflammatory responses seem to be missing, and the data on bacterial colonization are confusing (bacterial DNA expression or CFU assay?).

We thank the reviewer for the comment. New Figure S6 specifically addresses the effect of MgdE on bacterial colonization in the spleens of infected mice, which was assessed by quantitative PCR rather than by CFU assay.

We have now revised the legend of New Figure S6 as below (Lines 986-991):

“MgdE facilitates bacterial colonization in the spleens of infected mice. Bacterial colonization was assessed in splenic homogenates from infected mice (as described in Figure 7A) by quantifying bacterial DNA using quantitative PCR at 2, 14, 21, 28, and 56 days post-infection.”

(7) Line 112-116: Please provide the original experimental data demonstrating nuclear localization of the 56 proteins harboring putative NLS motifs.

We thank the reviewer for the comment. We will provide this data in the New Table S3.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

There are a few concerns about specific experiments:

Major Comments:

(1) Questions about the exact constructs used in their microscopy studies and the behavior of their controls. GFP is used as a negative control, but in the data they provide, the GFP signal is actually nuclear-localized (for example, Figure 1c, Figure 2a). Later figures do show other constructs with clear cytoplasmic localization, such as the delta-NLS-MgdE-GFP in Figure 2D. This raises significant questions about how the microscopy images were analyzed and clouds the interpretation of these findings. It is also not clear if their microscopy studies use the mature MdgE, lacking the TAT signal peptide after signal peptidase cleavage (the form that would be delivered into the host cell) or if they are transfecting the pro-protein that still has the TAT signal peptide (a form that would present in the bacterial cell but that would not be found in the host cell). This should be clarified, and if their construct still has the TAT peptide, then key findings such as nuclear localization and NLS function should be confirmed with the mature protein lacking the signal peptide.

We thank the reviewer for this question.  EGFP protein can passively diffuse through nuclear pores due to its smaller size (Petrovic et al., Science, 2022; Yaseen et al., Nat Commun, 2015; Bhat et al., Nucleic Acids Res, 2015). However, upon transfection with EGFP-tagged wild-type MdgE and its NLS deletion mutants (MdgE^ΔNLS1, MdgE^ΔNLS2, and MdgE^ΔNLS1-2), we observed significantly stronger nuclear fluorescence in cells expressing wild-type MdgE compared to the EGFP protein. Notably, the MdgE^ΔNLS1-2-EGFP mutant showed almost no detectable nuclear fluorescence (Figure 2C, D, and E). These results indicate that (i) MdgE-EGFP fusion protein could not enter the nucleus by passive diffusion, and (ii) EGFP does not interfere with the nuclear targeting ability of MdgE.

We did not construct a signal peptide-deleted MgdE for transfection assays. Instead, we performed an infection experiment using recombinant M. bovis BCG strains expressing Flag-tagged wild-type MgdE. The mature MgdE protein (signal peptide cleaved) can be detected in the nucleus fractionation (New Figure 2F), suggesting that the signal peptide does not play a role for the nuclear localization of MgdE.

(2) The localization of MdgE is not shown during actual infection. The study would be greatly strengthened by an analysis of the BCG strain expressing their MdgE-FLAG construct.

We thank the reviewer for the comment. In the revised manuscript, we constructed M. bovis BCG strains expressing FLAG-tagged wild-type MdgE as well as NLS deletion mutants (MdgE^ΔNLS1, MdgE^ΔNLS2, and MdgE^ΔNLS1-2). These strains were used to infect THP-1 cells, and nuclear-cytoplasmic fractionation was performed 24 hours post-infection.

Nuclear-cytoplasmic fractionation experiments showed that WT MgdE and the NLS single mutants could be detected both in the cytoplasm and in the nucleus by immunoblotting, while the double mutant MgdE^ΔNLS1-2 was detectable only in the cytoplasm (New Figure 2F) (Lines 146–155). These findings indicate that MdgE is capable of entering the host cell nucleus during BCG infection, and that this nuclear localization depends on the presence of both its N-terminal and C-terminal NLS motifs.

(3) Their pathogenesis studies suggesting a role for MdgE would be greatly strengthened by studying MdgE in virulent Mtb rather than the BCG vaccine strain. If this is not possible because of technical limitations (such as lack of a BSL3 facility), then at least a thorough discussion of studies that examined Rv1075c/MdgE in Mtb is important. This would include a discussion of the phenotype observed in a previously published study examining the Mtb Rv1075c mutant that showed a minimal phenotype in mice (PMID: 31001637) and would also include a discussion of whether Rv1075c was identified in any of the several in vivo Tn-Seq studies done on Mtb.

We thank the reviewer for this insightful comment. In the revised manuscript, we have incorporated a more thorough discussion of prior studies that examined Rv1075c/MgdE in Mtb, including the reported minimal phenotype of an Mtb MgdE mutant in mice (PMID: 31001637) (Lines 288–294).

In the latest TnSeq studies in M. tuberculosis, Rv1075c/MgdE was not classified as essential for in vivo survival or virulence (James et al., NPJ Vaccines, 2025; Zhang et al., Cell, 2013). However, this absence should not be interpreted as evidence of dispensability since these datasets also failed to identify some well characterized virulence factors including Rv2067c (Singh et al., Nat Commun, 2023), PtpA (Qiang et al., Nat Commun, 2023), and PtpB (Chai et al., Science, 2022) which were demonstrated to be required for the virulence of Mtb.

Minor Comments:

(1) Multiple figures with axes with multiple discontinuities used when either using log-scale or multiple graphs is more appropriate, including 3B, 7A.

We sincerely thank the reviewer for pointing this out. In the revised manuscript, we have updated Figure 3B and Figure 7A.

(2) Figure 1C - Analysis of only nuclear MFI can be very misleading because it is affected by the total expression of each construct. Ratios of nuclear to cytoplasmic MFI are a more rigorous analysis.

We thank the reviewer for this comment. We agree that analyzing the ratio of nuclear to cytoplasmic mean fluorescence intensity (MFI) provides a more rigorous quantification of nuclear localization, particularly when comparing constructs with different expression levels. However, the analysis presented in Figure 1C was intended as a preliminary qualitative screen to identify Tat/SPI-associated proteins with potential nuclear localization, rather than a detailed quantitative assessment.

(3) Figure 5C - Controls missing and unclear interpretation of their mutant phenotype. There is no mock or empty-vector control transfection, and their immunoblot shows a massive increase in total cellular H3K4me3 signal in the bulk population, although their prior transfection data show only a small fraction of cells are expressing MdgE. They also see a massive increase in methylation in cells transfected with the inactive mutant, but the reason for this is unclear. Together, these data raise questions about the specificity of the increasing methylation they observe. An empty vector control should be included, and the phenotype of the mutant explained.

We thank the reviewer for this comment. In the revised manuscript, we transfected HEK293T cells with an empty EGFP vector and performed a quantitative analysis of H3K4me3 levels. The results demonstrated that, at the same time point, cells expressing MdgE showed significantly lower levels of H3K4me3 compared to both the EGFP control and the catalytically inactive mutant MdgE (D²⁴⁴A/H²⁴⁷A) (New Figure 5D) (Lines 213–216). These findings support the conclusion that MdgE specifically suppresses H3K4me3 levels in cells.

(4) Figure S1A - The secretion assay is lacking a critical control of immunoblotting a cytoplasmic bacterial protein to demonstrate that autolysis is not releasing proteins into the culture filtrate non-specifically - a common problem with secretion assays in mycobacteria.

We thank the reviewer for this comment. To address the concerns, we examined FLAG-tagged MgdE and the secreted antigen Ag85B in the culture supernatants by monitoring the cytoplasmic protein GlpX. The absence of GlpX in the supernatant confirmed that there was no autolysis in the experiment. We could detect MgdE-Flag in the culture supernatant (New Figure S2A), indicating that MgdE is a secreted protein.

(5) The volcano plot of their data shows that the proteins with the smallest p-values have the smallest fold-changes. This is unusual for a transcriptomic dataset and should be explained.

We thank the reviewer for this comment. We are not sure whether the p-value is correlated with fold-change in the transcriptomic dataset. This is probably case by case.

Reviewer #3 (Recommendations for the authors):

There are several minor comments:

(1) Line 104-109: The number of proteins harboring NLS motifs and candidate proteins assigned to the four distinct pathways does not match the data presented in Table S2. Please recheck the details. Figure 1A and B, as well as Figure S1A and B, should also be corrected accordingly.

We thank the reviewer for the comment. We have carefully checked the details and the numbers were confirmed and updated.

(2) Please add the scale bar in all image figures, including Figure 1C, Figure 2D, Figure 5C, Figure 7B, and Figure S2.

We thank the reviewer for this suggestion. We have now added scale bars to all relevant image figures in the revised manuscript, including Figure 1C, New Figure 2C, Figure 5C, Figure 7B, and New Figure S2B.

(3) Please add the molecular marker in all immunoblotting figures, including Figure 2C, Figure 2F, Figure 4B, Figure 4C, Figure 5B, Figure 5D, and Figure S5.

We thank the reviewer for this suggestion. We have now added the molecular marker in all immunoblotting figures in the revised manuscript, including New Figure 2E–F, Figure 4B–C, Figure 5B and D, Figure S2A, New Figure S2E and New Figure S4C.

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eLife Assessment

This work describes a useful computational tool for automated morphometry of dynamic organelles from microscope images. However, the supporting evidence and novelty of the manuscript as presented are incomplete and could be improved. The work will be of interest to microscopists and bioimage analysts who are non-experts but wish to improve quantitative analysis of cellular structures.

Reviewer #1 (Public review):

Summary:

The authors develop a Python-based analysis framework for cellular organelle segmentation, feature extraction, and analysis for live-cell imaging videos. They demonstrate that their pipeline works for two organelles (mitochondria and lysosomes) and provide a step-by-step overview of the AutoMorphoTrack package.

Strengths:

The authors provide evidence that the package is functional and can provide publication-quality data analysis for mitochondrial and lysosomal segmentation and analysis.

Weaknesses:

(1) I was enthusiastic about the manuscript as a good end-to-end cell/organelle segmentation and quantification pipeline that is open-source, and is indeed useful to the field. However, I'm not certain AutoMorphoTrack fully fulfills this need. It appears to stitch together basic FIJI commands in a Python script that an experienced user can put together within a day. The paper reads as a documentation page, and the figures seem to be individual analysis outputs of a handful of images. Indeed, a recent question on the image.sc forum prompted similar types of analysis and outputs as a simple service to the community, and with seemingly better results and integrated organelle identity tracking (which is necessary in my opinion for live imaging). I believe this is a better fit in the methods section of a broader work. https://forum.image.sc/t/how-to-analysis-organelle-contact-in-fiji-with-time-series-data/116359/5.

(2) The authors do not discuss or compare to any other pipelines that can accomplish similar analyses, such as Imaris, CellProfiler, or integrate options for segmentation, etc., such as CellPose, StarDist.

(3) Although LLM-based chatbot integration seems to have been added for novelty, the authors do not demonstrate in the manuscript, nor provide instructions for making this easy-to-implement, given that it is directed towards users who do not code, presumably.

Reviewer #2 (Public review):

Summary:

AutoMorphoTrack provides an end-to-end workflow for organelle-scale analysis of multichannel live-cell fluorescence microscopy image stacks. The pipeline includes organelle detection/segmentation, extraction of morphological descriptors (e.g., area, eccentricity, "circularity," solidity, aspect ratio), tracking and motility summaries (implemented via nearest-neighbor matching using cKDTree), and pixel-level overlap/colocalization metrics between two channels. The manuscript emphasizes a specific application to live imaging in neurons, demonstrated on iPSC-derived dopaminergic neuronal cultures with mitochondria in channel 0 and lysosomes in channel 1, while asserting adaptability to other organelle pairs.

The tool is positioned for cell biologists, including users with limited programming experience, primarily through two implemented modes of use: (i) a step-by-step Jupyter notebook and (ii) a modular Python package for scripted or batch execution, alongside an additional "AI-assisted" mode that is described as enabling analyses through natural-language prompts.

The motivation and general workflow packaging are clear, and the notebook-plus-modules structure is a reasonable engineering choice. However, in its current form, the manuscript reads more like a convenient assembly of standard methods than a validated analytical tool. Key claims about robustness, accuracy, and scope are not supported by quantitative evidence, and the 'AI-assisted' framing is insufficiently defined and attributes to the tool capabilities that are provided by external LLM platforms rather than by AutoMorphoTrack itself. In addition, several figure, metric, and statistical issues-including physically invalid plots and inconsistent metric definitions-directly undermine trust in the quantitative outputs.

Strengths:

(1) Clear motivation: lowering the barrier for organelle-scale quantification for users who do not routinely write custom analysis code.

(2) Multiple entry points: an interactive notebook together with importable modules, emphasizing editable parameters rather than a fully opaque black box.

(3) End-to-end outputs: automated generation of standardized visualizations and tables that, if trustworthy, could help users obtain quantitative summaries without assembling multiple tools.

Weaknesses:

(1) "AI-assisted / natural-language" functionality is overstated.

The manuscript implies an integrated natural-language interface, but no such interface is implemented in the software. Instead, users are encouraged to use external chatbots to help generate or modify Python code or execute notebook steps. This distinction is not made clearly and risks misleading readers.

(2) No quantitative validation against trusted ground truth.

There is no systematic evaluation of segmentation accuracy, tracking fidelity, or interaction/overlap metrics against expert annotations or controlled synthetic data. Without such validation, accuracy, parameter sensitivity, and failure modes cannot be assessed.

(3) Limited benchmarking and positioning relative to existing tools.

The manuscript does not adequately compare AutoMorphoTrack to established platforms that already support segmentation, morphometrics, tracking, and colocalization (e.g., CellProfiler) or to mitochondria-focused toolboxes (e.g., MiNA, MitoGraph, Mitochondria Analyzer). This is particularly problematic given the manuscript's implicit novelty claims.

(4) Core algorithmic components are basic and likely sensitive to imaging conditions.

Heavy reliance on thresholding and morphological operations raises concerns about robustness across varying SNR, background heterogeneity, bleaching, and organelle density; these issues are not explored.

(5) Multiple figure, metric, and statistical issues undermine confidence.

The most concerning include:<br /> (i) "Circularity (4πA/P²)" values far greater than 1 (Figures 2 and 7, and supplementary figures), which is inconsistent with the stated definition and strongly suggests a metric/label mismatch or computational error.

(ii) A displacement distribution extending to negative values (Figure 3B). This is likely a plotting artifact (e.g., KDE boundary bias), but as shown, it is physically invalid and undermines confidence in the motility analysis.

(iii) Colocalization/overlap metrics that are inconsistently defined and named, with axis ranges and terminology that can mislead (e.g., Pearson r reported for binary masks without clarification).

(iv) Figure legends that do not match the displayed panels, and insufficient reporting of Ns, p-values, sampling units, and statistical assumptions.

Reviewer #3 (Public review):

Summary:

AutoMorphoTrack is a Python package for quantitatively evaluating organelle shape, movement, and colocalization in high-resolution live cell imaging experiments. It is designed to be a beginning-to-end workflow from segmentation through metric graphing, which is easy to implement. The paper shows example results from their images of mitochondria and lysosomes within cultured neurons, demonstrating how it can be used to understand organelle processing.

Strengths:

The text is well-written and easy to follow. I particularly appreciate tables 1 and 2, which clearly define the goals of each module, the tunable parameters, and the input and outputs. I can see how the provided metrics would be useful to other groups studying organelle dynamics. Additionally, because the code is open-source, it should be possible for experienced coders to use this as a backbone and then customize it for their own purposes.

Weaknesses:

Unfortunately, I was not able to install the package to test it myself using any standard install method. This is likely fixable by the authors, but until a functional distribution exists, the utility of this tool is highly limited. I would be happy to re-review this work after this is fixed.

The authors claim that there is "AI-Assisted Execution and Natural-Language Interface". However, this is never defended in any of the figures, and from quickly reviewing the .py files, there does not seem to be any built-in support or interface for this. Without significantly more instructions on how to connect this package to a (free) LLM, along with data to prove that this works reproducibly to produce equivalent results, this section should be removed.

Additionally, I have a few suggestions/questions:

(1) Red-green images are difficult for colorblind readers. I recommend that the authors change all raw microscopy images to a different color combination.

(2) For all of the velocity vs displacement graphs (Figure 3C and subpart G of every supplemental figure), there is a diagonal line clearly defining a minimum limit of detected movement. Is this a feature of the dataset (drift /shakiness /etc) or some sort of minimum movement threshold in the tracking algorithm? This should be discussed in the text.

(3) Integrated Correlation Summary (Figure 5) - Pearson is likely the wrong metric for most of these metric pairs because even interesting relationships may be non-linear. Please replace with Spearman correlation, which is less dependent on linearity.

Author response:

Reviewer #1

We thank the reviewer for their thoughtful and constructive assessment of AutoMorphoTrack and for recognizing its potential utility as an open-source end-to-end workflow for organelle analysis.

(1) Novelty and relationship to existing tools / FIJI workflows

We appreciate this concern and agree that many of the underlying image-processing operations (e.g., thresholding, morphological cleanup, region properties) are well-established. Our goal with AutoMorphoTrack is not to introduce new segmentation algorithms, but rather to provide a curated, reproducible, and extensible end-to-end workflow that integrates segmentation, morphology, tracking, motility, and colocalization into a single, transparent pipeline tailored for live-cell organelle imaging.

While an experienced user could assemble similar analyses ad hoc using FIJI or custom scripts, our contribution lies in:

Unifying these steps into a single workflow with consistent parameterization and outputs

Generating standardized, publication-ready visualizations and tables at each step,

Enabling batch and longitudinal analyses across cells and conditions, and

Lowering the barrier for users who do not routinely write custom analysis code.

We note that the documentation-style presentation of the manuscript is intentional, as it serves both as a methods paper and a practical reference for users implementing the workflow. We agree, however, that the manuscript currently overemphasizes step-by-step execution at the expense of positioning. In revision, we will more explicitly frame AutoMorphoTrack as a workflow integration and usability contribution, rather than a fundamentally new algorithmic advance.

We will also cite and discuss the image.sc example referenced by the reviewer, clarifying conceptual overlap and differences in scope.

(2) Comparison to existing pipelines (Imaris, CellProfiler, CellPose, StarDist)

We agree and thank the reviewer for highlighting this omission. In the revised manuscript, we will expand the related-work and positioning section to explicitly compare AutoMorphoTrack with established commercial (e.g., Imaris) and open-source (e.g., CellProfiler, MiNA, MitoGraph) platforms, as well as learning-based segmentation tools such as CellPose and StarDist.

Rather than claiming superiority, we will clarify trade-offs, emphasizing that AutoMorphoTrack prioritizes:

Transparency and parameter interpretability,

Lightweight dependencies suitable for small live-imaging datasets

Direct integration of morphology, tracking, and colocalization in a single workflow, and

Ease of modification for domain-specific use cases.

(3) AI / chatbot integration

We appreciate this critique and agree that the current description is insufficiently precise. AutoMorphoTrack does not implement a native natural-language interface. Instead, our intent was to convey that the workflow can be executed and modified with assistance from external large language models (LLMs) in a notebook-based environment.

In revision, we will revise this section to:

Clearly distinguish AutoMorphoTrack’s functionality from that of external LLM tools,

Remove any implication of a built-in AI interface, and

Provide concrete, reproducible examples of how non-coding users may interact with the pipeline using natural-language prompts mediated by external tools.

Reviewer #2

We thank the reviewer for their detailed and technically rigorous evaluation. We appreciate the recognition of the workflow’s motivation and structure, and we agree that several aspects of validation, positioning, and quantitative reporting must be strengthened.

(1) AI-assisted / natural-language functionality

We agree with this critique. AutoMorphoTrack does not provide a native natural-language execution layer, and the manuscript currently overstates this aspect. In revision, we will explicitly scope any reference to AI assistance as external, optional support for code generation and parameter editing, with clearly documented examples and stated limitations.

We agree that conflating external LLM capabilities with the software itself risks misleading readers, and we will correct this accordingly.

(2) Lack of quantitative validation

We fully agree that the current manuscript lacks formal quantitative validation. In the revised version, we will add a dedicated validation section including:

Segmentation accuracy compared to expert annotations using overlap metrics (e.g., Dice / IoU),

Tracking fidelity assessed using manually annotated tracks and/or synthetic ground truth,

Sensitivity analyses for key parameters (e.g., thresholding and linking distance), and

Explicit discussion of failure modes and quality-control indicators.

We acknowledge that without such validation, claims of robustness are not sufficiently supported.

(3) Benchmarking and positioning relative to existing tools

We agree and will substantially strengthen AutoMorphoTrack’s benchmarking and positioning relative to existing platforms. Rather than framing novelty algorithmically, we will clarify that the primary contribution is a reproducible, integrated workflow designed specifically for two-organelle live imaging in neurons, with transparent parameters and standardized outputs.

We note that our goal is not to exhaustively benchmark against all available tools, but rather to provide representative comparisons that clarify operating regimes, assumptions, and trade-offs. We will add a comparative table and/or qualitative comparison highlighting strengths, assumptions, and limitations relative to existing tools.

(4) Core algorithms and robustness

We agree that reliance on threshold-based segmentation introduces sensitivity to imaging conditions. In revision, we will:

Explicitly discuss the operating regime and assumptions under which AutoMorphoTrack performs reliably,

Clarify that the framework is modular and can accept alternative segmentation backends, and

Include guidance on when outputs should be treated with caution.

(5) Figure, metric, and statistical issues

We thank the reviewer for identifying several critical issues and agree that these undermine confidence. In revision, we will correct all figure, metric-definition, and reporting inconsistencies, including:

Resolving circularity values exceeding 1 by correcting computation and/or labeling errors,

Revising physically invalid displacement plots and clarifying kernel-density limitations,

Ensuring colocalization metrics are consistently defined, named, and interpreted, with explicit clarification of whether calculations are intensity- or mask-based,

Correcting figure legends to match displayed panels, and

Clearly reporting sample size, sampling units, and statistical assumptions, including handling of multiple comparisons where applicable.

(6) Value-added demonstration

We agree that the manuscript would benefit from a clearer demonstration of value-added use cases. In revision, we will include at least one realistic example showing how AutoMorphoTrack enables a complete, reproducible analysis workflow with reduced setup burden compared to manually assembling multiple tools.

(7) Editorial suggestions

We agree and will streamline the Results section to reduce procedural repetition and focus more on validation, limitations, and quality-control guidance.

Reviewer #3

We thank the reviewer for their positive assessment of clarity and organization, and for the constructive practical feedback.

Installation issues

We appreciate the detailed report of installation failures and acknowledge that the current packaging and distribution are inadequate. Prior to revision, we will:

Fix the package structure to support standard installation methods,

Ensure all required files (e.g., setup configuration, README) are correctly included,

Test installation on clean environments across platforms, and

Correct broken links to notebooks and documentation.

We agree that without a functional installation pathway, the utility of the tool is severely limited.

AI-assisted claims

We agree with the reviewer and echo our responses above. The AI-assisted description will be clarified and appropriately scoped in the revised manuscript.

Additional suggestions

Color accessibility: We will revise all figures to use colorblind-safe palettes.

Velocity–displacement diagonal: We will explicitly explain the origin of this relationship, including whether it reflects dataset properties, tracking assumptions, or minimum detectable motion.

Integrated correlation metric: We agree that Spearman correlation is more appropriate for many of these relationships and will replace Pearson correlations accordingly.

Supplementary movies: We agree that providing raw movies would improve interpretability and will add representative examples as supplementary material.

eLife Assessment

This important study by Bartas and colleagues examined how patterns of monosynaptic input to specific cell types in the ventral tegmental area are altered by drugs of abuse. The authors applied a dimensionality reduction approach (principal component analysis) and showed that various drugs of abuse, and somewhat surprisingly the anesthesia alone (ketamine/xylasin), caused changes in the distribution of inputs labeled by the transsynaptic rabies virus. The evidence supporting the conclusions is overall convincing and provides foundational information, as well as a cautionary note on the interpretation of rabies virus-based tracing experiments.

Reviewer #1 (Public review):

Summary:

In this study, the authors mapped afferent inputs to distinct cell populations in the ventral tegmental area (VTA) using dimensionality reduction techniques, revealing markedly different connectivity patterns under normal versus drug-treated conditions. They further showed that drug-induced changes in inputs were negatively correlated with the expression of ion channels and proteins involved in synaptic transmission. Functional validation demonstrated that knockdown of a specific voltage-gated calcium channel led to reduced afferent inputs, highlighting a causal link between gene expression and connectivity.

The authors have clearly addressed the reviewers' previous comments. The study's earlier weaknesses were thoroughly discussed, and additional data were provided to strengthen the findings. Overall, the revised version incorporates more extensive datasets and analyses, resulting in a more robust and compelling study.

Reviewer #2 (Public review):

The application of rabies virus (RabV)-mediated transsynaptic tracing has been widely utilized for mapping cell-type-specific neural connectivities and examining potential modifications in response to biological phenomena or pharmacological interventions. Despite the predominant focus of studies on quantifying and analyzing labeling patterns within individual brain regions based on labeling abundance, such an approach may inadvertently overlook systemic alterations. There exists a considerable opportunity to integrate RabV tracing data with the global connectivity patterns and the transcriptomic signatures of labeled brain regions. In the present study, the authors take an important step towards achieving these objectives.

Specifically, the authors conducted an intensive reanalysis of a previously generated large dataset of RabV tracing to the ventral tegmental area (VTA) using dimension reduction methods such as PCA and UMPA. This reaffirmed the authors's earlier conclusion that different cell types in the VTA, namely dopamine neurons (DA) and GABAergic neurons, exhibit quantitatively distinct input patterns, and a single dose of addictive drugs, such as cocaine and morphine, induced altered labeling patterns. Additionally, the authors illustrate that distinct axes of PCA can discriminate experimental variations, such as minor differences in the injection site of viral tracers, from bona fide alterations in labeling patterns caused by drugs of abuse. While the specific mechanisms underlying altered labeling in most brain regions remain unclear, whether involving synaptic strength, synaptic numbers, pre-synaptic activities, or other factors, the present study underscores the efficacy of an informatics approach in extracting more comprehensive information from the RabV-based circuit mapping data.

Moreover, the authors showcased the utility of their previously devised bulk gene expression patterns inferred by the Allen Gene Expression Atlas (AGEA) and "projection portrait" derived from bulk axon mapping data sourced from the Allen Mouse Brain Connectivity Atlas. The utilization of such bulk data rests upon several limitations. For instance, the collection of axon mapping data involves an arbitrary selection of both cell type-specific and non-specific data, which might overlook crucial presynaptic partners, and often includes contamination from neighboring undesired brain regions. Concerns arise regarding the quantitativeness of AGEA, which may also include the potential oversight of key presynaptic partners. Nevertheless, the authors conscientiously acknowledged these potential limitations associated with the dataset.

Notably, building on the observation of a positive correlation between the basal expression levels of Ca2+ channels and the extent of drug-induced changes in RabV labeling patterns, the authors conducted a CRISPRi-based knockdown of a single Ca2+ channel gene. This intervention resulted in a reduction of RabV labeling, supporting that the observed gene expression patterns have causality in RabV labeling efficiency. While a more nuanced discussion is necessary for interpreting this result (see below), overall I commend the authors for their efforts to leverage the existing dataset in a more meaningful way. This endeavor has the potential to contribute significantly to our understanding of the mechanisms underlying alterations in RabV labeling induced by drugs of abuse.

Finally, drawing upon the aforementioned reanalysis of previous data, the authors underscored that a single administration of ketamine/xylazine anesthesia could induce enduring modifications in RabV labeling patterns for VTA DA neurons, specifically those projecting to the nucleus accumbens and amygdala. Given the potential impact of such alterations on motivational behaviors at a broader level, I fully agree that prudent consideration is warranted when employing ketamine/xylazine for the investigation of motivational behaviors in mice.

Comments on revisions:

In the re-revised version, the authors have addressed all of my previous comments. I no longer have any major concerns.

Reviewer #3 (Public review):

Summary:

Authors mapped monosynaptic inputs to dopamine, GABA, and glutamate neurons in the ventral tegmental area (VTA) under different anesthesia methods, and under drug (cocaine, morphine, methamphetamine, amphetamine, nicotine, fluoxetine). First, they propose an analysis method to separate the actual manipulation effects from the variability caused by experimental procedures. Using this method, they found differences in the anatomical location of monosynaptic inputs to dopamine neurons under different conditions, and identified some key brain areas for such separation. They also searched the database for gene expression patterns that are common across input brain areas, with some changes by anesthesia or drug administration.

Strengths:

The whole-brain approach to address drug effects is appealing, and their conclusion is clear. The methodology and motivation are clearly explained.

Weaknesses:

While gene expression analyses may not be related to their findings on the anatomical effects of drugs, this is a nice starting point for follow-up studies.

Author response:

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

Public Reviews:

Reviewer #1(Public review):

Summary:

In this study, the authors distinguished afferent inputs to different cell populations in the VTA using dimensionality reduction approaches and found significantly distinct patterns between normal and drug treatment conditions. They also demonstrated negative correlations of the inputs induced by drugs with gene expression of ion channels or proteins involved in synaptic transmission and demonstrated the knockdown of one of the voltage-gated calcium ion channels caused decreased inputs.

Weaknesses:

(1) For quantifications of brain regions in this study, boundaries were based on the Franklin-Paxinos (FP) atlas according to previous studies (Beier KT et al 2015, Beier KT et al 2019). It has been reported significant discrepancies exist between the anatomical labels on the FP atlas and the Allen Brain Atlas (ref: Chon U et al., Nat Commun 2019). Although a summary of conversion is provided as a sheet, the authors need to describe how consistent or different the brain boundaries they defined in the manuscript with Allen Brain Atlas by adding histology images. Also, I wonder how reliable the annotations were for over a hundred of animals with manual quantification. The authors should briefly explain it rather than citing previous studies in the Material and Methods Section.

We thank the reviewer for attention to this point; indeed, neuroanatomical detail is often overlooked in modern neuroscience, occasionally leading to spurious conclusions. We acknowledge that there are significant discrepancies in brain region definitions across atlases, which can make cross-study comparisons difficult. Here, all cells were manually quantified by Dr. Kevin Beier, as in previous studies (Beier et al., Cell 2015; Nature 2017; Cell Reports 2019; Tian et al., Cell Reports 2022; Tian et al., Neuron 2024; Hubbard et al., Neuropsychopharmacology, 2025). As such, these studies are internally consistent as relates to the definition of brain regions, which is critical here since our analysis in this manuscript relates to data quantified only by a single individual. Several brain regions were quite easy to distinguish anatomically, such as the medial habenula and lateral habenula. Others, such as the extended amygdala area, are much more difficult. We have now provided example images in Figure S1 that detail the anatomical boundaries that we used, overlayed on images of Neurotrace blue (fluorescent Nissl stain).

(2) Regarding the ellipsoids in the PC, although it's written in the manuscript that "Ellipsoids were centered at the average coordinate of a condition and stretched one standard deviation along the primary and secondary axes", it's intuitively hard to understand in some figures such as Figure 2O, P and Figure S1. The authors need to make their data analysis methods more accessible by providing source code to the public.

The source code is now available to the public at https://github.com/ktbartas/Bartas_et_al_eLife_2024, which is noted in the Code Availability statement. The code for generating ellipsoids is in the first notebook, `0-dataexploration-master-euclidean.ipynb`, in the function `confidence_ellipse`, which is called from `make_pca_plots` and `umap_and_heatmap`. Example plots are all live in the notebooks as can be viewed directly from GitHub.

(3) In histology images (Figure 1B and 3K), the authors need to add dashed lines or arrows to guide the reader's attention.

Dashed lines have been added to these figure panels as requested.

(4) In Figure 2A and G, apparently there are significant differences in other brain regions such as NAcMed or PBN. If they are also statistically significant, the authors should note them as well and draw asterisks(*).

We appreciate the care in ensuring that statistics are being applied and shown appropriately. In panel A (now Figure 3A), the Two-way ANOVA interaction term was not significant (p = 0.9365), we did not find it justified to do further comparisons. However, for Figure 3G, the interaction term was significant (p = 0.0001), and thus further pairwise comparisons were performed with Sidak's correction for multiple comparisons. When done, the only two brain regions that were significantly different were the DStr (p = 0.0051) and GPe (p = 0.0036). While the NAcMed and PBN visually look different, according to the corrected statistics, they were not significantly different (NAcMed p = 0.5037, PBN p = 0.8123). The notations in our original figure thus accurately reflected these statistics.

(5) In Figure 2N about the spatial distribution of starter cells, the authors need to add histology images for each experimental condition (i.e. saline, fluoxetine, cocaine, methamphetamine, amphetamine, nicotine, and morphine) as supplement figures

We have now provided these as Figure S2.

(6) In the manuscript, it is necessary to explain why Cacna1e was selected among other calcium ion channels.

We have added a sentence to the "Functional validation of link between gene expression and RABV labeling" section (lines 722-724).

Reviewer #2 (Public review):

The application of rabies virus (RabV)-mediated transsynaptic tracing has been widely utilized for mapping celltype-specific neural connectivities and examining potential modifications in response to biological phenomena or pharmacological interventions. Despite the predominant focus of studies on quantifying and analyzing labeling patterns within individual brain regions based on labeling abundance, such an approach may inadvertently overlook systemic alterations. There exists a considerable opportunity to integrate RabV tracing data with the global connectivity patterns and the transcriptomic signatures of labeled brain regions. In the present study, the authors take an important step towards achieving these objectives. Specifically, the authors conducted an intensive reanalysis of a previously generated large dataset of RabV tracing to the ventral tegmental area (VTA) using dimension reduction methods such as PCA and UMPA. This reaffirmed the authors' earlier conclusion that different cell types in the VTA, namely dopamine neurons (DA) and GABAergic neurons, exhibit quantitatively distinct input patterns, and a single dose of addictive drugs, such as cocaine and morphine, induced altered labeling patterns. Additionally, the authors illustrate that distinct axes of PCA can discriminate experimental variations, such as minor differences in the injection site of viral tracers, from bona fide alternations in labeling patterns caused by drugs of abuse. While the specific mechanisms underlying altered labeling in most brain regions remain unclear, whether involving synaptic strength, synaptic numbers, pre-synaptic activities, or other factors, the present study underscores the efficacy of an informatics approach in extracting more comprehensive information from the RabV-based circuit mapping data. Moreover, the authors showcased the utility of their previously devised bulk gene expression patterns inferred by the Allen Gene Expression Atlas (AGEA) and "projection portrait" derived from bulk axon mapping data sourced from the Allen Mouse Brain Connectivity Atlas. The utilization of such bulk data rests upon several limitations. For instance, the collection of axon mapping data involves an arbitrary selection of both cell type-specific and non-specific data, which might overlook crucial presynaptic partners, and often includes contamination from neighboring undesired brain regions. Concerns arise regarding the quantitativeness of AGEA, which may also include the potential oversight of key presynaptic partners. Nevertheless, the authors conscientiously acknowledged these potential limitations associated with the dataset. Notably, building on the observation of a positive correlation between the basal expression levels of Ca2+ channels and the extent of drug-induced changes in RabV labeling patterns, the authors conducted a CRISPRi-based knockdown of a single Ca2+ channel gene. This intervention resulted in a reduction of RabV labeling, supporting that the observed gene expression patterns have causality in RabV labeling efficiency. While a more nuanced discussion is necessary for interpreting this result (see below), overall I commend the authors for their efforts to leverage the existing dataset in a more meaningful way. This endeavor has the potential to contribute significantly to our understanding of the mechanisms underlying alterations in RabV labeling induced by drugs of abuse. Finally, drawing upon the aforementioned reanalysis of previous data, the authors underscored that a single administration of ketamine/xylazine anesthesia could induce enduring modifications in RabV labeling patterns for VTA DA neurons, specifically those projecting to the nucleus accumbens and amygdala. Given the potential impact of such alterations on motivational behaviors at a broader level, I fully agree that prudent consideration is warranted when employing ketamine/xylazine for the investigation of motivational behaviors in mice.

Specific Points:

(1) Beyond advancements in bioinformatics, readers may find it insightful to explore whether the PCA/UMPAbased approach yields novel biological insights. For example, the authors are encouraged to discuss more functional implications of PBN and LH in the context of drugs of abuse, as their labeling abundance could elucidate the PC2 axis in Fig. 2M.

Thank you for this suggestion: we added text (Lines 787-795) discussing the LH and PBN (and GPe) specifically, but also highlighted the importance of our approach in hypothesis-generating science.

(2) While I appreciate the experimental data on Cacna1e knockdown, I am unclear about the rationale behind specifically focusing on Cacna1e. The logic behind the statement, "This means that expression of this gene is not inhibitory towards RABV transmission," is also unclear. Loss-of-function experiments only signify the necessity or permissive functions of a gene. In this context, Cacna1e expression levels are required for efficient RabV labeling, but this neither supports nor excludes the possibility that this gene expression instructively suppresses RabV labeling/transmission, which could be assessed through gain-of-function experiments.

We thank the reviewer for their suggestions regarding this result, and agree that a gain-of-function would be required to provide clearer evidence on this point.  We therefore understand that our original phrasing may be misleading. Thus, we have edited this section to the more conservative statement: “These results indicate that reduced levels of Cacna1e likely lower the number of RABV-labeled inputs from the NAcLat, and directly link the levels of Cacna1e and RABV input labeling” (lines 742-744) - we refrain from over-interpreting the results. As mentioned above in response to R1, we added a sentence to explain the rationale behind focusing on Cacna1e (lines 722-724).

Reviewer #3 (Public Review):

Summary:

Authors mapped monosynaptic inputs to dopamine, GABA, and glutamate neurons in VTA under different anesthesia methods, and under drugs (cocaine, morphine, methamphetamine, amphetamine, nicotine, fluoxetine). They found that input patterns under different conditions are separated, and identified some key brain areas to contribute to such separation. They also searched a database for gene expression patterns that are common across input brain areas with some changes by anesthesia or drug administration.

Strengths:

The whole-brain approach to address drug effects is appealing and their conclusion is clear. The methodology and motivation are clearly explained.

Weaknesses:

While gene expression analyses may not be related to their findings on the anatomical effects of drugs, this will be a nice starting point for follow-up studies. 

We understand and agree with the suggestion that gene expression allows us to provide correlative observations between in situ hybridization datasets and rabies mapping datasets, and that these results do not show causality. As such, future studies would be needed to assess this in more detail. We have added a line in the discussion to this effect (lines 851-853).

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Recommendations for improving the writing and presentation:

(1) There are a couple of packages available for 3D whole-brain reconstructions based on Allen Brain Atlas (eg. https://github.com/tractatus/wholebrain, https://github.com/lahammond/BrainJ), which would be helpful to align with the gene expression or other data from Allen Institute.

This comment is related to the noted weakness we responded to previously in this rebuttal also from R1 (see comment 1), about the discrepancies between the Franklin-Paxinos atlas and Allen Brain atlas. We agree that a systematic comparison of these two atlases using a tool like wholebrain or BrainJ would be valuable for the field. However, it would be a substantial amount of work, and likely would be an independent study in itself. We believe that the resolution of these atlases was sufficient to make our key conclusions here (e.g., identify gene expression patterns that relate to drug-induced changes rabies virus labeling patterns, and develop a testable hypothesis for CRISPR-based gene editing). They are also based on the same atlases and region definitions that have been applied in our previous studies (e.g., Beier et al., Cell 2015; Beier et al., Nature 2017; Beier et al., Cell Reports 2019; Tian et al., Cell Reports 2022; Tian et al., Neuron 2024; Hubbard et al., Neuropsychophamacology 2025, etc.)  The expression of Cacna1e is relatively consistent across the NAc, as we have now detailed in Figure S13.

(2) There are so far two kinds of rabies virus strains available in the neuroscience field (SAD-B19 or CVS-N2c). It is recommended to describe which strain was used in the Material and Methods Section because labeling efficiency and toxicity is quite different between the strains (Reardon TR et al., Neuron 2016).

We have now noted that we used SAD B19 for all experiments (Lines 141-142).

Minor corrections to the text and figures:

(1)  In Figure 1A, the color differences are not clear (i.e. light gray and dark gray). The figure can be simplified.

In addition, generally, images/figures are recommended not to be overlapped with other figures/images (Figures 2A-F, 2G-L).

(2)  In Figures 7C and D, the authors could add enlarged views of starter cells in VTA and NAcLat.

We have attempted to simplify schematics and figures throughout. High-magnification images of cells have been added as insets in what is now Figure 10 (formerly Figure 7).

Reviewer #2 (Recommendations For the authors):

The number of animals for each graph should be explicated within the figure legend. For example, Figure 1C and Figure 7E lack this information. It is also advisable to delineate the definition of error bars within the figure legend.

We have now added mouse numbers to all figures and/or legends, as appropriate. We also indicated in the legend at the end of Figure 1 how error bars and asterisks are defined. Furthermore, we added a sentence to the methods saying that in UMAP and PCA plots each dot is an animal (lines 244-245).

The visual representations, particularly in Figures 1 and 3, are overcrowding. Furthermore, the arrangement of figure subpanels does not consistently adhere to the sequence of explication in the main text, significantly compromising the readability of the text. The authors are encouraged to consider the possibility of segmenting dense figures into two if there exists no upper limit for the number of figure displays. To illustrate, in Figure 3Q, crucial details about experimental conditions are denoted by numerical references, owing to spatial constraints.

We agree that the figure layout and mis-alignment with a linear read of the text was unideal. Therefore, we broke our figures, especially the original Figures 1-4, into multiple sub-figures, including both main and supplemental figures. This facilitated the use of space to rearrange the figure panels, allowing the story to be told in a linear fashion. All figures and panels should now be read in order.

I am seeking clarification on how to interpret the term "overlap" at the bottom of figures illustrating Gene Ontology analysis.

We have clarified the meaning of overlap in this context (lines 324-325): The ‘overlap’ term on the x-axis of these plots means the number of genes in the correlated gene lists that were also within the list of genes for the corresponding GO term.

The authors could provide Cacna1e gene expression patterns within the NAc from the AGEA data.

Cacna1e expression data are now provided in Figure S13.

Additionally, the meaning of "controls" in Figure 7F, along with the "No gRNA" condition, remains ambiguous. While the text mentions "no shRNA", the involvement of shRNA in this experiment lacks clarity.

We now clarify that the control conditions are based on previously published data where no AAVs were injected into NAcLat. This is now clarified in the legend for Figure 10F (lines 1277-1578). We also corrected “shRNA” to “gRNA” in the text.

eLife Assessment

This important work shows that corticotrophin-releasing factor is delivered monosynaptically to dorsal striatal cholinergic interneurons from the central amygdala and bed nucleus of the stria terminalis. CRF increases cholinergic interneuron firing and release of acetylcholine, and this action is attenuated by pre-exposure to ethanol, suggesting a potential role in stress- and alcohol use disorders. This revision addressed prior concerns, presented convincing evidence supporting the conclusions, and set the stage for additional studies.

Reviewer #1 (Public review):

Summary:

The authors show that corticotropin-releasing factor (CRF) neurons in the central amygdala (CeA) and bed nucleus of the stria terminalis (BNST) monosynaptically target cholinergic interneurons (CINs) in the dorsal striatum of rodents. Functionally, activation of CRFR1 receptors increases CIN firing rate, and this modulation was reduced by pre-exposure to ethanol. This is an interesting finding, with potential significance for alcohol use disorders.

Strengths:

Well-conceived circuit mapping experiments identify a novel pathway by which the CeA and BNST can modulate dorsal striatal function by controlling cholinergic tone. Important insight into how CRF, a neuropeptide that is important in mediating aspects of stress, affective/motivational processes and drug-seeking, modulates dorsal striatal function.

Weaknesses:

(1) Tracing and expression experiments were performed both in mice and rats (often in non-overlapping ways). While these species are similar in many ways, differences do exist. The authors address this important point in their final text.

(2) As the authors point out, CRF likely modulates CIN activity in both direct and indirect ways. As justified, exploration of the network-level modulation of CINs by CRF (and how these processes may interact with direct modulation via CRFR1 on CINs) is left for future studies.

Reviewer #2 (Public review):

Summary:

Essoh and colleagues present a thorough and elegant study identifying the central amygdala and BNST as key sources of CRF input to the dorsal striatum. Using monosynaptic rabies tracing and electrophysiology, they show direct connections to cholinergic interneurons. The study builds on previous findings that CRF increases CIN firing, extending them by measuring acetylcholine levels in slices and applying optogenetic stimulation of CRF+ fibers. It also uncovers a novel interaction between alcohol and CRF signaling in the striatum, likely to spark significant interest and future research.

Strengths:

A key strength is the integration of anatomical and functional approaches to demonstrate these projections and assess their impact on target cells, striatal cholinergic interneurons.

Comments on revisions:

No further concerns or recommendations.

Reviewer #3 (Public review):

Summary:

The authors demonstrate that CRF neurons in the extended amygdala form GABAergic synapses on to cholinergic interneurons and that CRF can excite these neurons. The evidence is strong, however the authors lack to make a compelling connection showing CRF released from these extended amygdala neurons is mediating any of these effects. Further, they show that acute alcohol appears to modulate this action, although the effect size is not particularly robust.

Strengths:

This is an exciting connection from the extended amygdala to the striatum that provides a new direction for how these regions can modulate behavior. The work is rigorous and well done.

Weaknesses:

The effects of acute ethanol are modest but consistent, the potential role of this has yet to be determined. Further, the opto stim experiments are conducted in an ai32 mouse, so it is impossible to determine if that is from CEA and BNST, vs. another population of CRF containing neurons. This is an important caveat that was acknowledged.

Author response:

The following is the authors’ response to the original reviews

We appreciate the reviewers’ insightful comments. In response, we conducted three new experiments, summarized in Author response table 1. After the table, we provide detailed responses to each comment.

Author response table 1.

Summary of new experiments and results.

Reviewer #1 (Public review):

The authors show that corticotropin-releasing factor (CRF) neurons in the central amygdala (CeA) and bed nucleus of the stria terminalis (BNST) monosynaptically target cholinergic interneurons (CINs) in the dorsal striatum of rodents. Functionally, activation of CRFR1 receptors increases CIN firing rate, and this modulation was reduced by pre-exposure to ethanol. This is an interesting finding, with potential significance for alcohol use disorders, but some conclusions could use additional support.

Strengths:

Well-conceived circuit mapping experiments identify a novel pathway by which the CeA and BNST can modulate dorsal striatal function by controlling cholinergic tone. Important insight into how CRF, a neuropeptide that is important in mediating aspects of stress, affective/motivational processes, and drug-seeking, modulates dorsal striatal function.

Weaknesses:

(1) Tracing and expression experiments were performed both in mice and rats (in a mostly nonoverlapping way). While these species are similar in many ways, some conclusions are based on assumptions of similarities that the presented data do not directly show. In most cases, this should be addressed in the text (but see point number 2).

In the revised manuscript, we have clarified this limitation in the first paragraph of the Methods and the third paragraph of the Discussion and avoid cross-species claims, limiting our conclusions to the species in which each assay was performed. Specifically, we now state that while mice and rats share many conserved amygdalostriatal components, our tracing and expression studies were performed in a species-specific manner, and direct cross-species comparisons of CRF–CIN connectivity and CRFR1 expression were not assessed. We further note that future studies will be needed to determine the extent to which these observations are conserved across species as more tools become available.

(2) Experiments in rats show that CRFR1 expression is largely confined to a subpopulation of striatal CINs. Is this true in mice, too? Since most electrophysiological experiments are done in various synaptic antagonists and/or TTX, it does not affect the interpretation of those data, but non-CIN expression of CRFR1 could potentially have a large impact on bath CRF-induced acetylcholine release.

To address whether CRFR1 expression in striatal CINs is conserved across species, we performed new histological experiments using CRFR1-GFP mice. Striatal sections were immunostained with anti-ChAT, and we found that approximately 10% of CINs express CRFR1 (new Fig. 4D, 4E). This result indicates that, similar to rats, a subset of CINs in mice express CRFR1. However, the proportion of CRFR1⁺ CINs is lower than the proportion of CRF-responsive CINs observed during electrophysiology experiments, suggesting that CRF may also modulate CIN activity indirectly through network or synaptic mechanisms. We have also noted in the revised Discussion that while CRFR1 expression is confirmed in a subset of CINs, the broader distribution of CRFR1 among other striatal cell types remains to be determined (third paragraph of Discussion).

In our study, bath application of CRF increased striatal ACh release. Because striatal ACh is released primarily from CINs, and CRFR1 is an excitatory receptor, this effect is most likely mediated by CRF activation of CRFR1 on CINs, leading to enhanced CIN activity and ACh release. Although CRFR1 may also be expressed on other striatal neurons, these cell types—medium spiny neurons and GABAergic interneurons—are inhibitory. If CRF were to activate CRFR1 on these GABAergic neurons, the resulting increase in GABA release would suppress CIN activity and consequently reduce, rather than enhance, ACh release. Given that most CINs responded functionally while only a small subset expressed CRFR1, these findings imply that indirect mechanisms, such as CRF modulation of local circuits influencing CIN excitability, may also contribute to the observed increase in ACh release. Together, these data support a model in which CRF primarily enhances ACh release via activation of CRFR1-expressing CINs, while indirect network effects may further amplify this response.

(3) Experiments in rats show that about 30% of CINs express CRFR1 in rats. Did only a similar percentage of CINs in mice respond to bath application of CRF? The effect sizes and error bars in Figure 5 imply that the majority of recorded CINs likely responded. Were exclusion criteria used in these experiments?

We thank the reviewer for this insightful question. In our mouse cell-attached recordings, ~80% of CINs increased firing during CRF bath application, and all recorded cells were included in the analysis (no exclusions based on response direction/magnitude; cells were only required to meet standard recording-quality criteria such as stable baseline firing and seal).

Using a CRFR1-GFP reporter mouse, we found that ~10% of striatal CINs are GFP+, suggesting that the high proportion of CRF-responsive CINs cannot be explained solely by somatic reporter-labeled CRFR1 expression. Importantly, the CRF-induced increase in CIN firing is blocked by the selective CRFR1 antagonist NBI 35695 (Fig. 5B–C), supporting a CRFR1-dependent mechanism at the circuit level. We now discuss several non-mutually exclusive explanations for this apparent discrepancy: (i) reporter lines (e.g., CRFR1-GFP) may underestimate functional CRFR1 expression, particularly for low-level or compartmentalized receptor pools; (ii) bath-applied CRF may act indirectly via CRFR1 on presynaptic afferents, thereby enhancing excitatory drive onto CINs; and (iii) electrical coupling among CINs could allow direct effects in a subset of CINs to propagate through the CIN network (Ren, Liu et al. 2021). We added this discussion to the revised manuscript (fourth paragraph of the Discussion).

(4) The conclusion that prior acute alcohol exposure reduces the ability of subsequent alcohol exposure to suppress CIN activity in the presence of CRF may be a bit overstated. In Figure 6D (no ethanol preexposure), ethanol does not fully suppress CIN firing rate to baseline after CRF exposure. The attenuated effect of CRF on CIN firing rate after ethanol pre-treatment (6E) may just reduce the maximum potential effect that ethanol can have on firing rate after CRF, due to a lowered starting point. It is possible that the lack of significant effect of ethanol after CRF in pre-treated mice is an issue of experimental sensitivity. Related to this point, does pre-treatment with ethanol reduce the later CIN response to acute ethanol application (in the absence of CRF)?

In the revised manuscript, we have tempered our interpretation in the final Results section and throughout the Discussion to emphasize that ethanol pre-exposure attenuates, rather than abolishes, the CRFinduced increase in CIN firing. We also note the reviewer’s important point that in Figure 6D, ethanol does not fully suppress firing to baseline after CRF exposure, consistent with a partial effect. Regarding the reviewer’s question, our experiments were specifically designed to test interactions between CRF and ethanol, so we did not assess whether ethanol pre-treatment alters subsequent responses to ethanol alone. We now explicitly acknowledge CRF-dependent and CRF-independent effects of ethanol on CIN activity as an important point for future studies to disentangle (sixth paragraph of the Discussion). For example, comparing ethanol responses with and without prior ethanol without any treatment with CRF could resolve this question.

(5) More details about the area of the dorsal striatum being examined would be helpful (i.e., a-p axis).

We now provide more detail regarding the anterior–posterior axis of the dorsal striatum examined. Most recordings and imaging were performed in the posterior dorsomedial striatum (pDMS), corresponding to coronal slices posterior to the crossing of the anterior commissure and anterior to the tail of the striatum (starting around 0.62 mm and ending at −1.3 mm relative to the Bregma). While our primary focus was on posterior slices, some anterior slices were included to increase the sample size. These details have been added to the Methods (Last sentence of the ‘Histology and cell counting’ section and of the ‘Slice electrophysiology’ section).

Reviewer #2 (Public review):

Essoh and colleagues present a thorough and elegant study identifying the central amygdala and BNST as key sources of CRF input to the dorsal striatum. Using monosynaptic rabies tracing and electrophysiology, they show direct connections to cholinergic interneurons. The study builds on previous findings that CRF increases CIN firing, extending them by measuring acetylcholine levels in slices and applying optogenetic stimulation of CRF+ fibers. It also uncovers a novel interaction between alcohol and CRF signaling in the striatum, likely to spark significant interest and future research.

Strengths:

A key strength is the integration of anatomical and functional approaches to demonstrate these projections and assess their impact on target cells, striatal cholinergic interneurons.

Weaknesses:

(1) The nature of the interaction between alcohol and CRF actions on cholinergic neurons remains unclear. Also, further clarification of the ACh sensor used and others is required

We have clarified the nature of the interaction between alcohol and CRF signaling in CINs and have provided additional details regarding the acetylcholine sensor used. These issues are addressed in detail in our responses to the specific comments below.

Reviewer #2 (Recommendations for the authors):

(1) The interaction between the effects of alcohol and CRF is a novel and important part of this study. When considering possible mechanisms underlying the findings in the discussion, there is no mention of occlusion. Given that incubation with alcohol produced a similar increase in firing of CINs as CRF, occlusion could be a parsimonious explanation for the observed interaction. Have the author considered blocking the effects of alcohol on CIN with CRF-R1 antagonist? Another experiment that could address the occlusion would be to test if alcohol also increases ACh levels as it did CRF.

We thank the reviewer for proposing occlusion as a potential mechanism underlying the interaction between alcohol and CRF. We agree that, in principle, alcohol-induced endogenous CRF release could occlude subsequent exogenous CRF-mediated potentiation of CIN firing, and we carefully considered this possibility.

However, several observations from our data argue against occlusion driven by acute alcohol exposure or withdrawal in this preparation. First, as shown in Fig. 6A, bath application of alcohol transiently reduced CIN firing, and firing recovered to baseline levels after washout without any rebound increase. Second, in Fig. 6D–E, the baseline firing rates under control conditions and following alcohol pretreatment were comparable, indicating that acute alcohol exposure and short-term withdrawal did not produce a sustained increase in CIN excitability. Together, these results suggest that acute withdrawal in slices is less likely to trigger substantial endogenous CRF release capable of occluding subsequent exogenous CRF effects.

While we and others have previously reported increased spontaneous CIN firing following prolonged in vivo alcohol exposure and extended withdrawal periods (e.g., 21 days), short-term withdrawal (e.g., 1 day) does not robustly alter baseline CIN firing (Ma, Huang et al. 2021, Huang, Chen et al. 2024). Consistent with these prior findings, the absence of a rebound or elevated baseline firing in the present slice experiments discouraged further pursuit of an endogenous CRF occlusion mechanism under acute conditions.

We also considered experimentally testing occlusion by blocking CRFR1 signaling during alcohol pre-treatment. However, this approach is technically challenging in slice recordings, as CRFR1 antagonists require prolonged incubation (~1 hour) during alcohol exposure. Because it is unclear whether endogenous CRF release is triggered by alcohol incubation itself or by withdrawal, the antagonist would need to remain present throughout both the incubation and withdrawal periods. This leaves insufficient time for complete washout of the CRFR1 antagonist prior to subsequent bath application of exogenous CRF to assess its effects on CIN firing. Consequently, residual antagonist presence would confound the interpretation of the exogenous CRF response.

Finally, regarding the possibility that alcohol increases acetylcholine release, we did not observe alcohol-induced increases in CIN firing in slices, arguing against elevated ACh signaling under these conditions. Consistent with prior work (Ma, Huang et al. 2021, Huang, Chen et al. 2024), alcohol-induced increases in CIN excitability and cholinergic signaling appear to depend on prolonged in vivo exposure and extended withdrawal rather than acute slice-level manipulations.

We have now incorporated discussion of occlusion as a potential mechanism (seventh paragraph) and clarified why our data and technical considerations argue against it in the present study. We thank the reviewer for this wonderful suggestion, which we will test in future in vivo studies.

(2) Retrograde monosynaptic tracing of inputs to CIN. Results state the finding of labeling in all previously reported area..." Can the authors report these areas? A list in the text or a bar plot, if there is quantification, will suffice. This formation will serve as important validation and replication of previous findings.

We thank the reviewer for this constructive suggestion. We agree that summarizing the anatomical sources of CIN input provides important validation of our tracing results. In the revised Results, we now list the major input regions observed, including the striatum itself, cortex (e.g., cingulate cortex, motor cortex, somatosensory cortex), thalamus (e.g., parafascicular thalamic nucleus, centrolateral thalamic nucleus), globus pallidus, and midbrain (first paragraph of the Results). Quantitative analysis of relative input strength will be presented in a separate study that expands on these findings. Here, we limit the current manuscript to the functional characterization of CRF and alcohol modulation of CINs.

(3) Given the difference in connectivity among striatal subregions, it would be important to describe in more detail the injection site in the results and figures. In the figure, for example, you might want to include the AP coordinates, given that it is such a zoomed-in image, it is hard to tell how anterior/posterior the site is. I imagine that the picture is a representative image of the injection site, but maybe having a side image with overlay of injection sites in all the animals used, would help.

The anterior–posterior (AP) coordinates for representative images have been included in the panels and reiterated more clearly in the revised Results section and figure legends. In the legend for Figure 3B, a list of AP coordinates for each animal used for Figure 3A-3E has been added.

(4) Figure 1D inset, there seem to be some double-labeled cells in the zoomed in BNST images. The authors might want to comment on this. It seemed far from the injection site. Do D1-MSN so far away show connectivity to CINs?

Upon closer inspection of the BNST images, we noted a small number of double-labeled cells were indeed present, consistent with prior reports that a subset of D1R-expressing neurons (~10%) has been reported previously in our lab in the BNST, with the majority being D2R-expressing neurons (Lu, Cheng et al. 2021). Given the BNST’s anatomical proximity to the dorsal striatum, it is plausible that some D1Rexpressing neurons in this region provide monosynaptic input to CINs, highlighting a potential ventral-to-dorsal connection that merits further study.

(5) Can the author provide quantification of the onset delay of the optogenetic evoked CRF+ axon responses onto CINs? The claim of monosynaptic connectivity is well supported by the TTX/4AP experiment but additional information on the timing will strengthen that conclusion.

We thank the reviewer for this insightful suggestion. Quantifying the onset latency of optogenetically evoked CRFMsup+</sup> axon responses onto CINs provides valuable confirmation of monosynaptic connectivity. To address this, we performed new latency measurements under the same recording conditions as the TTX/4-AP experiments. The average onset latency from the start of the optical stimulation was 5.85 ± 0.37 ms (new Figure 3J), consistent with direct monosynaptic transmission.

As an additional reference, we analyzed latency data from a separate project in which we optogenetically stimulated cholinergic interneurons and recorded synaptic responses in medium spiny neurons. This circuit, known to involve disynaptic transmission from CINs to MSNs via nAChR-expressing interneurons (Autor response image 1) (English, Ibanez-Sandoval et al. 2011), exhibited a significantly longer latency (18.34 ± 0.70 ms; t₍₂₉₎ = 10.3, p < 0.001) compared to CRF⁺ CeA/BNST inputs to CINs (5.85 ± 0.37 ms). Together, these results further support that CRF⁺ axons form direct functional synapses onto CINs.

Author response image 1.

Latency of disynaptic transmission from CINs to MSNs via interneurons A) Schematic illustrating optogenetic stimulation of Chrimson-expressing CINs, leading to excitation of nAChRexpressing interneurons that release GABA onto recorded MSNs. B) Sample trace of disynaptic transmission (left) and bar graph summarizing onset latency (right) from light stimulation to synaptic response onset (n = 23 neurons from 3 mice).

(6) The ACh sensor reported is "AAV-GRABACh4m" but the reference is for GRAB-ACh3.0. Also, BrainVTA has GRAB-ACh4.3. Is this the vector? Could you please check the name of the construct and report the corresponding reference, as well as clarify the meaning of the additional "m". They have a mutant version of the GRAB-ACH that researchers use for control, and of course, you want to use it as a control, but not for the test experiment.

GRAB-ACh4m is the correct acetylcholine sensor used in this study. The ACh4 series (including ACh4h, ACh4m, and ACh4l; personal communication with Dr. Yulong Li’s lab) represents an updated generation following GRAB-ACh3.0. Although the ACh4 family has not yet been formally published, these constructs are publicly available through BrainVTA (https://www.brainvta.tech/plus/view.php?aid=2680).

The suffix “m” does not indicate a mutant control; rather, it denotes a medium-affinity variant within the ACh4 sensor family. Importantly, the mutant (non-responsive) control sensor is only available for GRAB-ACh3.0 (ACh3.0mut) and does not exist for the ACh4 series.

Our laboratory has previously used GRAB-ACh4m in multiple peer-reviewed publications (Huang, Chen et al. 2024, Gangal, Iannucci et al. 2025, Purvines, Gangal et al. 2025), and its use has also been reported by independent groups in recent preprints (Potjer, Wu et al. 2025, Touponse, Pomrenze et al. 2025). We have now clarified the construct name, its relationship to GRAB-ACh3.0, in the Methods ‘Reagents’ section, and we have corrected the reference accordingly.

(7) Are CRF-R1+ CINs equally abundant in the DMS and DLS? From the image in Figure 4, it seems that a larger percentage of CINs are CRFR1+ in the DLS than in DMS. Is this true? The authors probably already have this data, or it should be easy to get, and it could be additional information that was not studied before.

We did not perform a quantitative comparison of CRFR1+ CIN abundance between the DMS and DLS in the present study. While the representative images in Figure 4 may appear to suggest regional differences, these panels were selected to illustrate labeling quality rather than relative density and should not be interpreted as evidence of unequal distribution. We have clarified this point in the revised Discussion (last sentence of the third paragraph) and note that future studies will be needed to systematically evaluate potential regional differences in CRFR1 expression, which could have important implications for dorsal striatal function.

(8) The manuscript states several times that there are no CRF+ neurons in the dorsal striatum. At the same time, there are reports of the CRF+ neuron in the ventral striatum and its role in learning. Could the authors include mention of the studies by the Lemos group (10.1016/j.biopsych.2024.08.006)

We have revised the Discussion section to clarify that our findings pertain specifically to the dorsal striatum and now acknowledge the presence and functional relevance of CRF+ neurons in the ventral striatum, citing the Lemos group’s study (fifth paragraph of the Discussion).

(9) For the histology analysis, please express cell counts as "density", not just number of cells, by providing an area (e.g., "number of cell/ µm2").

In the revised manuscript, all histological outcomes have been recalculated as cell density (cells/mm²) by normalizing raw cell counts to the measured area of each region of interest (ROI). Figures that previously displayed absolute counts now present densities (cells/mm²), with corresponding updates made to figure legends and text. We note one exception in Figure 4B, where the comparison between the total number of CINs and CRFR1+ CINs is best represented as cell counts rather than normalized values, as the counting was conducted in the same area (within the same ROI) of the dorsostriatal subregion.

(10) Figure 2C, we can see there are some labeled fibers in the striatum cut. Would it be possible to get a better confocal image?

Figure 2C has been replaced with a higher-quality confocal image captured at the same magnification and scale. The updated image provides improved clarity and resolution, ensuring accurate visualization of labeled CRF+ fibers, but not cell bodies, within the striatum.

(11) The ACh measurements in the slice are very informative and an important addition. I first thought that these experiments with the GRAB-ACh sensor were performed in ChAT-eGFP mice. After reading more carefully, I realized they were done in wild-type mice. Would you include the wildtype label in the figure as well? The ChATeGFP BAC transgenic line was reported to have enhanced ACh packaging and increased ACh release, which could have magnified the signals. So, it is important to highlight the experiments were done in wildtype mice.

We now label with ‘WT mice’ and note in the legend that all GRAB-ACh experiments were performed in wild-type mice, not ChAT-eGFP, to avoid confounds in ACh release. We thank the reviewer for this important suggestion.

Reviewer #3 (Public review):

The authors demonstrate that CRF neurons in the extended amygdala form GABAergic synapses onto cholinergic interneurons and that CRF can excite these neurons. The evidence is strong, however, the authors fail to make a compelling connection showing CRF released from these extended amygdala neurons is mediating any of these effects. Further, they show that acute alcohol appears to modulate this action, although the effect size is not particularly robust.

Strengths:

This is an exciting connection from the extended amygdala to the striatum that provides a new direction for how these regions can modulate behavior. The work is rigorous and well done.

Weaknesses:

(1) While the authors show that opto stim of these neurons can increase firing, this is not shown to be CRFR1 dependent. In addition, the effects of acute ethanol are not particularly robust or rigorously evaluated. Further, the opto stim experiments are conducted in an Ai32 mouse, so it is impossible to determine if that is from CEA and BNST, vs. another population of CRF-containing neurons. This is an important caveat.

We added recordings with the CRFR1 antagonist antalarmin. Light-evoked increases in CIN firing were abolished under CRFR1 blockade, linking the effect to CRFR1 (Figure 5J, 5K). We also clarify that CRFCre;Ai32 does not isolate CeA versus BNST sources, so we temper regional claims and highlight this as a limitation. The acute ethanol effects are modest but consistent; we expanded the discussion of dose and preparation constraints in acute slice physiology and note that in vivo studies will be needed to define the network-level impact.

Reviewer #3 (Recommendations for the authors):

(1) The authors could bring some of this data together by examining CRFR1 dependence of optical stimulationinduced increases in firing. Further, the authors have devoted significant effort to exploring how the BNST and CEA project to the CIN, yet their ephys does not explore site-specific infusion of ChR2 into either region. How are we to be sure it is not some other population of CRF neurons mediating this effect? The alcohol data does not appear particularly robust, but I think if the authors wanted to, they could explore other concentrations. Mostly I think it is important to discuss the limitations of acute alcohol on 5a brain slice.

We thank the reviewer for these thoughtful comments, which helped us strengthen the mechanistic interpretation of the CRF-CIN interaction. In the revised manuscript, we have addressed each point as follows:

- CRFR1 dependence of optogenetically evoked responses: We performed new recordings in which optogenetic stimulation of CRF⁺ terminals in the dorsal striatum was conducted in the presence of the CRFR1 antagonist antalarmin. The increase in CIN firing evoked by light stimulation was abolished under CRFR1 blockade, confirming that this effect is mediated through CRFR1 activation (new Figure 5J, 5K, third paragraph of the corresponding Result section). These results directly link the functional effects of CRF⁺ terminal activation to CRFR1 signaling on CINs.

- CeA vs. BNST projection specificity: The reviewer is correct that CeA and BNST projections were not analyzed separately. As unknown pathways, our experiment was designed to first establish the monosynaptic connections between CeA/BNST CRF neurons to striatal CINs. Future studies would further explore the specific contribution of each site. However, our data exclude the possibility of other CRF neurons as we selectively infused Cre-dependent opsins into both CeA and BNST of CRF-Cre mice (Figure 3G-3J).

- Limitations of acute slice experiments: We have expanded the Discussion (sixth paragraph) to acknowledge that acute slice physiology cannot fully capture the dynamic and network-level effects of ethanol observed in vivo. While this preparation enables mechanistic precision, factors such as washout, diffusion constraints, and the absence of systemic feedback may underestimate ethanol’s impact on CINs. We now explicitly note this limitation and highlight the need for in vivo studies to examine behavioral and circuit-level implications of CRF–alcohol interactions.

Collectively, these revisions clarify the CRFR1 dependence of CRF⁺ terminal effects and reaffirm that both CeA and BNST projections contribute to CIN modulation while addressing the methodological limitations of the slice preparation.

Reviewer #4 Public Review):

This manuscript presents a compelling and methodologically rigorous investigation into how corticotropin-releasing factor (CRF) modulates cholinergic interneurons (CINs) in the dorsal striatum - a brain region central to cognitive flexibility and action selection-and how this circuit is disrupted by alcohol exposure. Through an integrated series of anatomical, optogenetic, electrophysiological, and imaging experiments, the authors uncover a previously uncharacterized CRF⁺ projection from the central amygdala (CeA) and bed nucleus of the stria terminalis (BNST) to dorsal striatal CINs.

Strengths:

Key strengths of the study include the use of state-of-the-art monosynaptic rabies tracing, CRF-Cre transgenic models, CRFR1 reporter lines, and functional validation of synaptic connectivity and neurotransmitter release. The finding that CRF enhances CIN excitability and acetylcholine (ACh) release via CRFR1, and that this effect is attenuated by acute alcohol exposure and withdrawal, provides important mechanistic insight into how stress and alcohol interact to impair striatal function. These results position CRF signaling in CINs as a novel contributor to alcohol use disorder (AUD) pathophysiology, with implications for relapse vulnerability and cognitive inflexibility associated with chronic alcohol intake. The study is well-structured, with a clear rationale, thorough methodology, and logical progression of results. The discussion effectively contextualizes the findings within broader addiction neuroscience literature and suggests meaningful future directions, including therapeutic targeting of CRFR1 signaling in the dorsal striatum.

Weaknesses:

(1) Minor areas for improvement include occasional redundancy in phrasing, slightly overlong descriptions in the abstract and significance sections, and a need for more concise language in some places. Nevertheless, these do not detract from the manuscript's overall quality or impact. Overall, this is a highly valuable contribution to the fields of addiction neuroscience and striatal circuit function, offering novel insights into stress-alcohol interactions at the cellular and circuit level, which requires minor editorial revisions.

We have streamlined the abstract and significance statement, reduced redundancy, and improved conciseness throughout the text. We appreciate the reviewer’s feedback, which has helped us further strengthen the clarity and readability of the manuscript.

Reviewer #4 (Recommendations for the authors):

(1) Line 29-30: Slightly verbose. Consider: "Alcohol relapse is associated with corticotropin-releasing factor (CRF) signaling and altered reward pathway function, though the precise mechanisms are unclear."

The sentence has been revised as recommended to improve clarity and conciseness in the introductory section (Lines 31-32).

(2) Lines 39-43: Good synthesis, but could better emphasize the novelty of identifying a CRF-CIN pathway.

The abstract has been revised to more clearly emphasize the novelty of identifying a CRF-CIN pathway and its functional significance (Line 42-43).

(3) Lines 66-68: Consider integrating clinical relevance more directly, e.g., "AUD affects over 14 million adults in the U.S., with relapse often triggered by stress...".

The introduction has been revised to more directly emphasize the clinical relevance of alcohol use disorder, including its high prevalence and the role of stress in relapse, thereby underscoring the translational significance of our findings (Lines 68-69).

(4) Line 83: Repetition of "goal-directed learning, habit formation, and behavioral flexibility" appears multiple times; consider variety.

We have varied the phrasing in the Introduction to avoid redundancy. Specifically, in place of repeating “goal-directed learning, habit formation, and behavioral flexibility,” we now use alternative terms such as “action selection,” “habitual responding,” and “cognitive flexibility,” depending on the context.

(5) Lines 107-116: Clarify why both rats and mice were used-do they serve different experimental purposes?

We now explain that each species was used for complementary experimental purposes. Rats were used for histological validation of CRFR1 expression using the CRFR1-Cre-tdTomato line, which has been extensively characterized in this species. Mice were used for the majority of electrophysiological, optogenetic, and GRAB-ACh sensor experiments due to the availability of well-established transgenic CRF-Cre-driver lines. This division allowed us to leverage the most appropriate tools in each species to address different aspects of the study. We have clarified this rationale in the Methods (first paragraph of the “Animals” section) and Discussion (third paragraph).

(6) Electrophysiology section: The distinction between acute exposure vs. withdrawal could be further emphasized.

To better highlight the distinction between acute alcohol exposure and withdrawal, we have clarified the timing and context of each condition within the Results section for Figure 6. Specifically, we now distinguish the immediate suppressive effects of alcohol observed during bath application (acute exposure) from the subsequent changes in CIN firing measured after washout (withdrawal). These revisions clarify the temporal dynamics and functional implications of CRF–alcohol interactions in our experimental design.

(7) Lines 227-229: Reword for clarity: "Significantly more BNST neurons projected to CINs compared to the CeA...".

The sentence has been reworded to clarify as recommended (Lines 247-248).

(8) Lines 373-374: Consider connecting the CRF-CIN circuit to behavioral inflexibility in AUD more directly.

We have modified the sentence (Lines 390-395) to more explicitly link alcohol-induced dysregulation of the CRF–CIN circuit to behavioral inflexibility in AUD, consistent with the established role of CINs in action selection and cognitive flexibility.

(9) Lines 387-389: This is an excellent point about stress resilience; consider expanding with examples or potential implications.

We thank the reviewer for this insightful suggestion. In the revised Discussion (sixth paragraph), we expanded this section to more directly connect alcohol-induced disruption of CRF–CIN signaling with impaired stress resilience and behavioral inflexibility. Specifically, we now note that such dysregulation may compromise stress resilience mechanisms mediated by CRF–cholinergic interactions in the striatum and related corticostriatal circuits. We further discuss how impaired CIN responsiveness could blunt adaptive behavioral adjustments under stress, biasing animals toward habitual or compulsive alcohol seeking. This addition highlights the broader implication that alcohol-induced alterations in CRF–CIN signaling may contribute to relapse vulnerability by undermining adaptive stress coping.

References

English, D. F., O. Ibanez-Sandoval, E. Stark, F. Tecuapetla, G. Buzsaki, K. Deisseroth, J. M. Tepper and T. Koos (2011). "GABAergic circuits mediate the reinforcement-related signals of striatal cholinergic interneurons." Nat Neurosci 15(1): 123–130.

Gangal, H., J. Iannucci, Y. Huang, R. Chen, W. Purvines, W. T. Davis, A. Rivera, G. Johnson, X. Xie, S. Mukherjee, V. Vierkant, K. Mims, K. O'Neill, X. Wang, L. A. Shapiro and J. Wang (2025). "Traumatic brain injury exacerbates alcohol consumption and neuroinflammation with decline in cognition and cholinergic activity." Transl Psychiatry 15(1): 403.

Huang, Z., R. Chen, M. Ho, X. Xie, H. Gangal, X. Wang and J. Wang (2024). "Dynamic responses of striatal cholinergic interneurons control behavioral flexibility." Sci Adv 10(51): eadn2446.

Lu, J. Y., Y. F. Cheng, X. Y. Xie, K. Woodson, J. Bonifacio, E. Disney, B. Barbee, X. H. Wang, M. Zaidi and J. Wang (2021). "Whole-Brain Mapping of Direct Inputs to Dopamine D1 and D2 Receptor-Expressing Medium Spiny Neurons in the Posterior Dorsomedial Striatum." Eneuro 8(1).

Ma, T., Z. Huang, X. Xie, Y. Cheng, X. Zhuang, M. J. Childs, H. Gangal, X. Wang, L. N. Smith, R. J. Smith, Y. Zhou and J. Wang (2021). "Chronic alcohol drinking persistently suppresses thalamostriatal excitation of cholinergic neurons to impair cognitive flexibility." J Clin Invest 132(4): e154969.

Potjer, E. V., X. Wu, A. N. Kane and J. G. Parker (2025). "Parkinsonian striatal acetylcholine dynamics are refractory to L-DOPA treatment." bioRxiv.

Purvines, W., H. Gangal, X. Xie, J. Ramos, X. Wang, R. Miranda and J. Wang (2025). "Perinatal and prenatal alcohol exposure impairs striatal cholinergic function and cognitive flexibility in adult offspring." Neuropharmacology 279: 110627.

Ren, Y., Y. Liu and M. Luo (2021). "Gap Junctions Between Striatal D1 Neurons and Cholinergic Interneurons." Front Cell Neurosci 15: 674399.

Touponse, G. C., M. B. Pomrenze, T. Yassine, V. Mehta, N. Denomme, Z. Zhang, R. C. Malenka and N. Eshel (2025). "Cholinergic modulation of dopamine release drives effortful behavior." bioRxiv.

eLife Assessment

The authors investigate how dominance hierarchy shapes defensive strategies in mice under two naturalistic threats: a transient visual looming stimulus and a sustained live rat. This study provides important insights into how social context and dominance hierarchy modulate innate defensive behaviors across distinct naturalistic threats. The strength of evidence is convincing, with detailed classification and analysis of behaviors.

Reviewer #1 (Public review):

Summary:

This study presents an interesting behavioral paradigm and reveals interactive effects of social hierarchy and threat type on defensive behaviors. However, addressing the aforementioned points regarding methodological detail, rigor in behavioral classification, depth of result interpretation, and focus of the discussion is essential to strengthen the reliability and impact of the conclusions in a revised manuscript.

Strengths:

The paper is logically sound, featuring detailed classification and analysis of behaviors, with a focus on behavioral categories and transitions, thereby establishing a relatively robust research framework.

Weaknesses:

Several points require clarification or further revision.

(1) Methods and Terminology Regarding Social Hierarchy:

The study uses the tube test to determine subordinate status, but the methodological description is quite brief. Please provide a more detailed account of the experimental procedure and the criteria used for determination.

The dominance hierarchy is established based on pairs of mice. However, the use of terms like "group cohesion" - typically applied to larger groups - to describe dyadic interactions seems overstated. Please revise the terminology to more accurately reflect the pairwise experimental setup.

(2) Criteria and Validity of Behavioral Classification:

The criteria for classifying mouse behaviors (e.g., passive defense, active defense) are not sufficiently clear. Please explicitly state the operational definitions and distinguishing features for each behavioral category.

How was the meaningfulness and distinctness of these behavioral categories ensured to avoid overlap? For instance, based on Figure 3E, is "active defense" synonymous with "investigative defense," involving movement to the near region followed by return to the far region? This requires clearer delineation.

The current analysis focuses on a few core behaviors, while other recorded behaviors appear less relevant. Please clarify the principles for selecting or categorizing all recorded behaviors.

(3) Interpretation of Key Findings and Mechanistic Insights:

Looming exposure increased the proportion of proactive bouts in the dominant zone but decreased it in the subordinate zone (Figure 4G), with a similar trend during rat exposure. Please provide a potential explanation for this consistent pattern. Does this consistency arise from shared neural mechanisms, or do different behavioral strategies converge to produce similar outputs under both threats?

(4) Support for Claims and Study Limitations:

The manuscript states that this work addresses a gap by showing defensive responses are jointly shaped by threat type and social rank, emphasizing survival-critical behaviors over fear or stress alone. However, it is possible that the behavioral differences stem from varying degrees of danger perception rather than purely strategic choices. This warrants a clear description and a deeper discussion to address this possibility.

The Discussion section proposes numerous brain regions potentially involved in fear and social regulation. As this is a behavioral study, the extensive speculation on specific neural circuitry involvement, without supporting neuroscience data, appears insufficiently grounded and somewhat vague. It is recommended to focus the discussion more on the implications of the behavioral findings themselves or to explicitly frame these neural hypotheses as directions for future research.

Reviewer #2 (Public review):

Summary:

The authors investigate how dominance hierarchy shapes defensive strategies in mice under two naturalistic threats: a transient visual looming stimulus and a sustained live rat. By comparing single versus paired testing, they report that social presence attenuates fear and that dominant and subordinate mice exhibit different patterns of defensive and social behaviors depending on threat type. The work provides a rich behavioral dataset and a potentially useful framework for studying hierarchical modulation of innate fear.

Strengths:

(1) The study uses two ecologically meaningful threat paradigms, allowing comparison across transient and sustained threat contexts.

(2) Behavioral quantification is detailed, with manual annotation of multiple behavior types and transition-matrix level analysis.

(3) The comparison of dominant versus subordinate pairs is novel in the context of innate fear.

(4) The manuscript is well-organized and clearly written.

(5) Figures are visually informative and support major claims.

Weaknesses:

Lack of neural mechanism insights.

Reviewer #3 (Public review):

Summary:

This study examines how dominance hierarchy influences innate defensive behaviors in pair-housed male mice exposed to two types of naturalistic threats: a transient looming stimulus and a sustained live rat. The authors show that social presence reduces fear-related behaviors and promotes active defense, with dominant mice benefiting more prominently. They also demonstrate that threat exposure reinforces social roles and increases group cohesion. The work highlights the bidirectional interaction between social structure and defensive behavior.

Strengths:

This study makes a valuable contribution to behavioral neuroscience through its well-designed examination of socially modulated fear. A key strength is the use of two ethologically relevant threat paradigms - a transient looming stimulus and a sustained live predator, enabling a nuanced comparison of defensive behaviors. The experimental design is robust, systematically comparing animals tested alone versus with their cage mate to cleanly isolate social effects. The behavioral analysis is sophisticated, employing detailed transition maps that reveal how social context reshapes behavioral sequences, going beyond simple duration measurements. The finding that social modulation is rank-dependent adds significant depth, linking social hierarchy to adaptive defense strategies. Furthermore, the demonstration that threat exposure reciprocally enhances social cohesion provides a compelling systems-level perspective. Together, these elements establish a strong behavioral framework for future investigations into the neural circuits underlying socially modulated innate fear.

Weaknesses:

The study exhibits several limitations. The neural mechanism proposed is speculative, as the study provides no causal evidence.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary: 

This study presents an interesting behavioral paradigm and reveals interactive effects of social hierarchy and threat type on defensive behaviors. However, addressing the aforementioned points regarding methodological detail, rigor in behavioral classification, depth of result interpretation, and focus of the discussion is essential to strengthen the reliability and impact of the conclusions in a revised manuscript. 

Strengths: 

The paper is logically sound, featuring detailed classification and analysis of behaviors, with a focus on behavioral categories and transitions, thereby establishing a relatively robust research framework. 

Weaknesses: 

Several points require clarification or further revision. 

(1) Methods and Terminology Regarding Social Hierarchy: 

The study uses the tube test to determine subordinate status, but the methodological description is quite brief. Please provide a more detailed account of the experimental procedure and the criteria used for determination. 

We will add more details about how the tube test was performed in the revised manuscript.

The dominance hierarchy is established based on pairs of mice. However, the use of terms like "group cohesion" - typically applied to larger groups - to describe dyadic interactions seems overstated. Please revise the terminology to more accurately reflect the pairwise experimental setup.

Thanks for the comment. We agree that the term “group cohesion” can be misleading and will replace it with “social engagement”.

(2) Criteria and Validity of Behavioral Classification: 

The criteria for classifying mouse behaviors (e.g., passive defense, active defense) are not sufficiently clear. Please explicitly state the operational definitions and distinguishing features for each behavioral category. 

Passive defense was defined as an immobility-based defensive strategy characterized by suppression of locomotor activity. This category included freezing and tail rattling, which in our study involved minimal body displacement aside from rapid tail vibration. Active defense was defined as movement- or posture-dependent defensive strategy, encompassing behaviors that involved locomotor engagement or spatial repositioning relative to the threat, including approach, investigation, withdrawal, and stretch-attend. We will clarify this in the revised manuscript.

How was the meaningfulness and distinctness of these behavioral categories ensured to avoid overlap? For instance, based on Figure 3E, is "active defense" synonymous with "investigative defense," involving movement to the near region followed by return to the far region? This requires clearer delineation. 

Defensive behaviors in the rat exposure paradigm were grouped into two categories: passive and active defense, each comprising distinct behaviors. All the manually annotated behaviors were mutually exclusive; that is, each video frame was assigned a single behavioral label to avoid overlap across behaviors. Active defense includes four behaviors: approach, investigation, withdrawal, and stretch-attend. We will clarify these points in the revised manuscript.

The current analysis focuses on a few core behaviors, while other recorded behaviors appear less relevant. Please clarify the principles for selecting or categorizing all recorded behaviors.

Thank you for pointing this out. In the current study, we focused primarily on defensive and social behaviors. We also included several neutral solitary behaviors related to anxiety and defensive state, such as sniffing, grooming, and rearing, which were consistently expressed across animals and closely linked to our main findings. We will clarify this rationale in the revised manuscript.

(3) Interpretation of Key Findings and Mechanistic Insights:

Looming exposure increased the proportion of proactive bouts in the dominant zone but decreased it in the subordinate zone (Figure 4G), with a similar trend during rat exposure. Please provide a potential explanation for this consistent pattern. Does this consistency arise from shared neural mechanisms, or do different behavioral strategies converge to produce similar outputs under both threats?

Thanks for bringing up this important question. The consistent increase in proactive bouts in dominant mice across both paradigms suggests a consistent rank-dependent reorganization of dyadic interaction under threats. We propose that this convergence reflects a shared neural mechanism that links defensive state with social-rank information, potentially mediated by overlapping hypothalamic and prefrontal circuits. We will expand the Discussion to incorporate this explanation.

(4) Support for Claims and Study Limitations:

The manuscript states that this work addresses a gap by showing defensive responses are jointly shaped by threat type and social rank, emphasizing survival-critical behaviors over fear or stress alone. However, it is possible that the behavioral differences stem from varying degrees of danger perception rather than purely strategic choices. This warrants a clear description and a deeper discussion to address this possibility.

We thank the reviewer for this insightful comment. We agree that, in principle, behavioral differences could arise from variations in perceived danger rather than strategic choice. In humans, decisions can sometimes reflect value-based strategies that override perceived danger. In contrast, under naturalistic threat conditions, mice likely rely predominantly on danger perception to make behavioral decisions, and such responses are expected to be consistent with value-based strategies shaped by natural selection. In the revised manuscript, we will expand the Discussion to address the role of threat perception and its relationship to decision-making in our behavioral paradigms.

The Discussion section proposes numerous brain regions potentially involved in fear and social regulation. As this is a behavioral study, the extensive speculation on specific neural circuitry involvement, without supporting neuroscience data, appears insufficiently grounded and somewhat vague. It is recommended to focus the discussion more on the implications of the behavioral findings themselves or to explicitly frame these neural hypotheses as directions for future research.

We will revise the Discussion to focus more directly on behavioral findings and add explicit neural hypotheses as potential future directions.

Reviewer #2 (Public review):

Summary:

The authors investigate how dominance hierarchy shapes defensive strategies in mice under two naturalistic threats: a transient visual looming stimulus and a sustained live rat. By comparing single versus paired testing, they report that social presence attenuates fear and that dominant and subordinate mice exhibit different patterns of defensive and social behaviors depending on threat type. The work provides a rich behavioral dataset and a potentially useful framework for studying hierarchical modulation of innate fear.

Strengths:

(1) The study uses two ecologically meaningful threat paradigms, allowing comparison across transient and sustained threat contexts.

(2) Behavioral quantification is detailed, with manual annotation of multiple behavior types and transition-matrix level analysis.

(3) The comparison of dominant versus subordinate pairs is novel in the context of innate fear.

(4) The manuscript is well-organized and clearly written.

(5) Figures are visually informative and support major claims.

Weaknesses:

Lack of neural mechanism insights.

The current study focused on behavior. In the revised manuscript, we will incorporate a discussion of potential neural mechanisms and highlight this as an important direction for future work.

Reviewer #3 (Public review):

Summary:

This study examines how dominance hierarchy influences innate defensive behaviors in pair-housed male mice exposed to two types of naturalistic threats: a transient looming stimulus and a sustained live rat. The authors show that social presence reduces fear-related behaviors and promotes active defense, with dominant mice benefiting more prominently. They also demonstrate that threat exposure reinforces social roles and increases group cohesion. The work highlights the bidirectional interaction between social structure and defensive behavior.

Strengths:

This study makes a valuable contribution to behavioral neuroscience through its well-designed examination of socially modulated fear. A key strength is the use of two ethologically relevant threat paradigms - a transient looming stimulus and a sustained live predator, enabling a nuanced comparison of defensive behaviors. The experimental design is robust, systematically comparing animals tested alone versus with their cage mate to cleanly isolate social effects. The behavioral analysis is sophisticated, employing detailed transition maps that reveal how social context reshapes behavioral sequences, going beyond simple duration measurements. The finding that social modulation is rank-dependent adds significant depth, linking social hierarchy to adaptive defense strategies. Furthermore, the demonstration that threat exposure reciprocally enhances social cohesion provides a compelling systems-level perspective. Together, these elements establish a strong behavioral framework for future investigations into the neural circuits underlying socially modulated innate fear.

Weaknesses:

The study exhibits several limitations. The neural mechanism proposed is speculative, as the study provides no causal evidence.

Establishing causal evidence for neural mechanisms is beyond the scope of the current behavioral study. We highlight this as an important direction for future work.

eLife Assessment

This valuable study tests whether prediction error or prediction uncertainty controls how the brain segments continuous experience into events. The paper uses validated models that predict human behavior to analyze multivariate neural pattern changes during naturalistic movie watching. The authors provide solid evidence that there are overlapping but partially distinct brain dynamics for each signal.

Reviewer #1 (Public review):

Summary:

This paper investigates the control signals that drive event model updating during continuous experience. The authors apply predictions from previously published computational models to fMRI data acquired while participants watched naturalistic video stimuli. They first examine the time course of BOLD pattern changes around human-annotated event boundaries, revealing pattern changes preceding the boundary in anterior temporal and then parietal regions, followed by pattern stabilization across many regions. The authors then analyze time courses around boundaries generated by a model that updates event models based on prediction error and another that uses prediction uncertainty. These analyses reveal overlapping but partially distinct dynamics for each boundary type, suggesting that both signals may contribute to event segmentation processes in the brain.

Strengths:

The question addressed by this paper is of high interest to researchers working on event cognition, perception, and memory. There has been considerable debate about what kinds of signals drive event boundaries, and this paper directly engages with that debate by comparing prediction error and prediction uncertainty as candidate control signals.

The authors use computational models that explain significant variance in human boundary judgments, and they report the variance explained clearly in the paper.

The authors' method of using computational models to generate predictions about when event model updating should occur is a valuable mechanistic alternative to methods like HMM or GSBS, which are data-driven.

The paper utilizes an analysis framework that characterizes how multivariate BOLD pattern dissimilarity evolves before and after boundaries. This approach offers an advance over previous work focused on just the boundary or post-boundary points.

Weaknesses:

Boundaries derived from prediction error and uncertainty are correlated for the naturalistic stimuli. This raises some concerns about how well their distinct contributions to brain activity can be separated. While the authors attempt to look at the unique variance, there is a limit to how effectively this can be done without experimentally dissociating prediction error and uncertainty.

The authors reports an average event length of ~20 seconds, and they also look +20 and -20 seconds around each event boundary. Thus, it's unclear how often pre- and post-boundary timepoints are part of adjacent events. This complicates the interpretations of the reported timecourses.

Reviewer #2 (Public review):

Summary:

Tan et al. examined how multivoxel patterns shift in time windows surrounding event boundaries caused by both prediction errors and prediction uncertainty. They observed that some regions of the brain show earlier pattern shifts than others, followed by periods of increased stability. The authors combine their recent computational model to estimate event boundaries that are based on prediction error vs. uncertainty and use this to examine the moment-to-moment dynamics of pattern changes. I believe this is a meaningful contribution that will be of interest to memory, attention, and complex cognition research.

Strengths:

The authors have shown exceptional transparency in terms of sharing their data, code, and stimuli which is beneficial to the field for future examinations and to the reproduction of findings. The manuscript is well written with clear figures. The study starts from a strong theoretical background to understand how the brain represents events and have used a well-curated set of stimuli. Overall, the authors extend the event segmentation theory beyond prediction error to include prediction uncertainty which is an important theoretical shift that has implications in episodic memory encoding, use of semantic and schematic knowledge and to attentional processing.

Weaknesses:

(1) I am not fully satisfied with the author's explanation of pattern shifts occurring 11.9s prior to event boundaries. The average length of time for an event was 21.4 seconds. The window around the identified event boundaries was 20 seconds on either side. The earliest identified pattern shift peaks occur at 11.9s prior to the actual event boundary. This would mean on average, a pattern shift is occurring approximately at the midway point of the event (11.9s prior to a boundary of a 21.4s event is approx. the middle of an event). The authors offer up an explanation in which top down regions signal an update that propagates to lower order regions closer to the boundary. To make this interpretation concrete, they added an example: "in a narrative where a goal is reached midway-for instance, a mystery solved before the story formally ends-higher-order regions may update the event representation at that point, and this updated model then cascades down to shape processing in lower-level regions". This might make sense in a one-off case of irregular storytelling, but it is odd to think this would generalize. If an event is occurring and a given collection of regions represent that event, it doesn't follow the accepted convention of multivariate representational analysis that that set of regions would undergo such a large shift in patterns in the middle of an event. The stabilization of these patterns taking so long is also odd to me. I suspect some of these findings may be due to the stimuli used in this experiment and I am not confident this would generalize and invite the authors to disagree and explain. In the case of the exercise routine video, I try to imagine going from the push-up event to the jumping jack event. The actor stops doing pushups, stands up, and moves minimally for 16 seconds (these lulls are not uncommon). At that point they start doing jumping jacks. It is immediately evident from that moment on that jumping jacks will be the kind of event you are perceiving which may explain the long delay in event pattern stabilisation. Then about 11.9s prior to the end of the event, when the person is still performing jumping jacks (at this point they have been performing jumping jacks for 6 seconds), I would expect the brain to still be expecting this " jumping jacks event". For some reason at this point multivariate patterns in higher order regions shift. I do not understand what kind of top down processing is happening here and the reviewers need to be more concrete in their explanation because as of right now it is ill-defined. I also recognize that being specific to jumping jacks is maybe unfair, but this would apply to the push-ups, granola bar eating, or table cleaning events in the same manner. I suspect one possibility is that the participants realize that the stereotyped action of jumping jacks is going to continue and, thus, mindwander to other thoughts while waiting for novel, informative information to be presented. This explanation would challenge the more active top down processing assumed by the authors.

I had provided a set of concerns to the authors that were not part of the public review and were not addressed. I was unaware of the exact format of the eLife approach, but I think they are worth open discussion so I am adding them here for consideration. Apologies for any confusion.

(2) Why did the authors not examine event boundary activity magnitude differences from the uncertainty vs error boundaries? I see that the authors have provided the data on the openneuro. However, it seems like the difference in activity maps would not only provide extra contextualization of the findings, but also be fairly trivial. Just by eye-balling the plots, it appears as though there may be activity differences in the mPFC occurring shortly after a boundary between the two. Given this regions role in prediction error and schema, it would be important to understand whether this difference is merely due to thresholding effects or is statistically meaningful.

(3) Further, the authors omitted all subcortical regions some of which would be especially interesting such as the hippocampus, basal ganglia, ventral tegmental area. These regions have a rich and deep background in event boundary activity, and prediction error. Univariate effects in these regions may provide interesting effects that might contextualize some of the pattern shifts in the cortex.

(3) I see that field maps were collected, but the fmriprep methods state that susceptibility distortion correction was not performed. Is there a reason to omit this?

(4) How many events were present in the stimuli?

Reviewer #3 (Public review):

Summary:

The aim of this study was to investigate the temporal progression of the neural response to event boundaries in relation to uncertainty and error. Specifically, the authors asked 1. How neural activity changes before and after event boundaries 2. If uncertainty and error both contribute to explaining the occurrence of event boundaries and 3. If uncertainty and error have unique contributions to explaining the temporal progression of neural activity.

Strengths:

One strength of this paper is that it builds on an already validated computational model. It relies on straightforward and interpretable analysis techniques to answer the main question, with a smart combination of pattern similarity metrics and FIR. This combination of methods may also be an inspiration to other researchers in the field working on similar questions. The paper is well written and easy to follow. The paper convincingly shows that 1. There is a temporal progression of neural activity change before and after an event boundary 2. Event boundaries are predicted best by the combination of uncertainty and error signals.

Weaknesses:

Regarding question 3, the results are less convincing. Although the analyses in Figure S1 show that there are some unique contributions of uncertainty and error, it is unclear to what extent the results in Figure 7 are driven by shared variance. Therefore, it is not clear to what extent the main claim in the abstract is due to shared or unique variance. More specific comments are provided below.

The other issue is the distance between events is short compared to the pre-onset effects that are observed. Halfway the distance between two events there are already neural signatures of change relating to the upcoming event boundary. I wonder if methodological issues could explain this effect and if not, what could allow participants to notice the impending event boundary.

Impact:

If these comments can be addressed sufficiently, I expect that this work will impact the field in its thinking on what drives event boundaries and spur interest in understanding the mechanisms behind the temporal progression of neural activity around these boundaries.

Comments

(1) The correlation between uncertainly and prediction error is very high, which makes it challenging to disentangle the effects of both on the neural response. The analysis in Figure S1 shows that the two predictors indeed have dissociable contributions. However, the results mainly reported in the discussion section and abstract still rely on models where only one of these factors is included at a time. This makes it debatable whether these specific networks mentioned really reflect unique contributions of each of these components. I specifically refer to this statement in the abstract: "Error-driven boundaries were associated with early pattern shifts in ventrolateral prefrontal areas, followed by pattern stabilization in prefrontal and temporal areas. Uncertainty-driven boundaries were linked to shifts in parietal regions within the dorsal attention network, with minimal subsequent stabilization. ". I would encourage repeating all analyses (also the ones in figure 7) with a models that includes both predictors and showing both results in the manuscript, so it is clear which regions really show unique variance related to one of the predictors. I also wonder why it is necessary to look at model comparisons between the combined and unique models, rather than simply reporting the significance of each predictor in the combined model.

(2) The distance between event boundaries ranges between 20 and 30 seconds. The early pre-boundary effect that are observed in the manuscript occur at -12 seconds. This means that these effects occur roughly halfway between the previous and current event. This seems much earlier than expected. That is why I worry that the FIR analyses might not be able to distinguish effects of the previous event from effects of the upcoming event. What evidence is there that the FIR analyses can actually properly show the return to baseline? One way to address this might be to randomize the locations of the event boundaries while preserving the distance between them and rerun the models. This will give a null-model with the same event distances and should be able to distinguish this temporal overlap from the true effects of event boundaries.

(3) If the analyses in point 2 confirm that there is indeed an event-boundary related change that occurs 12 seconds before event onset, it is important to consider what might cause these changes. Are there cues in the movie that indicate that an event boundary is coming? It would be interesting to investigate whether uncertainty and error are higher than expected at 12 seconds pre-onset.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

This paper investigates the control signals that drive event model updating during continuous experience. The authors apply predictions from previously published computational models to fMRI data acquired while participants watched naturalistic video stimuli. They first examine the time course of BOLD pattern changes around human-annotated event boundaries, revealing pattern changes preceding the boundary in anterior temporal and then parietal regions, followed by pattern stabilization across many regions. The authors then analyze time courses around boundaries generated by a model that updates event models based on prediction error and another that uses prediction uncertainty. These analyses reveal overlapping but partially distinct dynamics for each boundary type, suggesting that both signals may contribute to event segmentation processes in the brain.

Strengths:

(1) The question addressed by this paper is of high interest to researchers working on event cognition, perception, and memory. There has been considerable debate about what kinds of signals drive event boundaries, and this paper directly engages with that debate by comparing prediction error and prediction uncertainty as candidate control signals.

(2) The authors use computational models that explain significant variance in human boundary judgments, and they report the variance explained clearly in the paper.

(3) The authors' method of using computational models to generate predictions about when event model updating should occur is a valuable mechanistic alternative to methods like HMM or GSBS, which are data-driven.

(4) The paper utilizes an analysis framework that characterizes how multivariate BOLD pattern dissimilarity evolves before and after boundaries. This approach offers an advance over previous work focused on just the boundary or post-boundary points.

We appreciate this reviewer’s recognition of the significance of this research problem, and of the value of the approach taken by this paper.

Weaknesses:

(1) While the paper raises the possibility that both prediction error and uncertainty could serve as control signals, it does not offer a strong theoretical rationale for why the brain would benefit from multiple (empirically correlated) signals. What distinct advantages do these signals provide? This may be discussed in the authors' prior modeling work, but is left too implicit in this paper.

We added a brief discussion in the introduction highlighting the complementary advantages of prediction error and prediction uncertainty, and cited prior theoretical work that elaborates on this point. Specifically, we now note that prediction error can act as a reactive trigger, signaling when the current event model is no longer sufficient (Zacks et al., 2007). In contrast, prediction uncertainty is framed as proactive, allowing the system to prepare for upcoming changes even before they occur (Baldwin & Kosie, 2021; Kuperberg, 2021). Together, this makes clearer why these two signals could each provide complementary benefits for effective event model updating.

"One potential signal to control event model updating is prediction error—the difference between the system’s prediction and what actually occurs. A transient increase in prediction error is a valid indicator that the current model no longer adequately captures the current activity. Event Segmentation Theory (EST; Zacks et al., 2007) proposes that event models are updated when prediction error increases beyond a threshold, indicating that the current model no longer adequately captures ongoing activity. A related but computationally distinct proposal is that prediction uncertainty (also termed "unpredictability") can serve as a control signal (Baldwin & Kosie, 2021). The advantage of relying on prediction uncertainty to detect event boundaries is that it is inherently proactive: the cognitive system can start looking for cues about what might come next before the next event starts (Baldwin & Kosie, 2021; Kuperberg, 2021). "

(2) Boundaries derived from prediction error and uncertainty are correlated for the naturalistic stimuli. This raises some concerns about how well their distinct contributions to brain activity can be separated. The authors should consider whether they can leverage timepoints where the models make different predictions to make a stronger case for brain regions that are responsive to one vs the other.

We addressed this concern by adding an analysis that explicitly tests the unique contributions of prediction error– and prediction uncertainty–driven boundaries to neural pattern shifts. In the revised manuscript, we describe how we fit a combined FIR model that included both boundary types as predictors and then compared this model against versions with only one predictor. This allowed us to identify the variance explained by each boundary type over and above the other. The results revealed two partially dissociable sets of brain regions sensitive to error- versus uncertainty-driven boundaries (see Figure S1), strengthening our argument that these signals make distinct contributions.

"To account for the correlation between uncertainty-driven boundaries and error-driven boundaries, we also fitted a FIR model that predicted pattern dissimilarity from both types of boundaries (combined FIR) for each parcel. Then, we performed two likelihood ratio tests: combined FIR to error FIR, which measures the unique contribution of uncertainty boundaries to pattern dissimilarity, and combined FIR to uncertainty FIR, which measures the unique contribution of error boundaries to pattern dissimilarity. The analysis also revealed two dissociable sets of brain regions associated with each boundary type (see Figure S1)."

(3) The authors refer to a baseline measure of pattern dissimilarity, which their dissimilarity measure of interest is relative to, but it's not clear how this baseline is computed. Since the interpretation of increases or decreases in dissimilarity depends on this reference point, more clarity is needed.

We clarified how the FIR baseline is estimated in the methods section. Specifically, we now explain that the FIR coefficients should be interpreted relative to a reference level, which reflects the expected dissimilarity when timepoints are far from an event boundary. This makes it clear what serves as the comparison point for observed increases or decreases in dissimilarity.

"The coefficients from the FIR model indicate changes relative to baseline, which can be conceptualized as the expected value when far from event boundaries."

(4) The authors report an average event length of ~20 seconds, and they also look at +20 and -20 seconds around each event boundary. Thus, it's unclear how often pre- and post-boundary timepoints are part of adjacent events. This complicates the interpretations of the reported time courses.

This is related to reviewer's 2 comment, and it will be addressed below.

(5) The authors describe a sequence of neural pattern shifts during each type of boundary, but offer little setup of what pattern shifts we might expect or why. They also offer little discussion of what cognitive processes these shifts might reflect. The paper would benefit from a more thorough setup for the neural results and a discussion that comments on how the results inform our understanding of what these brain regions contribute to event models.

We thank the reviewer for this advice on how better to set the context for the different potential outcomes of the study. We expanded both the introduction and discussion to better set up expectations for neural pattern shifts and to interpret what these shifts may reflect. In the introduction, we now describe prior findings showing that sensory regions tend to update more quickly than higher-order multimodal regions (Baldassano et al., 2017; Geerligs et al., 2021, 2022), and we highlight that it remains unclear whether higher-order updates precede or follow those in lower-order regions. We also note that our analytic approach is well-suited to address this open question. In the discussion, we then interpret our results in light of this framework. Specifically, we describe how we observed early shifts in higher-order areas such as anterior temporal and prefrontal cortex, followed by shifts in parietal and dorsal attention regions closer to event boundaries. This pattern runs counter to the traditional bottom-up temporal hierarchy view and instead supports a model of top-down updating, where high-level representations are updated first and subsequently influence lower-level processing (Friston, 2005; Kuperberg, 2021). To make this interpretation concrete, we added an example: in a narrative where a goal is reached midway—for instance, a mystery solved before the story formally ends—higher-order regions may update the event representation at that point, and this updated model then cascades down to shape processing in lower-level regions. Finally, we note that the widespread stabilization of neural patterns after boundaries may signal the establishment of a new event model.

Excerpt from Introduction:

“More recently, multivariate approaches have provided insights into neural representations during event segmentation. One prominent approach uses hidden Markov models (HMMs) to detect moments when the brain switches from one stable activity pattern to another (Baldassano et al., 2017) during movie viewing; these periods of relative stability were referred to as "neural states" to distinguish them from subjectively perceived events. Sensory regions like visual and auditory cortex showed faster transitions between neural states. Multi-modal regions like the posterior medial cortex, angular gyrus, and intraparietal sulcus showed slower neural state shifts, and these shifts aligned with subjectively reported event boundaries. Geerligs et al. (2021, 2022) employed a different analytical approach called Greedy State Boundary Search (GSBS) to identify neural state boundaries. Their findings echoed the HMM results: short-lived neural states were observed in early sensory areas (visual, auditory, and somatosensory cortex), while longer-lasting states appeared in multi-modal regions, including the angular gyrus, posterior middle/inferior temporal cortex, precuneus, anterior temporal pole, and anterior insula. Particularly prolonged states were found in higher-order regions such as lateral and medial prefrontal cortex.

The previous evidence about evoked responses at event boundaries indicates that these are dynamic phenomena evolving over many seconds, with different brain areas showing different dynamics (Ben-Yakov & Henson, 2018; Burunat et al., 2024; Kurby & Zacks, 2018; Speer et al., 2007; Zacks, 2010). Less is known about the dynamics of pattern shifts at event boundaries (e.g. whether shifts observed in higher-order regions precedes or follow shifts observed in lower-level regions), because the HMM and GSBS analysis methods do not directly provide moment-by-moment measures of pattern shifts. Both the spatial and temporal aspects of evoked responses and pattern shifts at event boundaries have the potential to provide evidence about two potential control processes (error-driven and uncertainty-driven) for event model updating.”

Excerpt from Discussion:

“We first characterized the neural signatures of human event segmentation by examining both univariate activity changes and multivariate pattern changes around subjectively identified event boundaries. Using multivariate pattern dissimilarity, we observed a structured progression of neural reconfiguration surrounding human-identified event boundaries. The largest pattern shifts were observed near event boundaries (~4.5s before) in dorsal attention and parietal regions; these correspond with regions identified by Geerligs et. al as shifting their patterns on a fast to intermediate timescale (2022). We also observed smaller pattern shifts roughly 12 seconds prior to event boundaries in higher-order regions within anterior temporal cortex and prefrontal cortex, and these are slow-changing regions identified by Geerligs et. al (2022). This is puzzling. One prevalent proposal, based on the idea of a cortical hierarchy of increasing temporal receptive windows (TRWs), suggests that higher-order regions should update representations after lower-order regions do (Chang et al., 2021). In this view, areas with shorter TRWs (e.g., word-level processors) pass information upward, where it is integrated into progressively larger narrative units (phrases, sentences, events). This proposal predicts neural shifts in higher-order regions to follow those in lower-order regions. By contrast, our findings indicate the opposite sequence. Our findings suggest that the brain might engage in top-down event representation updating, with changes in coarser-grain representations propagating downward to influence finer-grain representations. (Friston, 2005; Kuperberg, 2021). For example, in a narrative where the main goal is achieved midway—such as a detective solving a mystery before the story formally ends—higher-order regions might update the overarching event representation at that point, and this updated model could then cascade down to reconfigure how lower-level regions process the remaining sensory and contextual details. In the period after a boundary (around +12 seconds), we found widespread stabilization of neural patterns across the brain, suggesting the establishment of a new event model. Future work could focus on understanding the mechanisms behind the temporal progression of neural pattern changes around event boundaries.”

Reviewer #2 (Public review):

Summary:

Tan et al. examined how multivoxel patterns shift in time windows surrounding event boundaries caused by both prediction errors and prediction uncertainty. They observed that some regions of the brain show earlier pattern shifts than others, followed by periods of increased stability. The authors combine their recent computational model to estimate event boundaries that are based on prediction error vs. uncertainty and use this to examine the moment-to-moment dynamics of pattern changes. I believe this is a meaningful contribution that will be of interest to memory, attention, and complex cognition research.

Strengths:

The authors have shown exceptional transparency in terms of sharing their data, code, and stimuli, which is beneficial to the field for future examinations and to the reproduction of findings. The manuscript is well written with clear figures. The study starts from a strong theoretical background to understand how the brain represents events and has used a well-curated set of stimuli. Overall, the authors extend the event segmentation theory beyond prediction error to include prediction uncertainty, which is an important theoretical shift that has implications in episodic memory encoding, the use of semantic and schematic knowledge, and attentional processing.

We thank the reader for their support for our use of open science practices, and for their appreciation of the importance of incorporating prediction uncertainty into models of event comprehension.

Weaknesses:

The data presented is limited to the cortex, and subcortical contributions would be interesting to explore. Further, the temporal window around event boundaries of 20 seconds is approximately the length of the average event (21.4 seconds), and many of the observed pattern effects occur relatively distal from event boundaries themselves, which makes the link to the theoretical background challenging. Finally, while multivariate pattern shifts were examined at event boundaries related to either prediction error or prediction uncertainty, there was no exploration of univariate activity differences between these two different types of boundaries, which would be valuable.

The fact that we observed neural pattern shifts well before boundaries was indeed unexpected, and we now offer a more extensive interpretation in the discussion section. Specifically, we added text noting that shifts emerged in higher-order anterior temporal and prefrontal regions roughly 12 seconds before boundaries, whereas shifts occurred in lower-level dorsal attention and parietal regions closer to boundaries. This sequence contrasts with the traditional bottom-up temporal hierarchy view and instead suggests a possible top-down updating mechanism, in which higher-order representations reorganize first and propagate changes to lower-level areas (Friston, 2005; Kuperberg, 2021). (See excerpt for Reviewer 1’s comment #5.)

With respect to univariate activity, we did not find strong differences between error-driven and uncertainty-driven boundaries. This makes the multivariate analyses particularly informative for detecting differences in neural pattern dynamics. To support further exploration, we have also shared the temporal progression of univariate BOLD responses on OpenNeuro (BOLD_coefficients_brain_animation_pe_SEM_bold.html and BOLD_coefficients_brain_animation_uncertainty_SEM_bold.html in the derivatives/figures/brain_maps_and_timecourses/ directory; https://doi.org/10.18112/openneuro.ds005551.v1.0.4) for interested researchers.

Reviewer #3 (Public review):

Summary:

The aim of this study was to investigate the temporal progression of the neural response to event boundaries in relation to uncertainty and error. Specifically, the authors asked (1) how neural activity changes before and after event boundaries, (2) if uncertainty and error both contribute to explaining the occurrence of event boundaries, and (3) if uncertainty and error have unique contributions to explaining the temporal progression of neural activity.

Strengths:

One strength of this paper is that it builds on an already validated computational model. It relies on straightforward and interpretable analysis techniques to answer the main question, with a smart combination of pattern similarity metrics and FIR. This combination of methods may also be an inspiration to other researchers in the field working on similar questions. The paper is well written and easy to follow. The paper convincingly shows that (1) there is a temporal progression of neural activity change before and after an event boundary, and (2) event boundaries are predicted best by the combination of uncertainty and error signals.

We thank the reviewer for their thoughtful and supportive comments, particularly regarding the use of the computational model and the analysis approaches.

Weaknesses:

(1) The current analysis of the neural data does not convincingly show that uncertainty and prediction error both contribute to the neural responses. As both terms are modelled in separate FIR models, it may be that the responses we see for both are mostly driven by shared variance. Given that the correlation between the two is very high (r=0.49), this seems likely. The strong overlap in the neural responses elicited by both, as shown in Figure 6, also suggests that what we see may mainly be shared variance. To improve the interpretability of these effects, I think it is essential to know whether uncertainty and error explain similar or unique parts of the variance. The observation that they have distinct temporal profiles is suggestive of some dissociation,but not as convincing as adding them both to a single model.

We appreciate this point. It is closely related to Reviewer 1's comment 2; please refer to our response above.

(2) The results for uncertainty and error show that uncertainty has strong effects before or at boundary onset, while error is related to more stabilization after boundary onset. This makes me wonder about the temporal contribution of each of these. Could it be the case that increases in uncertainty are early indicators of a boundary, and errors tend to occur later?

We also share the intuition that increases in uncertainty are early indicators of a boundary, and errors tend to occur later. If that is the case, we would expect some lags between prediction uncertainty and prediction error. We examined lagged correlation between prediction uncertainty and prediction error, and the optimal lag is 0 for both uncertainty-driven and error-driven models. This indicates that when prediction uncertainty rises, prediction error also simultaneously rises.

Author response image 1.

(3) Given that there is a 24-second period during which the neural responses are shaped by event boundaries, it would be important to know more about the average distance between boundaries and the variability of this distance. This will help establish whether the FIR model can properly capture a return to baseline.

We have added details about the distribution of event lengths. Specifically, we now report that the mean length of subjectively identified events was 21.4 seconds (median 22.2 s, SD 16.1 s). For model-derived boundaries, the average event lengths were 28.96 seconds for the uncertainty-driven model and 24.7 seconds for the error-driven model.

" For each activity, a separate group of 30 participants had previously segmented each movie to identify fine-grained event boundaries (Bezdek et al., 2022). The mean event length was 21.4 s (median 22.2 s, SD 16.1 s). Mean event lengths for uncertainty-driven model and error-driven model were 28.96s, and 24.7s, respectively (Nguyen et al., 2024)."

(4) Given that there is an early onset and long-lasting response of the brain to these event boundaries, I wonder what causes this. Is it the case that uncertainty or errors already increase at 12 seconds before the boundaries occur? Or if there are other makers in the movie that the brain can use to foreshadow an event boundary? And if uncertainty or errors do increase already 12 seconds before an event boundary, do you see a similar neural response at moments with similar levels of error or uncertainty, which are not followed by a boundary? This would reveal whether the neural activity patterns are specific to event boundaries or whether these are general markers of error and uncertainty.

We appreciate this point; it is similar to reviewer 2’s comment 2. Please see our response to that comment above.

(5) It is known that different brain regions have different delays of their BOLD response. Could these delays contribute to the propagation of the neural activity across different brain areas in this study?

Our analyses use ±20 s FIR windows, and the key effects we report include shifts ~12s before boundaries in higher-order cortex and ~4.5s pre-boundary in dorsal attention/parietal areas. Given the literature above, region-dependent BOLD delays are much smaller (~1–2s) than the temporal structure we observe (Taylor et al., 2018), making it unlikely that HRF lag alone explains our multi-second, region-specific progression.

(6) In the FIR plots, timepoints -12, 0, and 12 are shown. These long intervals preclude an understanding of the full temporal progression of these effects.

For page length purposes, we did not include all timepoints. We uploaded a brain animation of all timepoints and coefficients for each parcel in Openneuro (PATTERN_coefficients_brain_animation_human_fine_pattern.html and PATTERN_coefficients_lines_human_fine.html in the derivatives/figures/brain_maps_and_timecourses/ directory; https://doi.org/10.18112/openneuro.ds005551.v1.0.4) for interested researchers.

References

Taylor, A. J., Kim, J. H., & Ress, D. (2018). Characterization of the hemodynamic response function across the majority of human cerebral cortex. NeuroImage, 173, 322–331. https://doi.org/10.1016/j.neuroimage.2018.02.061

eLife Assessment

This study presents valuable analyses of single neuron activity in the subthalamic nucleus (STN) of monkeys performing a decision-making task that manipulates both perceptual evidence and reward. In particular, the study shows convincing evidence of multiple decision variables being represented in the STN. However, the evidence for sub-populations in STN with distinct involvements in decision-making is incomplete at this stage and requires either further efforts to provide stronger support or refinement of that conclusion.

Reviewer #1 (Public review):

Summary:

This manuscript offers a careful and technically impressive dissection of how subpopulations within the subthalamic nucleus support reward‑biased decision‑making. The authors recorded from STN neurons in monkeys performing an asymmetric‑reward version of a visual motion discrimination task and combined single‑unit analyses, regression modeling, and drift‑diffusion framework fitting to reveal functionally distinct clusters of neurons. Each subpopulation demonstrated unique relationships to decision variables - such as the evidence‑accumulation rate, decision bound, and non‑decision processes - as well as to post‑decision evaluative signals like choice accuracy and reward expectation. Together, these findings expand our understanding of the computational diversity of STN activity during complex, multi‑attribute choices.

Strengths:

(1) The use of an asymmetric‑reward paradigm enables a clean separation between perceptual and reward influences, making it possible to identify how STN neurons blend these different sources of information.

(2) The dataset is extensive and well‑controlled, with careful alignment between behavioral and neural analyses.

(3) Relating neuronal cluster activity to drift‑diffusion model parameters provides an interpretable computational link between neural population signals and observed behavior.

(4) The clustering analyses, validated across multiple parameters and distance metrics, reveal robust functional subgroups within STN. The differentiation of clusters with respect to both evidence and reward coding is an important advance over treating the STN as a unitary structure.

(5) By linking neural activity to predicted choice accuracy and reward expectation, the study extends the discussion of the STN beyond decision formation to include outcome monitoring and post‑decision evaluation.

Weaknesses:

(1) The inferred relationships between neural clusters and specific drift‑diffusion parameters (e.g., bound height, scaling factor, non‑decision time) are intriguing but inherently correlational. The authors should clarify that these associations do not necessarily establish distinct computational mechanisms.

(2) While the k‑means approach is well described, it remains somewhat heuristic. Including additional cross‑validation (e.g., cluster reproducibility across monkeys or sessions) would strengthen confidence in the four‑cluster interpretation.

(3) The functional dissociations across clusters are clearly described, but how these subgroups interact within the STN or through downstream basal‑ganglia circuits remains speculative.

(4) A natural next step would be to construct a generative multi‑cluster model of STN activity, in which each cluster is treated as a computational node (e.g., evidence integrator, bound controller, urgency or evaluative signal).

(5) Such a low‑dimensional, coupled model could reproduce the observed diversity of firing patterns and predict how interactions among clusters shape decision variables and behavior.

(6) Population‑level modeling of this kind would move the interpretation beyond correlational mapping and serve as an intermediate framework between single‑unit analysis and in‑vivo perturbation.

(7) Causal inference gap - Without perturbation data, it is difficult to determine whether the identified neural modulations are necessary or sufficient for the observed behavioral effects. A brief discussion of this limitation - and how future causal manipulations could test these cluster functions - would be valuable.

Reviewer #2 (Public review):

This study uses monkey single-unit recordings to examine the role of the STN in combining noisy sensory information with reward bias during decision-making between saccade directions. Using multiple linear regressions and k-means clustering approaches, the authors overall show that a highly heterogeneous activity in the STN reflects almost all aspects of the task, including choice direction, stimulus coherence, reward context and expectation, choice evaluation, and their interactions. The authors report in particular how, here too, in a very heterogeneous way, four classes of neurons map to different decision processes evaluated via the fitting of a drift-diffusion model. Overall, the study provides evidence for functionally diverse populations of STN neurons, supporting multiple roles in perceptual and reward-based decision-making.

This study follows up on work conducted in previous years by the same team and complements it. Extracellular recordings in monkeys trained to perform a complex decision-making task remain a remarkable achievement, particularly in brain structures that are difficult to target, such as the subthalamic nucleus. The authors conducted numerous rigorous and systematic analyses of STN activities, using sophisticated statistical approaches and functional computational modeling.

One criticism I would make is that the authors sometimes seem to assume that readers are familiar with their previous work. Indeed, the motivation and choices behind some analyses are not clearly explained. It might be interesting to provide a little more context and insight into these methodological choices. The same is true for the description of certain results, such as the behavioral results, which I find insufficiently detailed, especially since the two animals do not perform exactly the same way in the task.

Another criticism is the difficulty in following and absorbing all the presented results, given their heterogeneity. This heterogeneity stems from analytical choices that include defining multiple time windows over which activities are studied, multiple task-related or monkey behavioral factors that can influence them, multiple parameters underlying the decision-making phenomena to be captured, and all this without any a priori hypotheses. The overall impression is of an exploratory description that is sometimes difficult to digest, from which it is hard to extract precise information beyond the very general message that multiple subpopulations of neurons exist and therefore that the STN is probably involved in multiple roles during decision-making.

It would also have been interesting to have information regarding the location of the different identified subpopulations of neurons in the STN and their level of segregation within this nucleus. Indeed, since the STN is one of the preferred targets of electrical stimulation aimed at improving the condition of patients suffering from various neurological disorders, it would be interesting to know whether a particular stimulation location could preferentially affect a specific subpopulation of neurons, with the associated specific behavioral consequences.

Therefore, this paper is interesting because it complements other work from the same team and other studies that demonstrate the likely important role of the STN in decision-making. This will be of interest to the decision-making neuroscience community, but it may leave a sense of incompleteness due to the difficulty in connecting the conclusions of these different studies. For example, in the discussion section, the authors attempt to relate the different neuronal populations identified in their study and describe some relatively consistent results, but others less so.

Reviewer #3 (Public review):

Summary:

In this study, the authors investigate single neuron activity in the subthalamic nucleus (STN) of two monkeys performing a perceptual decision-making task in which both perceptual evidence and reward were manipulated. They find rich representations of decision variables (such as choice, perceptual evidence and reward) in neural activity, and following prior work, cluster a subset of these neurons into subpopulations with varying activity profiles. Further, they relate the activity of neurons within these clusters to parameters of drift diffusion models (DDMs) fit to animal behaviour on trial subsets by neural firing rates, finding heterogeneous and temporally varying relationships between different clusters and DDM parameters, suggesting that STN neurons may play multiple roles in decision formation and evaluation.

Strengths:

The behavioural task used by the authors is rich and affords disambiguation between decision variables such as perceptual evidence, value and choice, by independently manipulating stimulus strength and reward size. Both their monkeys show good performance on the task, and their population of ~150 neurons across monkeys reveals a rich repertoire of decision-related activity in single neurons, with individual neurons showing strong tuning to choice, stimulus strength and reward bias. There is little doubt that neurons in the STN are tuned to several decision variables and show heterogeneous tuning profiles.

Weaknesses:

The primary weakness of the paper lies in the claim that STN contains multiple sub-populations with distinct involvements in decision making, which is inadequately supported by the paper's methods and analyses.

First, while it is clear that the ~150 recorded neurons across 2 monkeys (91, 59 respectively) display substantial heterogeneity in their activity profiles across time and across stimulus/reward conditions, the claim of sub-populations largely rests on clustering a *subset of less than half the population - 66 neurons (48, 15 respectively) - chosen manually by visual inspection*. The full population seems to contain far more decision-modulated neurons, whose response profiles seem to interpolate between clusters. Moreover, it is unclear if the 4 clusters hold for each of the 2 monkeys, and the choice of 4-5 clusters does not seem well supported by metrics such as silhouette score, etc, that peak at 3 (1 or 2 were not attempted). From the data, it is easier to draw the conclusion that the STN population contains neurons with heterogeneous response profiles that smoothly vary in their tuning to different decision variables, rather than distinct sub-populations.

Second, assuming the existence of sub-populations, it is unclear how their time- and condition-varying relationship with DDM parameters is to be interpreted. These relationships are inferred by splitting trials based on individual neurons' firing rates in different task epochs and reward contexts, and regressing onto the parameters of separate DDMs fit to those subsets of trials. The result is that different sub-populations show heterogeneous relationships to different DDM parameters over time - a result that, while interesting, leaves the computational involvement of these sub-populations/implementation of the decision process unclear.

Outlook:

This is a paper with a rich dataset of neural activity in the STN in a rich perceptual decision-making task, and convincing evidence of heterogeneity in choice, value and evidence tuning across the STN, suggesting the STN may be involved in several aspects of decision-making. However, the authors' specific claims about sub-populations in the STN, each having distinct relationships to decision processes, are not adequately supported by their analyses.

eLife Assessment

This work represents a valuable finding of how single-trial functional connectivity may be used to infer different cognitive states involved in speech perception and production. Although the data and analyses are overall convincing, the theoretical advance and novelty of the finding are less clear. With a clearer idea of the functional significance of the connectivity data, the paper would be of interest to those interested in brain networks and communication.

Reviewer #1 (Public review):

In this study, the authors took advantage of a powerful method (iEEG) in a large participant cohort (N=42) to demonstrate specific functional connectivity signatures associated with speech. The results highlight the complementary utility of functional connectivity analysis to the more traditional iEEG approaches of characterizing local neural activity.

Strengths:

This is an interesting study on the important topic of cortical mechanisms of speech perception and production in humans. The authors provide strong evidence for specific functional connectivity signatures of speech-related cortical activity.

Weaknesses:

A potential issue of the work is the interpretation of the five studied experimental conditions as representing distinct cognitive states, where "task conditions" or "behavioral states" would have been more appropriate.

Reviewer #2 (Public review):

Summary:

This study, conducted by Esmaeili and colleagues, investigates the functional connectivity signatures of different auditory, visual, and motor states in 42 ECoG patients. Patients performed three tasks: picture naming, visual word reading, and auditory word repetition. They use an SVM classifier on correlation patterns across electrodes during these tasks, separating speech production from sensory perception, and incorporating baseline silence as another state. They find that it is possible to classify five states (auditory perception, picture viewing, word reading, speech production, and baseline) based on their connectivity patterns alone. Furthermore, they find a sparser set of "discriminative connections" for each state that can be used to predict each of these states. They then relate these connectivity matrices to high-gamma evoked data, and show largely overlapping relationships between the discriminative connections and the active high-gamma electrodes. However, there are still some connectivity nodes that are important in discriminating states, but that do not show high evoked activity, and vice versa. Overall, the study has a large number of patients, and the ability to decode cognitive state is compelling. The main weaknesses of the work are in placing the findings into a wider context for what additional information the connectivity analysis provides about brain processing of speech, since, as it stands, the analysis mostly reidentifies areas already known to be important for speaking, listening, naming, and visual processing.

Strengths:

(1) The authors were able to assess their connectivity analysis on a large cohort of patients with wide coverage across speech and language areas.

(2) The use of controlled tasks for picture naming, visual word reading, and auditory word repetition allows for parcellating specific components of stimulus perception and speech production.

(3) The authors chose not to restrict their connectivity analysis to previously identified high amplitude responses, which allowed them to find regions that are discriminative between different states in their speech tasks, but not necessarily highly active.

Weaknesses:

(1) Although the work identifies some clear connectivity between brain areas during speech perception and production, it is not clear whether this approach allows us to learn anything new about brain systems for speech. The areas that are identified have been shown in other studies and are largely unsurprising - the auditory cortex is involved in hearing words, picture naming involves frontal and visual cortical interactions, and overt movements include the speech motor cortex. The temporal pole is a new area that shows up, but (see below) it is important to show that this region is not affected by artifacts. Overall, it would help if the authors could expand upon the novelty of their approach.

(2) Because the connectivity is derived from single trials, it is possible that some of the sparse connectivity seen in noncanonical areas is due to a common artifact across channels. The authors do employ a common average reference, which should help to reduce common-mode noise across all channels, but not smaller subsets. Could the authors include more information to show that this is not the case in their dataset? For example, the temporal pole electrodes show strong functional connectivity, but these areas can tend to include more EMG artifact or ocular artifact. Showing single-trial traces for some of these example pairs of electrodes and their FC measures could help in interpreting how robust the findings are.

(3) The connectivity matrices are defined by taking the correlation between all pairs of electrodes across 500-ms epochs for each cognitive state, presumably for electrodes that are time-aligned. However, it is likely that different areas will interact with different time delays - for example, activity in one area may lead to activity in another. It might be helpful to include some time lags between different brain areas if the authors are interested in dynamics between areas that are not simultaneous.

(4) In Figure 3, the baseline is most commonly confused with other categories (most notably, speech production, 22% of the time). Is there any intuition for why this might be? Could some of this confusion be due to task-irrelevant speech occurring during the baseline / have the authors verified that all pre-stimulus time periods were indeed silent?

(5) How similar are discriminative connections across participants? Do they tend to reflect the same sparse anatomical connections? It is not clear how similar the results are across participants.

(6) The results in Figure 5F are interesting and show that frontal electrodes are often highly functionally connected, but have low evoked activity. What do the authors believe this might reflect? What are these low-evoked activity electrodes potentially doing? Some (even speculative) mention might be helpful.

(7) One comparison that seems to be missing, if the authors would like to claim the utility of functional connectivity over evoked measures, is to directly compare a classifier based on the high gamma activity patterns alone, rather than the pairwise connectivity. Does the FC metric outperform simply using evoked activity?

Reviewer #3 (Public review):

I read this manuscript with great interest. The purpose of this paper is to use human intracranial recordings in patients undergoing routine epilepsy surgery evaluation to investigate speech production and perception during five specific and controlled tasks (auditory perception, picture perception, reading perception, speech production, and baseline). Linear classifiers were used to decode specific states with a mean accuracy of 64.4%. The interpretation of these findings is that the classifiers reveal distinct network signatures "underlying auditory and visual perception as well as speech production." Perhaps the most interesting finding is that the network signatures, including both regions with robust local neuronal activity and those without. Further, this study addresses an important gap by examining functional connectivity during overt speech production.

The abbreviation ECoG is used throughout the manuscript, and the methods state that grids and strips were placed, though many epilepsy centers now employ intracerebral recordings. Does this manuscript only include patients with surface electrodes? Or are depth electrodes also included? The rendering maps show only the cortical surface, but depth recordings could be very interesting, given that this is a connectivity analysis.

Also interesting, given both the picture and reading task, is whether there is coverage of the occipitotemporal sulcus?

A major strength of the chosen paradigm is the combination of both perception (auditory or visual) and production (speech). Have the authors considered oculomotor EMG artifacts that can be associated with the change in visual stimuli during the task (see Abel et al. for an example PMID: 27075536, but see also PMID: 19234780 and PMID: 20696256).

I'm very interested in the findings in Figure 4D, with regard to the temporal pole. I would recommend that the authors unpack what it means that the ratio of electrodes with the strongest connections is highest, but active and discriminative is perhaps the lowest. We (I think many groups!) are interested in this region as a multimodal hub that provides feedback in various contexts (like auditory or visual perception).

Given the varieties of tasks and the fact that electrodes are always placed based on clinical necessity, are there concerns about electrode sampling bias?

This manuscript makes an important contribution by demonstrating that functional connectivity analysis reveals task-specific network signatures beyond what is captured by local neuronal activity measures (LFP). The finding that low-activity regions are engaged in task-specific classifications has important implications for future human LFP connectivity work.

eLife Assessment

This important study is of relevance for the fields of predictive processing, perception and learning, with a well-designed paradigm allowing the authors to avoid several common confounds in investigating predictions, such as adaptation. Using a state-of-the-art multivariate EEG approach, the authors test the opposing process theory and find evidence in support of it. Overall, the empirical evidence is solid, however, some conclusions rest on limited evidence and need further work to reconcile the present results with previous studies.

Reviewer #3 (Public review):

Summary:

In their study McDermott et al. investigate the neurocomputational mechanism underlying sensory prediction errors. They contrast two accounts: representational sharpening and dampening. Representational sharpening suggests that predictions increase the fidelity of the neural representations of expected inputs, while representational dampening suggests the opposite (decreased fidelity for expected stimuli). The authors performed decoding analyses on EEG data, showing that first expected stimuli could be better decoded (sharpening), followed by a reversal during later response windows where unexpected inputs could be better decoded (dampening). These results are interpreted in the context of opposing process theory (OPT), which suggests that such a reversal would support perception to be both veridical (i.e., initial sharpening to increase the accuracy of perception) and informative (i.e., later dampening to highlight surprising, but informative inputs).

Strengths:

The topic of the present study is of significant relevance for the field of predictive processing. The experimental paradigm used by McDermott et al. is well designed, allowing the authors to avoid common confounds in investigating predictions, such as stimulus familiarity and adaptation. The introduction provides a well written summary of the main arguments for the two accounts of interest (sharpening and dampening), as well as OPT. Overall, the manuscript serves as a good overview of the current state of the field.

Weaknesses:

In my opinion the study has a few weaknesses. Some method choices appear arbitrary (e.g., binning). Additionally, not all results are necessarily predicted by OPT. Finally, results are challenging to reconcile with previous studies. For example, while I agree with the authors that stimulus familiarity is a clear difference compared to previous designs, without a convincing explanation why this would produce the observed pattern of results, I find the account somewhat unsatisfying.

Author response:

The following is the authors’ response to the previous reviews

Reviewer 1

Minor

The main substance of my previous comment I suppose targeted a deeper issue - namely whether such a result is reflecting a resolution to a 'neural prediction' puzzle or a 'perceptual prediction' puzzle. Of course, these results tell us a great deal about a potential resolution for how dampening and sharpening might co-exist in the brain - but in the absence of corresponding perceptual effects (or a lack of correlation between neural and perceptual variables - as outlined in this revision) I do wonder if any claims about implications for perception might need moderation or caveating. To be honest, I don't think the authors *need* to make any more changes along these lines for this paper to be acceptable - it is more an issue they might wish to consider themselves when contextualizing their findings.

Thank you for the thoughtful comment. We have now added a caveat to the relevant section of the discussion to make it clearer that we are discussing neural results, not perceptual results (p.20, lines 378-379).

I am also happy with the changes that the authors have made justifying which claims can and cannot made based on a statistical decoding test against 'chance' in a single condition using t-tests. I was perhaps a little unclear when I spoke about 'comparisons against 0' in my original review, when the key issue (as the authors have intuited!) is about comparisons against 'chance' (where e.g., 0% decoding above chance is the same thing as 'chance'!). The authors are of course correct in the amendment they have made on p.29 to make clear this is a 'fixed effects analysis' - though I still worry this could be a little cryptic for the average reader. I am not suggesting that the authors run more analyses, or revise any conclusions, but I think it would be more transparent if a note was added along the lines of "while the fixed effects approach (one-sample t-test) enables us to establish whether some consistent informative patterns are detectable in these particular subjects, the results from our paired t-tests support inference to the wider population".

This sentence has been added for increased transparency (p. 27, lines 544-547).

Reviewer 3

Major

(1) In the previous round of comments, I noted that: "I am not fully convinced that Figures 3A/B and the associated results support the idea that early learning stages result in dampening and later stages in sharpening. The inference made requires, in my opinion, not only a significant effect in one-time bin and the absence of an effect in other bins. Instead to reliably make this inference one would need a contrast showing a difference in decoding accuracy between bins, or ideally an analysis not contingent on seemingly arbitrary binning of data, but a decrease (or increase) in the slope of the decoding accuracy across trials. Moreover, the decoding analyses seem to be at the edge of SNR, hence making any interpretation that depends on the absence of an effect in some bins yet more problematic and implausible". The authors responded: "we fitted a logarithmic model to quantify the change of the decoding benefit over trials, then found the trial index for which the change of the logarithmic fit was < 0.1%. Given the results of this analysis and to ensure a sufficient number of trials, we focused our further analyses on bins 1-2". However, I do not see how this new analysis addresses the concern that the conclusion highlights differences in decoding performance between bins 1 and 2, yet no contrast between these bins are performed. While I appreciate the addition of the new model, in my current understanding it does not solve the problem I raised. I still believe that if the authors wish to conclude that an effect differs between two bins they must contrast these directly and/or use a different appropriate analysis approach.

Relatedly, the logarithmic model fitting and how it justifies the focus on analysis bin 1-2 needs to be explained better, especially the rationale of the analysis, the choice of parameters (e.g., why logarithmic, why change of logarithmic fit < 0.1% as criterion, etc), and why certain inferences follow from this analysis. Also, the reporting of the associated results seems rather sparse in the current iteration of the manuscript.

We thank the reviewer for this important point. Following your suggestion, we conducted additional post-hoc tests directly comparing the first and second bins. We found significant differences between bins in the invalid trials, but not the valid trials, suggesting that sharpening/dampening effects are condition specific. This is discussed in the manuscript on p.14, lines 268-271; p.15, 280-284; p.20, lines 382-386.

A logarithmic analysis was chosen as learning is usually found to be a nonlinear process; learning effects occur rapidly before stabilising relatively early, as seen in Fig. 2D. This is consistent with other research which found that logarithmic fits efficiently describe learning curves in statistical learning (Kang et al., 2023; Siegelman et al., 2018; Choi et al., 2020). By utilising a change of logarithmic fit at <0.1% as a criterion, it is ensured that virtually zero learning took place after that point, allowing us to focus our analysis on learning effects as they developed and providing a more accurate model of representational change. This is explained in the manuscript on p.13, lines 250-251; p.27-28, lines 557-563.

(2) A critical point the authors raise is that they investigate the buildup of expectations during training. They go on to show that the dampening effect disappears quickly, concluding: "the decoding benefit of invalid predictions [...] disappeared after approximately 15 minutes (or 50 trials per condition)". Maybe the authors can correct me, but my best understanding is as follows: Each bin has 50 trials per condition. The 2:1 condition has 4 leading images, this would mean ~12 trials per leading stimulus, 25% of which are unexpected, so ~9 expected trials per pair. Bin 1 represents the first time the participants see the associations. Therefore, the conclusion is that participants learn the associations so rapidly that ~9 expected trials per pair suffice to not only learn the expectations (in a probabilistic context) but learn them sufficiently well such that they result in a significant decoding difference in that same bin. If so, this would seem surprisingly fast, given that participants learn by means of incidental statistical learning (i.e. they were not informed about the statistical regularities). I acknowledge that we do not know how quickly the dampening/sharpening effects develop, however surprising results should be accompanied with a critical evaluation and exceptionally strong evidence (see point 1). Consider for example the following alternative account to explain these results. Category pairs were fixed across and within participants,i.e. the same leading image categories always predicted the same trailing image categories for all participants. Some category pairings will necessarily result in a larger representational overlap (i.e., visual similarity, etc.) and hence differences in decoding accuracy due to adaptation and related effects. For example, house  barn will result in a different decoding performance compared to coffee cup  barn, simply due to the larger visual and semantic similarity between house and barn compared to coffee cup and barn. These effects should occur upon first stimulus presentation, independent of statistical learning, and may attenuate over time e.g., due to increasing familiarity with the categories (i.e., an overall attenuation leading to smaller between condition differences) or pairs.

We apologise for the confusion, there are 50 expected trials per bin per condition. The trial breakdown is as follows. Each participant completed 1728 trials, split equally across 3 mappings (two 2:1 maps and one 1:2 map), giving 1152 trials in the 2:1 mapping. Stimuli were expected in 75% of trials (864), leaving 216 per bin, and 54 per leading image in each bin. We have clarified this in the script (p.14, line 267; p.15, line 280). This is in line with similar studies in the field (e.g. Han et al., 2019).

(3) In response to my previous comment, why the authors think their study may have found different results compared to multiple previous studies (e.g. Han et al., 2019; Kumar et al., 2017; Meyer and Olson, 2011), particularly the sharpening to dampening switch, the authors emphasize the use of non-repeated stimuli (no repetition suppression and no familiarity confound) in their design. However, I fail to see how familiarity or RS could account for the absence of

sharpening/dampening inversion in previous studies.

First, if the authors argument is about stimulus novelty and familiarity as described by Feuerriegel et al., 2021, I believe this point does not apply to the cited studies. Feuerriegel et al., 2021 note: "Relative stimulus novelty can be an important confound in situations where expected stimulus identities are presented often within an experiment, but neutral or surprising stimuli are presented only rarely", which indeed is a critical confound. However, none of the studies (Han et al., 2019; Richter et al., 2018; Kumar et al., 2017; Meyer and Olson, 2011) contained this confound, because all stimuli served as expected and unexpected stimuli, with the expectation status solely determined by the preceding cue. Thus, participants were equally familiar with the images across expectation conditions.

Second, for a similar reason the authors argument for RS accounting for the different results does not hold either in my opinion. Again, as Feuerriegel et al. 2021 correctly point out: "Adaptation-related effects can mimic ES when the expected stimuli are a repetition of the last-seen stimulus or have been encountered more recently than stimuli in neutral expectation conditions." However, it is critical to consider the precise design of previous studies. Taking again the example of Han et al., 2019; Kumar et al., 2017; Meyer and Olson, 2011. To my knowledge none of these studies contained manipulations that would result in a more frequent or recent repetition of any specific stimulus in the expected compared to unexpected condition. The crucial manipulation in all these previous studies is not that a single stimulus or stimulus feature (which could be subject to familiarity or RS) determines the expectation status, but rather the transitional probability (i.e. cue-stimulus pairing) of a particular stimulus given the cue. Therefore, unless I am missing something critical, simple RS seems unlikely to differ between expectation condition in the previous studies and hence seems implausible to account for differences in results compared to the current study.

Moreover, studies cited by the authors (e.g. Todorovic & de Lange, 2012) showed that RS and ES are separable in time, again making me wonder how avoiding stimulus repetition should account for the difference in the present study compared to previous ones. I am happy to be corrected in my understanding, but with the currently provided arguments by the authors I do not see how RS and familiarity can account for the discrepancy in results.

The reviewer is correct in that the studies cited (Han et al., 2019; Kumar et al., 2017; Meyer and Olson, 2011) ensure that participants are equally familiar with the images across expectation conditions. Where the present study differs is that participants are not familiar with individual exemplars at all. Han et al., 2019 used a pool of 30 individual images, and subjects underwent exposure sessions lasting two hours each daily for 34 days prior to testing. Kumar et al., 2017 used a pool of 12 images with subjects being exposed to each sequential pair 816 times over the course of the training period. Meyer & Olsen, 2011 used pure tones at five different pitch levels. While familiarity of stimuli across conditions was controlled for in these studies in the sense that familiarity was constant across conditions, novelty was not controlled for. The present study uses a pool of ~3500 images, which are unrepeated across trials.

Feuerriegel et al., 2021 also points out: “There are also effects of adaptation that are dependent on the recent stimulation history extending beyond the last encountered stimulus and long-lag repetition effects that occur when the first and second presentation of a stimulus is separated by tens or even hundreds of intervening images”. Bearing this in mind, and given the very small pool of stimuli being used by Han et al., 2019; Kumar et al., 2017; Meyer and Olson, 2011, it stands to reason that these studies may still have built-in but unaccounted for effects relating to the repetition of exemplars. Thus, our avoidance of those possible confounds, in addition to foregoing any prior training, may elicit differing results. Furthermore, as pointed out by Walsh et al. 2020, methodological heterogeneity (such as subject training) can produce contrasting results as PP makes divergent predictions regarding the properties of prediction error given different permutations of variables such as training, transitional probabilities, and conditional probabilities. In our case, the use of differing methodology was intentional. These issues have been discussed in more detail on p.5, lines 112-115; p.19, lines 368-377; p.20, lines 378-379).

Minor

(1) The authors note in their reply to my previous questions that: "As mentioned above, we opted to target our ERP analyses on Oz due to controversies in the literature regarding univariate effects of ES (Feuerriegel et al., 2021)". This might be a lack of understanding on my side, but how are concerns about the reliability of ES, as outlined by Feuerriegel et al. (2021), an argument for restricting analyses to 1 EEG channel (Oz)? Could one not argue equally well that precisely because of these concerns we should be less selective and instead average across multiple (occipital) channels to improve the reliability of results?

The reviewer is correct in suggesting that a cluster of occipital electrodes may be more reliable than reporting one single electrode. We have amended the analysis to examine electrodes Oz, O1, and O2 (p.9, lines 187-188; p.11, lines 197-201).

(2) The authors provide a github link for the dataset and code. However, I doubt that github is a suitable location to share EEG data (which at present I also cannot find linked in the github repo). Do the authors plan to share the EEG data and if so where?

Thank you for bringing this to my attention. EEG data has now been uploaded at osf.io/x7ydf and linked to the github repository (p.28, lines 569-570).

(3) The figure text could benefit from additional information; e.g. Fig.1C and Fig.3 do not clarify what the asterisk indicates; p < ? with or without multiple comparison correction?

Thank you for pointing out this oversight, the figure texts have been amended (p. 9, line 168; p.16, line 289).

eLife Assessment

Muetter et al. provide an important argument that luminescence is a reliable, high-throughput alternative to colony-forming units (CFU) for super-MIC investigations, particularly when the quantity of interest is biomass. By examining 20 antimicrobials spanning 11 classes, the work shows that discrepancies between CFU and luminescence are often biological (filamentation, Viable But Not Culturable). The work provides a compelling view of how these three common measurements (luminescence, optical density, and CFU) relate to one another across a range of drug treatments, although testing on clinical isolates could be of further benefit.

Reviewer #1 (Public review):

Summary:

This study examines how luminescence can be used to measure bacterial population dynamics during antimicrobial treatment by comparing it directly with optical density and colony counts. The authors aim to determine when luminescence reflects changes in population size and when it instead captures metabolic or physiological states induced by drug exposure. By generating parallel datasets under controlled conditions, the work provides a detailed view of how these three common measurements relate to one another across a range of drug treatments.

Strengths:

The study is technically strong and thoughtfully designed. Measuring luminescence, optical density, and colony counts from the same cultures allows the authors to make clear and informative comparisons between methods. The data are compelling, and the analyses highlight both agreements and divergences in a way that is easy to interpret. The manuscript also succeeds in showing why these divergences arise. For example, the observation that filamentation and metabolic shifts can sustain luminescence even when colony counts drop provides valuable information on how different readouts capture distinct aspects of bacterial physiology. The writing is clear, the figures are effective, and the work will be useful for researchers who need high-throughput approaches to quantify microbial population dynamics experimentally.

Weaknesses:

The study also exposes some inherent limitations of luminescence-based measurements. Because luminescence depends on metabolic activity, it can remain high when cells are damaged or unable to resume growth, and it can fall quickly when drugs disrupt energy production, even if cells remain physically intact. These properties complicate interpretation in conditions that induce strong stress responses or heterogeneous survival states. In addition, the use of drug-free plates for colony counts may overestimate survival when filamented or stressed cells recover once the antibiotic is removed, making differences between luminescence and colony counts harder to attribute to killing alone. Finally, while the authors discuss luminescence in the context of clinically relevant concentration ranges, the current implementation relies on engineered laboratory strains and does not directly demonstrate applicability to clinical isolates. These limitations do not detract from the technical value of the work but should be kept in mind by readers who wish to apply the method more broadly.

Reviewer #2 (Public review):

Summary:

This preprint proposes luxCDABE-based luminescence as a high-throughput alternative (or complement) to CFU time-kill assays for estimating antimicrobial rates of population change at super-MIC concentrations, by comparing luminescence- and CFU-derived rates across 20 antimicrobials (22 assays) and attributing divergences primarily to filamentation (luminescence closer to biomass/volume than cell number) and changes in culturability/carryover (CFU undercounting viable cells).

Strengths:

The authors do not merely report discrepancies; they experimentally validate the biological causes. Specifically, they successfully attribute the slower decline of luminescence in certain drugs to bacterial filamentation (maintaining biomass despite halted division) and the rapid decline of CFU in others to loss of culturability or carryover effects.

The inclusion of 20 antimicrobials spanning 11 classes provides a robust dataset that allows for broad categorization of drug-specific assay behaviors.

The study critically exposes flaws in the "gold standard" CFU method, specifically regarding antimicrobial carryover (demonstrated with pexiganan) and the potential for CFU to overestimate cell death in the presence of VBNC (viable but non-culturable) states induced by drugs like ciprofloxacin.

The use of chromosomal integration for the lux operon to minimize plasmid copy-number effects and the validation of linearity between light intensity and cell density establish a solid technical foundation.

Weaknesses:

The study is conducted exclusively using Escherichia coli. While E. coli is a standard model organism, the paper claims to evaluate luminescence as a generalizable high-throughput tool. Many of the discrepancies observed are driven by filamentation. However, distinct morphological responses occur in other critical pathogens (e.g., Staphylococcus aureus does not filament in the same way).

The authors propose that luminescence data can be corrected using microscopy-derived volume data to better align with CFU counts. The primary appeal of luminescence is high-throughput efficiency. If a researcher must perform time-lapse microscopy to calculate cell volume changes to "correct" their luminescence data, the high-throughput advantage is lost.

The paper argues that for ciprofloxacin, CFU underestimates viability because cells remain intact and impermeable to propidium iodide. While the cells are metabolically active and membrane-intact, if they cannot divide to form a colony (even after drug removal/dilution), their clinical relevance as "living" pathogens is debatable.

Some other comments:

The use of a population dynamical model to simulate filamentation effects is excellent. The finding that light intensity tracks volume ($\psi_V$) better than cell number ($\psi_B$) is a key theoretical contribution.

The model assumes linear elongation. The authors should briefly comment on whether this holds true for the specific drug mechanisms tested (e.g., PBP inhibition vs. DNA gyrase inhibition).

The use of bootstrapping to estimate rate distributions is appropriate and robust.

Conclusion:

Muetter et al. provide a compelling argument that luminescence is a reliable, high-throughput alternative to CFU for super-MIC investigations, particularly when the quantity of interest is biomass. The paper effectively warns researchers that discrepancies between CFU and luminescence are often biological (filamentation, VBNC) rather than methodological failures.

Author response:

We are grateful for the effort and time invested in reviewing our manuscript. We find the comments and suggestions very helpful for improving the manuscript, and we will address them in a revised submission.

eLife Assessment

This valuable study examined how sensory adaptation supports visual perception in the presence of noise. The authors used a combination of human psychophysics, electroencephalography (EEG), and deep neural networks to show that adaptation to noise can improve perception. The results are solid but are, at present, weakened by a number of concerns, including some related to the experimental design and some regarding the interpretation of the results in terms of particular mechanisms. With these concerns adequately addressed, the study and conclusions would be likely to be of broad interest to the neuroscience community.

Reviewer #1 (Public review):

The authors sought to investigate the role of adaptation in supporting object recognition. In particular, the extent to which adaptation to noise improves subsequent recognition of objects embedded in the same or similar noise, and how this interacts with target contrast. The authors approach this question using a combination of psychophysics, electroencephalography, and deep neural networks. They find better behavioural performance and multivariate decoding of stimuli preceded by noise, suggesting a beneficial effect of adaptation to noise. The neural network analysis seeks to provide a deeper explanation of the results by comparing how well different adaptation mechanisms capture the empirical behavioural results. The results show that models incorporating intrinsic adaptation mechanisms, such as additive suppression and divisive normalisation, capture the behavioural results better than those that incorporate recurrent interactions. The study has the potential to provide interesting insights into adaptation, but there are alternative (arguably more parsimonious) explanations for the results that have not been refuted (or even recognised) in the manuscript. If these confounds can be compellingly addressed, then I expect the results would be of interest to a broad range of readers.

The study uses a multi-modal approach, which provides a rich characterisation of the phenomenon. The methods are described clearly, and the accompanying code and data are made publicly available. The comparison between univariate and multivariate analyses is interesting, and the application of neural networks to distinguish between different models of adaptation seems quite promising.

There are several concerning confounding factors that need to be addressed before the results can be meaningfully interpreted. In particular, differences in behavioural accuracy may be explained by a simple change detection mechanism in the "same noise" condition, and temporal cuing by the "adaptor" stimulus may explain differences in reaction time. Similarly, interference between event-related potentials may explain the univariate EEG results, and biased decoder training may explain the multivariate results. Thus, it is currently unclear if any of the results reflect adaptation.

My main concerns relate to how adaptation is induced and how differences between conditions are interpreted. The adaptation period is only 1.5 s. Although brief adaptors (~1 s) can produce stimulus history effects, it is unclear whether these reflect the same mechanisms as those observed with standard, longer adaptation durations (e.g., 10-30 s). Prior EEG work on visual adaptation using longer adaptors has shown that feature-specific effects emerge very early (<100 ms) after test onset in both univariate and multivariate responses (Rideaux et al., 2023, PNAS). In contrast, the present study finds no difference between same and different adaptor conditions until much later (>300 ms). These later effects likely reflect cognitive processes such as template matching or decision-making, rather than sensory adaptation. Although early differences appear between blank and adaptor conditions, these could be explained by interactions between ERPs elicited by adaptor onset/offset and those elicited by the test stimulus; therefore, they cannot be attributed to adaptation. This contradicts the statement in the Discussion that "Our EEG measurements show clear evidence of repetition suppression, in the form of reduced responses to the repeated noise pattern early in time."

A second concern is the brief inter-stimulus interval. The adaptor is shown for 1.5 s, followed by only a 134 ms blank before the target. When the "adaptor" and test noise are identical, improved performance could simply arise from detecting the pixels that change, namely, those forming the target number. Such change detection does not require adaptation; even simple motion detector units would suffice. If the blank period were longer-beyond the temporal window of motion detectors-then improved performance would more convincingly reflect adaptation. Given the very short blank, however, a more parsimonious explanation for the behavioural effect in the same-noise condition is that change detection mechanisms isolate the target.

Differences between the blank and adaptor conditions may also be explained by temporal cueing. In the noise conditions, the noise reliably signals the upcoming target time, whereas the blank condition provides no such cue. Given the variable inter-trial interval and the brief target presentation, this temporal cue would strongly facilitate target perception. This account is consistent with the reaction time results: both adaptor conditions produce faster reaction times than the blank condition, but do not differ from each other.

The decoding analyses are also difficult to interpret, given the training-testing protocol. All trials from the three main conditions (blank, same, different) were used to train the classifier, and then held-out trials - all from one condition-were decoded. Because ERPs in the adaptor conditions differ substantially from those in the blank condition, and because there are twice as many adaptor trials, the classifier is biased toward patterns from the adaptor conditions and will naturally perform worse on blank trials. To compare decoding accuracy meaningfully across conditions, the classifier should be trained on a separate unbiased dataset (e.g., the "clean" data), or each condition should be trained and tested separately using cross-fold validation.

Reviewer #2 (Public review):

Summary:

Neurons adapt to prolonged or repeated sensory inputs. One function of such adaptation may be to save resources to avoid representing the same inputs over and over again. However, it has been hypothesized that adaptation could additionally help improve the representation of sensory stimuli, especially during difficult recognition scenarios. This study sheds light on this question and provides behavioral evidence for such enhancement. The behavioral results are interesting and compelling. The paper also includes scalp electroencephalographic (EEG) data, which are noisy but point toward similar conclusions. The authors finally implement a deep convolutional neural network (DCNN) with adaptation mechanisms, which nicely capture human behavior.

Strengths:

(1) The authors introduce an interesting hypothesis about the role of adaptation in visual recognition.

(2) The authors present interesting and compelling behavioral data consistent with the hypothesis.

(3) The authors introduce a computational model that can capture mechanisms that can lead to adaptation, enhancing visual recognition.

Weaknesses:

(1) The main weakness is the scalp EEG data. As detailed below, the results are minimal at best and do not contribute to understanding the mechanisms of adaptation. The paper would be stronger without the EEG data.

(2) I wonder whether the hypothesis also holds with real-world objects in natural scenes, beyond the confines of MNIST digits.

Reviewer #3 (Public review):

Summary:

Brands and colleagues investigate how temporal adaptation can aid object recognition, and what neural computations may underlie these effects. They employed a previously published experimental paradigm to study how adaptation to temporally constant distractor input facilitates the recognition of a newly appearing target object. Specifically, they studied how this effect is modulated by the contrast of the target object.

They found that adaptation enhances the recognition of high-contrast objects more than that of low-contrast objects. This behavioral effect was mirrored by a larger effect of adaptation on the response to the high-contrast objects in relatively higher visual areas.

To investigate what neural computations can support this interaction, they implement several candidate neural mechanisms in a deep convolutional neural network: additive suppression, divisive suppression, and lateral recurrence. The authors conclude that divisive and additive suppression, which are intrinsic to the neuron, best explain the interaction between contrast and adaptation in the human data. They further show that these mechanisms, and divisive suppression in particular, show increased robustness to spatial shifts of the adaptor stimulus, hinting and potential perceptual benefits.

Strengths:

(1) Overall, this is a well-written paper, supported by thorough analyses and illustrated with clear, well-designed figures that effectively show overall trends as well as data variance. The authors tell a compelling story while responsibly steering away from overreaching conclusions.

(2) What makes this paper stand out is its comprehensive approach to understanding the behavioral benefit of neural adaptation and its mechanistic underpinnings. The authors effectively achieve this through integrating new behavioral and neural data with simulations using neural network models.

(3) The findings convincingly demonstrate that neuronally intrinsic adaptation mechanisms are sufficient to explain the observed interaction between temporal adaptation, contrast, and object recognition. Furthermore, the paper highlights that these intrinsic mechanisms offer superior robustness compared to learned lateral recurrence mechanisms, which, while being more expressive, can also be more brittle.

Weaknesses:

While the results and conclusion are well supported, there were a few major points that need clarification for me.

(1) Divisive normalization

I was confused by the author's classification of divisive normalization as a neuronally intrinsic mechanism, that is, one that operates within a single neuron, independent of interactions with other neurons.

My understanding is that divisive normalization, as originally proposed by Heeger in the early nineties, describes a mechanism where neurons integrate pooled activity from neighboring cells to mutually inhibit one another. In this form, divisive normalization is fundamentally an interneuronal mechanism involving recurrence. Adding to the confusion, the authors highlight in the introduction their interest in divisive normalization for its relation to stimulus contrast, a relation likely linked to neuronal pooling.

However, my reading of the methods section (Equations 6 and 7) suggests the authors implemented only a temporal feedback component, leaving out the pooling across neurons (Equation 5). This distinction should be disambiguated early in the paper. I recommend choosing a less ambiguous term than "divisive normalization". Even "temporal divisive normalization" is still ambiguous, as lateral neuronal interactions are also inherently temporal.

(2) Parietal electrodes

The paper's adapter-specific effects are centered around the P9/P10 electrodes, which the authors identify as "parietal." However, it is unclear to me which part of the cortex drives these electrodes, particularly whether it is actually the parietal cortex. I am no expert in EEG, but based on the topomaps in Figures 4 and 5, it appears that these electrodes cover more posterior occipito-temporal regions rather than truly parietal regions. Given the central role of P9/P10 to the main findings, the paper would be significantly improved for non-EEG readers by clarifying which cortical regions are covered by these electrodes.

(3) Interpretation of non-significant statistical results

In some places, the authors attach relatively strong claims to non-significant statistical results. For example, in Figure 5D, they claim that there is no effect of contrast on occipital electrodes, based on a non-significant p-value. P-values do not quantify evidence for the null hypothesis, so the authors should be careful with such claims. In fact, Figure 5D shows such a clear negative slope, with variance comparable to Figure 5A, that I am surprised that the p-value for the slope of Figure 5D was in fact so large. A similar issue arises in the discussion for Figure 6, where the authors claim that the effect of contrast is adapter-specific. However, this claim is based on the observation that is significant for same-noise trials, but not for different-noise or blank trials. To statistically substantiate the claims that there is an adapter-specific effect, the authors should directly compare the slope for same-noise trials with the slope for different-noise/blank trials.

(4) The match between behavior and models

The authors' claim that models with intrinsic adaptation better match the interaction between contrast and temporal adaptation observed in human behavior is not fully substantiated. This conclusion appears to be based on a qualitative assessment of Figure 8, which, in my view, does not unambiguously rule out an interaction for lateral recurrence. Furthermore, a potential confounding factor is the ceiling effect that limits higher accuracy values. Indeed, conditions where the interaction was not/less (i.e., shorter time sequences and lateral inhibition) are also the conditions where accuracy values are closer to this ceiling, which may mask a potential interaction.

eLife Assessment

This study presents a valuable and well-documented computational pipeline for the scalable analysis and spike sorting of large extracellular electrophysiology datasets, with particular relevance for high-density recordings such as Neuropixels. The authors demonstrate the pipeline's utility for benchmarking spike sorter performance and evaluating the effects of data compression, supported by thorough testing, clear figures, and openly available code. The workflow is reproducible, portable, and practical, providing concrete guidance on computational cost and runtime. Overall, the evidence supporting the pipeline's performance and output quality is compelling, and this work will be of broad interest to the systems neuroscience community.

Reviewer #1 (Public review):

Summary:

Extracellular electrophysiology datasets are growing in both number and size, and recordings with thousands of sites per animal are now commonplace. Analyzing these datasets to extract the activity of single neurons (spike sorting) is challenging: signal-to-noise is low, the analysis is computationally expensive, and small changes in analysis parameters and code can alter the output. The authors address the problem of volume by packaging the well-characterized SpikeInterface pipeline in a framework that can distribute individual sorting jobs across many workers in a compute cluster or cloud environment. Reproducibility is ensured by running containerized versions of the processing components.

The authors apply the pipeline in two important examples. The first is a thorough study comparing the performance of two widely used spike-sorting algorithms (Kilosort 2.5 and Kilosort 4). They use hybrid datasets created by injecting measured spike waveforms (templates) into existing recordings, adjusting those waveforms according to the measured drift in the recording. These hybrid ground truth datasets preserve the complex noise and background of the original recording. Similar to the original Kilosort 4 paper, which uses a different method for creating ground truth datasets that include drift, the authors find Kilosort 4 significantly outperforms Kilosort 2.5. The second example measures the impact of compression of raw data on spike sorting with Kilosort 4, showing that accuracy, precision, and recall of the ground truth units are not significantly impacted even by lossy compression. As important as the individual results, these studies provide good models for measuring the impact of particular processing steps on the output of spike sorting.

Strengths:

The pipeline uses the Nextflow framework, which makes it adaptable to different job schedulers and environments. The high-level documentation is useful, and the GitHub code is well organized. The two example studies are thorough and well-designed, and address important questions in the analysis of extracellular electrophysiology data.

Weaknesses:

The pipeline is very complete, but also complex. Workflows - the optimal artifact removal, best curation for data from a particular brain area or species - will vary according to experiment. Therefore, a discussion of the adaptability of the pipeline in the "Limitations" section would be helpful for readers.

Reviewer #2 (Public review):

Summary:

This work presents a reproducible, scalable workflow for spike sorting that leverages parallelization to handle large neural recording datasets. The authors introduce both a processing pipeline and a benchmarking framework that can run across different computing environments (workstations, HPC clusters, cloud). Key findings include demonstrating that Kilosort4 outperforms Kilosort2.5 and that 7× lossy compression has minimal impact on spike sorting performance while substantially reducing storage costs.

Strengths:

(1) Extremely high-quality figures with clear captions that effectively communicate complex workflow information.

(2) Very detailed, well-written methods section providing thorough documentation.

(3) Strong focus on reproducibility, scalability, modularity, and portability using established technologies (Nextflow, SpikeInterface, Code Ocean).

(4) Pipeline publicly available on GitHub with documentation.

(5) Clear cost analysis showing ~$5/hour for AWS processing with transparent breakdown.

(6) Good overview of previous spike sorting benchmarking attempts in the introduction.

(7) Practical value for the community by lowering barriers to processing large datasets.

Weaknesses:

No significant weaknesses were identified, although it is noted that the limitations section of the discussion could be expanded.

Reviewer #3 (Public review):

Summary:

The authors provide a highly valuable and thoroughly documented pipeline to accelerate the processing and spike sorting of high-density electrophysiology data, particularly from Neuropixels probes. The scale of data collection is increasing across the field, and processing times and data storage are growing concerns. This pipeline provides parallelization and benchmarking of performance after data compression that helps address these concerns. The authors also use their pipeline to benchmark different spike sorting algorithms, providing useful evidence that Kilosort4 performs the best out of the tested options. This work, and the ability to implement this pipeline with minimal effort to standardize and speed up data processing across the field, will be of great interest to many researchers in systems neuroscience.

Strengths:

The paper is very well written and clear in most places. The accompanying GitHub and ReadTheDocs are well organized and thorough. The authors provide many benchmarking metrics to support their claims, and it is clear that the pipeline has been very thoroughly tested and optimized by users at the Allen Institute for Neural Dynamics. The pipeline incorporates existing software and platforms that have also been thoroughly tested (such as SpikeInterface), so the authors are not reinventing the wheel, but rather putting together the best of many worlds. This is a great contribution to the field, and it is clear that the authors have put a lot of thought into making the pipeline as accessible as possible.

Weaknesses:

There are no major weaknesses. I have only a handful of very minor questions and suggestions that could clarify/generalize aspects of the pipeline or make the text more understandable to non-specialists.

(1) Could the authors please expand on the statement on line 274, that processing their test dataset serially "on a single GPU-capable cloud workstation... would take approximately 75 hours and cost over 90 USD." How were these values calculated? I was a bit surprised that this is a >4-fold slow-down from their pipeline, but only increases the cost by ~1.35x, if I understood correctly. More context on why this is, and maybe some context on what a g4dn.4xlarge is compared to the other instances, might help readers who are less familiar with AWS and cloud computing.

(2) One of the most commonly used preprocessing pipelines for Neuropixels data is the CatGT/ecephys pipeline from the developers of SpikeGLX at Janelia. It may be worth commenting very briefly, either in the preprocessing section or in the discussion, on how the preprocessing steps available in this pipeline compare to the steps available in CatGT. For example, is "destriping" similar to the "-gfix" option in catGT to remove high-amplitude artifacts?

(3) Why are there duplicate units (line 194), and how often is this an issue? I understand that this is likely more of a spike sorter issue than an issue with this pipeline, but 1-2 sentences elaborating why might be helpful for readers.

(4) It seems from the parameter files on GitHub that the cluster curation parameters are customizable - correct? If so, it may be worth explicitly saying so in the curation section of the text, as the presented recipe will not always be appropriate. A presence ratio of >0.8 could be particularly problematic for some recordings, for example, if a cell is only active during a specific part of the behavior, that may be a feature of the experiment, or the animal could be transitioning between sleep and wake states, in which different units may become active at different times.

(5) The axis labels in Figures 3d-e are too small to see, and Figure 3d would benefit from a brief description of what is shown.

(6) What is the difference between "neural" and "passing QC" in Figure 4?

(7) I understand the current paper is focused on spike data, so there may not be an answer to this, but I am curious about the NP2.0 probes that save data in wideband. Does the lossy compression negatively affect the LFP data? Is software filtering applied for the spike band before or after compression?

eLife Assessment

This manuscript presents a novel investigation of organizational principles governing brain activity at both global and local scales during naturalistic viewing paradigms, an important advance for theoretical neuroscience, functional neuroimaging, and neurology. The authors demonstrate that brain activity during naturalistic viewing is dominated by two anti-correlated states that toggle between each other with a third transitional state mediating between them. The evidence supporting this finding is compelling, with the successful replication across three independent datasets (StudyForrest, NarrattenTion, and CamCAN) a particular strength.

Reviewer #1 (Public review):

In this work, the authors provide a comprehensive investigation of antagonistic dynamics across large-scale brain networks. They characterize this phenomenon at the global (regional dynamics) and local (multivariate patterns of voxels within regions) levels.

Furthermore, as opposed to studying these dynamics under resting-state or explicit task conditions, the authors make use of naturalistic narratives, both auditory and visual.

Perhaps most importantly, this work provides evidence that event boundaries in narratives drive sensory responses, which, in turn, predict anticorrelated activity in task-positive networks and the default mode network. These findings open up new questions regarding the interaction across perceptual systems and these higher-order dynamics in association networks.

This work is methodologically solid and presents compelling findings that will surely invite new approaches and questions in this area.

Importantly, these data do not speak to the order or causal structure of these interactions. Time-resolved methods and direct causal interventions will be needed to understand how these interactions drive one another more precisely.

Reviewer #2 (Public review):

This manuscript presents an impressive and novel investigation of organizational principles governing brain activity at both global and local scales during naturalistic viewing paradigms. The proposed multi-scale nested structure offers valuable new insights into functional brain states and their dynamics. Importantly, investigation of global brain states in the context of a naturalistic viewing context represents an important and timely contribution that addresses unresolved issues about global signals and anticorrelations in resting-state fMRI. This manuscript presents a novel investigation of organizational principles governing brain activity at both global and local scales during naturalistic viewing paradigms. The authors demonstrate that brain activity during naturalistic viewing is dominated by two anti-correlated states that toggle between each other with a third transitional state mediating between them. The successful replication across three independent datasets (StudyForrest, NarrattenTion, and CamCAN) is a particular strength. The successful replication across three independent datasets (StudyForrest, NarrattenTion, and CamCAN) is a particular strength, and I appreciate the authors' careful documentation of both convergent and divergent findings across these samples.

Overall, this manuscript makes important contributions to our understanding of large-scale brain organization during naturalistic cognition. The multi-scale framework and robust replication across datasets are notable strengths. Addressing the concerns raised below will substantially strengthen the impact and interpretability of this work.

(1) Network Definition and Specificity

(a) The authors adopt an overly broad characterization of the Default Mode Network (DMN). The statement that "areas most active in the default mode state... consist of the precuneus, angular gyrus, large parts of the superior and middle temporal cortex, large parts of the somatomotor areas, frontal operculi, insula, parts of the prefrontal cortex and limbic areas" includes regions typically assigned to other networks. The insula is canonically considered a core node of the Salience Network/Ventral Attention Network (VAN), not the DMN. Also, not clear which limbic areas? The DMN findings reported need to be critically reassessed in this context.

(b) Given the proposed role of state switching in your framework, a detailed analysis of salience network nodes (particularly insula and dorsal ACC) would be highly informative.

(c) While you report transition-related signals in the visual and auditory cortex, the involvement of insular and frontal control systems in state transitions remains unaddressed.

(d) My recommendation is to provide a more anatomically precise characterization of network involvement, particularly distinguishing DMN from salience/VAN regions, and analyze the specific role of salience network nodes in mediating state transitions.

(2) Distinguishing Top-Down from Stimulus-Driven Effects

(a) The finding that "the superior parietal lobe (SPL) and the frontal eye fields (FEF) show the greatest overlap between their local ROI state switches and the global state switches" raises an important question: To what extent are these effects driven by overt changes in visual gaze or attention shifts triggered by stimulus features versus internally-generated state changes?

(b) Similarly, the observation that DAN areas show the highest overlap with global state changes in StudyForrest and NarrattenTion, while VAN shows the highest overlap in CamCAN, lacks sufficient anatomical detail regarding which specific nodes are involved. This information would help clarify whether insular regions and other VAN components play distinct roles in state switching.

(c) It will be important to (i) discuss potential confounds from eye movements and stimulus-driven attention shifts; (ii) provide detailed anatomical breakdowns of network nodes involved in state transitions, particularly for VAN; (iii) if eye-tracking data or any other relevant stimulus-related data are available, include analyses examining relationships between these measures and state transitions.

(3) Physiological Interpretation of the "Down" State

The linkage between the "Down" state and the Default Mode State (DMS) is intriguing but requires deeper physiological grounding. Recent work by Epp et al. (Nature Neuroscience, 2025) demonstrates that decreased BOLD signal in DMN regions does not necessarily indicate reduced metabolic activity and can reflect neurovascular coupling modes with specific metabolic profiles. It would be useful to discuss whether your "Down" state might represent a particular neurovascular coupling mode with distinct metabolic demands rather than simply reduced neural activity. Alternatively, your analytical approach might be insensitive to or unconfounded by such neurovascular uncoupling. This discussion would substantially enrich the biological interpretation of the DMS versus TPS dual mechanism framework.

(4) Statistical Validation of Bimodality Detection

The method of selecting bimodal timepoints using the Dip test followed by sign-alignment is novel and creative. However, this filter-then-align procedure could potentially introduce circularity by imposing the anticorrelated structure the authors aim to detect. It would be important to implement validation analyses to confirm that anticorrelation is an intrinsic property rather than a methodological artifact. Approaches include leave-one-subject-out cross-validation, unsupervised dimensionality reduction (e.g., PCA) applied independently to verify the anticorrelated structure, and split-half reliability analysis. Such validation would significantly strengthen the statistical foundation of findings.

(5) Quantifying Hyperalignment Contribution

The appendix notes that non-hyperaligned data show a coarser structure, but the specific contribution of hyperalignment to your findings requires more thorough quantification. Please provide a systematic comparison of results with and without hyperalignment, demonstrating that similar (even if weaker) anatomical correspondence exists in native subject space. This would establish that the mesoscale organizational principles you identify are not artifacts of the alignment procedure but reflect genuine neurobiological organization. Consider presenting correlation coefficients or overlap metrics quantifying the similarity of state structures before and after hyperalignment.

(6) Functional Characterization of the Unimodal State

The observation that the brain spends approximately 34% of its time in a "Unimodal State" is presented primarily as a transition period. This is an interesting observation. However, it would be useful to characterize the functional connectivity profile of the unimodal state. Specifically, investigate whether it represents a distinct functional state with its own characteristic connectivity pattern. More detailed analysis would provide a more complete picture of temporal brain dynamics during naturalistic viewing and could yield new perspectives on how the brain reorganizes between stable states.

eLife Assessment

This valuable study uses a computer vision pipeline to infer the motor control of cephalopod skin, revealing that individual chromatophores exhibit anisotropic deformations and can be associated with multiple putative motor units. The evidence supporting these claims is solid, although the study's conclusions are limited to stationary or sedated animals, and the analyses of motor unit characteristics and electrophysiological validation remain incomplete. This work will be of significant interest to biologists studying cephalopod behavior and motor control.

Reviewer #1 (Public review):

Summary:

Renard, Ukrow et al. applied their recently published computational pipeline (CHROMAS) to the skin of Euprymna berryi and Sepia officinalis to track the dynamics of cephalopod chromatophore expansion. By segmenting each chromatophore into radial slices and analyzing the co-expansion of slices across regions of the skin, they inferred the motor control underlying chromatophore groups.

Strengths:

The authors demonstrate that most motor units of cephalopod skin include a subregion of multiple chromatophores, creating "virtual chromatophores" in between the fixed chromatophores. This is an interesting concept that challenges prevailing models of chromatophore organization, and raises interesting possibilities for how chromatophore arrays may be patterned during development.

This study introduces new analyses of cephalopod skin that will be valuable for the quantitative study of cephalopod behavior.

Weaknesses:

The authors chose to image spontaneous skin changes in sedated animals, rather than visually-evoked skin changes in awake, freely-moving animals. Spontaneous chromatophore changes tend to be small shimmers of expansion and contraction, rather than obvious, sizable expansions. This may make it more challenging to distinguish truly co-occurring expansions from background activity. The authors don't provide any raw data (videos) of the skin, so it is difficult to independently assess the robustness of the inferred chromatophore groupings.

The patch-clamp experiments in E. berryi are used to test the validity of their approach for inferring motor units. The stimulations evoke expansions of sub-regions of each chromatophore, creating "virtual chromatophores" as predicted from the behavioral analysis. However, the authors were not able to predict these specific motor units from behavioral analysis before confirming them with patch-clamp, limiting the strength of the validation. It would be informative to quantify the results of the patch-clamp experiments - are the inferred motor units of similar sizes to those predicted from behavior?

The authors report testing multiple experimental conditions (e.g., age, size, behavioral stimuli, sedation, head-fixation, and lighting), but only a small subset of these data are presented. It is difficult to determine which conditions were used for which experiments, and the manuscript would benefit from pooling data from multiple experiments to draw general conclusions about the motor control of cephalopod skin.

The authors use a different clustering algorithm for E. berryi and S. officinalis, but do not discuss why different clustering approaches were required for the two species.

Impact:

The authors use their computational pipeline to generate a number of interesting predictions about chromatophore control, including motor unit size, their spatial distribution within the skin, and the independent control of subregions within individual chromatophores by putatively distinct motor neurons. While these observations are interesting, the current data do not yet fully support them.

The CHROMAS tool is likely to be valuable to the field, given the need for quantitative frameworks in cephalopod biology. The predictions outlined here provide a useful foundation for future experimental investigation.

Reviewer #2 (Public review):

Summary:

Overall, this is an excellent paper, making use of a newly developed system for monitoring the behaviour of chromatophores in the skin of (mostly) free-swimming bobtail squid and European cuttlefish. The manuscript is very well-written, clearly presented and very well-structured. The central finding, that individual chromatophores are connected to multiple motor neurones, is not new. Novelty instead comes from the ability to measure the actuation of chromatophore sections across wide areas of skin in free-swimming animals, showing the diversity of local motor units and reinforcing the notion that individual chromatophores are not necessarily the individual units of colour change, but rather local motor units that cover multiple neighbour and near-neighbour chromatophore muscles. This is an excellent finding and one that will shape our understanding of the neural control of cephalopod skin colour.

Strengths:

The methodological approach to collecting large amounts of data about local variations in the expansion of sections of chromatophores is exciting, and the analysis pipeline for clustering sections of chromatophores whose spontaneous activity correlated over time is powerful and exciting.

Weaknesses:

Some minor edits and typographical errors need correcting. I also had some concerns that the preparation for the electrophysiological section of the manuscript complies with the journal's ethical requirements, so I would urge that this be carefully checked.

Reviewer #3 (Public review):

Summary:

This study uses high-resolution videography and a custom computer-vision pipeline to dissect the motor control of cephalopod chromatophores in Euprymna berryi and Sepia officinalis. By quantifying anisotropic chromatophore deformations and applying dimensionality reduction methods, the authors infer that individual chromatophores can be a part of multiple motor units. Clustering analyses reveal putative motor units that often span multiple chromatophores, with diverse and overlapping geometries. Chromatophore expansion dynamics are faster and more stereotyped than relaxation, consistent with active neural contraction followed by passive recoil. Together, the results show that chromatophores function not as uniform pixels but as fractionated, coordinately controlled elements that enable flexible pattern generation

Strengths:

The authors present compelling, direct evidence that a). chromatophore deformations are anisotropic, and indirect evidence that b) individual chromatophores can be split across multiple putative motor units. This evidence is provided through data collected over large spatial scales, but also at a sub-chromatophore resolution. This combination of scale and resolution is not possible using traditional neuroanatomical and physiological approaches alone.

The authors also develop a new non-invasive, image analysis approach to extract information about chromatophore deformation across large spatial scales on the organism's body. In principle, this approach is applicable across species and may allow for further comparative characterization of chromatophore motor control. It is therefore a promising new tool and useful resource for the community.

Weaknesses:

An important weakness of the work is that the methods the authors develop can only be applied during resting, spontaneous 'flickering' activity of chromatophores. The inability to reliably apply their technique during any kind of realistic camouflage is a large limitation, as it means this method cannot be used to study the dynamics of motor control during realistic camouflage behaviors.

Another weakness of this paper is the rather limited electrophysiological validation of the computational findings. The authors present only one electrophysiology experiment in E. berryi, the species that they used only for 'methodological development' and not for detailed characterization. A complementary electrophysiological experiment in S. officinalis, or some visualization of neuron morphology confirming that motor neurons do indeed project to multiple chromatophores, would strengthen the generalizability of their computational analysis. This would be particularly pertinent to validate the author's claim that some motor units contain chromatophores that are quite distant from one another on the animal.

Overall, the authors' technical contributions and method development are an important advance. This work serves as an excellent proof of concept that their method can extract useful information about chromatophore motor control. Further validation of their method is needed to fully trust the fine-scale conclusions drawn about the distribution and composition of multi-innervated chromatophores. Furthermore, the authors raise many interesting ideas about developmental constraints on circuit wiring and potential adaptive significance of multi-innervated chromatophores for certain features of camouflage patterning. Their method may be able to help resolve some of these questions in the future if it is refined and applied across developmental stages, regions of the animal, and across species

Author response:

We thank all reviewers for their comments. We appreciate the acknowledgement that the paper is important and that results support the major conclusions. We are planning to address the specific concerns as noted by the reviewers in the following way:

Public Reviews:

Reviewer #2 (Public review):

(1) The authors generate a new tool, a Gal4 knock-in of the jam2b locus, to track EGFP-expressing cells over time and follow the developmental trajectory of jam2b-expressing cells. Figure 1 characterizes the line. However, it lacks quantification, e.g., how many etv2-expressing cells also show EGFP expression or the contribution of EGFP-expressing cells to different types of blood vessels. This type of quantification would be useful, as it would also allow for comparison of their findings to their previous data examining the contribution of SVF cells to different types of blood vessels. All the authors state that at 30 hpf, EGFP-expressing cells can be seen in the vasculature (apparently the PCV).

It is not clear why the authors do not use a nuclear marker for both ECs (as they did in their previous publication) and for jam2b-expressing cells. UAS:nEGFP and UAS:NLS-mcherry (e.g. pt424tg) transgenic lines are available. This would circumvent the problem the authors encounter with the strong fluorescence visible in the yolk extension. It would also facilitate quantifying the contribution of jam2b cells to different types of blood vessels.

We agree with the importance of quantification. We had performed quantification of jam2b^Gt(2A-Gal4);UAS:GFP contribution to different vascular beds, which was shown in Suppl. Fig. S3. We will clarify this in the revision. We also agree that nuclear GFP or mCherry would help to visualize and quantify cells. Unfortunately, we do not have nuclear UAS:GFP or UAS:mCherry line in our possession, and it will take too long to import it for the standard revision timeline. We are working on the construct, and will attempt to establish the line; therefore we are hoping to clarify these results with the nuclear line in the revised manuscript.

(2) The time-lapse movie in Figure 2 is not very informative, as it just provides a single example of a dividing cell contributing to the PCV. Also, quantifications are needed. As SVF cells appear to expand significantly after their initial specification, it would be informative to know how many cell divisions and which types of blood vessels jam2b-expressing cells contribute to. Can the authors observe cells that give rise to different types of blood vessels? Jam2b expression in LPM cells apparently precedes expression of etv2. Is etv2 needed for maintenance, or do Jam2b-expressing cells contribute to different types of tissues in etv2 mutant embryos? Comparing time-lapse analysis in wildtype and etv2 mutant embryos would address this question.

The time-lapse was meant to serve as an illustration and confirmation of jam2b cell contribution to vasculature. As noted above, Suppl. Fig. S3 provides quantification of jam2b cell contribution to different vascular beds. We had previously performed detailed time-lapse analysis and quantification of SVF cell migration to PCV, SIA and SIV using etv2-2A-Venus line (Metikala et al 2022, Dev Cell), which has some of the same (or similar) information. It is very challenging to obtain this data using jam2b reporter line due to extensive and bright GFP expression in the mesothelial layer over the yolk and yolk extension; for that reason we can only trace some GFP cells but not all of them. Regarding etv2 requirement for jam2b maintenance, we intend to address this question by analyzing jam2b cell contribution in etv2 MO injected embryos, which recapitulates the phenotype in jam2b mutants.

(3) In Figure 3, the authors generate UAS:Cre and UAS:Cre-ERT2 transgenic lines to lineage trace the jam2b-expressing cells. It is again not clear why the authors do not use a responder line containing nuclear-localized fluorescent proteins to circumvent the strong expression of fluorescent proteins in the yolk extension. It is also unclear why the two transgenic lines give very different results regarding the number of cells being labelled. The ERT2 fusions label around 3 cells in the SIA, while the Cre line labels only about 1.5 cells per embryo, with very little contribution of labelled cells to other blood vessels. One would expect the Cre line requiring tamoxifen induction to label fewer cells when compared to the constitutive Cre line. What is the reason for this discrepancy? Are the lines single integration? Is there silencing? This needs to be better characterized, also regarding the reproducibility of the experiments. If the Cre lines were to be multiple copy integrations, outcrossing the line might lead to lower expression levels in future generations. 

It is also not clear how the authors conclude from these findings that "SVF cells show major contribution to the SIA and SIV" when only 1.5 or 3 cells of the SIA are labelled, with even fewer cells labelled in other blood vessels. They speculate that this might be due to low recombination efficiency, a question they then set out to answer using photoconversion of etv2:KAEDE expressing cells, an experiment that they also performed in their 2014 and 2022 publications. To check for low recombination efficiency, the authors could examine the expression of Cre mRNA in their transgenic embryos. Do many more jam2b expressing cells express Cre mRNA than they observe in their switch lines? They could also compare their experiments using Cre recombinase with those using EGFP expression in jam2b cells. EGFP is relatively stable, and the time frames the authors analyze are short. As no quantification of EGFP-expressing cells is provided in Figure 1, this comparison is currently not possible. Do these two different approaches answer different questions here? 

The reviewer brings up important points, we appreciate that. Unfortunately, we do not have a nuclear switch line in our possession, and it is not possible to obtain it in the normal manuscript revision time line. Regarding UAS:Cre and UAS:CreERT2 lines, they both show rather similar labeling, with most labeled cells present in the SIA. The difference in cell number (1.5 versus 3) is likely due to different levels of Cre expression, which may vary dependent on the integration site. The lines most likely are multi-copy integrations, which can be helpful, as this would result in higher Cre expression. We will address the silencing question by performing in situ hybridization or HCR analysis for Cre or CreERT2 and comparing it with endogenous jam2b expression, as the reviewer suggested. We have noticed that the switch line used, actb2:loxP-BFP-loxP-dsRed, exhibits lower recombination frequency compared to other switch lines (we used it because it was compatible with endothelial fli1:GFP line). We will attempt to answer this question by crossing to other switch lines, which may exhibit higher recombination frequency. In principle, UAS:GFP and switch lines should produce a similar result, except that GFP decays over time and therefore our initial expectation was that switch lines may produce a more accurate result. However, this may not be the case due to low recombination efficiency, which we will attempt to address in the revision.

(4) Concerning the etv2:KAEDE photoconversion experiments: The percentages the authors report for SVF cells' contribution to the SIV and SIA differ from their previous study (Dev Cell, 2022). In that publication, SVF cells contributed 28% to the SIA and 48% to the SIV. In the present study, the numbers are close to 80% for both vessels. The difference is that the previous study analyzed 2dpf old embryos and the new one 4dpf old embryos. Do SVF-derived cells proliferate more than PCV-derived cells, or is there another explanation for this change in percentage contribution? 

These numbers refer to different experiments; we apologize for the confusion. As reported earlier in Metikala et 2022, 28% of SVF cells contributed to the SIA and 48% to the SIV by 3 dpf (not 2 dpf; only PCV analysis was done at 2 dpf); SIA and SIV analysis was done based on time-lapse image analysis of etv2-2A-Venus line at 3 dpf, shown in Fig. 3C in Metikala et al. However, this only refers to SVF cell contribution. It does not mean that 28% or 48% cells in SIA or SIV are derived from SVF. The total fraction of SIA and SIV cells that are derived from SVF has not been quantified in the previous study, because that would require accurate tracking of all SVF cells, which is experimentally challenging. Etv2:Kaede experiment is slighly different, because it reports newly formed cells after 24 hpf. It cannot tell if new cells are all derived from SVF cells, although we are not aware of any other source of new endothelial cells at these stages. In the previous study by Metikala et al 2022, we reported ~22 newly formed SIA and ~50 newly formed cells in SIV by 3 dpf (Fig. 1 in Metikala et al 2022), although the entire number of cells was not quantified, therefore the percentage was not known. In the current study, we attempted to estimate the entire percentage of green only Kaede cells, which was close to 80% in both SIA or SIV at 4 dpf. Please note that this estimate was performed in the posterior portion of SIA and SIV that overlies the yolk extension and where SVF cells are observed. We did not quantify cells in the anterior SIV portion, which forms the basket over the yolk.

(5) Single-cell sequencing data: Why do the authors not show jam2b expression in their single-cell sequencing data? They sorted for (presumably) jam2b-expressing cells and hypothesize that jam2b expression in ECs at this time point is important for the generation of intestinal vasculature. Do ECs in cluster 15 express jam2b? Why are no other top marker genes (tal1, etv2, egfl7, npas4l) included in the dot blot in Figure 5b?

We appreciate the suggestion and will include additional marker genes as well as jam2b in the revised version of the manuscript.

(6) Concerns about cell autonomy of mutant phenotypes: The authors need to perform in situ hybridization to characterize jam2a expression. Can it be seen in SVF cells? The double mutants show a clear phenotype in intestinal vessel development; however, it is unclear whether this is due to a cell-autonomous function of jam2a/b within SVF cells. The authors need to address this issue, as jam2b and potentially also jam2a are expressed within the tissue surrounding the forming SVF. For instance, do transplanted mutant cells contribute to the intestinal vasculature to the same extent as wild-type cells do?

jam2a expression has been characterized in the previous studies and it is shown in the Suppl. Fig. S4E. It is primarily enriched in the skeletal muscle. However, our single-cell RNA-seq analysis shows that SVF cells also express jam2a. We will include additional data on jam2a expression in the revised manuscript. We agree that transplation to address cell autonomy is an important experiment, yet there are some practical challenges to it. Jam2a,jam2b mutant phenotype is only partially penetrant, and about 50% reduction in SVF cell number, as well as partial SIA and SIV phenotypes are observed. Only a small number of transplanted cells may contribute to intestinal vasculature, therefore it may be challenging to see the differences, given the partial penetrance. In an attempt to address cell -autonomy question, we will try a different approach. We will overexpress jam2b labeled with 2A-mCherry, and test if it can rescue the mutant phenotype in cell autonomous manner. Overexpression will be done in a mosaic manner, with higher number of cells labeled than in a typical transplantation experiment.

(7) Finally, the authors analyze the phenotypes of hand2 mutants and their impact on the expression of jam2b and etv2. They observe a reduction in jam2b and etv2 expression in SVF cells. However, they do not show the vascular phenotypes of hand2 mutants. Is the formation of the SIA and SIV disturbed? Is hand2 cell autonomously needed in ECs? The authors suggest that hand2 controls SVF development through the regulation of jam2b. However, they also show that jam2b mutants do not have a phenotype on their own. Clearly, hand2, if it were to be required in ECs, regulates other genes important for SVF development. These might then regulate jam2b expression. The clear linear relationship, as the title suggests, is not convincingly shown by the data.

As suggested, we will add the analysis of SIA and SIV in hand2 mutants during the revision process. We could not assess that easily because the line was not maintained in vascular fli1:GFP background. We do not know if hand2 is required cell-autonomously. This is an important question, but it may be answered better in a separate study. Regarding hand2-jam2b axis, it is very clear that jam2b expression in the posterior lateral plate mesoderm is completely lost in hand2 mutants, except for its more anterior domain over the yolk. This does support the idea that hand2 functions upstream of jam2b. However, the relationship may not be necessarily direct. We agree that hand2 may regulate additional genes involved in SVF cell development. We will attempt to clarify this relationship and test if jam2b overexpression may rescue hand2 mutant phenotype.

Reviewer #3 (Public review):

(1) Overall molecular mechanisms of Jam2 function are not fully uncovered in the study. How do the adhesion molecules Jam2a and Jam2b regulate SVF cell formation? Are they responsible for migration, adhesion or fate determination of these structures? The authors should provide a more in-depth study of the jam2a, jam2b mutations and assess the processes affected in these mutants. Combining these mutants with etv2:Kaede can also provide a stronger causative link between their functions and defects in SVF formation.

Our data argue that the initial SVF cell specification (based on etv2 expression) is reduced in jam2a;jam2b mutants. We do not know if the migration or fate determination of the remaining SVF cells is also affected, although this may be more challenging to answer, as there are only few SVF cells remaining. We agree that further mechanistic studies of jam2a,jam2b function are needed. However, we think that this would be better addressed in a separate study. We are currently raising mutants crossed into fli1:Kaede line, which should confirm that there are fewer new cells that emerge after Kaede photoconversion in jam2a,jam2b mutants.

(2) Have the authors tested the specificity of the jam2b knock-in reporter line? This is an important experiment, as many of the conclusions derive from lineage tracing and fluorescence reporting from this knock-in line. One suggestion is to cross the jam2b:GFP or jam2b:Gal4, UAS:GFP line to the generated jam2b mutants, and examine the expression pattern of these lines. Considering that the ISH experiment showed lack of jam2b expression, the reporter line should not be expressed in the jam2b mutants.

We show in Suppl. Fig. 2 that jam2b^Gt(2A-Gal4);UAS:GFP knock-in line has similar expression pattern as jam2b mRNA by in situ hybridization, which argues for its specificity. In the revision, we plan to use HCR analysis to confirm than jam2b mRNA is expressed in the same cells as jam2b^Gt(2A-Gal4);UAS:GFP, as an additional evidence for its specificity. Unfortunately, it is not feasible to cross jam2b knock-in line into jam2b mutants, as suggested by the reviewer. Because jam2b knock-in line targets the endogenous jam2b genomic locus, which is very close in the genome to jam2b promoter deletion in jam2b mutants, the recombination frequency would be very low, and we would not get double jam2b knock-in and knock-out events in the same chromosome.

(3) The rationale behind the regeneration study is not clear, and the mechanisms underlying the phenotype are not well described. How do the authors explain the phenotype with the impaired regeneration, and what is the significance of this finding as it relates to SVF formation and function? 

We apologize for this omission. This experiment was more thouroughly described in our previous study by Metikala et al 2022. In that study we showed that when endothelial cells are ablated by treating with MTZ from 6 to 45 hpf, this results in ablation of all vascular endothelial cells except for SVF cells, because they originate later than other cells. We subsequently showed that these SVF cells can partially form PCV and intestinal vasculature, helping them regenerate, which was confirmed by time-lapse imaging. In the current study, we tested if jam2a; jam2b double mutants show defects in such vascular regeneration. Indeed, regeneration after cell ablation was reduced, which correlated with reduction in SVF cell number. This argues that jam2a/b function is required for SVF cell emergence and vascular recovery after endothelial cell ablation. We will provide better description of this experiment and discuss interpretations in the revised manuscript.

(4) The authors need to include representative images of jam2b>CreERT2 with 4-OH activation at different timepoints in Figure 3.

Yes, thanks for noting this; these images will be included in the revised manuscript.

(5) The etv2:Kaede photoconversion experiment to show that the majority of intestinal vasculature derives after 24 hours needs to be supplemented with additional data on photoconverted post-24-hour-old endothelial cells, with the expectation that the majority of intestinal endothelial cells at 4 days will then be labeled with red Kaede. In addition, there have been data that show the red Kaede protein is not stable past several days in vivo, and 3 days might be sufficient for the removal or degradation of this photoconverted protein. Thus, the statement that intestinal vasculature forms largely by new vasculogenesis might be too strong based on existing data.

It is apparent from Fig. 4B that many other vessels, such as the dorsal aorta and many intersegmental vessels show robust red Kaede expression at 4 dpf, arguing that there is sufficient photoconverted Kaede present at this stage, and its degradation is unlikely to be the reason. However, we are planning to include additional control experiments, as suggested by the reviewer, to make this argument stronger.

(6) To strengthen the claim that hand2 acts upstream of jam2b, the authors can perform combinatorial genetic epistatic analysis and examine whether jam2b mutations worsen hand2 homozygous or heterozygous effects on the SVF. Similarly, overexpressing jam2b might rescue the loss of SVF/etv2 expression in hand2 mutants. 

We appreciate this suggestion. Double epistatic analysis, while informative, can be tricky. In this case, we are dealing with jam2a; jam2b redundancy and also the maternal effect. It may take a while considerable effort to generate different combinations of tripple mutant lines (jam2a,jam2b,hand2), and it is unclear whether double or tripple heterozygous embryos will show any defects to clarify their epistatic relationship. Instead, as suggested, we are planning to overexpress jam2b in wild-type and hand2 mutants to address this point.

eLife Assessment

This important study addresses the question of how organ-specific blood vessels form during different stages of development, and how specific genes may regulate these processes. New genetic tools were developed to label distinct endothelial cell populations and track them over time in different mutant backgrounds. The results are solid; however, additional data quantification, lineage tracing, and cell autonomy experiments would further strengthen the conclusions.

Reviewer #1 (Public review):

The manuscript by Griciunaite et al. explores jam2b functions in the formation of late vascular precursors in what is termed the secondary heart field. The authors nicely show that expression of jam2b defines these cells in the lateral plate mesoderm and the intestinal vasculature using a target integration of Gal4 into the jam2b locus. This analysis is followed by using a UAS:cre approach to follow the lineage of jam2b expressing cells, demonstrating their contributions to the vasculature during a second round of specification of vascular precursors. This is confirmed with single-cell analysis of jam2b-gal4 expressing cells. The authors then explore the genetic requirements of jam2a and b in zebrafish and also show that hand2 functions in the secondary heart field upstream of jam2b.

Overall, the experimental evidence and results support the major conclusions. The study elucidates a novel role for jam2 in the specification of vascular precursors at later stages of development.

This understanding has important implications for treating vascular disease and regenerative therapies. The manuscript is very clearly written, and the major conclusions are likely to have a lasting impact on the field.

Reviewer #2 (Public review):

Summary:

Griciunaite et al. report on the function of jam2b and hand2 in the formation of the intestinal vasculature derived from late-forming endothelial cells (ECs) within the secondary vascular field (SVF). They generate transgenic lines that allow for the tracking of jam2b-expressing cells, both with fluorescent proteins and through Cre-mediated recombination in reporter lines. They also show that double maternal zygotic mutants in jam2a and jam2b, as well as hand2 mutants, display defects in the formation of the intestinal vasculature.

Strengths:

The results are interesting, as they address the important question of how blood vessels form during later developmental time points and potentially identify specific genes regulating this process.

Weaknesses:

(1) The authors generate a new tool, a Gal4 knock-in of the jam2b locus, to track EGFP-expressing cells over time and follow the developmental trajectory of jam2b-expressing cells. Figure 1 characterizes the line. However, it lacks quantification, e.g., how many etv2-expressing cells also show EGFP expression or the contribution of EGFP-expressing cells to different types of blood vessels. This type of quantification would be useful, as it would also allow for comparison of their findings to their previous data examining the contribution of SVF cells to different types of blood vessels. All the authors state that at 30 hpf, EGFP-expressing cells can be seen in the vasculature (apparently the PCV).

It is not clear why the authors do not use a nuclear marker for both ECs (as they did in their previous publication) and for jam2b-expressing cells. UAS:nEGFP and UAS:NLS-mcherry (e.g. pt424tg) transgenic lines are available. This would circumvent the problem the authors encounter with the strong fluorescence visible in the yolk extension. It would also facilitate quantifying the contribution of jam2b cells to different types of blood vessels.

(2) The time-lapse movie in Figure 2 is not very informative, as it just provides a single example of a dividing cell contributing to the PCV. Also, quantifications are needed. As SVF cells appear to expand significantly after their initial specification, it would be informative to know how many cell divisions and which types of blood vessels jam2b-expressing cells contribute to. Can the authors observe cells that give rise to different types of blood vessels? Jam2b expression in LPM cells apparently precedes expression of etv2. Is etv2 needed for maintenance, or do Jam2b-expressing cells contribute to different types of tissues in etv2 mutant embryos? Comparing time-lapse analysis in wildtype and etv2 mutant embryos would address this question.

(3) In Figure 3, the authors generate UAS:Cre and UAS:Cre-ERT2 transgenic lines to lineage trace the jam2b-expressing cells. It is again not clear why the authors do not use a responder line containing nuclear-localized fluorescent proteins to circumvent the strong expression of fluorescent proteins in the yolk extension. It is also unclear why the two transgenic lines give very different results regarding the number of cells being labelled. The ERT2 fusions label around 3 cells in the SIA, while the Cre line labels only about 1.5 cells per embryo, with very little contribution of labelled cells to other blood vessels. One would expect the Cre line requiring tamoxifen induction to label fewer cells when compared to the constitutive Cre line. What is the reason for this discrepancy? Are the lines single integration? Is there silencing? This needs to be better characterized, also regarding the reproducibility of the experiments. If the Cre lines were to be multiple copy integrations, outcrossing the line might lead to lower expression levels in future generations.

It is also not clear how the authors conclude from these findings that "SVF cells show major contribution to the SIA and SIV" when only 1.5 or 3 cells of the SIA are labelled, with even fewer cells labelled in other blood vessels. They speculate that this might be due to low recombination efficiency, a question they then set out to answer using photoconversion of etv2:KAEDE expressing cells, an experiment that they also performed in their 2014 and 2022 publications. To check for low recombination efficiency, the authors could examine the expression of Cre mRNA in their transgenic embryos. Do many more jam2b expressing cells express Cre mRNA than they observe in their switch lines? They could also compare their experiments using Cre recombinase with those using EGFP expression in jam2b cells. EGFP is relatively stable, and the time frames the authors analyze are short. As no quantification of EGFP-expressing cells is provided in Figure 1, this comparison is currently not possible. Do these two different approaches answer different questions here?

(4) Concerning the etv2:KAEDE photoconversion experiments: The percentages the authors report for SVF cells' contribution to the SIV and SIA differ from their previous study (Dev Cell, 2022). In that publication, SVF cells contributed 28% to the SIA and 48% to the SIV. In the present study, the numbers are close to 80% for both vessels. The difference is that the previous study analyzed 2dpf old embryos and the new one 4dpf old embryos. Do SVF-derived cells proliferate more than PCV-derived cells, or is there another explanation for this change in percentage contribution?

(5) Single-cell sequencing data: Why do the authors not show jam2b expression in their single-cell sequencing data? They sorted for (presumably) jam2b-expressing cells and hypothesize that jam2b expression in ECs at this time point is important for the generation of intestinal vasculature. Do ECs in cluster 15 express jam2b? Why are no other top marker genes (tal1, etv2, egfl7, npas4l) included in the dot blot in Figure 5b?

(6) Concerns about cell autonomy of mutant phenotypes: The authors need to perform in situ hybridization to characterize jam2a expression. Can it be seen in SVF cells? The double mutants show a clear phenotype in intestinal vessel development; however, it is unclear whether this is due to a cell-autonomous function of jam2a/b within SVF cells. The authors need to address this issue, as jam2b and potentially also jam2a are expressed within the tissue surrounding the forming SVF. For instance, do transplanted mutant cells contribute to the intestinal vasculature to the same extent as wild-type cells do?

(7) Finally, the authors analyze the phenotypes of hand2 mutants and their impact on the expression of jam2b and etv2. They observe a reduction in jam2b and etv2 expression in SVF cells. However, they do not show the vascular phenotypes of hand2 mutants. Is the formation of the SIA and SIV disturbed? Is hand2 cell autonomously needed in ECs? The authors suggest that hand2 controls SVF development through the regulation of jam2b. However, they also show that jam2b mutants do not have a phenotype on their own. Clearly, hand2, if it were to be required in ECs, regulates other genes important for SVF development. These might then regulate jam2b expression. The clear linear relationship, as the title suggests, is not convincingly shown by the data.

Reviewer #3 (Public review):

Summary:

This study by Griciunaite et al. investigates the function of the adhesion molecule Jam2 in initiating the formation of organ (intestinal)-specific vasculature in zebrafish. Their previous studies identified a group of late-forming vascular progenitors from the lateral plate mesoderm along the yolk extension termed the secondary vascular field (SVF), which can contribute to intestinal vasculature. Transcriptomic analysis of the zebrafish trunk region identified SVF-enriched marker genes, which include jam2b. They then performed expression analysis of jam2b using whole-mount in situ hybridization and Gal4 knock-in transgenic line analysis. These analyses show that jam2b is expressed in the SVF cells that correspond to etv2 and kdrl expression past 24 hours. Lineage tracing combining jam2b:Gal4 and UAS:Cre or UAS:CreERT2 show the contribution of jam2b in SVF and intestinal vasculature formation. jam2b mutations did not cause observable defects in the vasculature, but combined jam2a; jam2b mutations led to impaired ISV, PCV, SIA, SIV and thoracic duct lymphatic vasculature formation. Finally, the authors show that mutations in the transcription factor hand2 led to reduced jam2b expression and impaired SVF formation.

Strengths:

The authors accomplished many feats in generating new reporter lines and mutations that are valuable to the community. The study provided an interesting perspective on organ-specific vascular development and origin heterogeneity. The genetic aspects of the study are clean, and the mutational phenotypes are convincing.

Several suggestions and major comments that can improve the manuscript include:

(1) Overall molecular mechanisms of Jam2 function are not fully uncovered in the study. How do the adhesion molecules Jam2a and Jam2b regulate SVF cell formation? Are they responsible for migration, adhesion or fate determination of these structures? The authors should provide a more in-depth study of the jam2a, jam2b mutations and assess the processes affected in these mutants. Combining these mutants with etv2:Kaede can also provide a stronger causative link between their functions and defects in SVF formation.

(2) Have the authors tested the specificity of the jam2b knock-in reporter line? This is an important experiment, as many of the conclusions derive from lineage tracing and fluorescence reporting from this knock-in line. One suggestion is to cross the jam2b:GFP or jam2b:Gal4, UAS:GFP line to the generated jam2b mutants, and examine the expression pattern of these lines. Considering that the ISH experiment showed lack of jam2b expression, the reporter line should not be expressed in the jam2b mutants.

(3) The rationale behind the regeneration study is not clear, and the mechanisms underlying the phenotype are not well described. How do the authors explain the phenotype with the impaired regeneration, and what is the significance of this finding as it relates to SVF formation and function?

(4) The authors need to include representative images of jam2b>CreERT2 with 4-OH activation at different timepoints in Figure 3.

(5) The etv2:Kaede photoconversion experiment to show that the majority of intestinal vasculature derives after 24 hours needs to be supplemented with additional data on photoconverted post-24-hour-old endothelial cells, with the expectation that the majority of intestinal endothelial cells at 4 days will then be labeled with red Kaede. In addition, there have been data that show the red Kaede protein is not stable past several days in vivo, and 3 days might be sufficient for the removal or degradation of this photoconverted protein. Thus, the statement that intestinal vasculature forms largely by new vasculogenesis might be too strong based on existing data.

(6) To strengthen the claim that hand2 acts upstream of jam2b, the authors can perform combinatorial genetic epistatic analysis and examine whether jam2b mutations worsen hand2 homozygous or heterozygous effects on the SVF. Similarly, overexpressing jam2b might rescue the loss of SVF/etv2 expression in hand2 mutants.

eLife Assessment

This important work investigates cooperative behaviors in adolescents using a repeated Prisoner's Dilemma game. The approach used in the study is solid. The impact of this work could be further enhanced with more rigorous modelling procedures and more modeling selection/comparison details, as well as by framing the findings in terms of the specific game-theoretic context, rather than general cooperation. Findings from this study will be of interest to developmental psychologists, economists, and social psychologists.

Reviewer #1 (Public review):

Summary:

Wu and colleagues aimed to explain previous findings that adolescents, compared to adults, show reduced cooperation following cooperative behaviour from a partner in several social scenarios. The authors analysed behavioural data from adolescents and adults performing a zero-sum Prisoner's Dilemma task and compared a range of social and non-social reinforcement learning models to identify potential algorithmic differences. Their findings suggest that adolescents' lower cooperation is best explained by a reduced learning rate for cooperative outcomes, rather than differences in prior expectations about the cooperativeness of a partner. The authors situate their results within the broader literature, proposing that adolescents' behaviour reflects a stronger preference for self-interest rather than a deficit in mentalising.

Strengths:

The work as a whole suggests that, in line with past work, adolescents prioritise value accumulation, and this can be, in part, explained by algorithmic differences in weighted value learning. The authors situate their work very clearly in past literature, and make it obvious the gap they are testing and trying to explain. The work also includes social contexts which move the field beyond non-social value accumulation in adolescents. The authors compare a series of formal approaches that might explain the results and establish generative and model-comparison procedures to demonstrate the validity of their winning model and individual parameters. The writing was clear, and the presentation of the results was logical and well-structured.

Weaknesses:

I had some concerns about the methods used to fit and approximate parameters of interest. Namely, the use of maximum likelihood versus hierarchical methods to fit models on an individual level, which may reduce some of the outliers noted in the supplement, and also may improve model identifiability.

There was also little discussion given the structure of the Prisoner's Dilemma, and the strategy of the game (that defection is always dominant), meaning that the preferences of the adolescents cannot necessarily be distinguished from the incentives of the game, i.e. they may seem less cooperative simply because they want to play the dominant strategy, rather than a lower preferences for cooperation if all else was the same.

The authors have now addressed my comments and concerns in their revised version.

Appraisal & Discussion:

Overall, I believe this work has the potential to make a meaningful contribution to the field. Its impact would be strengthened by more rigorous modelling checks and fitting procedures, as well as by framing the findings in terms of the specific game-theoretic context, rather than general cooperation.

Comments on revisions:

Thank you to the authors for addressing my comments and concerns.

Reviewer #2 (Public review):

Summary:

This manuscript investigates age-related differences in cooperative behavior by comparing adolescents and adults in a repeated Prisoner's Dilemma Game (rPDG). The authors find that adolescents exhibit lower levels of cooperation than adults. Specifically, adolescents reciprocate partners' cooperation to a lesser degree than adults do. Through computational modeling, they show that this relatively low cooperation rate is not due to impaired expectations or mentalizing deficits, but rather a diminished intrinsic reward for reciprocity. A social reinforcement learning model with asymmetric learning rate best captured these dynamics, revealing age-related differences in how positive and negative outcomes drive behavioral updates. These findings contribute to understanding the developmental trajectory of cooperation and highlight adolescence as a period marked by heightened sensitivity to immediate rewards at the expense of long-term prosocial gains.

Strengths:

Rigid model comparison and parameter recovery procedure. Conceptually comprehensive model space. Well-powered samples.

Weaknesses:

A key conceptual distinction between learning from non-human agents (e.g., bandit machines) and human partners is that the latter are typically assumed to possess stable behavioral dispositions or moral traits. When a non-human source abruptly shifts behavior (e.g., from 80% to 20% reward), learners may simply update their expectations. In contrast, a sudden behavioral shift by a previously cooperative human partner can prompt higher-order inferences about the partner's trustworthiness or the integrity of the experimental setup (e.g., whether the partner is truly interactive or human). The authors may consider whether their modeling framework captures such higher-order social inferences. Specifically, trait-based models-such as those explored in Hackel et al. (2015, Nature Neuroscience)-suggest that learners form enduring beliefs about others' moral dispositions, which then modulate trial-by-trial learning. A learner who believes their partner is inherently cooperative may update less in response to a surprising defection, effectively showing a trait-based dampening of learning rate.

This asymmetry in belief updating has been observed in prior work (e.g., Siegel et al., 2018, Nature Human Behaviour) and could be captured using a dynamic or belief-weighted learning rate. Models incorporating such mechanisms (e.g., dynamic learning rate models as in Jian Li et al., 2011, Nature Neuroscience) could better account for flexible adjustments in response to surprising behavior, particularly in the social domain.

Second, the developmental interpretation of the observed effects would be strengthened by considering possible non-linear relationships between age and model parameters. For instance, certain cognitive or affective traits relevant to social learning-such as sensitivity to reciprocity or reward updating-may follow non-monotonic trajectories, peaking in late adolescence or early adulthood. Fitting age as a continuous variable, possibly with quadratic or spline terms, may yield more nuanced developmental insights.

Finally, the two age groups compared-adolescents (high school students) and adults (university students)-differ not only in age but also in sociocultural and economic backgrounds. High school students are likely more homogenous in regional background (e.g., Beijing locals), while university students may be drawn from a broader geographic and socioeconomic pool. Additionally, differences in financial independence, family structure (e.g., single-child status), and social network complexity may systematically affect cooperative behavior and valuation of rewards. Although these factors are difficult to control fully, the authors should more explicitly address the extent to which their findings reflect biological development versus social and contextual influences.

Comments on revisions:

The authors have addressed most of my previous comments adequately. I only have a minor question: The models with some variations of RL seem to have very similar AIC. What were the authors' criteria in deciding which model is the "winning" model when several models have similar AIC? Are there ways of integrating models with similar structures into a "model family"? Alternatively, is it possible that different models fit better for different subgroups of participants (e.g., high schoolers vs. college students)?

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

Wu and colleagues aimed to explain previous findings that adolescents, compared to adults, show reduced cooperation following cooperative behaviour from a partner in several social scenarios. The authors analysed behavioural data from adolescents and adults performing a zero-sum Prisoner's Dilemma task and compared a range of social and non-social reinforcement learning models to identify potential algorithmic differences. Their findings suggest that adolescents' lower cooperation is best explained by a reduced learning rate for cooperative outcomes, rather than differences in prior expectations about the cooperativeness of a partner. The authors situate their results within the broader literature, proposing that adolescents' behaviour reflects a stronger preference for self-interest rather than a deficit in mentalising.

Strengths:

The work as a whole suggests that, in line with past work, adolescents prioritise value accumulation, and this can be, in part, explained by algorithmic differences in weighted value learning. The authors situate their work very clearly in past literature, and make it obvious the gap they are testing and trying to explain. The work also includes social contexts that move the field beyond non-social value accumulation in adolescents. The authors compare a series of formal approaches that might explain the results and establish generative and modelcomparison procedures to demonstrate the validity of their winning model and individual parameters. The writing was clear, and the presentation of the results was logical and wellstructured.

We thank the reviewer for recognizing the strengths of our work.

Weaknesses:

(Q1) I also have some concerns about the methods used to fit and approximate parameters of interest. Namely, the use of maximum likelihood versus hierarchical methods to fit models on an individual level, which may reduce some of the outliers noted in the supplement, and also may improve model identifiability.

We thank the reviewer for this suggestion. Following the comment, we added a hierarchical Bayesian estimation. We built a hierarchical model with both group-level (adolescent group and adult group) and individual-level structures for the best-fitting model. Four Markov chains with 4,000 samples each were run, and the model converged well (see Figure supplement 7)

We then analyzed the posterior parameters for adolescents and adults separately. The results were consistent with those from the MLE analysis (see Figure 2—figure supplement 5). These additional results have been included in the Appendix Analysis section (also see Figure supplement 5 and 7). In addition, we have updated the code and provided the link for reference. We appreciate the reviewer’s suggestion, which improved our analysis.

(Q2) There was also little discussion given the structure of the Prisoner's Dilemma, and the strategy of the game (that defection is always dominant), meaning that the preferences of the adolescents cannot necessarily be distinguished from the incentives of the game, i.e. they may seem less cooperative simply because they want to play the dominant strategy, rather than a lower preferences for cooperation if all else was the same.

We thank the reviewer for this comment and agree that adolescents’ lower cooperation may partly reflect a rational response to the incentive structure of the Prisoner’s Dilemma.

However, our computational modeling explicitly addressed this possibility. Model 4 (inequality aversion) captures decisions that are driven purely by self-interest or aversion to unequal outcomes, including a parameter reflecting disutility from advantageous inequality, which represents self-oriented motives. If participants’ behavior were solely guided by the payoff-dominant strategy, this model should have provided the best fit. However, our model comparison showed that Model 5 (social reward) performed better in both adolescents and adults, suggesting that cooperative behavior is better explained by valuing social outcomes beyond payoff structures.

Besides, if adolescents’ lower cooperation is that they strategically respond to the payoff structure by adopting defection as the more rewarding option. Then, adolescents should show reduced cooperation across all rounds. Instead, adolescents and adults behaved similarly when partners defected, but adolescents cooperated less when partners cooperated and showed little increase in cooperation even after consecutive cooperative responses. This pattern suggests that adolescents’ lower cooperation cannot be explained solely by strategic responses to payoff structures but rather reflects a reduced sensitivity to others’ cooperative behavior or weaker social reciprocity motives. We have expanded our Discussion to acknowledge this important point and to clarify how the behavioral and modeling results address the reviewer’s concern.

“Overall, these findings indicate that adolescents’ lower cooperation is unlikely to be driven solely by strategic considerations, but may instead reflect differences in the valuation of others’ cooperation or reduced motivation to reciprocate. Although defection is the payoffdominant strategy in the Prisoner’s Dilemma, the selective pattern of adolescents’ cooperation and the model comparison results indicate that their reduced cooperation cannot be fully explained by strategic incentives, but rather reflects weaker valuation of social reciprocity.”

Appraisal & Discussion:

(Q3) The authors have partially achieved their aims, but I believe the manuscript would benefit from additional methodological clarification, specifically regarding the use of hierarchical model fitting and the inclusion of Bayes Factors, to more robustly support their conclusions. It would also be important to investigate the source of the model confusion observed in two of their models.

We thank the reviewer for this comment. In the revised manuscript, we have clarified the hierarchical Bayesian modeling procedure for the best-fitting model, including the group- and individual-level structure and convergence diagnostics. The hierarchical approach produced results that fully replicated those obtained from the original maximumlikelihood estimation, confirming the robustness of our findings. Please also see the response to Q1.

Regarding the model confusion between the inequality aversion (Model 4) and social reward (Model 5) models in the model recovery analysis, both models’ simulated behaviors were best captured by the baseline model. This pattern arises because neither model includes learning or updating processes. Given that our task involves dynamic, multi-round interactions, models lacking a learning mechanism cannot adequately capture participants’ trial-by-trial adjustments, resulting in similar behavioral patterns that are better explained by the baseline model during model recovery. We have added a clarification of this point to the Results:

“The overlap between Models 4 and 5 likely arises because neither model incorporates a learning mechanism, making them less able to account for trial-by-trial adjustments in this dynamic task.”

(Q4) I am unconvinced by the claim that failures in mentalising have been empirically ruled out, even though I am theoretically inclined to believe that adolescents can mentalise using the same procedures as adults. While reinforcement learning models are useful for identifying biases in learning weights, they do not directly capture formal representations of others' mental states. Greater clarity on this point is needed in the discussion, or a toning down of this language.

We sincerely thank the reviewer for this professional comment. We agree that our prior wording regarding adolescents’ capacity to mentalise was somewhat overgeneralized. Accordingly, we have toned down the language in both the Abstract and the Discussion to better align our statements with what the present study directly tests. Specifically, our revisions focus on adolescents’ and adults’ ability to predict others’ cooperation in social learning. This is consistent with the evidence from our analyses examining adolescents’ and adults’ model-based expectations and self-reported scores on partner cooperativeness (see Figure 4). In the revised Discussion, we state:

“Our results suggest that the lower levels of cooperation observed in adolescents stem from a stronger motive to prioritize self-interest rather than a deficiency in predicting others’ cooperation in social learning”.

(Q5) Additionally, a more detailed discussion of the incentives embedded in the Prisoner's Dilemma task would be valuable. In particular, the authors' interpretation of reduced adolescent cooperativeness might be reconsidered in light of the zero-sum nature of the game, which differs from broader conceptualisations of cooperation in contexts where defection is not structurally incentivised.

We thank the reviewer for this comment and agree that adolescents’ lower cooperation may partly reflect a rational response to the incentive structure of the Prisoner’s Dilemma. However, our behavioral and computational evidence suggests that this pattern cannot be explained solely by strategic responses to payoff structures, but rather reflects a reduced sensitivity to others’ cooperative behavior or weaker social reciprocity motives. We have expanded the Discussion to acknowledge this point and to clarify how both behavioral and modeling results address the reviewer’s concern (see also our response to Q2).

(Q6) Overall, I believe this work has the potential to make a meaningful contribution to the field. Its impact would be strengthened by more rigorous modelling checks and fitting procedures, as well as by framing the findings in terms of the specific game-theoretic context, rather than general cooperation.

We thank the reviewer for the professional comments, which have helped us improve our work.

Reviewer #2 (Public review):

Summary:

This manuscript investigates age-related differences in cooperative behavior by comparing adolescents and adults in a repeated Prisoner's Dilemma Game (rPDG). The authors find that adolescents exhibit lower levels of cooperation than adults. Specifically, adolescents reciprocate partners' cooperation to a lesser degree than adults do. Through computational modeling, they show that this relatively low cooperation rate is not due to impaired expectations or mentalizing deficits, but rather a diminished intrinsic reward for reciprocity. A social reinforcement learning model with asymmetric learning rate best captured these dynamics, revealing age-related differences in how positive and negative outcomes drive behavioral updates. These findings contribute to understanding the developmental trajectory of cooperation and highlight adolescence as a period marked by heightened sensitivity to immediate rewards at the expense of long-term prosocial gains.

Strengths:

(1) Rigid model comparison and parameter recovery procedure.

(2) Conceptually comprehensive model space.

(3) Well-powered samples.

We thank the reviewer for highlighting the strengths of our work.

Weaknesses:

(Q1) A key conceptual distinction between learning from non-human agents (e.g., bandit machines) and human partners is that the latter are typically assumed to possess stable behavioral dispositions or moral traits. When a non-human source abruptly shifts behavior (e.g., from 80% to 20% reward), learners may simply update their expectations. In contrast, a sudden behavioral shift by a previously cooperative human partner can prompt higher-order inferences about the partner's trustworthiness or the integrity of the experimental setup (e.g., whether the partner is truly interactive or human). The authors may consider whether their modeling framework captures such higher-order social inferences. Specifically, trait-based models-such as those explored in Hackel et al. (2015, Nature Neuroscience)-suggest that learners form enduring beliefs about others' moral dispositions, which then modulate trial-bytrial learning. A learner who believes their partner is inherently cooperative may update less in response to a surprising defection, effectively showing a trait-based dampening of learning rate.

We thank the reviewer for this thoughtful comment. We agree that social learning from human partners may involve higher-order inferences beyond simple reinforcement learning from non-human sources. To address this, we had previously included such mechanisms in our behavioral modeling. In Model 7 (Social Reward Model with Influence), we tested a higher-order belief-updating process in which participants’ expectations about their partner’s cooperation were shaped not only by the partner’s previous choices but also by the inferred influence of their own past actions on the partner’s subsequent behavior. In other words, participants could adjust their belief about the partner’s cooperation by considering how their partner’s belief about them might change. Model comparison showed that Model 7 did not outperform the best-fitting model, suggesting that incorporating higher-order influence updates added limited explanatory value in this context. As suggested by the reviewer, we have further clarified this point in the revised manuscript.

Regarding trait-based frameworks, we appreciate the reviewer’s reference to Hackel et al. (2015). That study elegantly demonstrated that learners form relatively stable beliefs about others’ social dispositions, such as generosity, especially when the task structure provides explicit cues for trait inference (e.g., resource allocations and giving proportions). By contrast, our study was not designed to isolate trait learning, but rather to capture how participants update their expectations about a partner’s cooperation over repeated interactions. In this sense, cooperativeness in our framework can be viewed as a trait-like latent belief that evolves as evidence accumulates. Thus, while our model does not include a dedicated trait module that directly modulates learning rates, the belief-updating component of our best-fitting model effectively tracks a dynamic, partner-specific cooperativeness, potentially reflecting a prosocial tendency.

(Q2) This asymmetry in belief updating has been observed in prior work (e.g., Siegel et al., 2018, Nature Human Behaviour) and could be captured using a dynamic or belief-weighted learning rate. Models incorporating such mechanisms (e.g., dynamic learning rate models as in Jian Li et al., 2011, Nature Neuroscience) could better account for flexible adjustments in response to surprising behavior, particularly in the social domain.

We thank the reviewer for the suggestion. Following the comment, we implemented an additional model incorporating a dynamic learning rate based on the magnitude of prediction errors. Specifically, we developed Model 9:  Social reward model with Pearce–Hall learning algorithm (dynamic learning rate), in which participants’ beliefs about their partner’s cooperation probability are updated using a Rescorla–Wagner rule with a learning rate dynamically modulated by the Pearce–Hall (PH) Error Learning mechanism. In this framework, the learning rate increases following surprising outcomes (larger prediction errors) and decreases as expectations become more stable (see Appendix Analysis section for details).

The results showed that this dynamic learning rate model did not outperform our bestfitting model in either adolescents or adults (see Figure supplement 6). We greatly appreciate the reviewer’s suggestion, which has strengthened the scope of our analysis. We now have added these analyses to the Appendix Analysis section (also Figure Supplement 6) and expanded the Discussion to acknowledge this modeling extension and further discuss its implications.

(Q3) Second, the developmental interpretation of the observed effects would be strengthened by considering possible non-linear relationships between age and model parameters. For instance, certain cognitive or affective traits relevant to social learning-such as sensitivity to reciprocity or reward updating-may follow non-monotonic trajectories, peaking in late adolescence or early adulthood. Fitting age as a continuous variable, possibly with quadratic or spline terms, may yield more nuanced developmental insights.

We thank the reviewer for this professional comment. In addition to the linear analyses, we further conducted exploratory analyses to examine potential non-linear relationships between age and the model parameters. Specifically, we fit LMMs for each of the four parameters as outcomes (α+, α-, β, and ω). The fixed effects included age, a quadratic age term, and gender, and the random effects included subject-specific random intercepts and random slopes for age and gender. Model comparison using BIC did not indicate improvement for the quadratic models over the linear models for α⁺ (ΔBIC_{quadratic-linear} = 5.09), α^-(ΔBIC_{quadratic-linear} = 3.04), β (ΔBIC_{quadratic-linear} = 3.9), or ω (ΔBIC_{quadratic-linear}= 0). Moreover, the quadratic age term was not significant for α⁺, α⁻, or β (all ps > 0.10). For ω, we observed a significant linear age effect (b = 1.41, t = 2.65, p = 0.009) and a significant quadratic age effect (b = −0.03, t = −2.39, p = 0.018; see Author response image 1). This pattern is broadly consistent with the group effect reported in the main text. The shaded area in the figure represents the 95% confidence interval. As shown, the interval widens at older ages (≥ 26 years) due to fewer participants in that range, which limits the robustness of the inferred quadratic effect. In consideration of the limited precision at older ages and the lack of BIC improvement, we did not emphasize the quadratic effect in the revised manuscript and present these results here as exploratory.

Author response image 1.

Linear and quadratic model fits showing the relationship between age and the ω parameter, with 95% confidence intervals.

(Q4) Finally, the two age groups compared - adolescents (high school students) and adults (university students) - differ not only in age but also in sociocultural and economic backgrounds. High school students are likely more homogenous in regional background (e.g., Beijing locals), while university students may be drawn from a broader geographic and socioeconomic pool. Additionally, differences in financial independence, family structure (e.g., single-child status), and social network complexity may systematically affect cooperative behavior and valuation of rewards. Although these factors are difficult to control fully, the authors should more explicitly address the extent to which their findings reflect biological development versus social and contextual influences.

We appreciate this comment. Indeed, adolescents (high school students) and adults (university students) differ not only in age but also in sociocultural and socioeconomic backgrounds. In our study, all participants were recruited from Beijing and surrounding regions, which helps minimize large regional and cultural variability. Moreover, we accounted for individual-level random effects and included participants’ social value orientation (SVO) as an individual difference measure.

Nonetheless, we acknowledge that other contextual factors, such as differences in financial independence, socioeconomic status, and social experience—may also contribute to group differences in cooperative behavior and reward valuation. Although our results are broadly consistent with developmental theories of reward sensitivity and social decisionmaking, sociocultural influences cannot be entirely ruled out. Future work with more demographically matched samples or with socioeconomic and regional variables explicitly controlled will help clarify the relative contributions of biological and contextual factors. Accordingly, we have revised the Discussion to include the following statement:

“Third, although both age groups were recruited from Beijing and nearby regions, minimizing major regional and cultural variation, adolescents and adults may still differ in socioeconomic status, financial independence, and social experience. Such contextual differences could interact with developmental processes in shaping cooperative behavior and reward valuation. Future research with demographically matched samples or explicit measures of socioeconomic background will help disentangle biological from sociocultural influences.”

Reviewer #3 (Public review):

Summary:

Wu and colleagues find that in a repeated Prisoner's Dilemma, adolescents, compared to adults, are less likely to increase their cooperation behavior in response to repeated cooperation from a simulated partner. In contrast, after repeated defection by the partner, both age groups show comparable behavior.

To uncover the mechanisms underlying these patterns, the authors compare eight different models. They report that a social reward learning model, which includes separate learning rates for positive and negative prediction errors, best fits the behavior of both groups. Key parameters in this winning model vary with age: notably, the intrinsic value of cooperating is lower in adolescents. Adults and adolescents also differ in learning rates for positive and negative prediction errors, as well as in the inverse temperature parameter.

Strengths:

The modeling results are compelling in their ability to distinguish between learned expectations and the intrinsic value of cooperation. The authors skillfully compare relevant models to demonstrate which mechanisms drive cooperation behavior in the two age groups.

We thank the reviewer’s recognition of our work’s strengths.

Weaknesses:

(Q1) Some of the claims made are not fully supported by the data:

The central parameter reflecting preference for cooperation is positive in both groups. Thus, framing the results as self-interest versus other-interest may be misleading.

We thank the reviewer for this insightful comment. In the social reward model, the cooperation preference parameter is positive by definition, as defection in the repeated rPDG always yields a +2 monetary advantage regardless of the partner’s action. This positive value represents the additional subjective reward assigned to mutual cooperation (e.g., reciprocity value) that counterbalances the monetary gain from defection. Although the estimated social reward parameter ω was positive, the effective advantage of cooperation is Δ=p×ω−2. Given participants’ inferred beliefs p, Δ was negative for most trials (p×ω<2), indicating that the social reward was insufficient to offset the +2 advantage of defection. Thus, both adolescents and adults valued cooperation positively, but adolescents’ smaller ω and weaker responsiveness to sustained partner cooperation suggest a stronger weighting on immediate monetary payoffs.

In this light, our framing of adolescents as more self-interested derives from their behavioral pattern: even when they recognized sustained partner cooperation and held high expectations of partner cooperation, adolescents showed lower cooperative behavior and reciprocity rewards compared with adults. Whereas adults increased cooperation after two or three consecutive partner cooperations, this pattern was absent among adolescents. We therefore interpret their behavior as relatively more self-interested, reflecting reduced sensitivity to the social reward from mutual cooperation rather than a categorical shift from self-interest to other-interest, as elaborated in the Discussion.

(Q2) It is unclear why the authors assume adolescents and adults have the same expectations about the partner's cooperation, yet simultaneously demonstrate age-related differences in learning about the partner. To support their claim mechanistically, simulations showing that differences in cooperation preference (i.e., the w parameter), rather than differences in learning, drive behavioral differences would be helpful.

We thank the reviewer for raising this important point. In our model, both adolescents and adults updated their beliefs about partner cooperation using an asymmetric reinforcement learning (RL) rule. Although adolescents exhibited a higher positive and a lower negative learning rate than adults, the two groups did not differ significantly in their overall updating of partner cooperation probability (Fig. 4a-b). We then examined the social reward parameter ω, which was significantly smaller in adolescents and determined the intrinsic value of mutual cooperation (i.e., p×ω). This variable differed significantly between groups and closely matched the behavioral pattern.

Following the reviewer’s suggestion, we conducted additional simulations varying one model parameter at a time while holding the others constant. The difference in mean cooperation probability between adults and adolescents served as the index (positive = higher cooperation in adults). As shown in the Author response image 2, decreases in ω most effectively reproduced the observed group difference (shaded area), indicating that age-related differences in cooperation are primarily driven by variation in the social reward parameter ω rather than by others.

Author response image 2.

Simulation results showing how variations in each model parameter affect the group difference in mean cooperation probability (Adults – Adolescents). Based on the bestfitting Model 8 and parameters estimated from all participants, each line represents one parameter (i.e., α+, α-, ω, β) systematically varied within the tested range (α±:0.1–0.9; ω, β:1–9) while other parameters were held constant. Positive values indicate higher cooperation in adults. Smaller ω values most strongly reproduced the observed group difference, suggesting that reduced social reward weighting primarily drives adolescents’ lower cooperation.

(Q3) Two different schedules of 120 trials were used: one with stable partner behavior and one with behavior changing after 20 trials. While results for order effects are reported, the results for the stable vs. changing phases within each schedule are not. Since learning is influenced by reward structure, it is important to test whether key findings hold across both phases.

We thank the reviewer for this thoughtful and professional comment. In our GLMM and LMM analyses, we focused on trial order rather than explicitly including the stable vs. changing phase factor, due to concerns about multicollinearity. In our design, phases occur in specific temporal segments, which introduces strong collinearity with trial order. In multi-round interactions, order effects also capture variance related to phase transitions.

Nonetheless, to directly address this concern, we conducted additional robustness analyses by adding a phase variable (stable vs. changing) to GLMM1, LMM1, and LMM3 alongside the original covariates. Across these specifications, the key findings were replicated (see GLMM_sup2 and LMM_sup4–5; Tables 9-11), and the direction and significance of main effects remained unchanged, indicating that our conclusions are robust to phase differences.

(Q4) The division of participants at the legal threshold of 18 years should be more explicitly justified. The age distribution appears continuous rather than clearly split. Providing rationale and including continuous analyses would clarify how groupings were determined.

We thank the reviewer for this thoughtful comment. We divided participants at the legal threshold of 18 years for both conceptual and practical reasons grounded in prior literature and policy. In many countries and regions, 18 marks the age of legal majority and is widely used as the boundary between adolescence and adulthood in behavioral and clinical research. Empirically, prior studies indicate that psychosocial maturity and executive functions approach adult levels around this age, with key cognitive capacities stabilizing in late adolescence (Icenogle et al., 2019; Tervo-Clemmens et al., 2023). We have clarified this rationale in the Introduction section of the revised manuscript.

“Based on legal criteria for majority and prior empirical work, we adopt 18 years as the boundary between adolescence and adulthood (Icenogle et al., 2019; Tervo-Clemmens et al., 2023).”

We fully agree that the underlying age distribution is continuous rather than sharply divided. To address this, we conducted additional analyses treating age as a continuous predictor (see GLMM_sup1 and LMM_sup1–3; Tables S1-S4), which generally replicated the patterns observed with the categorical grouping. Nevertheless, given the limited age range of our sample, the generalizability of these findings to fine-grained developmental differences remains constrained. Therefore, our primary analyses continue to focus on the contrast between adolescents and adults, rather than attempting to model a full developmental trajectory.

(Q5) Claims of null effects (e.g., in the abstract: "adults increased their intrinsic reward for reciprocating... a pattern absent in adolescents") should be supported with appropriate statistics, such as Bayesian regression.

We thank the reviewer for highlighting the importance of rigor when interpreting potential null effects. To address this concern, we conducted Bayes factor analyses of the intrinsic reward for reciprocity and reported the corresponding BF10 for all relevant post hoc comparisons. This approach quantifies the relative evidence for the alternative versus the null hypothesis, thereby providing a more direct assessment of null effects. The analysis procedure is now described in the Methods and Materials section:

“Post hoc comparisons were conducted using Bayes factor analyses with MATLAB’s bayesFactor Toolbox (version v3.0, Krekelberg, 2024), with a Cauchy prior scale σ = 0.707.”

(Q6) Once claims are more closely aligned with the data, the study will offer a valuable contribution to the field, given its use of relevant models and a well-established paradigm.

We are grateful for the reviewer’s generous appraisal and insightful comments.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) I commend the authors on a well-structured, clear, and interesting piece of work. I have several questions and recommendations that, if addressed, I believe will strengthen the manuscript.

We thank the reviewer for commending the organization of our paper.

(2) Introduction: - Why use a zero-sum (Prisoner's Dilemma; PD) versus a mixed-motive game (e.g. Trust Task) to study cooperation? In a finite set of rounds, the dominant strategy can be to defect in a PD.

We thank the reviewer for this helpful comment. We agree that both the rationale for using the repeated Prisoner’s Dilemma (rPDG) and the limitations of this framework should be clarified. We chose the rPDG to isolate the core motivational conflict between selfinterest and joint welfare, as its symmetric and simultaneous structure avoids the sequential trust and reputation dependencies/accumulation inherent to asymmetric tasks such as the Trust Game (King-Casas et al., 2005; Rilling et al., 2002).

Although a finitely repeated rPDG theoretically favors defection, extensive prior research shows that cooperation can still emerge in long repeated interactions when players rely on learning and reciprocity rather than backward induction (Rilling et al., 2002; Fareri et al., 2015). Our design employed 120 consecutive rounds, allowing participants to update expectations about partner behavior and to establish stable reciprocity patterns over time. We have added the following clarification to the Introduction:

“The rPDG provides a symmetric and simultaneous framework that isolates the motivational conflict between self-interest and joint welfare, avoiding the sequential trust and reputation dynamics characteristic of asymmetric tasks such as the Trust Game (Rilling et al., 2002; King-Casas et al., 2005)”

(3) Methods:

Did the participants know how long the PD would go on for?

Were the participants informed that the partner was real/simulated?

Were the participants informed that the partner was going to be the same for all rounds?

We thank the reviewer for the meticulous review work, which helped us present the experimental design and reporting details more clearly. the following clarifications: I. Participants were not informed of the total number of rounds in the rPDG. This prevented endgame expectations and avoided distraction from counting rounds, which could introduce additional effects. II. Participants were told that their partner was another human participant in the laboratory. However, the partner’s behavior was predetermined by a computer program. This design enabled tighter experimental control and ensured consistent conditions across age groups, supporting valid comparisons. III. Participants were informed that they would interact with the same partner across all rounds, aligning with the essence of a multiround interaction paradigm and stabilizing partner-related expectations. For transparency, we have clarified these points in the Methods and Materials section:

“Participants were told that their partner was another human participant in the laboratory and that they would interact with the same partner across all rounds. However, in reality, the actions of the partner were predetermined by a computer program. This setup allowed for a clear comparison of the behavioral responses between adolescents and adults. Participants were not informed of the total number of rounds in the rPDG.”

(4) The authors mention that an SVO was also recorded to indicate participant prosociality. Where are the results of this? Did this track game play at all? Could cooperativeness be explained broadly as an SVO preference that penetrated into game-play behaviour?

We thank the reviewer for pointing this out. We agree that individual differences in prosociality may shape cooperative behavior, so we conducted additional analyses incorporating SVO. Specifically, we extended GLMM1 and LMM3 by adding the measured SVO as a fixed effect with random slopes, yielding GLMM_sup3 and LMM_sup6 (Tables 12–13). The results showed that higher SVO was associated with greater cooperation, whereas its effect on the reward for reciprocity was not significant. Importantly, the primary findings remained unchanged after controlling for SVO. These results indicate that cooperativeness in our task cannot be explained solely by a broad SVO preference, although a more prosocial orientation was associated with greater cooperation. We have reported these analyses and results in the Appendix Analysis section.

(5) Why was AIC chosen rather an BIC to compare model dominance?

Sorry for the lack of clarification. Both the Akaike Information Criterion (AIC, Akaike, 1974) and Bayesian Information Criterion (BIC, Schwarz, 1978) are informationtheoretic criterions for model comparison, neither of which depends on whether the models to be compared are nested to each other or not (Burnham et al., 2002). We have added the following clarification into the Methods.

“We chose to use the AICc as the metric of goodness-of-fit for model comparison for the following statistical reasons. First, BIC is derived based on the assumption that the “true model” must be one of the models in the limited model set one compares (Burnham et al., 2002; Gelman & Shalizi, 2013), which is unrealistic in our case. In contrast, AIC does not rely on this unrealistic “true model” assumption and instead selects out the model that has the highest predictive power in the model set (Gelman et al., 2014). Second, AIC is also more robust than BIC for finite sample size (Vrieze, 2012).”

(6) I believe the model fitting procedure might benefit from hierarchical estimation, rather than maximum likelihood methods. Adolescents in particular seem to show multiple outliers in a^+ and w^+ at the lower end of the distributions in Figure S2. There are several packages to allow hierarchical estimation and model comparison in MATLAB (which I believe is the language used for this analysis;

see https://journals.plos.org/ploscompbiol/article?id=10.1371/journal.pcbi.1007043).

We thank the reviewer for this helpful comment and for referring us to relevant methodological work (Piray et al., 2019). We have addressed this point by incorporating hierarchical Bayesian estimation, which effectively mitigates outlier effects and improves model identifiability. The results replicated those obtained with MLE fitting and further revealed group-level differences in key parameters. Please see our detailed response to Reviewer#1 Q1 for the full description of this analysis and results.

(7) Results: Model confusion seems to show that the inequality aversion and social reward models were consistently confused with the baseline model. Is this explained or investigated? I could not find an explanation for this.

The apparent overlap between the inequality aversion (Model 4) and social reward (Model 5) models in the recovery analysis likely arises because neither model includes a learning mechanism, making them unable to capture trial-by-trial adjustments in this dynamic task. Consequently, both were best fit by the baseline model. Please see Response to Reviewer #1 Q3 for related discussion.

(8) Figures 3e and 3f show the correlation between asymmetric learning rates and age. It seems that both a^+ and a^- are around 0.35-0.40 for young adolescents, and this becomes more polarised with age. Could it be that with age comes an increasing discernment of positive and negative outcomes on beliefs, and younger ages compress both positive and negative values together? Given the higher stochasticity in younger ages (\beta), it may also be that these values simply represent higher uncertainty over how to act in any given situation within a social context (assuming the differences in groups are true).

We appreciate this insightful interpretation. Indeed, both α+ and α- cluster around 0.35–0.40 in younger adolescents and become increasingly polarized with age, suggesting that sensitivity to positive versus negative feedback is less differentiated early in development and becomes more distinct over time. This interpretation remains tentative and warrants further validation. Based on this comment, we have revised the Discussion to include this developmental interpretation.

We also clarify that in our model β denotes the inverse temperature parameter; higher β reflects greater choice precision and value sensitivity, not higher stochasticity. Accordingly, adolescents showed higher β values, indicating more value-based and less exploratory choices, whereas adults displayed relatively greater exploratory cooperation. These group differences were also replicated using hierarchical Bayesian estimation (see Response to Reviewer #1 Q1). In response to this comment, we have added a statement in the Discussion highlighting this developmental interpretation.

“Together, these findings suggest that the differentiation between positive and negative learning rates changes with age, reflecting more selective feedback sensitivity in development, while higher β values in adolescents indicate greater value sensitivity. This interpretation remains tentative and requires further validation in future research.”

(9) A parameter partial correlation matrix (off-diagonal) would be helpful to understand the relationship between parameters in both adolescents and adults separately. This may provide a good overview of how the model properties may change with age (e.g. a^+'s relation to \beta).

We thank the reviewer for this helpful comment. We fully agree that a parameter partial correlation matrix can further elucidate the relationships among parameters. Accordingly, we conducted a partial correlation analysis and added the visually presented results to the revised manuscript as Figure 2-figure supplement 4.

(10) It would be helpful to have Bayes Factors reported with each statistical tests given that several p-values fall within the 0.01 and 0.10.

We thank the reviewer for this important recommendation. We have conducted Bayes factor analyses and reported BF10 for all relevant post hoc comparisons. We also clarified our analysis in the Methods and Materials section:

“Post hoc comparisons were conducted using Bayes factor analyses with MATLAB’s bayesFactor Toolbox (version v3.0, Krekelberg, 2024), with a Cauchy prior scale σ = 0.707.”

(11) Discussion: I believe the language around ruling out failures in mentalising needs to be toned down. RL models do not enable formal representational differences required to assess mentalising, but they can distinguish biases in value learning, which in itself is interesting. If the authors were to show that more complex 'ToM-like' Bayesian models were beaten by RL models across the board, and this did not differ across adults and adolescents, there would be a stronger case to make this claim. I think the authors either need to include Bayesian models in their comparison, or tone down their language on this point, and/or suggest ways in which this point might be more thoroughly investigated (e.g., using structured models on the same task and running comparisons: https://journals.plos.org/plosone/article?id=10.1371/journal.pone.0087619).

We thank the reviewer for the comments. Please see our response to Reviewer 1 (Appraisal & Discussion section) for details.

Reviewer #2 (Recommendations for the authors):

(1) The authors may want to show the winning model earlier (perhaps near the beginning of the Results section, when model parameters are first mentioned).

We thank the reviewer for this suggestion. We agree that highlighting the winning model early improves clarity. Currently, we have mentioned the winning model before the beginning of the Results section. Specifically, in the penultimate paragraph of the Introduction we state:

“We identified the asymmetric RL learning model as the winning model that best explained the cooperative decisions of both adolescents and adults.”

Reviewer #3 (Recommendations for the authors):

(1) In addition to the points mentioned above, I suggest the following:

Clarify plots by clearly explaining each variable. In particular, the indices 1 vs. 1,2 vs 1,2,3 were not immediately understandable.

We thank the reviewer for this suggestion. We agree that the indices were not immediately clear. We have revised the figure captions (Figure 1 and 4) to explicitly define these terms more clearly:

“The x-axis represents the consistency of the partner’s actions in previous trials (t₋₁: last trial; t_−1,2: last two trials;_t−1,2,3: last three trials).”

(2) It's unclear why the index stops at 3. If this isn't the maximum possible number of consecutive cooperation trials, please consider including all relevant data, as adolescents might show a trend similar to adults over more trials.

We thank the reviewer for raising this point. In our exploratory analyses, we also examined longer streaks of consecutive partner cooperation or defection (up to four or five trials). Two empirical considerations led us to set the cutoff at three in the final analyses. First, the influence of partner behavior diminished sharply with temporal distance. In both GLMMs and LMMs, coefficients for earlier partner choices were small and unstable, and their inclusion substantially increased model complexity and multicollinearity. This recency pattern is consistent with learning and decision models emphasizing stronger weighting of recent evidence (Fudenberg & Levine, 2014; Fudenberg & Peysakhovich, 2016). Second, streaks longer than three were rare, especially among some participants, leading to data sparsity and inflated uncertainty. Including these sparse conditions risked biasing group estimates rather than clarifying them. Balancing informativeness and stability, we therefore restricted the index to three consecutive partner choices in the main analyses, which we believe sufficiently capture individuals’ general tendencies in reciprocal cooperation.

(3) The term "reciprocity" may not be necessary. Since it appears to reflect a general preference for cooperation, it may be clearer to refer to the specific behavior or parameter being measured. This would also avoid confusion, especially since adolescents do show negative reciprocity in response to repeated defection.

We thank you for this comment. In our work, we compute the intrinsic reward for reciprocity as p × ω, where p is the partner cooperation expectation and ω is the cooperation preference. In the rPDG, this value framework manifests as a reciprocity-derived reward: sustained mutual cooperation maximizes joint benefits, and the resulting choice pattern reflects a value for reciprocity, contingent on the expected cooperation of the partner. This quantity enters the trade-off between U_cooperation and U_defection and captures the participant’s intrinsic reward for reciprocity versus the additional monetary reward payoff of defection. Therefore, we consider the term “reciprocity” an acceptable statement for this construct.

(4) Interpretation of parameters should closely reflect what they specifically measure.

We thank the reviewer for pointing this out. We have refined the relevant interpretations of parameters in the current Results and Discussion sections.

(5) Prior research has shown links between Theory of Mind (ToM) and cooperation (e.g., Martínez-Velázquez et al., 2024). It would be valuable to test whether this also holds in your dataset.

We thank the reviewer for this thoughtful comment. Although we did not directly measure participants’ ToM, our design allowed us to estimate participants’ trial-by-trial inferences (i.e., expectations) about their partner’s cooperation probability. We therefore treat these cooperation expectations as an indirect representation for belief inference, which is related to ToM processes. To test whether this belief-inference component relates to cooperation in our dataset, we further conducted an exploratory analysis (GLMM_sup4) in which participants’ choices were regressed on their cooperation expectations, group, and the group × cooperation-expectation interaction, controlling for trial number and gender, with random effects. Consistent with the ToM–cooperation link in prior research (MartínezVelázquez et al., 2024), participants’ expectations about their partner’s cooperation significantly predicted their cooperative behavior (Table 14), suggesting that decisions were shaped by social learning about others’ inferred actions. Moreover, the interaction between group and cooperation expectation was not significant, indicating that this inference-driven social learning process likely operates similarly in adolescents and adults. This aligns with our primary modeling results showing that both age groups update beliefs via an asymmetric learning process. We have reported these analyses in the Appendix Analysis section.

(6) More informative table captions would help the reader. Please clarify how variables are coded (e.g., is female = 0 or 1? Is adolescent = 0 or 1?), to avoid the need to search across the manuscript for this information.

We thank the reviewer for raising this point. We have added clear and standardized variable coding in the table notes of all tables to make them more informative and avoid the need to search the paper. We have ensured consistent wording and formatting across all tables.

(7) I hope these comments are helpful and support the authors in further strengthening their manuscript.

We thank the three reviewers for their comments, which have been helpful in strengthening this work.

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eLife Assessment

This important and compelling study establishes a robust computational and experimental framework for the large-scale identification of metallophore biosynthetic clusters. The work advances beyond current standards, providing theoretical and practical value across microbiology, bioinformatics, and evolutionary biology.

Reviewer #1 (Public review):

This work by Reitz, Z. L. et al. developed an automated tool for high-throughput identification of microbial metallophore biosynthetic gene clusters (BGCs) by integrating knowledge of chelating moiety diversity and transporter gene families. The study aimed to create a comprehensive detection system combining chelator-based and transporter-based identification strategies, validate the tool through large-scale genomic mining, and investigate the evolutionary history of metallophore biosynthesis across bacteria.

Major strengths include providing the first automated, high-throughput tool for metallophore BGC identification, representing a significant advancement over manual curation approaches. The ensemble strategy effectively combines complementary detection methods, and experimental validation using HPLC-HRMS strengthens confidence in computational predictions. The work pioneers global analysis of metallophore diversity across the bacterial kingdom and provides a valuable dataset for future computational modeling.

Some limitations merit consideration. First, ground truth datasets derived from manual curation may introduce selection bias toward well-characterized systems, potentially affecting performance assessment accuracy. Second, the model's dependence on known chelating moieties and transporter families constrains its ability to detect novel metallophore architectures, limiting discovery potential in metagenomic datasets. Third, while the proposed evolutionary hypothesis is internally consistent, it lacks further validation.

The authors successfully achieved their stated objectives. The tool demonstrates robust performance metrics and practical utility through large-scale application to representative genomes. Results strongly support their conclusions through rigorous validation, including experimental confirmation of predicted metallophores via HPLC-HRMS analysis.

The work provides significant and immediate impact by enabling transition from labor-intensive manual approaches to automated screening. The comprehensive phylogenetic framework advances understanding of bacterial metal acquisition evolution, informing future studies on microbial metal homeostasis. Community utility is substantial, since the tool and accompanying dataset create essential resources for comparative genomics, algorithm development, and targeted experimental validation of novel metallophores.

Comments on revisions:

I am satisfied with the revisions made by the authors, and they have adequately addressed the concerns raised in the previous version of the manuscript.

Reviewer #2 (Public review):

Summary:

This study presents a systematic and well-executed effort to identify and classify bacterial NRP metallophores. The authors curate key chelator biosynthetic genes from previously characterized NRP-metallophore biosynthetic gene clusters (BGCs) and translate these features into an HMM-based detection module integrated within the antiSMASH platform.

The new algorithm is compared with a transporter-based siderophore prediction approach, demonstrating improved precision and recall. The authors further apply the algorithm to large-scale bacterial genome mining and, through reconciliation of chelator biosynthetic gene trees with the GTDB species tree using eMPRess, infer that several chelating groups may have originated prior to the Great Oxidation Event.<br /> Overall, this work provides a valuable computational framework that will greatly assist future in silico screening and preliminary identification of metallophore-related BGCs across bacterial taxa.

Strengths:

(1) The study provides a comprehensive curation of chelator biosynthetic genes involved in NRP-metallophore biosynthesis and translates this knowledge into an HMM-based detection algorithm, which will be highly useful for the initial screening and annotation of metallophore-related BGCs within antiSMASH.

(2) The genome-wide survey across a large bacterial dataset offers an informative and quantitative overview of the taxonomic distribution of NRP-metallophore biosynthetic chelator groups, thereby expanding our understanding of their phylogenetic prevalence.

(3) The comparative evolutionary analysis, linking chelator biosynthetic genes to bacterial phylogeny, provides an interesting and valuable perspective on the potential origin and diversification of NRP-metallophore chelating groups.

Weaknesses:

(1) Although the rule-based HMM detection performs well in identifying major categories of NRP-metallophore biosynthetic modules, it currently lacks the resolution to discriminate between fine-scale structural or biochemical variations among different metallophore types.

(2) While the comparison with the transporter-based siderophore prediction approach is convincing overall, more information about the dataset balance and composition would be appreciated. In particular, specifying the BGC identities, source organisms, and Gram-positive versus Gram-negative classification would improve transparency. In the supplementary tables, the "Just TonB" section seems to include only BGCs from Gram-negative bacteria-if so, this should be clearly stated, as Gram type strongly influences siderophore transport systems.

Comments on revisions:

The authors have adequately addressed all of my previous comments. I have no further comments on the revised manuscript.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

This work by Reitz, Z. L. et al. developed an automated tool for high-throughput identification of microbial metallophore biosynthetic gene clusters (BGCs) by integrating knowledge of chelating moiety diversity and transporter gene families. The study aimed to create a comprehensive detection system combining chelator-based and transporter-based identification strategies, validate the tool through large-scale genomic mining, and investigate the evolutionary history of metallophore biosynthesis across bacteria.

Major strengths include providing the first automated, high-throughput tool for metallophore BGC identification, representing a significant advancement over manual curation approaches. The ensemble strategy effectively combines complementary detection methods, and experimental validation using HPLC-HRMS strengthens confidence in computational predictions. The work pioneers a global analysis of metallophore diversity across the bacterial kingdom and provides a valuable dataset for future computational modeling.

Some limitations merit consideration. First, ground truth datasets derived from manual curation may introduce selection bias toward well-characterized systems, potentially affecting performance assessment accuracy. Second, the model's dependence on known chelating moieties and transporter families constrains its ability to detect novel metallophore architectures, limiting discovery potential in metagenomic datasets. Third, while the proposed evolutionary hypothesis is internally consistent, it lacks direct validation and remains speculative without additional phylogenetic studies.

The authors successfully achieved their stated objectives. The tool demonstrates robust performance metrics and practical utility through large-scale application to representative genomes. Results strongly support their conclusions through rigorous validation, including experimental confirmation of predicted metallophores via HPLC-HRMS analysis.

The work provides a significant and immediate impact by enabling the transition from labor-intensive manual approaches to automated screening. The comprehensive phylogenetic framework advances understanding of bacterial metal acquisition evolution, informing future studies on microbial metal homeostasis. Community utility is substantial, since the tool and accompanying dataset create essential resources for comparative genomics, algorithm development, and targeted experimental validation of novel metallophores.

We thank the reviewer for their valuable feedback. We appreciate the positive words, and agree with their listed limitations. Regarding the following comment:

“Third, while the proposed evolutionary hypothesis is internally consistent, it lacks direct validation and remains speculative without additional phylogenetic studies.”

We agree that additional phylogenetic analyses are needed in future studies. For the revised manuscript, we have validated our evolutionary hypotheses by additionally analyzing two gene families using the likelihood-based tool AleRax, which implements a probabilistic DTL model. The results were consistent with the eMPRess parsimony-based reconstructions, showing comparable patterns of rare duplication, moderate gene loss, and extensive horizontal transfer. Both methods identified similar lineages as the most probable origin and major recipients of transfer events. This agreement between independent reconciliation frameworks supports the reliability of our evolutionary conclusions. We have added a statement referencing this cross-method validation in the revised manuscript.

Reviewer #2 (Public review):

Summary:

This study presents a systematic and well-executed effort to identify and classify bacterial NRP metallophores. The authors curate key chelator biosynthetic genes from previously characterized NRP-metallophore biosynthetic gene clusters (BGCs) and translate these features into an HMM-based detection module integrated within the antiSMASH platform.

The new algorithm is compared with a transporter-based siderophore prediction approach, demonstrating improved precision and recall. The authors further apply the algorithm to large-scale bacterial genome mining and, through reconciliation of chelator biosynthetic gene trees with the GTDB species tree using eMPRess, infer that several chelating groups may have originated prior to the Great Oxidation Event.

Overall, this work provides a valuable computational framework that will greatly assist future in silico screening and preliminary identification of metallophore-related BGCs across bacterial taxa.

Strengths:

(1) The study provides a comprehensive curation of chelator biosynthetic genes involved in NRP-metallophore biosynthesis and translates this knowledge into an HMM-based detection algorithm, which will be highly useful for the initial screening and annotation of metallophore-related BGCs within antiSMASH.

(2) The genome-wide survey across a large bacterial dataset offers an informative and quantitative overview of the taxonomic distribution of NRP-metallophore biosynthetic chelator groups, thereby expanding our understanding of their phylogenetic prevalence.

(3) The comparative evolutionary analysis, linking chelator biosynthetic genes to bacterial phylogeny, provides an interesting and valuable perspective on the potential origin and diversification of NRP-metallophore chelating groups.

We greatly appreciate these comments.

Weaknesses:

(1) Although the rule-based HMM detection performs well in identifying major categories of NRP-metallophore biosynthetic modules, it currently lacks the resolution to discriminate between fine-scale structural or biochemical variations among different metallophore types.

We agree that this is a current limitation to the methodology. More specific metallophore structural prediction is among our future goals for antiSMASH. We have added a statement to this effect in the conclusion.

(2) While the comparison with the transporter-based siderophore prediction approach is convincing overall, more information about the dataset balance and composition would be appreciated. In particular, specifying the BGC identities, source organisms, and Gram-positive versus Gram-negative classification would improve transparency. In the supplementary tables, the "Just TonB" section seems to include only BGCs from Gram-negative bacteria - if so, this should be clearly stated, as Gram type strongly influences siderophore transport systems.

The reviewer raises good points here. An additional ZIP file containing all BGCs used for the manual curation was inadvertently left out of the supplemental dataset for the first version of the manuscript. We have added columns with source organisms and Gram stain (retrieved from Bacdive) to Table S2. F1 scores were similar for Gram positive and negative subsets, as seen in the new Table S2.

We thank the reviewer for suggesting this additional analysis, and have added a brief statement in the revised manuscript.

The “Just TonB” section (in which we tested the performance of requiring TonB without another transporter) was not used for the manuscript. We will preserve it in the revised Table S2 for transparency.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) In line 43:

"excreted" should be replace by "secreted".

Done.

(2) In lines 158-159:

"we manually predicted metallophore production among a large set of BGCs."

If they are first "annotated with default antiSMASH v6.1", then it is not entirely manual, right? I would suggest making this sentence clearer.

We have revised the language.

(3) In lines 165-169:

It would be good to show the confusion matrix of these results.

The confusion matrices are found in Table S2, columns AL-AR.

(4) In Table 1:

Method names (AntiSMASH rules/Transporter genes) could be misleading, since they are all AntiSMASH-based, right?

We have adjusted the methods to clarify that while the transporter genes were detected using a modified version of antiSMASH, they are not related to our chelator-based detection rule (which is now correctly singular throughout the text).

(5) Line 198:

There are accidental spaces and characters inserted here.

We could not find any accidental spaces and characters here.

(6) Line 209:

"In total, 3,264 NRP metallophore BGC regions were detected"

Is this number correct? I don't see a correspondence in Table 1.

We have added the following sentence to the Table 1 legend: “An additional 54 BGC regions were detected as NRP metallophores without meeting the requirements for the antiSMASH NRPS rule.”

(7) Line 294:

"From B. brennerae, we identified four catecholic compounds"

From the bacterial cells or the culture supernatant? I think it is important to state this in a more precise way. If it is from the supernatant, it could be from EVs.

We state in line 292 that “organic compounds were extracted from the culture supernatants”. As our goal was only to confirm the ability of the strains to produce the predicted metallophores, the precise localization (including cell pellet or EVs) was not explored.

(8) Lines 349-357:

These results would benefit greatly from a visualization strategy.

Thank you, we have added a reference to the existing visualization in Fig. 5, Ring C.

(9) Lines 452-454:

How could clusters be de-replicated? Is there an identity equivalence scheme or similarity metric?

The BGC regions were de-replicated with BiG-SCAPE, which uses multiple similarity metrics as described in Navarro-Muñoz et al, 2020. Clusters could be dereplicated further using a more strict cutoff.

(10) Line 457:

"relatively low number of published genomes."

Could metagenome-assembled genomes help in that matter?

This is a good question, but we find that MAGs are usually too fragmented to yield complete NRPS BGC regions. We’ve added additional sentences earlier in the discussion: “Detection rates were also lower for fragmented genomes; unfortunately, this limitation (inherent to antiSMASH itself) may hinder the identification of metallophore biosynthesis in metagenomes. As long-read sequencing of metagenomes becomes more common, we expect that detection will improve.”

(11) Lines 514-515:

"Adequately-performing pHMMs for Asp and His β-hydroxylase subtypes could not be constructed using the above method."

What is the overall impact of this discrepancy in the methodology for these specific groups?

The phylogeny-based methodology was used to reduce false positives. We expect this method will have improved precision at the possible expense of recall.

(12) Lines 543-545:

"RefSeq representative bacterial genomes were dereplicated at the genus level using R, randomly selecting one genome for each of the 330 genera determined by GTDB"

Isn't it more of a random sampling than a dereplication? Dereplication would involve methods such as ANI computation.

You are correct; we have adjusted the language to clarify.

(13) Lines 559-560: "were filtered to remove clusters on contig edges."

This sentence is confusing because networks will be mentioned soon, and they also have edges (not the edges mentioned here), and they could also be clustered (not the clusters mentioned here). Is there a way to make the terminology clearer?

Thank you, we have adjusted the text to read “BGC regions on contig boundaries”

(14) Line 560:

"The resulting 2,523 BGC regions, as well as 78 previously reported BGCs "

How many were there before filtering?

We have added the number: 3,264

(15) Lines 579-580:

Confusing terminology, as mentioned in Lines 559-560.

Adjusted as above.

General comments and questions:

An objective suggestion to enrich the discussion is to address the role of bacterial extracellular vesicles (EVs) as metallophore carriers. Studies show that EVs, such as outer membrane vesicles, can transport siderophores or other metallophores for iron acquisition in various bacteria, functioning as "public goods" for community-wide nutrient sharing. Highlighting this mechanism would add ecological and functional context to the manuscript. In the future, EV-associated metallophore transport could also be considered for integration into computational detection tools.

We thank the reviewer for the suggestion; however, we do not think that such a discussion is needed. We briefly discuss the ecological function of metallophores as public goods (and public bads) in the first paragraph of the introduction. We did not find any reports that EV-associated genes co-localize with metallophore BGCs, which would be required for their presence to be a useful marker of metallophore production.

Is there a feasible path to more generalizable detection of chelating motifs using chemistry-aware features? For example, a machine learning classifier trained on submolecular descriptors (e.g., functional groups, coordination motifs, SMARTS patterns, graph fingerprints, metal-binding propensity scores) could complement the current genome-based approach and broaden coverage beyond known metallophore families. While the discussion mentions future extensions centered on genomic features, integrating chemical information from predicted or known products (or biosynthetic logic inferred from BGC composition) could be explored. A hybrid framework-linking BGC-derived features with chemistry-derived features-may improve both recall for novel metallophore classes and precision in distinguishing true chelators from confounders, thereby increasing overall accuracy.

We can envision a classifier that uses submolecular descriptors to predict the ability of a molecule to bind metal ions. However, starting with a BGC and accurately predicting the structure of a hitherto unknown chelating moiety will likely prove difficult.  We have added a sentence to the discussion stating that a future tool could use accessory genes to more completely predict chemical structure.

Although the initial analysis was conducted using RefSeq genomes, what are the anticipated challenges and limitations when scaling this method for BGC prospecting in metagenome-assembled genomes (MAGs), particularly considering the inherent quality differences, assembly fragmentation, and taxonomic uncertainties that characterize MAG datasets compared to curated reference genomes?

Please see our response to comment 10, line 457. Our pHMM-based approach is designed to be robust to organism taxonomy; however, fragmentation is a significant barrier to accurate antiSMASH-based BGC detection (including in contig-level single-isolate genomes, see Table 1).

Reviewer #2 (Recommendations for the authors):

(1) In the "Chemical identification of genome-predicted siderophores across taxa" section, it would be helpful to annotate the cross-species similarities between predicted metallophore BGCs and their reference clusters (Ref BGCs). As currently described, the main text seems to highlight the cross-species resolving power of BiG-SCAPE itself rather than demonstrating the taxonomic generalizability of the chelator HMM-based detection module.

Thank you for this comment. We intended to display that the new rule is useful for detecting BGCs in unexplored taxa, but we acknowledge that there is not a great diversity in the strains we selected. We have removed “across taxa” to avoid misleading the reader and clarify our intent.

(2) In addition to using eMPRess for gene-species reconciliation, it may be beneficial to explore or at least reference alternative reconciliation tools to validate the inferred duplication, transfer, and loss (DTL) scenarios. Incorporating such cross-method comparisons would enhance the robustness and credibility of the evolutionary conclusions.

We appreciate this valuable suggestion. To validate the robustness of our reconciliation-based inferences, we additionally analyzed two gene families using the likelihood-based tool AleRax, which implements a probabilistic DTL model. The results were consistent with the eMPRess parsimony-based reconstructions, showing comparable patterns of rare duplication, moderate gene loss, and extensive horizontal transfer. Both methods identified similar lineages as the most probable origin and major recipients of transfer events. This agreement between independent reconciliation frameworks supports the reliability of our evolutionary conclusions. We have added a brief statement referencing this cross-method validation in the revised manuscript.